INTRODUCTION

Pierre Duhem (1861-1916) was a French physicist who wrote extensively on the history and philosophy of science. From a contemporary
perspective, the attractive and unusual feature of Duhem's thought is
its combination of original historical research and philosophical analysis. His most important works in history and philosophy of science are:
La thdorie physique, son objet et sa structure (Paris, 1906); Sozein ta
phainomena: Essai sur la notion de thdorie physique (Paris, 1908);
Etudes sur Ldonard de Vinci, 3 vols., (Paris, 1906-13); and Le Syst~me
du Monde, 10 vols., (Paris, 1913-59).
Duhem's philosophical works had an immediate influence. They were
discussed by the founders of twentieth-century philosophy of science,
including Ernst Mach, Henri Poincar6, the members of the Vienna
Circle, and Karl Popper. A second wave of interest in Duhem's philosophy began with W. V. O. Quine's reference (Quine 1953) to Duhem's
thesis that experimental evidence alone cannot conclusively falsify hypotheses. (This and related theses are referred to in the literature
as the Duhem-Quine thesis.) As a result, Duhem's predominantly
philosophical works were translated into English - as The Aim and
Structure of Physical Theory and To Save the Phenomena (Duhem 1954
and 1969). Moreover, the Librairie Philosophique J. Vrin, a leading
French publisher, reissued both volumes in 1981-82.
By contrast, few of Duhem's far more extensive historical works have
been translated, with five volumes of the Syst~me du Monde actually
remaining in manuscript form until 1954-59. Lately, two volumes of
Duhem's predominantly historical work have appeared in translation as The Evolution of Mechanics and Medieval Cosmology (Duhem 1980
and 1985).
There has been a recent resurgence of interest in Duhem's history
and philosophy of science, as evidenced by the publication of numerous
articles and several books dealing with Duhem, for example, those
of Stanley Jaki (1984), Roberto Maiocchi (1985), and Niall Martin
(forthcoming).
Synthese 83: 179-182, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

The current interest in Duhem's work can be attributed to a change
of climate in the history and philosophy of science. While the dominant
methodology in philosophy of science was logical analysis, discussion
of the Duhem-Quine thesis strayed further and further from any real
contact with Duhem. The decline of logic-based philosophy of science,
and the emergence of new historical approaches, has reopened many
issues addressed by Duhem at the turn of the century: the relation
between history of science and philosophy of science, the nature of
conceptual change, the historical structure of scientific knowledge, and
the relation between science and religion.
In his historical studies, Duhem argued that there were no abrupt
discontinuities between medieval and early modern science (the socalled continuity thesis); that religion played a positive role in the
development of science in the Latin west; and that the history of physics
could be seen as a cumulative whole, defining the direction in which
progress could be expected. Although Duhem's coverage of primary
sources in the medieval and early modern periods is rivaled perhaps
only by Thorndike's History of Magic and Experimental Science, his
work has not been effectively incorporated into the continuing dialogue.
There are several reasons for this. Unlike his philosophical work,
Duhem's historical work was not sympathetically received by influential
contemporaries, notably George Sarton. His supposed main conclusions
were rejected by the next generation of historians of science who presented modern science as discontinuous with the science of the middle
ages. This view was echoed by historically-oriented philosophers of
science who, from the early 1960s, emphasized discontinuities as a
recurrent feature of historical change in science (Thomas Kuhn in The
Structure of Scientific Revolutions, for example). However, the rejection
of Duhem's conclusions occurred before the majority of his historical
works were fully published or translated.
We feel the time is ripe for a reevaluation of Duhem's positions in the
history and philosophy of science. Recently philosophers have begun to
show a genuine interest in historical work. Duhem's historical corpus
is now available in its entirely, and significant portions of it have been
translated. New commentaries are being written on Duhem's thought,
but that work is still isolated and uncoordinated. Historians and philosophers alike are beginning to reject the picture of science as an activity
lurching from one scientific revolution to another, especially for the
period of the Copernican revolution, the chief focus of Duhem's work.

The relations between science and religion are again a matter of active
scholarly interest. In all of the areas Duhem may be seen as a potential
contributor to current debates.
In March 1989, we held a conference entitled "Pierre Duhem: Historian and Philosopher of Science" at Virginia Polytechnic Institute and
State University, as a way of bringing together historians, philosophers,
and others with an active interest in the range of issues sketched above.
Before the conference we circulated our translations of two essays:
'Logical Examination of Physical Theory', and 'Research on the History
of Physical Theories', corresponding to the second and third parts of
Duhem's summary of his own work supporting his candidacy for the
Acad6mie des Sciences. These are reproduced at the beginning of the
present issue. The balance of the present work consists of an edited
selection from the papers presented at the conference. We regret that
limitations of space have made it impossible to present all the contributions to the conference. In several cases the papers have been substantially revised by their authors. We have followed a topical arrangement,
grouping together papers on related subjects, and those that comment
on each other.
We would like to express our thanks to the following individuals,
who led discussions, chaired sessions, or generally facilitated intellectual
exchange: Brian Baigrie, Ezra Brown, Mordechai Feingold, Daniel
Fouke, Steve Fuller, Allen Gabbey, Daniel Garber, James Garrison,
Marjorie Grene, Bernard R. Goldstein, David Lux, Deborah Mayo,
Albert Moyer, Robert Paterson, and Joseph Pitt. We gratefully acknowledge the support of the National Endowment for the Humanities,
an independent Federal Agency, and of the College of Arts and Sciences at Virginia Polytechnic Institute and State University, through
the Center for the Study of Science in Society, the Center for Programs
in the Humanities, the Department of Philosophy and the Department
of History.
REFERENCES
Duhem, P.: 1906, La Thdorie Physique, son objet et sa structure, Chevalier et Rivi6re,
Paris. Translated as Duhem 1954.
Duhem, P.: 1906-13, Etudes sur Ldonard de Vinci, 3 volumes, Hermann, Paris.
Duhem, P.: 1908a, 'Sozein Ta Phainomena: Essai sur la notion de la th6orie physique
de Platon ~ Galil6e', Annales de Philosophic Chrdtienne 156, 113-39,277-302, 352-77,
482-514, 561-92. Republished as Duhem 1908b; translated as Duhem 1969.

Platon ~ Galilde, Hermann, Paris.
Duhem, P.: 1913-59, Le syst~me du monde, Histoire des doctrines cosmologiques de
Platon ~ Copernic, 10 volumes, Hermann, Paris.
Duhem, P.: 1954, The Aim and Structure of Physical Theory, Wiener (trans.), Princeton
University Press, Princeton.
Duhem, P.: 1969, To Save the Phenomena: An essay on the idea of physical theory from
Plato to Galileo, E. Dolan and C. Maschler (trans.), University of Chicago Press,
Chicago.
Duhem, P.: 1980, The Evolution of Mechanics, M. Cole (trans.), Sijthoff and Noordhoff,
Alphen aan den Rijn.
Duhem, P.: 1985, Medieval Cosmology, Theories of lnfinity, Place, Time, Void and
Plurality of Worlds, R. Ariew (trans.), University of Chicago Press, Chicago.
Jaki, S.: 1984, Uneasy Genius: The Life and Work of Pierre Duhem, Nijhoff, The Hague,
The Netherlands.
Maiocchi, R.: 1985, Chimica e filosofia: Scienza, epistemologia, storia e religione nell' opera
de Pierre Duhem, Florence.
Martin, N.: forthcoming, The Philosophy of Physics According to Pierre Duhem, Open
Court, La Salle, Illinois.
Quine, W. V. O.: 1953, 'Two Dogmas of Empiricism', in From a Logical Point of View,
Harvard University Press, Cambridge, Massachusetts.

Virginia Polytechnic Institute and State University
Blacksburg, Virginia 24061
U.S.A.

LOGICAL

EXAMINATION

OF PHYSICAL

THEORY*

Theoretical physics may be treated in the fashion of Cartesians and
Atomists. They resolve the bodies perceived by the senses and instruments into immensely numerous and much smaller bodies of which
reason alone has knowledge. Observable motions are regarded as the
combined effects of the imperceptible motions of these little bodies.
These little bodies are assigned shapes which are few in number and
well defined. Their motions are given by very simple and entirely
general laws. These bodies and these motions are, strictly speaking,
the only real bodies and the only real motions. When they have been
suitably combined, and recognized as together capable of producing
effects equivalent to the phenomena we observe, it is claimed that the
explanation of these phenomena has been discovered.
Our own view, Energetics, does not proceed in this manner. The
principles it embodies and from which it derives conclusions do not
aspire at all to resolve the bodies we perceive or the motions we report
into imperceptible bodies or hidden motions. Energetics presents no
revelations on the true nature of matter. Energetics claims to explain
nothing. Energetics simply gives general rules of which the laws observed by the experimentalist are particular cases.
Alternatively, theoretical physics may be conceived in the [737b]
manner of Newtonians. They reject all hypotheses about imperceptible
bodies and hidden motions, of which the bodies and motions accessible
to the senses and instruments may be composed. The [152] only principles admitted are very general laws known through induction, based
on the observation of facts.
Energetics does not follow the method of the Newtonians. Energetics
recognizes without doubt an experimental origin to the principles it
admits, in the sense that observation has suggested them, and that
experiment has many times counselled their modification. But Energetics does not regard these experiments, which explain the possible
genesis of the principles that Energetics embodies, as capable of conferring any certainty whatever on these principles. Energetics regards
Synthese 83: 183-188, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

these principles as pure postulates, or arbitrary decrees of reason. When
they produce numerous consequences conforming to experimental laws,
Energetics regards them as playing their assigned roles well. Agreement
with the teaching of observation is not, therefore, as the Newtonian
method would require, the beginning of physical theory; it has its place
at the end.
Is Energetics being wise when it refuses equally to follow the method
of Cartesians and Atomists, and the method of the Newtonians? Does
careful examination of the epistemological methods of physics justify
the attitude that Energetics adopts? To this question we have replied:
Yes.
We have criticized the method of the Cartesians and Atomists for
not being autonomous (Duhem 1892, 1906a). The physicist who wishes
to follow it cannot use [738a] exclusively the methods proper to physics,
since, behind perceptible bodies and motions which he regards as appearances, he aspires to get hold of other bodies and other appearances,
which are the only true ones. Here he enters the domain of cosmology.
He no longer has the right to shut his ears to what metaphysics wishes
to tell him about the real nature of matter; hence, as a consequence,
through dependence on metaphysical cosmology, his physics suffers
from all the uncertainties and from all the vicissitudes of that doctrine.
Theories constructed by the method of Cartesians and Atomists are
also condemned to infinite multiplication and to perpetual reformulation. They do not appear to be in any state to assure consensus and
continual progress to science.
We have criticized the Newtonian method for being impractical
(Duhem 1894, 1906a).
A science may progress following the Newtonian method [153] while
its epistemological methods remain those of common sense (sens commun). When science no longer observes facts directly, but substitutes
for them measurements, given by instruments, of magnitudes that mathematical theory alone defines, induction can no longer be practiced in
the manner that the Newtonian method requires.
An experiment in physics is not simply the observation of a phenomenon...An experiment
in physics is the precise observation of a group of phenomena accompanied by the
interpretation of these phenomena. For concrete sense-impressions [donndes] really collected by observation, this interpretation substitutes abstract and symbolic representations, which correspond to them in virtue of physical theories admitted by the observer.
(Duhem 1894, 1906a)

F r o m this t r u i s m f o l l o w n u m e r o u s c o n s e q u e n c e s s t r o n g l y o p p o s e d to
the idea of a science in which each principle may be supplied by
induction:
The physicist can never submit an isolated hypothesis to the control of experiment, but
only a whole group of hypotheses. When experiment is in disagreement with his predictions, it teaches him that one at least of the hypotheses that constitute this group is wrong
and must be modified. But experiment does not show him the one that must be changed.
Here we are a long way from the mechanism of experiment such as people who are
strangers to its functioning readily imagine it. One commonly thinks [738b] that each of
the hypotheses used by physics may be taken in isolation, submitted to the control of
experience, and then, when varied and repeated proofs have established its value, placed
into the totality of science, in an almost definitive fashion. In reality, it is not so; physics
is not a machine that lets itself be disassembled. We cannot address each piece in
isolation, and wait to adjust it until its soundness has been minutely controlled. Physical
science is an organism one must take hold of in one piece. It is an organism in which
one part cannot be made to function without the parts most distant from it coming into
play, some more, some less, all to some degree. If some difficulty, some malaise reveals
itself in its functioning, the physicist will be obliged to discover the organ that needs to
be adjusted or modified without it being possible for him to isolate that organ and [154]
to examine it on its own. The clockmaker to whom one gives a clock that does not work
takes all the wheels out of it and examines them one by one until he finds the bent or
broken one. But the doctor to whom one brings a sick person cannot dissect the patient
to establish his diagnosis; he must discover the seat of the illness only through the
inspection of effects produced on the whole body. The physicist responsible for repairing
a rickety theory resembles the latter, not the former. (Duhem 1894,1906a)
P h y s i c a l t h e o r y is n o t a n e x p l a n a t i o n o f t h e i n o r g a n i c w o r l d ; still less
is it a n i n d u c t i v e g e n e r a l i z a t i o n o f t h e t e a c h i n g s of e x p e r i e n c e . So w h a t
is it? ( D u h e m 1 8 9 3 b , 1 9 0 6 a , 1908a, 1908d). Is t h e o r y s i m p l y , as t h e
P r a g m a t i s t s w o u l d like it, a t o o l [device] t h a t gives us t r u t h s o f e m p i r i c a l
k n o w l e d g e i n t h e e a s i e s t m a n n e r , p e r m i t s u s to m a k e f a s t e r a n d m o r e
p r o f i t a b l e u s e o f it i n o u r a c t i o n o n t h e e x t e r n a l w o r l d , b u t d o e s n o t
t e a c h us a n y t h i n g a b o u t this w o r l d t h a t we w o u l d n o t a l r e a d y h a v e b e e n
taught by experience alone?
O r , o n t h e c o n t r a r y , d o e s t h e o r y t e a c h us a b o u t w h a t is r e a l s o m e t h i n g t h a t e x p e r i e n c e h a s n o t t a u g h t us a n d w o u l d n o t b e a b l e to
t e a c h us, s o m e t h i n g t h a t w o u l d b e t r a n s c e n d e n t to p u r e l y e m p i r i c a l
knowledge?
If w e w e r e to r e s p o n d a f f i r m a t i v e l y to this last q u e s t i o n , we w o u l d
b e s a y i n g t h a t p h y s i c a l t h e o r y is t r u e , t h a t it h a s v a l u e as k n o w l e d g e .
If, o n t h e c o n t r a r y it is t h e first q u e s t i o n t h a t c o n s t r a i n s us to say " Y e s " ,
w e w o u l d h a v e to say also t h a t p h y s i c a l t h e o r y is n o t t r u e , b u t s i m p l y

c o n v e n i e n t ; t h a t it h a s n o v a l u e as k n o w l e d g e ,
v a l u e . [739a]

but solely practical

When the physicist, turning his attention to the science he is constructing, submits the
procedures that he has used to a rigorous examination, he discovers nothing able to
introduce into the edifice the least particle of truth, except experimental observation. Of
propositions attempting to state the facts of experience and of these alone we may say:
It is true or: It is false. Of these alone we may assert that they will not permit illogicality,
and that of two contradictory propositions one at least must be rejected. As for propositions introduced by theory, they are neither true nor false. They are simply convenient
or inconvenient. If the physicist finds it convenient to construct two chapters [155] of
physics with the aid of hypotheses that contradict each other., he is free to do so. The
principle of contradiction is able to judge truth and falsity decisively. It has no ability to
decide what is useful and what is not. Therefore, to require physical theory to observe
a rigorous logical unity in its development would be to exert an unjust and insupportable
tyranny on the intellect of the physicist.
When, after having submitted the science that concerns him to this minute examination,
the physicist returns to his own concerns, when he takes notice of the tendencies that
direct the steps of his reasoning, he recognizes at the same time that all his most profound
and most powerful aspirations are crushed by the heartbreaking conclusions of his analysis. No, he cannot bring himself to see in physical theory only a collection of practical
procedures, a bag full of tools. No, he cannot believe that physical theory only catalogs
knowledge accumulated through empirical science, without changing the nature of this
knowledge in the least, and without imprinting it with a character that experience alone
would not be able to engrave at all. If there were no more in physical theory than critical
examination had shown him in it, he would stop devoting his time and his efforts to a
work of so little importance. The study o f the method o f physical science is powerless to
show the physicist the reason that leads him to construct physical theory.
No physicist, however positivistic we imagine him to be, would be able to deny this
declaration. But his positivism must be sufficiently rigorous that he would not go beyond
this declaration, and say that his efforts towards a physical theory, which is always more
unitary and always more general, are reasonable, although critical examination of the
method of physical science has not been able to discover a reasonable basis for it. Such
a basis, might be [739b] expressed precisely in the following propositions:
Physical theory gives us a type of knowledge of the external world not reducible to
purely empirical knowledge. This knowledge comes neither from experience nor from
the mathematical procedures the theory employs. Purely logical dissection of the theory
would not discover the crack by which this knowledge introduces itself into the edifice
of physics, through a route which the physicist can no more deny is real, any more than
he can describe its course. This knowledge derives from a truth [156] other than the
truths which our instruments are appropriate to grasp. The order into which theory places
the results of observation does not find its full and complete justification in its practical
or aesthetic aspects. We come to see, on the other hand, that this order is, or tends to
become, a natural classification. Through an analogy the nature of which escapes the
grasp of physics, but the existence of which imposes itself on the mind of the physicist
as certain, we come to know that this order corresponds better and better to a certain
overarching order.

In a word, the physicist is forced to recognize that it would be irrational to work towards
the progress o f physical theory if that theory were not the more and more clear, and more
and more precise reflection o f a metaphysics. The belief in an order transcending physics
is the sole reason for the existence o f physical theory.

The attitude, hostile or favorable by turns, which all physicists take towards this
declaration is captured in this saying of Pascal: "Our powerlessness to prove anything is
invulnerable to Dogmatism; our idea of truth is invulnerable to Skepticism [Pyrrhonisme]." (Duhem 1908a)
Separated from the various schools of Pragmatists on the subject of
the value of physical theory, we do not take our stand, in any circumstances, among the number of their followers. The analysis we have
given of experiments in physics shows fact to be completely interpenetrated by theoretical interpretation, to the point where it becomes
impossible to express fact in isolation from theory, in such experiments.
This analysis has found great favor on the side of many Pragmatists.
They have applied it to the most diverse fields: to history, to exegesis,
to theology. We do not deny that this extension is legitimate to some
extent. However different the problems may be, it is always the same
human intellect that exerts itself to resolve them. In the same way,
there is always something common in the several procedures reason
employs. But if it is good to notice the analogies between our diverse
scientific methods [740a], it is on condition that we do not forget the
differences separating them. And, when we compare the method of
physics, so strangely specialized in the application of mathematical
theory and by the use of instruments of measurement, to other methods,
there are surely more differences to describe than analogies to discover.
[157] We accept that physical theory is able to obtain a certain type
of knowledge of the nature of things; but this knowledge, which is
purely analogical, appears to us as the terminus of theoretical progress,
as the limit which theory endlessly approaches without ever reaching
it. On the contrary, the schools of the Cartesians and Atomists place
hypothetical knowledge of the nature of things at the origin of physical
theory. If, therefore, we separate ourselves from the Pragmatists, it is
not to take a place among the Cartesians or the Atomists.
The school of the neo-Atomists, the doctrines of which center on the
concept of the electron, have taken up again with superb confidence
the method we refuse to follow. This school thinks its hypotheses attain
at last the inner structure of matter: that they make us see the elements
as if some extraordinary ultra-microscope were to enlarge them until
they are made perceptible to us.

We do not share this confidence. We are not able to recognize in
these hypotheses a clairvoyant vision of what there is beyond sensible
things; we regard them only as models. We have never denied the
usefulness of these models, dear to physicists of the English school
(Duhem 1893a, 1906a): We believe they lend an indispensable aid to
minds more broad than deep, more able to imagine the concrete than
to conceive the abstract. But the time will undoubtedly come when,
through their increasing complications, these representations or models
will cease to be aids for the physicist. H e will regard them instead
as embarrassments and impediments. Putting aside these hypothetical
mechanisms, he will carefully release from them the experimental laws
they have helped to discover. Without pretending to explain these laws,
he will seek to classify them according to the method we have just
analyzed and to understand them within a modified and a broader
Energetics.
NOTES

* Part II of Duhem 1917, pp. 151-57, translated by Peter Barker and Roger Ariew;
published also by Duhem in Duhem 1913a, pp. 73740.

RESEARCH

ON T H E H I S T O R Y OF P H Y S I C A L
THEORIES*

All abstract thought requires the control of facts; all scientific theories
call for comparison with experience. Our logical considerations about
the proper method of physics cannot be judged rationally unless they are
confronted with the teachings of history. We must now apply ourselves
toward gathering these teachings.
During antiquity, the Middle Ages, and the Renaissance, there has
hardly been more than one part of physical theory in which mathematical theory had sufficient development and observation had sufficient
precision for Us to discuss their mutual relations; this part is astronomy.
With regard to the nature and value of astronomical theory, one
might say that the Greek mind, so admirably supple, penetrating, and
varied, conceived all the systems that our time has seen flourish again
(Duhem 1908b). But among these systems, there is one that wins over
the approbation of the most profound thinkers. It can be summarized
in the following principle that Plato taught to those who wanted to
work in astronomy: "When taking certain assumptions as our point of
departure, one must attempt to save what appears to the senses Tinon upotethenton .... sozein ta phainomena." And this principle spans
the Arabic, Jewish, and Christian Middle Ages, is repeated at the time
of the Renaissance, is explained, specified, or contested, up to the day
when Andre.as Osiander formulates it thus, in the preface that he placed
at the head of Copernicus' book: "Neque enim necesse est eas hypotheses
esse veras, imo, ne verisimiles quidem, sed sufficit hoc u n u m [159] si
calculum observationibus congruentem exhibeant. (It is neither necessary that these hypotheses be true nor even that they be likely, but
only one thing suffices, namely, that the calculation to which they
lead agrees with the result of observation.)" For two thousand years,
therefore, the majority of those who reflected on the nature and value
of the mathematical theory used by the physicists agreed to proclaim
the axiom that Energetics came to take as its own: the first postulates
of physical theory are not given as affirmations of certain suprasensible
realities; they are general rules which would have played their role
Synthese 83: 189-200, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

admirably if the particular consequences deduced from them agreed
with the observed phenomena.
The method followed by Energetics is not an innovation; it can call
forth the most ancient, most continuous, and most noble tradition
for itself. But, what should we say about the essential notions and
fundamental principles of that science? Logic does not require any
justification of Energetics when it defines these notions and posits these
principles; Logic leaves it free to posit its foundations as it wishes, as
long as, having reached its zenith, the edifice is capable of accommodating without constraint or disorder the laws ascertained by the experimenter. Is that to say that Energetics defines these notions haphazardly
and posits these principles without reason? Not at all. Although Logic
does not impose any constraint upon Energetics, the teachings of history
are an extremely sure and meticulous guide for it; the remembrance of
past attempts, and of their happy or unhappy fate, prevents Energetics
from receiving hypotheses which have led older theories to their ruin,
or persuades it to adopt ideas which have already been shown to be
fruitful. Energetics would not be able to prove its postulates, and does
not have to prove them; but by retracing the vicissitudes they have
gone through before they came to have their present form, it can gain
our confidence for them - that is, it can obtain some credit for them
at the moment when their consequences would be receiving the experimental confirmation we have anticipated.
We undertook to write the history of the great laws of statics and
dynamics in order for Energetics to be in the position to understand and
exhibit the evolution experienced by each of its fundamental principles.
It was known that important reflections on statics were sketched in
the manuscript notes of Leonardo da Vinci. Our reading of Leonardo
da Vinci and Cardano drew our attention to the unexplored statics of
the Middle Ages; and soon, the act of [160] laying bare all the manuscripts on statics at the public libraries of Paris yielded unexpected
discoveries in abundance (Duhem 1905-1906, vol. 1). The Christian
Middle Ages had known the writings on statics composed by the
Greeks; some of these writings came to it directly and others through
the intermediary of Arabic commentaries. But the Latins who read
those works were not at all the slavish commentators, devoid of any
invention, that people were pleased to depict to us. The remains of
Greek thought that they received from Byzantium or from Islamic
science did not remain in their minds as in a sterile depository; these

relics were sufficient to awaken their attention, to fertilize their intellect. And, from the thirteenth century on, perhaps even before that
time, the school of Jordanus opened to students of mechanics some
paths that antiquity had not known.
At first, the intuitions of Jordanus de Nemore were extremely vague
and extremely uncertain; some grave errors were intermixed with some
great truths. But soon, the disciples of the inventor refined the master's
thought. The errors were eclipsed and began to disappear; the truths
became more precise and firmer, and several of the most important
laws of statics were finally established with complete certainty.
Specifically, we owe to the school of Jordanus a principle whose
importance was demonstrated, with ever-growing clarity, during the
development of statics. Without analogy to the postulates specific to
the lever, of which Archimedes' deductions made use, this principle
has only a distant affinity to the inexact axiom invoked by Aristotle's
Mechanical Questions. It affirms that the same motive force can lift
different weights to different heights, as long as the heights are inversely
proportional to the weights. Applied by Jordanus only to the straight
lever, this principle allowed one of his disciples to ascertain the law of
the equilibrium of weights on an inclined plane and, by an admirable
geometric device, the law of the equilibrium of the bent lever.
Descartes took up almost without change what this anonymous mathematician of the thirteenth century had written; and henceforth, from
Descartes to Wallis, from Wallis to Bernoulli, and from the former to
Lagrange, then to Gibbs, the principle of virtual displacements continued to be extended.
[161] Toward the year 1360, Albert of Saxony, a master of arts of
the University of Paris, wrote:
It is not true that every part of a weight tends toward its center becoming the center of
the world - which would be impossible. It is the whole that descends in such a way that
its center becomes the center of the world, and all the parts tend toward the goal that
the center of the whole becomes the center of the world; therefore, they do not impede
one another ....

This center, this point which, in every weight, tends to place itself at
the center of the world, is, as Albert repeated on several occasions,
the center of gravity.
Therefore, every weight moves as if its center of gravity sought the
center of the world - a false idea that, during the seventeenth century,

engendered many errors, engaged the greatest geometers, and yielded
only after a fierce discussion (Duhem 1905-1906, vol.1); but, in the
meanwhile, it was a fertile idea that imparted new truths to statics. In
fact, it immediately gave statics the following proposition: a system of
weights is in equilibrium when the center of gravity is as low as possible.
Torricelli and Pascal one day accepted that proposition as the foundation of all statics, and it gave rise to the theorem of Lagrange and
Lejeune-Dirichlet on the stability of equilibrium.
Leonardo da Vinci, that indefatigable reader, leafed through and
meditated endlessly upon the writings of the school of Jordanus, on the
one hand, and the scholastic questions of Albert of Saxony, on the
other. The former, by acquainting him with the law of the equilibrium
of the bent lever, led him to the following memorable law, which
governs the composition of concurrent forces: with respect to a point
taken on one of the composing forces or on the resulting force, the two
other forces have equal moments (Duhem 1904, 1905-1906, vol.2,
1906-1913, vol. 1, pp. 257-319). Moreover, Albert of Saxony's ideas
on the role of the center of gravity allowed him to discover the rule of
the polygon of support (Duhem 1905-1906, vol. 2, 1906-1913, vol. 1,
pp. 257-319), which Villalpand plagiarized (Duhem 1905-1906, vol. 2,
1906-1913, vol. 1, pp. 53-89). Thus, we find the origins of several
principles essential to statics in the writings composed during the thirteenth and fourteenth centuries.
Was it the same for dynamics?
The dynamics begun by Galileo - and by those who emulated him
and his disciples, such as Baliani, Torricelli, Descartes, Beeckmann,
and Gassendi - is not an innovation; the modern intellect did not
produce it, suddenly and completely, as soon as the reading [162] of
Archimedes revealed the art of applying geometry to natural effects.
Galileo and his contemporaries made use of the mathematical skill,
acquired in antiquity by the geometers while they practiced their trade,
in order to render more precise and to develop a science of mechanics,
a science whose principles and most essential propositions had been
posited by the Christian Middle Ages. The physicists who taught this
mechanics during the fourteenth century at the University of Paris had
conceived it by taking observation as their guide; they substituted it for
Aristotle's dynamics, convinced of its inability to 'save the phenomena'.
At the time of the Renaissance, the superstitious archaism, which
delighted equally in the wit of the humanists and in the Averroist

habit of retrograde scholasticism, rejected this doctrine of the 'Moderns'. The reaction against the dynamics of the 'Parisians' and the
inadmissible dynamics of the Stagirite was powerful, particularly in
Italy (Duhem 1906-1913, vol. 3, pp. 113-261). But, in spite of this
hardheaded resistance, the Parisian tradition found some masters and
savants to maintain it and develop it outside the schools, as well as in
the universities. Galileo and his followers were the heirs of this Parisian
tradition. When we see the science of Galileo triumph over the stubborn
Peripatetism of Cremonini, we believe, since we are ill-informed about
the history of human thought, that we are witness to the victory of
modern, young science over medieval philosophy, so stubborn in its
mechanical repetition. In truth, we are contemplating the well-paved
triumph of the science born at Paris during the fourteenth century over
the doctrines of Aristotle and Averroes, restored into repute by the
Italian Renaissance.
No motion can last unless it is maintained by the continuous action
of a motive power directly and immediately applied to the mobile. That
is the axiom upon which all of Aristotle's dynamics rests.
In conformity with this principle, the Stagirite wanted to apply a
motive power for transporting the arrow, which continues to fly after
having left the bow. He believed he had found this power in the
perturbation of air; it is air, struck by a hand or by a ballistic machine,
which supports and carries forth the projectile.
This hypothesis, which seems to push verisimilitude to the brink of
ridicule, appears to have been accepted almost unanimously [163] by
the physicists of Antiquity (Duhem 1906-1913, vol. 2, pp. 97-281).
Only one of them spoke clearly against it, and he, living during the final
years of Greek philosophy, is almost separated from that philosophy by
his Christian faith; we are referring to John of Alexandria, surnamed
Philoponus. After having demonstrated what was inadmissible about
the Peripatetic doctrine of projectile motion, John Philoponus declared
that the arrow continues to move without any motor applied to it,
because the string has given it an energy that plays the role of motive
virtue.
The last Greek thinkers and Arabic philosophers did not even mention the doctrine of John the Christian, for whom Simplicius and Averroes had only sarcastic comments. The Christian Middle Ages, in the
grip of a naive admiration for the newly discovered Peripatetic science,
at first shared the Greek and Arabic commentators' disdain for Philoponus' hypotheses; Saint Thomas Aquinas mentions the hypothesis only
to warn those who might be seduced by it.

But, following the condemnations brought forth in 1277 by Etienne
Tempier, the Bishop of Paris, against a set of theses upheld by 'Aristotle
and his followers', there appeared a large movement that liberated
Christian thought from the shackles of Peripatetic and Neoplatonic
philosophy and produced what the Renaissance archaically called the
science of the 'Moderns'.
William of Ockham attacked Aristotle's theory of projectile motion
with his customary zeal (Duhem 1906-1913, vol. 2, pp. 97-281). He
w a s content, however, in destroying without building, but his critiques
restored into repute the doctrine of John Philoponus for some of Duns
Scotus' disciples. The energy, the motive virtue of which Philoponus
spoke, reappeared under the name impetus. The hypothesis of impetus
what was impressed into the projectile by the hand or the machine
that launches i t - w a s taken over by a secular master of the Faculty of
Arts of Paris, a physicist of great genius (Duhem 1906-1913, vol. 3,
pp. 1-112). Toward the middle of the fourteenth century, John Buridan
took impetus as the foundation of a dynamics that 'accords with all the
phenomena'.
The role that impetus played in Buridan's dynamics is exactly the
one that Galileo attributed to impeto or momento, Descartes to quantity
of motion, and Leibniz finally to vis viva. So exact is this correspondence
that, in order to exhibit [164] Galileo's dynamics, Torricelli, in his
Lezioni accademiche, often took up Buridan's reasons and almost his
exact words.
Buridan took this impetus, which remains without change within the
projectile unless constantly destroyed by the resistance of the medium
and by the action of weight contrary to the motion, to be proportional
to the quantity of primary matter within the body; he conceived and
described that quantity in terms almost identical to those Newton used
to define mass. With equal masses, the impetus increases as the speed
increases; Buridan prudently abstained from further specifying the relation between the magnitude of the impetus and that of the speed.
More daring, Galileo and Descartes affirmed that this relation is reduced to proportionality; thus they obtained an erroneous estimation
for impeto and for quantity of motion, which Leibniz needed to rectify.
Gravity increases indefinitely, as does the resistance of the medium,
and it ends up annihilating the impetus of a mobile thrown upward,
since such a motion is contrary to the natural tendency of that gravity.
But with a falling mobile, motion conforms to the tendency of gravity.
-

Thus, the impetus must be augmented indefinitely and speed must
increase constantly during the motion. Such is, according to Buridan,
the explanation for the acceleration observed in the fall of a weight,
an acceleration that Aristotle's science already understood, but for
which the Greek, Arabic, or Christian commentators of the Stagirite
had given unacceptable reasons.
This dynamics exposited by Buridan presents in a purely qualitative,
but always exact fashion the truths that the notions of vis viva and work
allow us to formulate in qu~intitative language.
The philosopher of B6thune was not alone in professing this dynamics; his most brilliant disciples, Albert of Saxony and Nicole Oresme,
adopted it and taught it. The French writings of Oresme allowed it to
be understood even by those who were not clerics (Duhem 1906-1913,
vol. 3, pp. 261-583).
When no resistant medium, when no natural tendency analogous to
gravity is opposed to motion, the impetus maintains a constant intensity.
The mobile, to which a motion of translation or of rotation has been
communicated, continues [165] to move indefinitely in the same
manner, with a constant speed. That is the form under which the law
of inertia preseffted itself to the mind of Buridan; it is the form under
which it was received by Galileo.
From this law of inertia, Buridan derived a corollary whose novelty
we should admire (Duhem 1906-1913, vol. 2, pp. 97-281). The celestial
orbs move eternally with a constant speed, because, according to the
axiom of Aristotle's dynamics, each one of them is subject to an eternal
motor of immutable power. The Stagirite's philosophy required that
such a motor be an intelligence separated from matter. The study of
the motive intelligences of the celestial orbs was not only the crowning
glory of Peripatetic metaphysics, it was the doctrine about which revolved all the Neoplatonic metaphysics of the Greeks and Arabs; the
Scholastics of the thirteenth century did not hesitate to receive this
heritage of the pagan theologies into their Christian systems.
Now, Buridan had the boldness to write these lines:
Since the creation of the world, G o d has m o v e d the heavens by m o v e m e n t s identical to
those by which they are actually moved. Hence, he has impressed upon t h e m some
impetus by which they continue to be m o v e d uniformly. In effect, these impetus, encountering no contrary resistance, are never destroyed or weakened . . . . According to this
imagination, it is not necessary to posit the existence of intelligences moving the celestial
bodies in an appropriate manner.

Buridan expressed this thought in various places; Albert of Saxony
formulated it also (Duhem 1906-1913, vol. 2, pp. 97-281); and Nicole
Oresme, in order to formulate it, made use of this comparison: "Violence excepted, the situation is similar to a man making a clock and
letting it go and move by itself."
If we wanted to draw a precise line separating the period of ancient
science from the period of modern science, we would have to draw it
at the instant when John Buridan conceived this theory, at the instant
when the stars stopped being perceived as moved by divine beings,
when celestial motions and sublunar motions were admitted as dependent upon a single mechanics.
This mechanics, both celestial and terrestrial, to which Newton gave
the form we admire today, [166] was attempting to constitute itself ever
since the fourteenth century. The writings of Francis of Mayronnes
(Duhem 1913b) and of Albert of Saxony (Duhem 1909) during the
whole of that century teach us that there were physicists who maintained
that one could construct a more satisfactory astronomical system than
the one in which the earth is deprived of motion, by assuming the earth
mobile, and heaven and the fixed stars immobile. Of these physicists,
Nicole Oresme developed the reasons for this doctrine (Duhem 1909)
with a fullness, clarity, and precision that Copernicus was far from
achieving. He attributed to the earth a natural impetus similar to the
one Buridan attributed to the celestial orbs. In order to account for
the vertical fall of weights, he allowed that one must compose this
impetus by which the mobile rotates around the earth with the impetus
engendered by weight. The principle he distinctly formulated was only
obscurely indicated by Copernicus and merely repeated by Giordano
Bruno (Duhem 1906-1913, vol. 3, pp. 113-261). Galileo used geometry
to derive the consequences of that principle but without correcting the
incorrect form of the law of inertia implied in it.
While dynamics was being established, the laws of falling weights
were being discovered a few at a time.
In 1368, Albert of Saxony proposed these two hypotheses: the speed
of the fall is proportional to the time elapsed from the start; the speed
of the fall is proportional to the path travelled (Duhem 1908c,
1906-1913, vol. 3, 261-568). He did not choose between these two
laws. The theologian, Peter Tataret, who taught at Paris toward the
end of the fifteenth century, reproduced textually what Albert of

Saxony had said. The great reader of Albert of Saxony, Leonardo da
Vinci, after having accepted the second of these two hypotheses, rallied
to the first. But he was not able to discover the law of spaces traversed
by a falling weight; by a reasoning that Baliani took up, he concluded
that the spaces traversed in laps of equal and successive times are as
the series of whole numbers, while, in truth, they are as the series of
odd numbers.
However, the rule that allowed the evaluation of the space traversed,
in a certain time, by a mobile moving in a uniformly varied motion was
known for a long time. Whether this rule was discovered at Paris,
during the time of John Buridan, or at Oxford, during the time of
Swineshead, it was formulated clearly in the work in which Nicole
Oresme posited the essential principles of analytic geometry (Duhem
1906-1913, vol. 3, 261-568). [167] Moreover, the demonstration that
serves to justify it is identical to the one Galileo gave for it.
This rule was not forgotten from the time of Nicole Oresme to the
time of Leonardo da Vinci; formulated in most of the treatises produced
by the thorny dialectics of Oxford, it was discussed in the various
commentaries of which these treatises were the object, during the fifteenth century, in Italy, and then in the various works of physics written
at the start of the sixteenth century by Parisian Scholasticism.
Noiae of the treatises of which we have just spoken, however, contains
the thought of applying this rule to the fall of weights. We encounter
that thought for the first time in the Questions on Aristotle's Physics
published in 1545 by Domingo de Soto (Duhem 1906-1913, vol. 3,
261-568). A student of the Parisian Scholastics, most of whose physical
theories he received and adopted, the Spanish Dominican de Soto
admitted that the fall of a weight is uniformly accelerated, that the
vertical rise o f a projectile is uniformly retarded, and, in order to
calculate the path traversed in each of these two movements, correctly
used the rule formulated by Oresme. That is to say, he knew the law
of falling weights, whose discovery is attributed to Galileo. Moreover,
he did not claim the discovery of these laws; rather, he seemed to be
giving them as commonly received truths. No doubt they were accepted
at the time by the Paris masters whose lessons de Soto followed. Thus,
from William of Ockham to Domingo de Soto, we see the physicists of
the Parisian school posit the foundations of the mechanics Galileo, his
contemporaries, and his disciples developed.

Among those who, before Galileo, received the tradition of Parisian
Scholasticism, there was none who deserved more attention than Leonardo da Vinci. During the time he lived, Italy firmly resisted the
penetration of the mechanics of the 'moderni', of the 'juniores'. Among
the university masters, even those who leaned in the direction of the
terminalist doctrines of Paris, merely reproduced, under an abridged
and often hesitant form, the essential assertions of that mechanics; they
were far from being capable of having it produce any of the fruits of
which it was the flower.
Leonardo da Vinci, on the contrary, was not satisfied in admitting
the general principles of the dynamics of impetus. [168] He meditated
endlessly upon these principles, and turned them every which way,
pressing them in some fashion to deliver the consequences they enclosed
(Duhem 1906-1913, vol. 3, 113-261). The essential hypothesis of that
dynamics was similar to the first form of the law of vis viva; da Vinci
perceived in it the idea of the conservation of energy, and he found
some terms of almost prophetic clarity to express that idea (Duhem
1906-1913, vol. 2, pp. 97-281). Albert of Saxony had left his reader
in suspense between the two laws of falling weights, the one correct
and the other inadmissible. After some tentative steps that Galileo also
went through, da Vinci came upon the choice of the correct law. He
extended it happily to the fall of a weight along an inclined plane
(Duhem 1906-1913, vol. 3, 261-568). Through a study of composite
impeto, he attempted the first explanation of the curvilinear trajectory
of projectiles, an explanation that was completed by Galileo and Torricelli (Duhem 1906-1913, vol. 2, pp. 97-281). He glimpsed the correction that needed to be brought to the law of inertia announced by
Buridan, and he prepared for the work that Benedetti and Descartes
accomplished (Duhem 1906-1913, vol. 3, pp. 113-261).
No doubt, da Vinci did not always recognize the richness of the
treasures accumulated by Parisian Scholasticism. He set aside some of
them, which would have been complementary to his doctrine of mechanics. He misunderstood the role that impetus must play in the
explanation of the accelerated fall of weights (Duhem 1906-1913, vol.
3, pp. 113-261). He was unaware of the rule which allows the calculation of the path traversed by a body moving of uniformly accelerated
motion. It is no less true that the whole of his physics placed him among
those the Italians of his time called the Parisians.
Moreover, this title was properly given to him. In fact, his principles

of physics were derived from an assiduous reading of Albert of Saxony,
and probably also from a meditation upon the writings of Nicholas of
Cusa (Duhem 1906-1913, vol. 2, pp. 97-281); and Nicholas of Cusa
was also an initiate of the Parisian mechanics. Da Vinci is therefore
given his proper place among the Parisian precursors of Galileo.
We have just retraced, in broad strokes, the essential laws of equilibrium and motion at their infancy. On occasion, we have described
some portions of physics at the time when that science had reached
adolescence. Thus, we have inquired into the sources of the hydrostatic
theories of Pascal (Duhem 1905), detailed the role that Mersenne
played in the discovery of the weight of air (Duhem 1906b), and
sketched the genesis of [169] the doctrine of universal attraction
(Duhem 1906a). Now, we did not see any essential principles proceed
from the desire to resolve the bodies we perceive and touch into imperceptible, but simpler bodies; we saw none that had as aim to explain
sensible motions by means of hidden motions. Atomism did not contribute to their formation in any way. All of them were born from the
desire to formulate some very general rules whose consequences 'saved
the phenomena'. Thus, the history of the development of physics has
come to confirm what the logical analysis of the methods used by that
science had taught us. From the former and from the latter, we have
gained a renewal of faith in the future fruitfulness of the method of
Energetics.
NOTE
*Part III of Duhem 1917, pp. 158-69, translated by Roger Ariew and Peter Barker.

REFERENCES
Duhem, P.: 1892, 'Quelques rdflexions au sujet des th6ories physiques', Revue des Questions scientifiques 1.
Duhem, P.: 1893a, 'L'Ecole anglaise et les th6ories physiques', Revue des Questions
scientifiques 2.
Duhem, P.: 1893b, 'Physique et M6taphysique', Revue des Questions scientifiques 2.
Duhem, P.: 1894, 'Quelques rdflexions au sujet de la Physique exp6rimentale', Revue
des Questions scientifiques 3.
Duhem, P.: 1904, 'Ldonard de Vinci et la composition des forces concourantes', Bibliotheca mathematica 4.
Duhem, P.: 1905, 'Le principe de Pascal; essai historique', Revue gdn(rale des Sciences
pures et appliqu~es.

Duhem, P.: 1905-1906, Les origines de la statique, 2 vols., Paris.
Duhem, P.: 1906a, La Thdorie physique, son objet et sa structure, Paris.
Duhem, P.: 1906b, 'Le P. Matin Mersenne et la Pesanteur de l'air - Premi6re partie: Le
P. Mersenne et le poids sp6cifique de Fair', and'Le P. Marin Mersenne et la Pesanteur
de Fair - Seconde partie: Le P. Mersenne et l'exp6rience du Puy-de-D6me', Revue
gdndrale des Sciences pures et appliqudes.
Duhem, P.: 1906-1913, Etudes sur L~onard de Vinci, ceux qu'il a lus et ceux qui l'ont lu,
3 vols., Paris.
Duhem, P.: 1908a, 'La valeur de la th6orie physique, ~ propos d'un livre r6cent',
Revue g~n~rale des Sciences pures et appliqudes.
Duhem, P.: 1908b, Sozein Ta Phainomena - Essai sur la notion de thdorie physique de
Platon gl Galilde, Paris.
Duhem, P.: 1908c, 'Sur la d6couverte de la loi des chute des graves', Comptes rendus
des sgances de l'Acad~mie des Sciences 146.
Duhem, P.: 1908d, 'Sur un fragment, inconnu jusqu'ici, de l'Opus Tertium de Roger
Bacon', Archivium Franciscannum historicum 1.
Duhem, P.: 1909, 'Un pr6curseur frangais de Copernic: Nicole Oresme (1377)', Revue
gdndrale des Sciences pures et appliqu(es.
Duhem, P.: 1913a, 'Examen logique de th6orie physique', Revue Scientifique (Revue
Rose).
Duhem, P.: 1913b, 'Frangois de Meyronnes O.F.M. et la question de la rotation de la
terre', Archivium Franciscannum historicum 6.
Duhem, P.: 1917, 'Notice sur les titres et travaux scientifiques de Pierre Duhem, r6dig6e
par lui-m6me lors de sa candidature ~ l'acad6mie des sciences (mai 1913)', in M~moires
de la soci(t( des sciences physiques et naturelles de Bordeaux, series 7, vol. 1.

D U H E M , THE A R A B S ,

AND THE HISTORY

OF

COSMOLOGY

ABSTRACT. Duhem has generally been understood to have maintained that the major
Greek astronomers were instrumentalists. This view has emerged mainly from a reading
of his 1908 publication To Save the Phenomena. In it he sharply contrasted a sophisticated
Greek interpretation of astronomical models (for Duhem this was that they were mathematical contrivances) with a naive insistence of the Arabs on their concrete reality. But
in Le Syst~me du monde, which began to appear in 1913, Duhem modified his views on
Greek astronomy considerably; his more subtle understanding included the recognition
that many Greeks subordinated mathematical astronomy to physical theory. But he could
not completely repudiate his earlier views about Greek astronomy in part because his
extreme nineteenth century prejudices led him to continue to insist on a clear-cut demarcation between Greek and Arabic astronomy. The inevitable result is a certain unevenness
in the Syst~me and some glaring inconsistencies.

Given the totality of Duhem's enormous output, one would be hard
put to claim that Arabic science played more than a peripheral role in
his historical and philosophical writings. And because Duhem, who
did not know Arabic, was often grossly mistaken in his views and
interpretations of Arabic science, leaving it little more than a grotesque
caricature, it is appropriate to ask: why bother? There are several
reasons, which may serve both as an introduction and an apologia. It
is a far from worthless exercise to try to discover why a great thinker
goes so far off the track. It is rather facile to claim that Duhem's views
were a result of his anti-Semiticism; but this takes us only so far and
fails to put his views into historical perspective. Yes, D u h e m was rather
extreme in his notions of Arabic science, but I think he only took to a
logical conclusion views that were until recently fairly prevalent. And
the continuing influence of Duhem's historical works makes an evaluation of his attitude toward Arabic science even more imperative than
it would otherwise be. A n o t h e r reason to look at Duhem's understanding of Arabic astronomy is because of his use of it as a foil to p u t in
bolder relief the genius of G r e e k science. As we know from recent
debates, D u h e m left himself open to interpretation in the use of his
cherished 'saving the phenomena'. Because in Duhem's view the Arabs
could never rise to the Greeks' elevated understanding of astronomical
Synthese 83: 201-214, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

theory, a study of what he said about their failure - indeed ignorance
- can provide, I believe, some useful insight into what he intended by
'saving the phenomena'. My own contention will be that there was a
marked evolution and refinement in his thinking about Greek astronomy between To Save the Phenomena (herein abbreviated STP), which
appeared in 1908, and the second volume of Le Syst~me du monde,
which was published in 1914. But there was no similar change in thinking about Arabic astronomy, a situation that ted to a major inconsistency in the Syst~me; ironically this inconsistency could have been dealt
with, though perhaps not completely resolved, if Duhem had been
willing to be less hostile toward the Arabs. But he was unable, or
perhaps unwilling, to do this.
In order to illustrate my point, I shall be concentrating on the question of Duhem's understanding of the relation of ancient physics to
mathematical astronomy. I believe that by examining this issue (rather
than, say, the much more intractable question of the reality of astronomical models) 1 one can most clearly understand Duhem's evolution
as well as the importance, and limitation, of the criticism of G. E. R.
Lloyd (1978), Duhem's most severe critic on this point. Without going
into a detailed exposition or analysis of STP, I should like to give a
brief overview of some of its main points. 2
According to Duhem, there were basically two methods for dealing
with the celestial realm: the method of the astronomer and the method
of the physicist. Plato had set forth the method of the astronomer,
namely to save the appearances of the planets using only uniform,
circular motions. This was the method of Eudoxus and Callippus, who
sought to save the appearances with homocentric spheres. On the other
hand, Aristotle, representing the physicists, went beyond the merely
mathematical saving of the appearances and sought to impose other
restrictions that had to do with the nature of the heavenly bodies.
Thus the fictitious models of Eudoxus were turned by Aristotle into
combinations of real spheres whose nature it was to move with uniform,
circular motion. Because they were real and not simply mathematical,
Aristotle needed to add extra counterspheres in order to keep the
system of spheres for each planet from interfering with the others.
At this point, Duhem was illustrating the relation of physics to astronomy by using the example of a physicist, in this case Aristotle, attempting to make real the mathematical models of the astronomers. But the
relationship became more complicated when the Greek astronomers

found that different hypotheses or models could equally well save the
phenomena. This was emphasized by Hipparchus who was struck by
the fact that an epicycle on a concentric deferent could be made mathematically equivalent to an eccentric model. The relationship was further
complicated by the fact that an astronomy using epicycles and eccentrics
was no longer compatible with an Aristotelian physics that demanded
that all celestial motion be uniform about the center of the Universe.
Among others Adrastus of Aphrodisias and Theon of Smyrna sought to
accommodate the new astronomy by proposing a modified Aristotelian
physics that exempted celestial motion from being about the center of
the world but still held that the orbs, whether eccentric, epicyclic, or
concentric, had to be solid bodies.
As we have seen, Duhem claimed that Eudoxus and Callippus had
followed the method of the astronomers as laid out by Plato; he also
put Hipparchus in this category. But it was with Ptolemy that a new,
much more sophisticated understanding of the relation of mathematical
astronomy to physics was reached. Since "no craftsman could have
constructed a wooden or metal representation of [his hypotheses in the
Syntaxis]... Ptolemy's followers were bound - on pain of abandoning
their own doctrines - to liberate astronomical hypotheses from the
conditions to which physicists had generally subjected t h e m " ? Duhem
quoted a number of passages to support his position but the most
important by far was from the Almagest, Bk. 13, Chap. 2, 4 in which
Ptolemy, according to Duhem, "means to indicate...that the many
motions he compounds in the Syntaxis to determine the trajectory of a
planet have no physical reality; only the resultant motion is actually
produced in the heavens". 5 Duhem related this interpretation of Ptolemy to the earlier doctrine of the Stoic Cleanthes (d.ca. 230 inc.),
who held that the planet was self-propelled and described whatever
curves were observed, and to the later view of the neo-Platonist Proclus
(d. 485 A.D.), who, in Duhem's reading, took the essence of the heavenly motions to be irregularity. The final freeing of the astronomers
from the restrictions of the physicists was complete. And what would
be the role of the physicist?
But only the physicist would be authorized to say whether or not [the mathematical
models] conform to reality. Generally speaking, the principles he is able to affirm are
too general, too remote from particulars, to e m p o w e r him to pronounce that kind of
judgment. 6

In other words, the method of the astronomer was eventually victorious
in ancient Greece.
Lloyd has severely criticized most of Duhem's contentions in a detailed way. There is no need to rehearse the entire list; it is only
important for our purposes to identify three of his main objections.
First he makes the case that D u h e m has ignored the strong evidence
that the astronomers, far from being independent, took their startingpoints or principles from the physicists. This, for example, was stated
explicitly by Geminus, whom D u h e m took as a witness for the opposite
point of view. 7
A second criticism by Lloyd concerns Ptolemy. Whatever one may
wish to say about his position in the Almagest, there is the matter of
the Planetary Hypotheses in which there is no doubt that he is taking
a realist stance. How else is one to understand the transforming of the
circles of the Almagest into physical bodies, a metamorphosis effected
in Book II of the Planetary Hypotheses? And even if one were to
excuse D u h e m in 1908 for not having gotten hold of L. Nix's German
translation from the Arabic of the nonextant G r e e k text of Book II, a
work published in 1907, s one could still argue, as does Lloyd, that the
physical arguments in Book I of the Almagest should have alerted
D u h e m that Ptolemy was ostensibly basing his mathematical models,
indeed subordinating them, to a revised Aristotelian physics. 9
Lloyd's third criticism has to do with Proclus. D u h e m did not hesitate
to compare him to the positivists,, indeed to John Stuart Mill; 1° but
Lloyd systematically shows that whatever Proclus's neo-Platonist position may have been, and if anything it is ambiguous, he was fairly
consistent in arguing from realist assumptions whether he was criticizing
realist or instrumentalist alternatives. 11
One cannot but admire the incisive way Lloyd has gone about refuting
Duhem's contentions in To Save the Phenomena. It is a masterful piece
of writing, but i t has not gone without criticism. Niall Martin (1987)
has criticized Lloyd and others for viewing D u h e m too simplistically;
Martin claims that D u h e m was more than aware that the ancients were
not instrumentalists per se but rather tied their instrumentalism, if
we can call it that, to cosmological and epistemological stances. Thus
Ptolemy's instrumentalism was not to be separated from his stoicism
just as Maimonides' should not be understood as separable from his
religious beliefs; in both cases their skepticism about the possibility
of a complete understanding of celestial phenomena, as distinct from

sublunar phenomena, led them to their quasi-instrumentalism.~'Now
both Lloyd and Martin are basing their positions on STP; from that
context alone, Martin may have a point but one must admit that Duhem
certainly seems to be attributing instrumentalist views to the Greeks.
After all it was Duhem, not Lloyd, who evoked the name of John
Stuart Mill in his discussion of Proclus. But to judge Duhem solely with
reference to STP, as Lloyd and Martin both do, is to do him a grave
disservice. For this was not Duhem's final word; in Volume II of Le
Syst~me du monde (1914) he took up many of the issues of Greek and
Arabic astronomy that he had dealt with before in STP but in a much
more careful way. This is Duhem's mature work, and I think it only
fair that we take it into account when we discuss his views on Greek
astronomy. And on the crucial issue of the relation of physics to astronomy, Duhem has made a number of significant shifts.
While one can hardly say that Duhem has repudiated the thesis of
STP, one can say that he has modified it in subtle and at times decisive
ways in the SystOme. On the surface Duhem seems to carry the main
theme of STP into his later work. For example in the Syst~me, he
characterized what he calls "this war" as being between "those who
want Physics [in the modern sense] to be deducible from a set philosophical system a n d . . , between those who require nothing more from
[physics] than that it agree exactly with experience". 13 But whereas
many points made in STP were repeated, sometimes verbatim, in the
Systkme, the important relationship between the principles of physics
and mathematical models in Greek astronomy was explored with much
greater depth and precision, and Duhem reached certain conclusions
that undermine, if not contradict, various assertions of STP. For example, in discussing the homocentric spheres of Eudoxus and Callippus in
the SystOme, Duhem posed a question never addressed in STP, namely
If Plato and Aristotle were only interested in obtaining mathematical rules that would
permit them to predict with certainty and precision the movements of the stars, why
would they impose in advance of these rules the obligation to be constructed in a
certain m a n n e r ? . . . Why would they constrain [astronomy]... with circular and uniform
movements? Why would they further restrain [astronomy's] ability to choose by obliging
it to configure the World with a system of homocentric spheres? Such requirements are
enough to give notice that neither Plato nor Aristotle would have consented to reduce
the object of astronomy to the [following] single problem: to conceive of geometrical
hypotheses that would save the phenomena. 14

There is more than one thing surprising here. After all Plato in STP

had been assigned the role of initiator of the call to the astronomers
'to save the phenomena'. Duhem had mentioned there that Plato had
required that this be done with uniform, circular motions, but the
obvious physicalist implications had been ignored. Here, however, we
see that he has not only recognized the problem but has also drawn
the obvious conclusion about Plato, namely that he was hardly an
instrumentalist. 15
But there is another aspect to the problem that was new in the
Syst~me. Did an astronomer who accepted uniform, circular motion as
a starting point for astronomy accept ipso facto the constraints of the
physicists? And if so, what did this do to the radical separation between
astronomers and physicists in STP? Again the ambiguities and silence
of STP gave way to a direct assault on the problem in the Syst~me. In
discussing Dercyllides, Duhem noted that he was not an innovator when
he "affirms the dependence, generally recognized by the philosophers,
between astronomy and physics; others...have also detailed the character of this dependence". This is not very different from what one might
find in STP. But then he went on to say that "those who compose
astronomical treatises, respectful [respectueux] observers of these precepts, begin by enunciating the postulates, borrowed from Physics,
which must [devaient] serve as points of departure for their deductions", a6 We should recall here that one of Lloyd's criticisms was that
Duhem ignored the relation of the physical principles to the starting
points of the astronomers. But in addressing his future critic, Duhem
has made the previously clear-cut notion of 'saving the phenomena'
rather ambiguous in the Syst~me.
Lest one think that this is somehow unrepresentative, we should
examine what Duhem said in the Syst~me about Ptolemy, who was
after all the Greek astronomer Duhem had claimed in STP most clearly
represented the doctrine of 'saving the phenomena'. Far from denying
that Ptolemy was constrained by physics, Duhem must admit that "at
the beginning of his work, Ptolemy formulates his postulates as if
astronomy must be entirely based upon principles of complete certitude,
upon incontestable verities from Physics". But Duhem found that "at
the end [of the w o r k ] . . , instructed by experience, the author does not
grant his hypotheses to be anything more than contrivances that are
appropriate to save, as simply as possible, the phenomena". 17 Here
one would have expected the Duhem of STP to end the matter; Ptolemy

had paid lip service to the physical principles, found them too constraining, and ended by rejecting them. But instead Duhem provided a real
surprise. At this point he himself introduced the same weapon that
Lloyd and others have used to question the Duhemian interpretation
of Ptolemy, namely the Planetary Hypotheses. After assuring his readers, no doubt sadly, that the text is authentic, he proceeded to give a
fairly detailed summary of the second book in which Ptolemy attempted
to physicalize his models from the Almagest.~s Duhem was fully aware
of what this meant for his interpretation of Ptolemy. But he tried to
salvage what he could:
Ptolemy had rightly been able to scorn this desire to represent the movements of the
celestial and imperishable bodies by means of these rough and changing bodies that make
up for us the sublunar world; his criticisms had not won a definitive victory; the error
that they were combatting was one of those which, apparently vanquished, overturned
one moment, rise up again without ceasing, because they are the necessary consequence
of an incorrigible failing of the human spirit. What Dercyllides, Adrastus and Theon had
wanted was to embody abstract thoughts in concrete models that the eyes could see, that
the hands could touch and move; it was to drive away reason in order to put imagination
in its place. Ptolemy, after having defended reason, became, in his turn, a slave of the
imagination. 19

At this point Duhem turned to the neo-Platonists, in particular Proclus. What he found was someone less ambiguous and much more to
his liking. But he had to retranslate the relevant passages from the
Hypotyposes since he realized, long before Lloyd would make the point,
that Father Halma's translation that he had depended on in STP was
seriously defective. Thus Duhem could no longer have Proclus saying
that the "essence of [the celestial] movements...is irregularity"Y But
Duhem still held that Proclus viewed astronomical hypotheses as mere
fictions in part because he chose to concentrate on his Platonic worldview, a philosophical stance that led Proclus to be sceptical of all
attempts to deal with the celestial appearances as distinct from the real
heavens, which to him were, as they had been to the divine Plato,
beyond perception. Lloyd, on the other hand, while recognizing this
aspect of Proclus's position, 21 could counter Duhem's contentions by
pointing to Proclus's realist (or perhaps it would be better to call them
physicalist) suppositions under which he operated even when dealing
with the appearances.
But again where did this leave Duhem? After losing both Plato

and Ptolemy as pure representatives of the view that the astronomical
hypotheses were mere contrivances, he was basically left with Proclus,
someone that Lloyd has accurately characterized as "not exactly one
of the leading lights in the history of G r e e k astronomical theory". 22
One would think that D u h e m would be forced to back off from some
of the more extreme claims of STP. But D u h e m did not draw the
obvious conclusion from his work, namely that the most important
G r e e k thinkers held a basically realist position and subordinated mathematical astronomy to physics. It was not a pure position, it was not
completely clear-cut, but his work could lead to no other conclusion.
Though it is too much to expect that D u h e m would have completely
repudiated the major thesis of STP, it still comes as a shock to find the
following passage from STP repeated in the Syst~me:
After some initial hesitation [the Greeks] balked at the idea that the eccentrics and
epicycles are bodies, really up there on the vault of the heavens. For the Greeks they
were simply geometric fictions requisite to the subjection of celestial phenomena to
calculation. If these calculations are in accord with the results of observation, if the
hypotheses succeed in saving the phenomena, the astronomer's problem is solved. 23

Interestingly enough, this passage does not occur in the chapter on the
Greeks but rather in the introduction to the one on the 'Semites'. All
the ambiguity, the subtlety of the previous chapter on the Greeks
is lost; Ptolemy once again becomes someone whose hypotheses are
'calculating devices' .24 The Planetary Hypotheses are conveniently forgotten. Why D u h e m chose to start his chapter on the 'Semites' in this
way is apparent from the next paragraph:
The prodigious geometric ingenuity of the Greeks did not form part of the heritage they
passed on to the Arabs. Nor did the Arabs have the Greeks' remarkably sure and precise
logical sense. They brought only some very minor improvements to the hypotheses
whereby the Greek astronomers had managed to resolve the complex course of the
planets into simple motions. Moreover, when they did at last come to examine these
hypotheses in an attempt to make out their nature, their vision could not match the
penetration of a Posidonius, a Ptolemy, a Proclus, or a Simplicius; slaves to their imagination, they tried to see and touch what the Greek thinkers had declared fictive and
abstract. 25

It is this stark contrast between the Greek mind and the Arab mind
that D u h e m wished to bring out in both STP and the SystOme. The fact
that the Greeks were no longer so pure and that Ptolemy himself had
been called a slave to the imagination did not prevent D u h e m from
repeating verbatim in the Syst~me what he had written in STP. Duhem's

antipathy toward the Arabs is not in doubt; indeed one can see it as
part of the nineteenth century European cultural baggage. 26 But even
for the nineteenth century Duhem was extreme. The person closest to
his view on Arabic science was Ernest Renan, with whom Duhem
shared hardly anything e l s e Y Renan had denied both the Arabs and
Islam a role in the history of science; nomadic Arabs were incapable
of science or philosophy and Islam was too hostile to allow science to
flourish. What went under the name Arabic or Islamic science was due
to Christians, Jews, Persians, and others, or Muslims who, like Galileo,
had heroically freed themselves of their religion. 28 But Duhem went
Renan one better; while Renan had not discounted the contributions
that went under the name Arabic or Islamic science, Duhem essentially
denied that there was anything of importance in Arabic astronomy. 29
When he did find something worthwhile, such as the homocentric system of the Spanish Arab Bit.rfiji (ft. 1200 A.D.), which he claimed
helped pave the way for Copernicus by providing an alternative to the
Ptolemaic system, he rejected the possibility that any Arab could have
been responsible for it? ° The way he did this is extraordinary; Duhem
maintained that the ordering of letters in the diagrams of Bit.rfiji followed the Greek alphabet and hence his system must depend on or be
plagiarized from a Greek original? ~ It would be hard to exaggerate the
silliness of this argument, and it is incredible to me that someone of
Duhem's immense abilities could have fallen for something so ludicrous. 32 Since the Arabic alphanumeric system follows the old Semitic
ordering, the one used, for example, by the Phoenicians who bequeathed it to the Greeks, it is no wonder that the Greek and Arabic
ordering would be the same. Thus using Duhem's reasoning, one could
hardly escape the conclusion that virtually every Arabic scientific text
was plagiarized from some Greek original. 33
We have seen how Duhem's wish to draw a sharp dichotomy between
the Greeks and Arabs led him to gloss over what I consider to be some
of his most important work in the history of cosmology. What is sad,
and indeed unfortunate for the history of science, is that Duhem did
not notice, or did not wish to notice, that the ambiguous Greek attitude
toward the relation of physics and astronomy that he brought to light
in the SystOmewas dealt with in interesting ways in Islamic astronomy.
If Duhem had simply drawn the obvious conclusion from his own
research that the major Greek philosophers and astronomers were
committed in varying degrees to the proposition that the principles of

mathematical astronomy must come from both mathematics and physics, he would have been more sensitive to the fact that the Arab thinkers
that he studied were not so much naive realists as scientists interested
in reconciling the inconsistencies in astronomical theory that they had
inherited from the Greeks. Let me try to make this point as clear as
possible. In accepting that astronomy was based on both mathematical
and physical principles, Arab astronomers reached a rather simple
conclusion - the mathematical models had to be consistent with the
physical principles. Ptolemy had not been able to accomplish this in
the Alrnagest, and indeed in Bk. 13, Chap. 2, he does seem to be
taking refuge in some neo-Platonic worldview. But starting with Ibn alHaytham in the eleventh century, this was seen not so much as a
serious position on the relation of physics to mathematics but as simple
inconsistency .34
Despite the fact that Duhem in the Syst~rne had understood the
difference between metaphysics and physics in the Greek context and
in fact had used it to distinguish between the justifications of Aristotle
and Plato for uniform, circular motion, I would agree with Martin that
Duhem remained committed to the view that "'astronomy' is the
ancient correlate of modern physics, and 'physics' the ancient correlate
of modern metaphysics".35 This was what led him, as well as other
historians of astronomy such as E. S. Kennedy and Otto Neugebauer,
not to take the physical principles of ancient and medieval astronomy
as seriously as the physical principles of modern physics. (This is reflected in the terminology regarding these physical principles, which
are usually referred to as 'philosophical'.) 36 Thus it is easy to see why
for Duhem, such figures as Ptolemy, Proclus, and Maimonides were the
heroes of his story because they, as 'neo-Platonists', sharply separated
astronomy from some true metaphysical reality. But what this ignores
is that the physical principles were not justified solely in a metaphysical
way either by the Greeks or Arabs and were regarded as having, for.
example, empirical justifications. Thus Aristotle, despite having what
we would call metaphysical reasons for preferring uniform, circular
motion in the heavens, did not shy away from giving 'empirical
proofs'. 37 For reasons that we need not go into here, Islamic astronomers and physicists sought at various times to disentangle the physical
principles from any metaphysical taint. 38 Uniform, circular motion
could therefore be understood as justified physical premises that were
established both from observation and from successful usage. In this

regard it is interesting that when a physical premise did not seem to
have empirical justification, a position taken by .TGsi concerning the
Earth's state of rest, the response by his successors was to find an
empirical justification, not to insist on some metaphysical principle. 39
It may be argued that Duhem did not know enough about Arabic
science to be able to form a proper judgement. Obviously he did not
know of some of the more recent discoveries nor of the relation of ,
Copernicus to Islamic astronomy. 4° He did, however, know of Na.sir
al-Din al-TQsi's attempt to reform the Ptolemaic system since this was
in a French translation that Duhem cited in the Syst~me. 41 Duhem
should have realized that TGsi's proposed model that circumvented the
equant, a device used by Ptolemy in his planetary theory that led to an
irregular motion of the orb, resulted from a desire to deal with logical
inconsistency in the Ptolemaic system, not from naive realism. This
should have been especially clear to him in view of his understanding
of the relation of physics and mathematics that he had come to in the
Systkme. And it should have also been clear to him since TQsI, like
Duhem himself, took seriously the logical foundations of his discipline.
Thus if one begins with certain principles it only seems reasonable to
stick with them, something that Ptolemy did not do. Whether Duhem
would have seen the Arabic contribution in this light we shall never
know. I take this as a tragedy not only for Duhem but for the history
of science since he was a man of great insights and intuitions. But
blinded by prejudice, he did not care to delve into the problems of
those who were 'slaves to the imagination'.
NOTES
1 AS I shall elaborate on below, the issue that became of paramount importance in
Islamic astronomy was that of the consistency between the physical and mathematical
principles, I would argue that given the admitted mathematical equivalence between
various astronomical models that were considered physically acceptable, the question of
whether the models represented the 'real world' became rather secondary.
2 Cf. Duhem (1908), pp. 1-27; translation, 1969, pp. 3-24.
3 Ibid., p. 17; translation, p. 16.
4 Heiberg (1903), pp. 532-34; translation, Toomer (1984), pp. 600--601.
5 Duhem (1908), p. 18; translation, 1969, p. 17.
6 Ibid., p. 27; translation, p. 25.
7 Lloyd (1978), pp. 212-14.
8 Heiberg (1907), pp. 111-45.
9 Lloyd (1978), pp. 215-17.

son with the positivists by remarking that "the line of demarcation [separating the objects
accessible to human knowledge from those that are essentially unknowable to man] is
not the same for Proclus as it is for John Stuart Mill".
11 Lloyd (1978), pp. 204-11.
Martin (1987), pp. 309-12.
13 Duhem (1914), 2, 62-63.
14 Ibid., 2, 69-70.
The quoted passage is rather less Shocking as regards Aristotle since in STP we had
already been apprised of his physicalist leanings. But Duhem explored the implications
of both Plato's and Aristotle's positions in much greater depth in the Systdrne. He
concluded that for Plato the insistence on uniform, circular motion was a theological
requirement that resulted from an ontological hierarchy in which the true motions, as
distinct from the observed ones, were as perfect as possible. For Aristotle this was a
physical requirement that resulted from an epistemological hierarchy that made geometrical astronomy subordinate to physics (ibid., 2, 71). Duhem's entire discussion of the
relation of physics and astronomy before Ptolemy (ibid., 2, 67-83) is extremely valuable.
It is now clear to me that had I read the Syst~me more carefully earlier, I would have
seen that the Islamic discussion of this relation owes more to Greek precedents than I
had assumed in Ragep (1982), 1, 129-89; I was there still, at least partially, under the
spell of STP, even while reacting against it, and did not take into account the extent to
which Greek astronomy subordinated itself to physics.
16 Duhem (1913), 1, 469.
17 Duhem (1914), 2, 86.
18 Ibid., 2, 86--99.
19 Ibid., 2, 99.
20 Duhem (1908), p. 20; translation, 1969, p. 19. Duhem (1914), 2, 103 (n. 1) criticized
Halma's translation (1820, p. 151) that he had depended on in 1908. In one of the few
places he refers to the Systdme, Lloyd (1978), p. 205, n. 20, notes Duhem's correction
of Halma.
21 See Lloyd (1978), esp. pp. 207,209.
22 Ibid., p. 211.
23 Duhem (1908), p. 27 (translation, 1969, p. 25); Duhem (1914), 2, 117. I have not
modified the translation though it does introduce minor changes to Duhem's text.
24 Duhem (1914), 2, 118.
25 Duhem (1908), pp. 27-28 (translation, 1969, pp. 25-26); Duhem (1914), 2, 117-18.
26 Recent books that have rather provocatively described this 'baggage' are Said (1978)
and Bernal (1987).
27 Some of the antipathy between Renan's 'scientific' worldview and Duhem's 'religious'
one can be gleaned from Jaki (1984), passim.
2s Renan (1883), esp. pp. 14-19.
29 "Islamic science is in large part the plundered spoils of decadent Greek science" [italics
added] (Duhem 1914, 2, 179).
30 Ibid., 2, 156-71.
31 Ibid., 2, 156-57.
32 Duhem stated that he got this argument from Friedrich Hultsch, who claimed that the

ordering of letters in Arabic is a "sure indication by which one may recognize a work of
Greek origin that has been translated into Arabic" (ibid., 2, 157). Hultsch, who is
principally remembered today for his editions of Greek mathematical and scientific texts,
does not seem to have dealt with Arabic works, at least as far as I have been able to
ascertain. If he did study Arabic, one would have to conclude that he did not get as far
as the alphabet.
33 It is perhaps worth noting here in passing that Duhem's position cannot be simply
characterized as anti-Semitic; for one of the people he admired and who Duhem felt had
something of the Greek spirit of Proclus and Ptolemy was Maimonides. In this assessment
Duhem parted company with Renan, who had lumped Maimonides with Averroes; cf.
Duhem (1908), pp. 37-40 (translation, 1969, pp. 33-35) and Duhem (1914), 2, 140-41.,
34 On the question of consistency between physics and astronomy in Islam, see Sabra
(1978) and Sabra (1984), pp. 133-34, esp. n. 3; cf. Ragep (1982), 1, 129-89.
as Martin (1987), p. 303. Duhem expresses this explicitly in his introduction to STP
(1908), pp. 1-2 (translation, 1969, pp. 3-4).
36 See, for example, Kennedy (1966), pp. 366-67; Neugebauer (1975), 1, p. 1; 2, 572,
942; Hartner (1975), p. 9; and Goldstein (1980), p. 142. For different viewpoints, see
Sabra (1984), esp. n. 3, pp. 145-46 and Ragep (1987), pp. 330-31.
37 See, for example, Aristotle, On the Heavens, Bk. I, Chap. 3, 270b5-16 where he says
"our theory seems to confirm phenomena and to be confirmed by them"; cf. Metaphysics,
Bk. XII, Chap 7, 1072a20-23. For an extended discussion of this point, see Ragep (1982),
1, 149--61.
38 Ragep (1982), 1, 166-74.
39 For an elaboration, and the possible effect of this discussion on Copernicus, see Ragep
(forthcoming), commentary to II.I[6].6-14.
40 For a discussion of this relationship and further references, see Kennedy (1966),
Hartner (1975), and Sabra (1984), n. 5, p. 146.
41 Duhem (1914), 2, 129. The translation was due to Carra de Vaux (1893), whose
pejorative characterization of T~asi's efforts no doubt met with Duhem's approval: "Le
chapitre dont nous allons donner la traduction suffira peut-~tre a faire sentir ce que la
science musulmane avait de faiblesse, de mesquinerie, qnand elle voulait ~tre origirlale".

REFERENCES
Aristotle: 1984, The Complete Works of Aristotle, 2 vols., Princeton University Press,
Princeton; New Jersey.
Bernal, M.: 1987, Black Athena: The Afroasiatic Roots of Classical Civilization, vol. I,
The Fabrication of Ancient Greece 1785-1985, Free Association Books, London.
Carra de Vaux: 1893, 'Les sph6res c61estes selon Nasir-Eddin Attasr, in P. Tannery,
Recherches sur rhistoire de l'astronomie ancienne, Gauthier-Villars & Fils, Paris.
Duhem, P.: 1908, '5~I2ZEIN TA ~bAINOMENA: Essai sur la notion de th6orie physique
de Platon ~ Galil6e', Annales de philosophie chrdtienne 6 (4¢ s6fie), 113-39, 277-302,
352-77,482-514,561-92. Issued in book form also in 1908 by Hermann, Paris; reprinted
1982 by J. Vrin, Paris. Page references are to the 1908 Hermann publication.

vol. 2 = 1914.
Duhem, P.: 1969, To Save the Phenomena: An Essay on the Idea of Physical Theory from
Plato to Galileo, translation of Duhem (1908) by E. Doland and C. Maschler, University of Chicago Press, Chicago.
Goldstein, B. R.: 1980, 'The Status of Models in Ancient and Medieval Astronomy',
Centaurus 24, 132-47.
Halma, N.: 1820, HypothOses et ~poques des plan~tes de C. Ptolgmde et Hypotyposes de
Proclus Diadochus, Merlin, Paris.
Hartner, W.: 1975, 'The Islamic Astronomical Background to Nicholas Copernicus', in
O. Gingerich and J. Dobrzycki (eds.), Studia Copernicana XIII (Colloquia Copernicana
II1), Ossolineum (The Polish Academy of Sciences Press), Wroclaw etc., pp. 7-16.
Heiberg, J. L. (ed.): 1898, 1903, Claudii Ptolemaei opera quae exstant omnia, vol. I,
Syntaxis Mathematica (2 vols.), Teubner, Leipzig.
Heiberg, J. L. (ed.): 1907, Claudii Ptolemaei opera quae exstant omnia, vol. II, Opera
astronomica minora (2 vols.), Teubner, Leipzig.
Jaki, S.: 1984, Uneasy Genius: The Life and Work of Pierre Duhem, Martinus Nijhoff
Publishers, The Hague, The Netherlands.
Kennedy, E. S.: 1966, 'Late Medieval Planetary Theory', Isis 57, 365-78.
Lloyd, G. E. R.: 1978, 'Saving the Appearances', Classical Quarterly 28,202-22.
Martin, R. N. D.: 1987, 'Saving Duhem and Galileo: Duhemian Methodology and the
Saving of the Phenomena', History of Science 25,301-19.
Neugebauer, O.: 1975, A History of Ancient Mathematical Astronomy, 3 vols., SpringerVerlag, New York.
Ragep, F. J.: 1982, Cosmography in the 'Tadhkira' of Nas.rr al-D?n al-Ttis~, 2 vols., Ph.D.
dissertation, Harvard University Press, Cambridge, Massachusetts.
Ragep, F. J.: 1987, 'The Two Versions of the TQsi Couple', in D. A. King and G. Saliba
(eds.), From Deferent to Equant: Studies in Honor of E. S. Kennedy (The Annals of
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Ragep, F. J.: (forthcoming), Nasrr al-Drn al Tf~sFs 'Tadhkira'. An Edition, Translation and
Commentary, Springer-Verlag, New York.
Renan, E.: 1883, L'islamisme et la science, Calmann Ldvy, Paris.
Sabra, A. I.: 1978, 'An Eleventh-Century Refutation of Ptolemy's Planetary Theory', in
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Ossolineum (The Polish Academy of Science Press), Wroclaw etc. 117-31.
Sabra, A. I.: 1984, 'The Andalusian Revolt Against Ptolemaic Astronomy: Averroes and
al-Bit.rQji', in E. Mendelsohn (ed.), Transformation and Tradition in the Sciences,
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History of Mathematics Department
Brown University
Providence, Rhode Island 02912
U.S.A.

DESCARTES AND SOME PREDECESSORS
DIVINE CONSERVATION

ON T H E

OF M O T I O N *

ABSTRACT. Here I reexamine Duhem's question of the continuity between medieval
dynamics and early modern conservation theories. I concentrate on the heavens. For
Aristotle, the motions of the heavens are eternally constant (and thus mathematizable)
because an eternally constant divine Reason is their mover. Duhem thought that impetus
and conservation theories, by extending sublunar mechanics to the heavens, made a
divine renewer of motion redundant. By contrast, I show how Descartes derives his law
of conservation by extending Aristotelian celestial dynamics to the earth. Descartes
argues that motion is intrinsically linear, not circular. But he agrees that motion is
mathematically intelligible only where divine Reason moves bodies in a constant and
eternal motion. Descartes strips bodies of active powers, leaving God as the only
natural mover; thus both celestial and sublunar motions are constant, and uniformly
mathematizable. The law of conservation of the total quantity of motion is an attempt
to harmonize the constancy derived a priori with the phenomenal inconstancy of
sublunar motions.

1. INTRODUCTION
The physicists of the seventeenth century destroyed one system of
the world and replaced it with another. The old system, which Galileo
called Ptolemaic but which is eclually Platonist and Aristotelian, posited
a finite spherical universe with the heavenly bodies moving around
the circumference and the earth at rest in the center. According to
this system, the heavenly bodies must have an eternally uniform rotary
motion, both because they are eternal and incorruptible by nature,
and because they are moved by separate incorporeal movers; in contrast, the sublunar elements are naturally corruptible, and move only
a limited distance up or down before they are destroyed and changed
into other elements. The new physics of the seventeenth century
denied this fundamental contrast between celestial and sublunar things:
it posited only a single kind of matter present everywhere in the
universe, whose various configurations and motions must produce all
the phenomena of nature. Thus it becomes a fundamental problem to
find simple and universal laws of motion underlying the phenomena.
The seventeenth-century physicists all hold some form of the doctrine
Synthese 83: 215-238, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

of the conservation of motion: at a minimum, they hold what has
misleadingly come to be called the principle of inertia, that a body
in motion tends to remain in motion, and does not naturally come to
rest. The apparent tendency of sublunar bodies to slow and stop must
be explained, like all other phenomena, through the reciprocal impacts
of a system of moving bodies. This 'principle of inertia' distinguishes
the philosophers of the seventeenth century from their Aristotelian
predecessors, and serves as an emblem for their revolution in physics.
It was Pierre Duhem, in his Studies on Leonardo da Vinci, ~ who
opened the question: what sources did this revolutionary science of
motion have in the older tradition? Duhem found a key part of the
answer in studying scholastic discussions of projectile motion. Aristotle
had held that no motion could exist at any time without an external
mover contiguous to the moved body; he had thus been forced to
bizarre expedients to explain how a projectile could continue to move
after leaving the hand of the thrower. But Duhem found that in
addition to Aristotle's theory there was an alternate account, according
to which the thrower imparts a certain impetus to the projectile: this
impetus remains naturally in the projectile, and is sufficient to account
for its continued motion. Duhem traced the doctrine of impetus from
the Christian neo-Platonist John Philoponus in the sixth century to
the students of the scholastic master John Buridan in the fourteenth
century; and he tried to indicate the subsequent stages by which the
doctrine of impetus developed, taking on increasing mathematical
precision, into the dynamics of Galileo and his contemporaries,
founded on the natural preservation of motion.
Duhem's work has been challenged by Anneliese Maier. While she
agrees that impetus theory provided the historical point of departure
for the discovery of the law of inertia, she argues that Duhem has
read the scholastic sources too "charitably", and so exaggerated the
agreement between impetus theory and seventeenth-century mechanics. Maier argues convincingly that Duhem misread the views of
Buridan and his school on the permanence of impetus in the
projectile: while Buridan entertains the hypothesis that a celestial
impetus might last forever, he and all scholastics agree that any impetus
in a sublunar body would perish through the natural resistance of
matter. Maier thinks that this indicates a fundamental difference between the scholastic conception of impetus and the modern conception of inertial motion; impetus in a kind of energy which the thrower

deposits in the projectile, and which converts itself into motion at
each instant until it is depleted; on the modern conception, by contrast,
motion is a naturally persisting state of the body and does not need
to be explained by reference to any moving force. Thus Maier argues,
against Duhem, that the scholastic theory of impetus needed more
than just mathematical precision to become modern dynamics; a further
conceptual revolution was needed to produce the concept that the
motion imparted by a finite agent to a sublunar body is intrinsically
permanent. 2
The history of the laws of motion is extremely complex. We have
no reason to suppose that there is a single linear path which leads
from Aristotelianism through impetus theory to the principle of
inertia; on the contrary, it is clear that different seventeenth-century
physicists held different and incompatible laws of conservation of
motion, and that these laws did not all share the same historical
genealogy. Here I propose to test Duhem's claim of continuity, and
Maier's counterclaim of discontinuity, by looking at the particular
case of Descartes's law of the conservation of motion. Descartes is
an interesting case, both because he holds a strong and precise (though
false) principle of conservation, and because he justifies this principle
by an argument from natural theology. This argument might seem at
first to be an ad hoc justification, but I will show that it has deep roots
in older Aristotelian and Platonist philosophy. I will thus trace one of
the many paths which led from the medieval discussions of motion
to the modern consensus that motion is conserved; and I will hope to
shed light on the meaning of one seventeenth-century version of the
law of conservation.
The path which I will indicate from medieval to modern physics is
not quite the same as the path which Duhem had suggested. Maier
proves, against Duhem, that the impetus-theorists did not think of
motion as a permanent being which could remain stable without the
continued influence of a moving cause; she therefore concludes that
they did not possess the principle of inertia. But, as we will see,
Descartes also did not think of motion as stable in this sense; thus
Maier's argument cannot be sufficient to demonstrate a break between
medieval and early modern discussions of motion. Without in any way
diminishing the importance of the modern abrogation of the .............
distinction between heaven and earth, we can uphold Duhem's insight
that (at least some of) the theories of inertial motion continued a

scholastic discussion; but for Descartes, at least, it was not the concept
of a permanent impetus in sublunar projectiles that was his starting
point. My results on the particular case of Descartes will thus confirm
Duhem's main contention against Maier, while disconfirming some of
his subsidiary theses.

2.

ARISTOTLE

AND

SOME

SUCCESSORS

ON

CONSTANT

ETERNAL

MOVERS

In examining the medieval antecedents of Descartes's law of conservation of motion, I want to bear in mind Maier's remark that "the
scholastic analogue to inertial motion", the only "constant velocity
motion occurring in the absence of resistance", is celestial motion
(Maier 1982, p. 99). In this section I will indicate some themes from
the history of Aristotelian and Platonist thought about the nature
and causes of celestial motion; in the next section I will turn to
Descartes's discussions of the law of conservation. I will try to show
how Descartes's theological argument for the conservation of all
motion, celestial or terrestrial, continues and transforms the Platonist
and Aristotelian discussion of celestial motion. I will emphasize the
ways in which the older tradition gave Descartes a point of departure
for thinking about the laws of motion and the intelligibility of nature,
but I will also try to bring out the depth of the disagreement between
Cartesian and Aristotelian-Platonist philosophy.
All Aristotelians, and almost all Platonists, 3 claim that the motions
of the heavenly spheres are constant and eternal. They confirm this
claim by reasoning from the effects, the apparent positions of the
planets observed by the astronomers, but they think that the true
certainty of the claim lies in the c a u s e s which necessitate the
uniformity of celestial motion. Since Aristotelians and Platonists (like
Descartes) assume that all motion requires a mover, the cause of
the uniformity of celestial motion must lie in the nature of the
movers: a mover which itself varies will produce a variable motion, but
a mover which remains constant in itself and always moves a body will
produce an always constant motion in that body.
But what is this constant mover which produces the constant motion
of the heavens? It is surprisingly difficult for the Aristotelian to answer
this basic question, because in different texts Aristotle gives at least

two and perhaps three different answers, which may or may not be
consistent with each other (some modern commentators believe that
they can trace a development in Aristotle's views). In Books I and II
of the De Caelo Aristotle argues that the heavens are moved
circularly around the center of the world by their own nature, in
the same way that earth is moved toward the centre and fire away
from the centre. But in Metaphysics XII (and in other works) Aristotle
maintains that the heavens are moved by one or more incorporeal
movers separate from the heavens themselves: in the Metaphysics
the mover at least of the outermost sphere is described as nous or
Reason. 4 Nous moves its sphere only as a final or exemplar cause, by
being the good which the sphere desires to attain or imitate by its
motion. This seems to imply that the efficient cause of the sphere's
motion must be a soul which animates the sphere and desires its good,
and so produces a voluntary motion in its body. Thus the basic problem
of celestial dynamics for later Aristotelians is to make simultaneously
intelligible the statements that nature is the cause of celestial motion,
that soul is the cause of celestial motion, and that nous is the cause
of celestial motion.
This picture of the heavens does not at first seem promising for
scientific progress. The heavens are pictured as divine living beings,
moving in desire of further divine powers. Duhem regarded these
Aristotelian Movers as pagan, animistic, and unscientific, and he
thought that John Buridan had made decisive progress by proposing to
bury them. 5 Duhem was not all wrong: there are certainly elements
of fantasy in the doctrine of the separate movers. But I will'try to
show that beneath the fantasy this doctrine contained important
philosophical ideas, which could be useful even for a philosopher who,
like Descartes, had rejected the system of the spheres and the
priority of circular motion.
I will try to show this by elucidating some views of the problem
of celestial dynamics that were current within the Aristotelian and
Platonist tradition. First I will review some of the main data of the
problem as posed by the assertions of Aristotle (and also of Plato);
then I will show how some major figures of the later Aristotelian and
Platonist tradition, in harmonizing Aristotle's different statements with
each other (and often also with Plato or with revealed scriptures), were
forced to develop Aristotle's theory further than Aristotle himself had
done, yielding results of lasting philosophical interest. 6

I may begin at the top, with the n o u s which is for Aristotle the
highest cause of the celestial motions. Some translators render n o u s as
'mind' or 'intellect', but this is often inadequate. The word n o u s
sometimes means the act, sometimes the habit, and sometimes the
faculty, of intellectual perception; but often (as in the common
phrases n o u n e c h e i n or n o u n k e k t e s t h a i , to be reasonable; cp. French
a v o i r r a i s o n ) , it means that which we possess or share in when we do
or think something rationally. Following Ralph Hackforth, I will translate n o u s in this sense as 'Reason'. 7 Reason is not a 'mind', in the sense
of a rational soul: it is what souls participate in, in order to think
rationally or rightly. If we are to say that Reason 'thinks', it does not
think in the same way that rational souls think, but rather by being the
standard by which thought is measured, according to which thought
can be called rational or irrational, right or wrong. When St. Augustine
wishes to find a Latin equivalent for the Greek word n o u s as used in
Plotinus, he sometimes says 'intellectus' but more usually 'veritas',
truth: I will not use this rendering, but it is helpful to recall that it is
possible, s
Plato says in the P h i l e b u s (28C) that "all the wise agree that n o u s
is king of heaven and earth"; and he means, not a rational soul, but
Reason itself. There is an objective rational order in bodies, especially
in the heavenly bodies, which can be grasped by the rational faculty
in us; Plato believes that we can explain the existence of this order
only by supposing that there is a separate n o u s , a Reason-itself, and
that this Reason has the power to impose at least some degree of
rational order on bodies. Plato fills out this account in the T i m a e u s
with a hypothetical story of h o w Reason, as the 'demiurge' or
craftsman of the physical world, might impose sufficient order on an
originally chaotic matter to produce something like the world we now
inhabit. Aristotle too asserts, in D e A n i m a III, 5, that there is a
separate n o u s or Reason which is the source of intellectual knowledge
to the soul, and he follows Plato in asserting that n o u s is king, not
directly of the earth, but at least of the heavens. Sublunar motions
are not rational or constant enough to be the object of a mathematical
science; but celestial motions are, and they must therefore somehow
proceed from Reason. Aristotle's disagreement with Plato concerns the
means by which Reason communicates rational order to bodies.
Plato's demiurge sometimes resorts to violent means in rationalizing
bodies, imposing numerical constraints on a resisting matter. Aristotle,

in rejecting these means, is continuing Plato's own critique of Anaxagoras. Anaxagoras too had claimed to derive the world from nous,
but Plato charges that Anaxagoras' actual explanations relied on merely
mechanical constraints, and not on rationality and the best order of
things. Aristotle continues this critique by insisting that Reason cannot
cause order in things by forcing them to move to their proper positions,
but only by being the good or the model which the things aspire
to or imitate.
But Plato had already offered a less violent account of how rational
order descends from nous to bodies, and this Aristotle finds more
acceptable. Nous cannot directly move bodies, because bodies cannot
directly participate in Reason; but souls can participate in Reason, and
souls can move their bodies. Plato thinks that souls have an innate
internal motion, which becomes rational and orderly when the soul
participates in Reason. When the soul communicates this motion to
its body, it regularizes and rationalizes the body. Aristotle rejects
Plato's doctrine that the soul moves itself, but he accepts that the
soul moves the body. Aristotle can therefore give an essentially
Platonic answer to the question of the sources of rationality and
constancy to the celestial motions: the ultimate source is Reason
itself, but this rationality can only communicate itself to the heaven
by being first received in the rational soul which immediately moves
the heavens. Once this soul grasps Reason as its goal or model, it will
not pass back and forth between right and wrong thoughts, but will
remain eternally in a constant state of thought and will, and therefore
eternally produce a constant motion in its body.
Thus far it is not so difficult to harmonize Aristotle with himself and
(up to a point) with Plato. It is a greater challenge to harmonize
Metaphysics XII with Aristotle's assertion in the De Caelo that the
heavenly bodies move around the center by their own nature. In De
Caelo II, 1, Aristotle explicitly rejects the contention that the heavens
remain in their circles because of a "psychic constraint" (ananke
empsuchos). Aristotle's language here echoes Plato's critique of Anaxagoras (like Plato at Phaedo 99C, he describes his opponents as seeking
a new Atlas to keep the heavens up), but it is clear to any unbiased
reader that Aristotle's prime target is Plato. Plato had said (Timaeus
36E) that the soul which turns the heaven enjoys an "unceasing
[apaustos] and intelligent [emphron] life for all time". Aristotle too says
here that the motion of the heaven is "unceasing [apaustos] for

infinite time", but he insists that if a soul is needed to constrain a body
"which is naturally moved in some other way" (as it would be if, as
Plato says, the heavens are made mostly of fire), then this soul must
devote itself to violent effort, and will have no "intelligent [emphron]
leisure"; its ceaselessness will not be a blessing but a curse.
Aristotle's conclusion is that the heaven is moved, not by the
constraint or necessitation of a soul, but by its nature. It might seem
difficult to harmonize this, not just with Plato, but even with Metaphysics XII. But, as all harmonistic commentators note, Aristotle does not
deny in the De Caelo that the heavens are moved by souls, but only
that they are constrained (anankazesthai) by souls. Perhaps they might
be moved by souls without violence or constraint, if it is also true that
they are moved in circles by their natures. Different commentators,
in different ways, try to harmonize the De Caelo with the Metaphysics
by bringing together the statements that nous and soul are causes of
celestial motion and also that nature is a cause of celestial motion. As
we will see, they tend through time to give greater emphasis to the
separate movers, and to devalue nature as a cause of celestial motion.
We must first point out that, for an Aristotelian, the nature of a
body is not the same as the body: it is the form immanent within
the body. To say that a body is moved naturally is to say that it is
moved by its form. Since Aristotle holds that a soul is the form of a
living body, the obvious way to reconcile the De Caelo with the
Metaphysics is to identify the natures of the heavens with their
souls. This is the solution of Alexander of Aphrodisias, but it is
rejected by the later Greek commentators, who are trying to reconcile
Aristotle with Platonism. The harmonizers of Plato and Aristotle agree
that 'natures' are forms which are immanent within bodies and are
therefore destroyed with their bodies. If rational souls were natures
then they would be mortal at least in principle (although those souls
inhabiting immortal bodies would never actually die), and this is unacceptable. 9
Consequently, such philosophers as Proclus and Simplicius must posit
not two but three distinct causes, nous, soul, and nature, all working
in harmony to produce the motion of the spheres. According to
Proclus's scheme, nous is an unmoved mover, soul is a self-moved
mover, nature or immanent form is a moved mover, and body is a
moved nonmover (see Proclus 1968, p. 60 and elsewhere). Proclus goes
beyond what we have already seen mainly in his account of the

different ways in which soul and nature are causes of motion to bodies.
While natures or other immanent forms are said to be the immediate
movers of bodies, in fact soul becomes the principal mover, and
nature moves bodies only in a peculiar sense. Natures and other immanent forms receive their being from souls, and they can move bodies
only when they themselves are first moved by souls: thus they merely
communicate motion from souls to bodies. Invoking a distinction from
Aristotle (Physics VIII, 4), Proclus and his followers say that nature is
a principle of being-moved (arche tou kineisthai), while only soul is a
principle of moving-something (arche ton kinein). Nature is a principle
of being-moved by endowing the body with an epitedeiotes, a preparedness or disposition to be moved; but no actual motion occurs unless
some soul initiates it. The heavens, in particular, have a nature which
disposes them to be moved circularly (and Proclus endeavours to show
that Plato as well as Aristotle believed this); if they did not possess
this nature, then when a soul moved them circularly in would move
them violently and contrary to nature, as when a human being throws
a stone upward; such violent motion could not be regular or eternal,
as is the motion of the heavens. This satisfies Aristotle's concerns
in the De Caelo, while diminishing the role of nature, and preserving
soul as the principal cause of motion. Simplicus summarizes the
harmonious causality of nous, soul, and nature as follows:

If s o m e o n e asks which local motion of the heaven comes from nature and which from soul,
we say that soul, through the mediation of nature, m a k e s the heaven move [kineisthai] in
a circle, and that it is one and the same motion. But it has from nature the connatural
and unforced disposition [epitedeiotes], according to its very form, for being m o v e d
[kineisthai]; while from soul it has the actuality [energeia] of motion towards which it was
disposed by nature. So, too, it has from nous its turning always and in the same way and
according to the same and about the same and in the same [expanding on Timaeus 34A].
For by these things, u n d e r the leadership of nous, the psychic motion which is impressed
through nature in body is constituted, and stabilized in the likeness of the activity
[energeia] of nous. W h e n c e also that divine man, having asked why the heaven moves in
a circle, says that it is because it imitates nous.l°

The neo-Platonic doctrine that natures, and more transient immanent
forms, are intermediate movers, the agents of soul in bodies, is the
background for scholastic discussions of impetus or vis impressa. I will
not try to summarize these discussions here: but I want to cite one

particular text, from Avicenna in the early eleventh century, on the
causes of celestial motion.
Avicenna occupies a key juncture in the history of reflection about
the causes of motion. For the Latin scholastics Avicenna becomes,
after Averroes, the most authoritative interpreter of Aristotelian
philosophy. But Avicenna is a rather loose Aristotelian, as the Greek
Platonizing commentators had been: while he is not fully committed to
harmonizing Aristotle with Plato, often (sometimes for religious reasons) he preserves Platonizing interpretations of particular Aristotelian
doctrines. In particular, he takes up the neo-Platonist interpretation of
Aristotle's doctrine of the causes of celestial motion, and he transmits
to the West his revised version of this doctrine. Looking at Avicenna
allows us to see how the theory of impetus, especially in the celestial
case, develops out of the Aristotelian and Platonist concerns we have
been discussing. The text of Avicenna I will cite is helpful because it
has close echoes with both Simplicius and Buridan, and also with
Descartes: Avicenna is certainly one of the key links in the development and transmission of impetus theory (although I make no attempt
here to trace all the links in the chain), and he also illustrates very
clearly the way a whole tradition thought about how incorporeal
movers move bodies. 1~
Avicenna modifies the neo-Platonist doctrine of nature, soul and
nous in a number of ways (most notoriously by accepting a hierarchy of
Reasons shared in by different levels of souls), but his most important
modification for our purposes is in his conception of nature. Avicenna
does not accept the full neo-Platonist hierarchy of being: he asserts
that all souls are the forms of their bodies, and he denies that there
can be two substantial forms, soul and nature, within the same body.
For this reason, Avicenna goes even further than Proclus and Simplicius
in devaluing the role of nature as a cause of celestial motion: he
will not identify the natures of the heavens with their souls, but
he also cannot accept them as substantial forms inferior to souls, so
that they seem to be squeezed out of his system. And yet he must
preserve the doctrine of the D e Caelo that the heavens are
essentially different from sublunar things and that they rotate by their
nature.
Avicenna devotes a chapter of the Shifa' to the proposition "that
the proximate mover of the heavens is neither a nature nor a nous
but a soul, and that the more remote principle is a nous".~a He begins

by denying that the rotation of the heavens is "natural", in the
sense of proceeding from a nature; he then adds that the motion is
"by nature" in a looser sense, in that "its presence in its body is not
contrary to the determination of any other nature in its body: for
the thing which moves it, even though it is not a natural power, is
something natural to this body and not alien to it; it is as if it were its
nature".
But Avicenna wishes to find a more positive sense in which the
rotation proceeds from a nature. He solves the problem, in essentially
neo-Platonic terms, as follows:
Furthermore, every power moves only by the mediation of some inclination [mayl],
and the inclination is the thing [ma'na] which is perceived in the moved body: even if it
is forced to rest this inclination will still be perceived in it, resisting the obstacle and
seeking motion even while it is at rest. This is doubtless something other than the motion,
and other than the moving power, for the moving power still exists when it has completed
the motion, and the inclination does not. Similarly, too, in the case of the first motion,
its m o v e r does not cease to generate inclination after inclination in its body. Nothing
prevents this inclination from being called a nature: for it is not a soul, nor is it from
without, nor does it have will or choice, nor can it not move, or move in other than a
definite direction; nor, further, it is contrary to the determination of an alien nature in
this body. A n d if this thing [ma'na] is called a nature, then you may say that the heaven
is m o v e d by nature; but its nature is an e m a n a t i o n from soul, which is multiplied in
accordance with the soul's activity of thinking. A n d it is already clear that the principle
of the sphere's motion is not a nature [accepting a variant reading]; and it is already clear
that it is not violence; it is therefore doubtless from will.

It is this theory which, in one or another variant, is accepted by
Buridan and his school in the fourteenth century. As Duhem noted,
Buridan went beyond earlier thinkers in proposing an irnaginatio according to which all incorporeal movers inferior to God would be
eliminated, but for Buridan this was only an imaginatio, while the
theory of moving intelligentiae was the truth. 13 The fourteenth-century
Parisians, then, when beyond Avicenna chiefly in the possibilities
they considered, not in what they really believed. But even their
imaginationes were, in the fourteenth-century context, a natural step
beyond Avicenna's position. Duhem rightly stressed the importance
for these physicists of theological voluntarism: it was open to them
(as it had not been to Avicenna) to consider scenarios in which God
would do by himself what he is normally thought to do through secondary causes. But it was easy and painless for them to modify Avicenna's
scheme in this way, because he had already effectively eliminated the

heavenly bodies and their natures as causes of celestial motion. The
real mover for Avicenna is the soul, which looks to Reason, then wills
the body to move and so produces in it an inclination disposing it to
motion: the body itself cooperates only negatively, by not having the
form of a sublunar body which would resist a rational circular motion.
If we abolish soul and Reason as separate entities, and have G o d step
in to fill their roles, we may retain the basic structure of the doctrine
of celestial motion. If soul and Reason are immutable enough to guarantee the rationality and constancy of celestial motion, then afortiori
G o d provides the same guarantee. What has remained is the doctrine
that an immutable incorporeal mover, which has rationality intrinsically
and of itself, will produce an eternally constant motion which can be
the object of a mathematical science. As we will see, this is also the
fundamental doctrine of Descartes's dynamics.
3.

DESCARTES

ON

THE

DIVINE

CONSERVATION

OF

MOTION

Descartes is not a part of the Aristotelian and Platonist tradition I
have been describing. H e rejects any essential distinction between celestial and sublunar bodies; indeed, he rejects immanent forms, the
finite universe, the celestial spheres, and the priority of circular
motion. This is well-known and unsurprising. What is more surprising
is the extent to which Descartes is able to use themes from the
older tradition in constructing his new physics. Descartes draws his
metaphysics (on which his physics is to be based) largely from the
Platonizing doctrines of St. Augustine, and he is trying to persuade
readers nurtured on scholastic Aristotelianism. It is thus natural for
Descartes to call up themes from the Aristotelian and Platonist
discussion of the causes of motion; we will see how he uses and
transforms them. 14
Descartes always sets out his philosophy in a definite order, beginning
with metaphysics and then turning to physics. Metaphysics concerns
G o d and the soul; physics concerns bodies, their essence and existence
and their various motions. Descartes's metaphysics follows the discipline of ascending from the soul of God which Descartes had taken
from Augustine, Augustine from Plotinus, and Plotinus, ultimately,
from Aristotle's De Anima III, 5: first we consider ourselves as rational
souls, as potential knowers, and then we raise our sights to consider
G o d as Reason or Truth, as the source of our rationality and the

standard by which we judge that we are thinking rightly. Descartes's
physics begins with this knowledge of God, and descends to infer a
knowledge of the creatures which proceed from him. Descartes uses
premises about God to argue that the essence of body consists only
in extension, then that a world of bodies actually exists; then, finally,
that bodies obey certain universal laws of motion, from which particular
physical phenomena are derived.
We may schematically contrast the way physics and metaphysics fit
together for Descartes with the way they fit together for Aristotle.
Starting from two different parts of his philosophy, the psychology
and the celestial physics, Aristotle leads us up to contemplate the
divine Reason: in De Anima III he takes us from the potential
reason in ourselves to Reason absolutely, while in Physics VIII and
Metaphysics XII he takes us from the constancy of the primary
celestial motion to immutable Reason as its source. When Descartes
ascends, in the Meditations or in Part One of the Principles, from
the human mind to God, he is following the path De Anima III (at
least as it is interpreted by Plotinus, and taken over by Augustine); but
when Descart.es descends, in Part Two of the Principles, from God
to bodily motion, he is reversing the path of Metaphysics XII, arguing
from the immutability of God to the constancy of the motion
which proceeds from him.
This attempt to reverse Aristotle's order, descending from God to
bodies, has important implications for Descartes's philosophy. An Aristotelian may simply observe by watching the skies that the celestial
motions are constant; or again, he may begin with the fact of
inconstant motion and argue that it must be contained and measured
by a constant motion. In either case, he discovers God only as the
cause of the primary constant motion and not of all motion. Descartes, by contrast, has sought to think away all experience of the
physical world in constructing his knowledge of God, and he has no
grounds for restricting God's causality to one region of space rather
than another. Abstracting from all evidence of the senses, Descartes
finds the essence of body to be a uniform spatial extension, lacking
any outermost limit: he is therefore led, together with such contemporaries as Galileo, to abolish the distinction between celestial and
sublunar physics. Descartes concludes that not only celestial but also
sublunar motions are constant, because they all proceed equally from
God: they are therefore all equally objects of mathematical physics.

As Duhem would surely have suggested, Descartes's divergence from
the traditional Aristotelian view is rooted (at least in part) in a Christian
rejection of pagan limitations on the power of God. But it is
insufficient to say that Descartes refuses (as any Christian would) to
restrict God's power to only the outermost portion of the universe.
This would still be compatible with a broad acceptance of the Aristotelian system. For any even moderately Platonizing Aristotelian, there
is nothing in the nature of divine Reason which prevents it from
ruling over the whole world of bodies; the obstacle comes rather
from the nature of bodies, which are not all capable of receiving
the divine ordering without resistance and distortion. On an Aristotelian view, the natures of sublunar bodies incline them to move a finite
distance and then stop, if they are not first corrupted; such mutable
things can receive order only to the extent of observing a rough
periodicity in their transformations. Only the heavens receive constant
circular motion without resistance, because (as Simplicius says), only
they have a natural disposition to receive it, or even more negatively
because (as Avicenna says) only they have no other nature which could
resist it. Thus for Descartes to assert, against such Aristotelians as
these, that God produces a constant motion in sublunar as well as
celestial bodies, it is not enough for him to modify their conception
of God; he must modify their conception of body as well.
We may contrast Descartes's conception of corporeal nature with
Avicenna's conception. Avicenna denies that the heavenly bodies
have an intrinsic source of natural motion and concludes that they do
not resist the constant motion. Descartes, however, denies that any
bodies have an instrinsic source of natural motion and concludes that
no bodies resist the constant motion. This follows from Descartes's
conception of body as pure extension, which is designed precisely to
strip bodies of any natures, immanent forms, or active powers. Only
human and angelic minds, exceptional beings within the natural world,
remain to counteract the divine determination of bodies toward a
constant motion.
This elimination of natures from bodies depends on a theological
voluntarism much more radical than Buridan's: it is connected with
Descartes's doctrine of the creation of the eternal truths. In a famous
passage from a letter to Mersenne, Descartes declares that the eternal
truths "have been established by God and depend on him entirely, as

much as do all other creatures" (Descartes 1964, vol. I, p. 145):
Indeed, it is speaking of God as of a Jupiter or Saturn, and subjecting him to Styx and
the fates, to say that these truths are independent of him. I beg you, be bold to assert
and proclaim everywhere that it is G o d who has established these laws in nature, as a
king establishes laws in his kingdom. (ibid.)

Descartes is here rejecting the Aristotelian view that there is a radical
plurality of essences or natures which make each body the kind of
thing it is, and so govern its behavior: rather, all bodies are g o v e r n e d
by universal laws, and these laws are immutable because God is
immutable. Descartes's voluntarism is not an irrationalism: God's laws
are not tyrannical whims, but rational truths, proceeding from a God
who is the source of truth and rationality. We might therefore derive
these laws from a knowledge of God's nature, reversing the procedure
of Metaphysics XII.
Descartes is applying this principle in Part Two of the Principles of
Philosophy, art. 36 and following, where he sets out to derive the laws
of motion. 15 Descartes begins by saying that God is the universal and
primary cause of all motion, and this is in itself not controversial; but
Descartes ther~ goes on to assert that the secondary causes of the
particular m o t i o n s of bodies are not bodies themselves, nor forms
immanent in bodies, but certain laws proceeding from God. When God
preserves and governs the world through his ordinary concourse (as
opposed to miracles), he "conserves all that matter in [or by] the same
modus and the same ratio in which he previously created it" (art. 36),
or "by the same action and with the same laws with which he created
it" (art. 42). In both of these parallel passages (and a third, earlier in
art. 36), the conclusion is immediately drawn that, in conserving the
totality of matter, God "also always conserves the same amount of
motion in it" (art. 36). The argument seems to be that motion is
constant because it proceeds from God, or more precisely because it
proceeds from the modus, ratio, action, or laws by which God governs
the totality of matter: for "we understand the perfection to be in God,
not only that he is immutable in himself, but also that he operates in
a supremely constant and immutable modus" (art. 36). Because bodies
have no active natures of their own, all their motions are governed
solely by this constant modus or ratio of God's operation, and therefore

all their motions are constant. The only possible exception would be
for motions proceeding from human and angelic minds, and Descartes
explicitly refuses to explore this exceptional case (end of art. 40),
reserving it for a treatise De Homine, which he was never to write.
All this seems too easy. Three questions arise: what is this modus or
ratio, or what are these laws? How do they decide whether bodies
move in straight lines or in circles? Finally, how will Descartes meet the
obvious Aristotelian objection, that the sublunar motions we ordinarily
experience do not remain constant, but change and stop?
The first question has two obvious answers, both of which I find
unsatisfactory. The first is that there is no entity which is this modus:
the modus is just the manner of God's operation, and manners should
not be reified. I think this answer is wrong: it cannot account for the
parallel passage in art. 42, which has actio and leges instead of modus
and ratio. 16 Descartes recognizes a special ontological status for nonsubsistent entities, which are not strictly things but are also nothing:
sometimes he calls these entities eternal truths, but ratio and lex are
also among his favorite terms for this kind of being. Thus Descartes
says (at Descartes 1964, vol. VII, p. 435) that there is nothing which
does not depend on God: "not just nothing subsistent, but also no
order, no law, and no ratio of truth or goodness". Orders, laws, and
rationes of truth or goodness are not subsistent ~
things, but they are
norms or standards by which things are measured and which serve to
guide or channel God's operation among the things. These laws do not
subsist in God, as accidents in his substance; rather, they proceed from
God, both toward the minds which know them and toward the bodies
which obey them. In particular, the ratio or lex of God's conservation
of matter proceeds from God towards the bodies, and, being immutable, always produces in them the same amount of motion.
We can now see what is wrong with the second obvious answer:
namely, that the ratio and the laws are simply the three 'rules or laws
of nature' which Descartes deduces, in art. 37 and following, from the
general principle of divine immutability. Descartes says that the rules
or laws of nature are "the secondary and particular causes of the various
motions which we observe in individual bodies" (art. 37). But Descartes
does not intend to suggest that propositions are causes, though he may
speak loosely as if they were. Laws or rationes or eternal truths may
be causes, but eternal truths are not ultimately propositions: they are
the real essences that are the subject matter of the propositions and

make the propositions true. ~7 The laws which cause motion are not
Descartes's three propositions, but the reality which those three propositions describe.
I think the true answer is that Descartes conceives the law by which
G o d moves bodies to be something very much like Avicenna's "inclination to motion", which proceeds to the heavenly bodies from their
separate movers, and which substitutes for an active nature in the
bodies themselves. In various passages Descartes speaks about such an
inclination to motion, in terms similar to Avicenna's. Thus in a letter
to H e n r y More, Descartes agrees that "matter left freely to itself, and
receiving no impulse from elsewhere", (Descartes 1964, vol. V, p. 404)
will remain at rest; but in fact "it is impelled by God, who conserves
in it as much motion or translation as he put in it from the beginning".
The impulse to motion does not come from the nature of matter, but,
Descartes immediately adds, the motion is "no more violent to matter
than rest is", because bodies have no contrary action or positive force
with which to resist it; motion proceeding from the divine impulse can
therefore be said to be natural to matter.
If we understand this similarity between Descartes and the older
philosophical tradition (of which Avicenna is a representative), we can
also understand the divergence which comes in their answers to our
second question: how do the laws (whatever they are) determine
whether bodies should move in straight lines or in circles?
Descartes believes that the divine impulse to motion leads bodies
to move in straight lines, because only rectilinear motion is rational
motion:
O n e must say that God alone is the author of all the motions which there are in the
world, inasmuch as they are, and inasmuch as they are straight, but that it is the various
dispositions of matter which render t h e m irregular and curved; just as the theologians
teach us that G o d is also the author of all our actions, inasmuch as they are, and inasmuch
as they have some goodness, but that it is the various dispositions of our wills which can
render them vicious. (Descartes 1964, vol. XI, pp. 46-7)

Now the older tradition had maintained, in very similar terms, that
only rational motions proceeded from divine Reason, and that deviations from rational motion were due to the incapacity of matter; but
Aristotelians and Platonists identify the rational motion as circular
motion.
Descartes, unlike Avicenna, unlike Buridan, and unlike Galileo,

cannot possibly regard circular motion as the rational motion; this is
ruled out by his abstract consideration of body as bare geometrical
extension, without limit or center. Descartes agrees with Avicenna that
the will of the divine mover "does not cease to generate inclination
after inclination in its body" (Avicenna, as quoted above); these inclinations last only for a moment and pass immediately out of existence,
but are continually replaced by equivalent inclinations, because the will
of the divine mover is constant. Because of the "immutability and
simiplicity of the operation through which G o d conserves motion in
matter" (art. 39), God always conserves motion "precisely as it is in
that same m o m e n t of time in which he conserves it, having no regard
[nulla habita ratione] to what perhaps it was a little while before".
Avicenna would say that the conservation of circular motion satisfies
this condition: the sun's mover always gives the sun an inclination to
move westward around the earth, and it always reproduces this inclination in the same direction, westward, without referring to the sun's
previous history. But we can say that this inclination is in 'the same
direction' from moment to moment only by referring it to the center
of rotation, which is (for Avicenna) the center of the universe. For
Descartes, however, the universe has no center, and any reference to
a center of rotation is extrinsic to the inclination to motion. Thus
of all motions, it is only the straight which is entirely simple, and whose whole nature is
c o m p r e h e n d e d in an instant: for to conceive it, it is enough to think that a body is in the
act of moving in a certain direction, which occurs in each of the instants which can be
picked out while it is in motion. Whereas, to conceive circular motion, or any other there
m a y be, one must consider at least two of its instants, or rather two of its parts, and the
relation between them. (Descartes 1964, vol. XI, pp. 44-45)

Descartes knows that no actual motion, rectilinear or otherwise, can
take place in an instant; but he insists that "all that is required to
produce [rectilinear motion] is found in bodies in each instant which
can be picked out while they are in motion, but not all that is required
to produce circular motion" (ibid.). In terms of a modern mathematical
understanding of motion, this is nonsense: there is no sense in which
the first derivative of a body's position is 'comprehended in an instant',
but the second derivative is not. But in terms of a theory of inclination
or impetus, Descartes's assertion makes excellent sense: at each instant
what G o d creates in a body is a bare inclination to move with a certain
speed in a certain direction, not rectilinearly or circularly or in any
other determinate way; but at eaeh instant G o d renews in this body an

inclination to move with the same speed and in the same direction, and
so he produces a uniform rectilinear motion.
So far, we have avoided the greatest and most obvious problem for
Descartes's theory of the causes of motion: on Descartes's account, God
produces only rational motion, which is uniform rectilinear motion. But
God is the only source of motion, excepting the case of finite minds:
how then is it that motions other than uniform rectilinear motion are
in fact observed, both in the heavens and on the earth?
The way Descartes deals with the difficulty reveals perhaps his most
profound divergence from the old Platonic-Aristotelian tradition. The
older philosophers held that circular motion was the only rational motion and that this motion was perfectly realized in the heavens: since
the phenomenal motions of the heavenly bodies are not perfectly circular, they encouraged the construction of astronomical hypotheses to
resolve the phenomenal motions into perfect circles. But since rational
motion does not appear to be fully realized beneath the moon, they
concluded that sublunar bodies were not fully rational, that their natures prevented them from fully receiving the divine impulse toward
order; thus while sublunar bodies obey an approximate rationality, we
cannot construct an exact science of their motions, and there is no point
in trying. Descartes refuses to accept this solution: for him bodies are
purely intelligible in their essence, and he will not consign any portion
of the physical world to the realm of mere semi-intelligible phenomena.
The world is highly complex, but it must be, in principle, fully intelligible. Thus for Descartes the problem of sublunar physics is the same
as the problem of celestial physics: to explain how simple laws or
inclinations to rational motion, compounded with one another in complex configurations, yield the apparently disorderly phenomena which
we observe.
Now we have already quoted Descartes as saying, in very traditional
language, that "the various dispositions of matter" can distort the
impulse to motion into crooked and irregular paths, just as our will can
distort the divine impulse towards the good. But by Descartes's own
view the analogy cannot be perfect: minds have the power to resist the
divine determination, and bodies do not. The dispositions of matter
can render motion crooked and irregular only by complicating it, by
bringing two impulses to motion together in the same part of matter,
forcing them to be resolved into a single resultant motion which will
no longer be uniform.

This happens when bodies collide, as a plenum of bodies in rectilinear
motion inevitably must, unless the whole universe is moving with a
single rigid motion. For the Aristotelians, this had been an argument
that the primary motion must be circular, since no rectilinear motion
could continue indefinitely. Descartes agrees that actual motion must
go in circles, but he insists that all motion is intrinsically rectilinear and
that a moving body tends to continue in a straight line unless some
other body prevents it. Thus circular motion, even in the heavens,
cannot simply be posited: it must be explained as the result of collisions
of bodies moving in straight lines.
Descartes insists that collisions are not violations of the law of conservation of motion; they are just circumstances dictating that this law
must be observed in a complicated way. Motion, or rather the impulse
to motion continually proceeding from God, remains constant: but this
constant power "now applies itself to some and now to other parts of
matter" (Descartes 1964, vol. V, p. 405), so that in a collision one body
can transfer some of its motive force to another. Descartes attempts to
calculate how much motion bodies will lose and gain in collisions, and
so discover universal rules of impact. Descartes's way of calculating
the quantity of motion is crude and unargued, and all his subsequent
conclusions are wrong. He is struggling, with inadequate data and
inadequate conceptual equipment, to explain how a simple constant
force, governed by a universal law of conservation, can produce phenomena of indefinite complexity, so that "even this continual mutation
in creatures is an argument of the immutability of God" (art. 42). If
Descartes had little success in explaining phenomena through simple
laws, he at least succeeded in laying down a challenge for other physicists.
Now, in setting out Descartes's thought on the causes of motion, and
on the role of God in establishing the law of conservation, it would
have been possible to start at the end, with Descartes's law of the
conservation of the total quantity of motion in the universe. But this
would give a distorted picture of the way Descartes thinks about conservation. Descartes's fundamental idea, shared with Aristotelians and
Platonists, is that God communicates his constancy to the world by
continually reproducing a constant impulse to motion in a given body.
Because Descartes makes this conservation universal, not restricting it
to bodies with apparently uniform motion, he is forced to invoke the
transference of motion in collisions in order to save the phenomena.

In the process, Descartes speaks of an amount or quantity of motion,
and formulates what looks like a modern conservation law, with a
specified "conserved quantity". But this is just an accidental by-product
of Descartes's great innovation, which is to extend to all the parts of a
uniform space the divine conservation of motion formerly restricted to
the heavenly bodies.
My report on Descartes generally supports Duhem's thesis of continuity between medieval and early modern discussions of the causes of
motion. At a sufficiently abstract level, Descartes's theory of the causes
of motion is very close to the older theory represented by Avicenna;
the great difference, of course, is Descartes's conception of body as
extension, which abolishes the finite universe and the privileged status
of the heavens. The study of Descartes, again, confirms Duhem's view
of the importance of medieval discussions of impetus: but we must
consider impetus theory in a broad way, not as a particular explanation
of the motion of projectiles, but as the Platonist (or Platonizing Aristotelian) discussion of the relation between separate and immanent forms
as causes of motion. The doctrine of a natural permanence of impetus,
which Duhem claimed to find and Maier claimed not to find in various
fourteenth-century figures, proves not to be important for Descartes:
conservation of motion is consistent with the doctrine that all motion
always proceeds from a mover, as long as that mover is God.
Perhaps our most surprising result is the continued vitality, for Descartes, of the Aristotelian and Platonist doctrine of separate incorporeal
movers. In a way this would have pleased Duhem, for Descartes is
certainly dismissing any angelic movers, and letting the will of God
take over their functions. But Duhem suggests that "the instant when
the stars stopped being perceived as moved by divine beings" marked
the divide between ancient and modern science (Duhem 1913, p. ix).
This division does not work, at least not for the one peculiar strand of
early modern science which is Cartesian physics. The less naturalistic
the Aristotelian account of celestial motion became, the closer it came
to Descartes. Descartes could not have used an account of bodies as
naturally disposed to motion by their own substantial form; he could
and did use an account of bodies as moved by a separate divine Reason.
Precisely because the separate movers were outside the natural order,
they could survive the destruction of the old world picture, and play a
constructive role in one variety of the new physics.

NOTES
* I would like to thank Daniel Garber, Alison Laywine, and Ian Mueller for their
comments. Since I have not seen a text of Professor Westman's remarks, either before
or after he delivered them, I cannot respond to his criticisms.
1 Duhem (1913). My summary of Duhem's work corresponds closely to his own review
of (what he saw as) his chief results in his preface to this volume.
2 Here I am summarizing Maier's main points in criticism of Duhem in her article 'The
Significance of the Theory of Impetus for Scholastic Natural Philosophy', collected (in
English translation) in Maier (1982), pp. 77-102.
3 By an 'Aristotelian' I mean here any writer who accepts Aristotle as an authority in
philosophy, and who therefore prefers not to disagree with Aristotle when he can avoid
it; some Aristotelians will be more ready than others to disagree with Aristotle on special
occasions, or to interpret Aristotle's text in implausible ways to harmonize him with
other authorities. How far Aristotle himself was an Aristotelian depends on how far he
tried to remain consistent with himself, an issue I will not address here. A 'Platonist',
similarly, is a writer who accepts Plato as an authority. Thus the Athenian and Alexandrian philosophers of the fifth and sixth centuries A.O. are (to varying degrees) both
Aristotelians and Platonists at once. The histories of Aristotelianism and Platonism are
closely interwoven, and it is a serious mistake to look only at Aristotelians (or, worse,
only at 'pure' Aristotelians) in studying the medieval background to early modern science.
4 I will frequently keep nous in the original, and use it as a technical term within an
English context. It is translated into Arabic as 'aql, which often becomes intellectus in
Latin, but in the context of celestial physics becomes instead intelligentia. In citing Arabic
texts, I will retranslate the Arabic 'aql back into the Greek nous. For what follows, I
will be chiefly interested in the paradigmatic case of the outermost heaven; I will not
explore the problem of the plurality of unmoved movers and their relation to the first
mover.
5 See Duhem (1913), p. ix. He adds there that the moment when Buridan made this
proposal marked the line "separating the reign of ancient science from the reign of
modern science".
6 I will necessarily be brief and will discuss only selected thinkers and texts. I give some
interpretations which are controversial, particularly of the Philebus and Timaeus (where
I generally agree with Hackforth and with the consensus of the ancient Platonists), and
of Aristotle De Anima III, 5 (where I agree with Alexander of Aphrodisias). I cannot
defend these interpretations adequately here; this is inevitable, in a study not primarily
devoted to Plato and Aristotle. I will develop these interpretations at length in other
works.
7 See Hackforth (1945) and Hackforth, 'Plato's Theism', collected in Allen (1965).
8 Compare Plato: "nous is either the same as truth, or it is of all things the most like to
it and the truest" (Philebus 65D).
9 Simplicius In Aristotelis Physicorum Libros Quattuor Posteriores Commentaria, in
(1882), vol. 10, p. 1219, quotes Alexander as saying this in his (now lost) commentary
on De Caelo Book II. Simplicus remarks there that Alexander is interpreting Aristotle
"harmoniously to his own opinion about the soul", namely that soul is inseparable from
the body (and thus mortal), as a nature would be; it is clear that this implication for the

soul is why all the Platonizing commentators object to Alexander's doctrine of the causes
of celestial motion. They routinely refer to the doctrine of the soul's mortality as "his
[Alexander's] own opinion", and accuse him of forcing Aristotle to agree with him; in
fact their charge suits themselves better than Alexander. Their arguments (besides the
doctrine of immortality) for denying that Aristotle could count the soul as a nature come
from Aristotle's description of the soul as the entelechy of a certain kind of natural body:
soul is therefore something superadded to a body which already possesses a nature.
10 Simplicius In Aristotelis De Caelo Commentaria, in (1882), vol. 7, p. 382; Simplicius
is commenting on De Caelo II, 1, which he is harmonizing with Timaeus 34A and other
Platonic texts. The 'divine man' is not (as the editor wrongly says) Plato, but Plotinus;
the reference is to the opening sentences of Plotinus II.2, 'On the Motion of the Heaven',
which in turn are explicating Timaeus 34A.
u While I do not mean to devalue the role of John Philoponus in the history of impetus
theory, I do think it is important to bring out the rote of Avicenna, who is much more
squarely in the mainstream of the history of philosophy and science. Duhem, pp. VI-VII,
says that the late Greek and Arab philosophers do not even mention impetus theory,
and he implies that this is because they despised its (supposed) Christian origins. While
everyone now knows that Duhem was wrong about this, I think it is important to bring
out just how universally Platonists and Platonizing Aristotelians accepted some version
of impetus theory.
12 This chapter, from which the subsequent quotations are drawn, is Book IX, Chapter
2 of the Metaphysics of the Shifa'. I translate from Ibn Sina 1960, in which the chapter
is pp. 381-93.
13 Buridan proposes this imaginatio, explicitly qualifying it as such, at Buridan (1942),
pp. 180-81, and in other works. Throughout this work (e.g., at p. 132), and in other
works, Buridan continues to uphold and presuppose the theory of moving intelligentiae.
14 For a discussion of Descartes's use of the older tradition, see my unpublished.dissertation, Menn 1989. I am better able there than here to defend some controversial
interpretations.
15 The Principles of Philosophy is found in Descartes (1964), vol. IX, pt. 1. I will refer
to the different sections of Part Two of the Principles simply by their article numbers.
16 The French translator also uses "les mesmes loix" for the "eadem ratione" of art. 36.
17 Thus Descartes says at Descartes (1964), vol. I, p. 152: "he [God] is the author of the
essence as well as of the existence of creatures: but his essence is nothing other than
these eternal truths"; and there are quite a few parallels. It is not possible to read
Descartes as explaining essence in terms of eternal truths; in context, the explanation is
clearly the other way around.

REFERENCES
Allen, R. E. (ed.): 1965, Studies in Plato's Metaphysics, Routledge & Kegan Paul,
London.
Buridan, J.: 1942, Quaestiones Super Libris Quattuor De Caelo et Mundo, Mediaeval
Academy of America, Cambridge, Massachusetts.

Descartes, R.: 1964: Oeuvres de Descartes, Adam et Tannery (ed.), Nouvelle Pr6sentation, Vrin, Paris.
Duhem, P.: 1913, Etudes sur LOonard de Vinci, troisibme s6rie, Les Prgcurseurs Parisiens
de Galilde, Hermann, Paris.
Hackforth, R.: 1945, Plato's Examination of Pleasure, Cambridge University Press, Cambridge, England.
Ibn Sina: 1960, Al-Shifa', Al-llahiyyat (2), Government Printing Organization, Cairo.
Maier, A.: 1982, On the Threshold o f Exact Science, University of Pennsylvania Press,
Philadelphia, Pennsylvania.
Menn, S.: 1989, Descartes and Augustine, unpublished University of Chicago dissertation.
Proclus: 1968, Thdologie Platonicienne, Livre I, Les Belles Lettres, Paris.
Simplicius: In Aristotelis De Caelo Commentaria, in 1882., Commentaria in Aristotelem
Graeca, Reimer, Berlin, Vol. 7.
Simplicius: In Aristotelis Physicorum Libros Quattuor Posteriores Commentaria, in 1882,
Commentariu in Aristotelem Graeea, Vol. 10.
Department of Philosophy
Princeton University
Princeton, New Jersey 08544
U,S.A.

D U H E M A N D KOYR]~ ON D O M I N G O

DE SOTO

ABSTRACT. Galileo's view of science is indebted to the teaching of the Jesuit professors
at the Collegio Romano, but Galileo's concept of mathematical physics also corresponds
to that of Giovan Battista Benedetti. Lacking documentary evidence that would connect
Benedetti directly with the Jesuits, or the Jesuits with Benedetti, I infer a common
source: the 'Spanish connection', that is, Domingo de Soto. I then give indications that
the fourteenth-century work at Oxford and Paris on calculationes was transmitted via
Spain and Portugal to Rome and other centers where Jesuits had colleges, and figured
in the rise of mathematical physics at the beginning of the seventeenth century. A result
of these researches is their vindication of Duhem, as contrasted with Koyr6, on the
origins of modern mechanics.

Pierre Duhem and Alexandre Koyr6, both eminent French historians
of science, held radically different views of the importance of Domingo
de Soto for the evolution of modern science. For Duhem, L6onardo
da Vinci was the linchpin in a development that stretched from the
Doctores Parisienses to Soto, and Soto himself was the proximate source
of Galileo's early writings and of the ideas contained in his later works
(Duhem 1906-1913). Duhem based his analysis on two of Galileo's
early manuscripts, now numbered 46 and 71 in the Galileo Collection
in Florence, which had been transcribed and published by Antonio
Favaro in the National Edition of 1890 with the titles Juvenilia and De
motu respectively. For Koyr6, on the other hand, Soto was merely an
enigma, a Spanish scholastic isolated from the main flow of European
thought (Koyr6 1964). In his view neither Soto nor the Parisian doctors
nor L6onardo figured importantly as sources of Galileo's science. Following Favaro's lead, Koyr6 preferred to see the whole of that tradition
summarized in the writings of two of Galileo's Italian predecessors,
Francesco Buonamici and Giovan Battista Benedetti (Koyr6 1939,
1978). The first he discerned behind Galileo's MS 46 and the second
behind his MS 71. The medieval and Renaissance development that
had been traced in such detail by Duhem might be of antiquarian
interest, but it was not at all necessary for Koyrd's understanding of
Galileo and the 'new science' he had brought into being.
Some years ago, at a conference in this Center, I focused on the
Synthese 83: 239-260, 1990.
© 1990 Kluwer Academic Publishers. Printecl in the Netherlands.

debate between Duhem and Favaro as recorded in Favaro's 1916 review
of Duhem's l~tudes sur Ldonard de Vinci and his 1918 resumption of
that review in an essay entitled 'Galileo Galilei e i Doctores Parisienses'
(Favaro 1916, 1918). My conclusion then was that, eminent though
both were as scholars, neither had gone far enough in his researches;
if they had, the dispute between them could have been dissolved in
terms of what I was then developing as a 'qualified continuity thesis'
(Wallace 1978, 1984b). In this essay I wish to enlarge on that theme
by focusing not on Favaro but on Koyr6, and by doing so in light of a
third Galileo manuscript that was completely misjudged by Favaro,
excluded by him from the National Edition, and as a consequence was
unknown to both Duhem and Koyr6. I refer to MS 27, the manuscript
containing Galileo's treatises on Aristotle's Posterior Analytics, recently
transcribed and edited by William F. Edwards and myself (Galilei
1988). This manuscript provides yet stronger support for Duhem's continuity thesis - but in a way that is somewhat surprising in that it allows
one to integrate Koyr6's findings into it and so include Benedetti as
another possible link between Galileo and Soto. The intermediary that
makes the linkage possible is the one that enabled me to dissolve the
Duhem-Favaro controversy well over a decade ago, namely, the Jesuit
tradition at the Collegio Romano. It is clear now that Galileo's MS 27
derives from lectures given at the Roman College, and, in light of that
derivation, that MSS 46 and 71 derive similarly from the same source
(Wallace 1986). What is more problematical is how to relate Benedetti
to the Roman Jesuits. I shall therefore start with the Benedetti-Jesuit
relationship and then work back from this to Domingo de Soto.

BENEDETTI

AND JESUIT

SCIENCE

At first glance there would seem to be little that would connect the
Collegio Romano, the Jesuit university founded by Ignatius Loyola in
Rome in 1551, with Giovan Battista Benedetti, the patrician of Venice
whose life spanned the years from 1530 to 1590. Benedetti's visits to
Rome apparently were few. He is recorded as having lectured there on
the science of Aristotle in the winter of 1559-1560, when the Collegio
was but a fledgling institution, but to my knowledge had no contact
with Jesuits at that time. From the Collegio side, in the years up to
Benedetti's death there seems to have been little appreciation of his

scientific work on the part of its philosophy professors, although he
was known to the eminent mathematician on the faculty, Christopher
Clavius. Such tenuous connections offer little basis for a documentary
analysis of possible ties between Benedetti and the Roman Jesuits
(Wallace 1987b, nn. 1-5).
In the absence of such evidence, I shall turn to a conceptual study
and focus instead on the role of mathematics in the study of nature as
an apt basis for comparison. In it I aim to show that by the time of
Benedetti's death in 1590, the faculty at the Collegio R o m a n o had
come to a view of mathematical physics very similar to his. This would
seem to be an important consideration, for it was such a conception of
mathematical physics that channeled into MSS 27, 46, and 71 of the
young Galileo and thence exerted an influence on the development of
his science. Thus the terminus ad quem of my investigation is Galileo's
writings on motion and mechanics around the year 1590. The terminus
a quo is somewhat more problematical, and I will come to that later.
For the moment I shall identify it simply as 'the Spanish connection',
based on the facts that, on the one hand, Benedetti's father was a
Spanish philosopher and physicist (or physician) and that many of his
own professional contacts were with Spaniards, and, on the other, that
the early Jesuit professors at the Collegio R o m a n o were also Spanish
and imported from the Iberian peninsula several ideas that proved
seminal in the new mathematical physics (Wallace 1987b, nn. 6-9).
Starting, then, in s o m e w h a t ahistorical fashion with the terminus ad
quem, let me characterize briefly the concept of science that emerges
clearly in Galileo's early treatises on motion in MS 71 and that continued to dominate his later writings down to the Two New Sciences of
1638. This was very much a mathematical physics that proposed itself
as a scientia and presented its reasonings in the form of demonstrationes;
its model was ostensibly that of Archimedes, but the ideal was already
Aristotle's as formulated in his Posterior Analytics. Working out the
implications of his new scientia (in effect a scientia mixta or scientia
media, subalternating physics to mathematics), Galileo was sharply
critical of the causal analyses found in Aristotle's Physics and De caelo,
while at the same time he was intent on searching out, in an Aristotelian
mode, the verae causae of natural phenomena. Local motion (motus
localis) was his major concern; to explain this he invoked the principal
concepts used by Aristotle - nature and violence, time, place and space,
force and resistance, causality - although he rejected others associated

with the medium through which the moving object passed, e.g., Aristotle's teaching on the void and his solution to the projectile problem. In
their place Galileo substituted the scholastic concept of impetus, which
he used to explain both violent and natural motion. His most important
methodological innovation was his clever use of suppositiones when
framing his demonstrations, making them amenable to the use of limit
concepts and to applications in experimental situations where a mathematical ideal could be closely approximated in the physical world (Wallace 1987b, nn. 10-14).
Much of my recent research has been directed at showing how this
view of science is indebted to the teaching of Jesuit professors at the
Collegio Romano, whose lecture notes on logic and natural philosophy
were the proximate source of Galileo's MSS 27 and 46 and prepared
for the De motu antiquiora of MS 71. But those who are acquainted
with the works of Benedetti will surely have noticed how closely Galileo's concept of mathematical physics just sketched by me corresponds
to that of Benedetti. Such correspondence suggests points of comparison between Benedetti and the professors of the Collegio. To develop
it, we must look in detail at Benedetti's main theses and then see how
these compare with related teachings among the Jesuits whose lecture
notes I have studied (Wallace 1987b, nn. 15-16).
BENEDETTI'S

MATHEMATICAL

PHYSICS

For convenience let me divide my consideration of Benedetti's physics
into two parts, the first concentrating on its logical and methodological
foundations, the second on its treatment of problems relating to local
motion. With regard to the first, there can be no doubt that, from the
outset of his career, Benedetti wished to reinforce his arguments as
much as possible with 'mathematical demonstrations' (Benedetti 1553);
in his last and most important work he identifies his basic disagreement
with Aristotle as based "on the unshakable foundation of mathematical,
philosophy, on which I always take my stand" (Benedetti 1585, p.
196). This presupposes, of course, a difference between physics and
mathematics, of which Benedetti was well aware: "balances or levers
are not pure mathematical lines", he writes, "but are physical, and as
such exist in material bodies" (144). 2 Again, "since balances are material and are s u s t a i n e d . . , not by a mathematical point but by a line
or a physical surface having a material existence, some resistance arises
to the motion of the arms" (153). Yet he wished to use mathematical

principles, such as that "a sphere touches a plane at only one point"
(155), to establish physical conclusions. The only way he could do this,
he recognized, was through the use of appropriate suppositions and
thought experiments. It is thus important to recognize how frequently
the terms suppositio and i m a g i n e m u r (and their variants) recur in Benedetti's writings. Well known are his disagreements with Tartaglia and
Jordanus Nemorarius in his solution of mechanical problems; invariably
these are occasioned by the divergent suppositiones on which the
respective solutions are based. For example, Benedetti frequently reproves Tartaglia for supposing that the "lines of inclination" going from
the ends of a balance to a distant center of gravity are parallel (150).
Yet on some occasions he makes the same supposition himself, noting
that the line of inclination is fere perpendicularis to the beam of the
balance or that, if the angle it makes is not a right angle, the deviation
is negligible. But, when discussing the imagined case of a balance
situated close to the earth's center, he rightly insists that the approximation cannot be made and that the simplifying supposition cannot be
employed in a rigorous proof (143).
Such suppositions are important in the treatment of problems in
statics, but they.are crucial for the development of a science of dynamics. Benedetti was intent on discovering the verae causae - an expression
that occurs repeatedly in his writings - of various kinds of motion in
the universe, both natural and forced. An important contribution was
his study of horizontal motions on the earth's surface; here he was
convinced that the only truly natural motion is circular, for this alone
can be perpetual (184). But, he reasons, there is "no noteworthy difference" between a perfect sphere and a plane surface of small extent.
For this reason one will encounter no difficulty in moving a sphere
along a horizontal surface; indeed, it can be moved by "a force no
matter how small" (156). In another context he qualified an argument
to specify that it holds only "when all impediment is removed" (154).
Such insights, plus Benedetti's frequent allusion to the natural tendency
of a body when released from a sling to move in a straight line, shows
how close he came to the principle of inertia later formulated by Sir
Isaac Newton.
Moving on to his study of problems relating to local motion, we can
treat these under three headings, namely, those relating to motion in
general, those relating to falling motion, and those relating to the
movement of projectiles. With regard to the first, Benedetti was Aristotelian in his conviction that nature is an inner source of motion in a

body; even forced or violent motion he saw as caused by an impetus
or virtus movens impressed within a body. But unlike Aristotle he
seems not to have invoked a sharp dichotomy between natural and
violent motion, or between curvilinear and rectilinear motion, regarding
the latter two as mathematically comparable (194). He does not discuss
explicitly the possibility of a motus medius, i.e., one intermediate between the natural and the violent, but for him horizontal motion for
limited distances would answer to that description. And in the case of
reflex motion, he invokes the principle that a circle touches a line at
only one point to argue that no intermediate rest (quies medius) interrupts the upward and downward motion of a body, making its motion
truly continuous (184).
Benedetti is most known, of course, for his study of falling motion,
especially for his argument contra Aristotelem et omnes philosophos
that velocity of fall is dependent not on weight but on specific gravity,
and therefore is conditioned by the medium in which the body falls and
the resistance it encounters (Maccagni 1983). He proposed that velocity
of fall increases with distance of travel because impetus builds up
naturally in the falling body, and that all bodies would fall with the
same speed in vacuo, where buoyancy and resistive effects can be
neglected. Gravity and levity became for him relative concepts, so that
air has no weight in air, nor water in water. And he analyzes the case
of a body falling through the center of the earth to argue that it would
oscillate about the center, on the analogy of the motion of the bob of
a pendulum of exceedingly long length (Benedetti 1985, pp. 174-85,
368-69).
Equally ingenious is Benedetti's study of projectile motion, which is
dominated by his skillful use of the concept of impetus, already referred
to. This he regarded as a force impressed on a body from without but
that moves it from within, decreasing gradually and continually with
the body's motion (160). Most motions involving trajectories of bodies
he saw resulting from a composition of motions, partly natural and
partly forced (161), and in this is seen as having noticeably advanced
beyond the teaching of Tartaglia.

COUNTERPARTS

IN JESUIT

TEACHINGS

Such was the contribution of Benedetti to the foundations of mathematical physics by the time of his death in 1590. The question I now would

raise is this: how similar were the teachings of Benedetti as I have just
outlined them to those at the Collegio Romano during the years, say,
from 1560 to 15907 An answer is difficult because of the paucity of
records that have survived from this period. At the beginning, Francisco
Toletus taught the physics course in Rome during the academic year
1560-61, and his printed text gives indication that his ideas were fairly
similar to Benedetti's. But only a year or two later, Benedictus Pererius
took over the course in 1562-63, and, as his textbook indicates, set it
on a path almost diametrically opposite to his predecessor's. Decidedly
antimathematical and Averroist in his approach, Pererius combatted
most of the Benedetti's theses concerning motion, not naming him
explicitly or even being aware of his teachings, but simply rejecting out
of hand the principles on which they were based (Giacobbi 1977).
This mentality apparently persisted at the Collegio for some fifteen
years, and then gradually changed owing to two factors: the influence
of Clavius, who fought strenuously to give mathematics a respectable
place in the curriculum, not merely in its own right but also as an
adjunct to natural philosophy; and the advent of a new physics professor, Antonius'Menu, who was much interested in 'calculatory' techniques and imported them where possible into his lectures. A series of
professors who followed Menu - Paulus Vallius, Muzius Vitelleschus,
and Ludovicus Rugerius - developed their teachings on motion and the
heavens along lines more acceptable to Clavius, and thus closer to
Benedetti. Finally one of Clavius's special students, Giuseppe Biancani,
synthesized all this work by systematically elaborating a mathematical
physics capable of dealing with the problems of natural philosophy
(Giacobbi 1976).
I shall elaborate more fully on this development later in the essay.
Suffice it here to call attention to Vallius's commentary on the Posterior
Analytics, particularly to his treatise De praecognitionibus, which was
appropriated by Galileo in his MS 27 (Galilei 1988); this, taken in
conjunction with Clavius's preface to his Elements and Biancani's later
emendations, shows how suppositiones can be employed to uncover
causes and supply demonstrationes in these difficult subject matters.
Menu and Vallius recovered the concept of impetus and showed how it,
and other notions in the scholastic tradition, could improve Aristotelian
teachings as these were being advanced by the peripatetics of their day
(Wallace 1981c). Vitelleschus and Rugerius built on these foundations.
Vitelleschus is particularly important for his awareness of Benedetti's
analysis of falling motion, though he knew it only through a work

by Jean Taisnier that plagiarized Benedetti's Demonstratio of 1554
(Maccagni 1967). The reference occurs in Vitelleschus's lectures on the
De caelo of Aristotle (given in 1590), where he questions Aristotle's
laws of motion as stated in Books 4 and 7 of the Physics, and directs
his students to the treatises of Bradwardine and Taisnier on the ratios
of motions. In the same manuscript Vitelleschus echoes Benedetti's
sentiment against the authority of Aristotle, stating that it is safer to
abandon some of his teachings than it is to interpret them, for the
authority of a philosopher should be used to confirm the truth, not
abandon it, seeing that truth is the philosopher's friend. Rugerius then
took up Vitelleschus's teachings on the ratios of motion, noting that
Aristotle's rules for comparing motions labor under severe difficulties.
For a fuller discussion of how they might be revised he then refers his
students to the commentaries of Toletus and Soto, among others, in
their commentaries on the Physics (Wallace 1987b, nn. 53-57).
In the writings of Jesuit professors from Menu to Rugerius, therefore,
one can find illuminating discussions of the internal causes of motion,
of the possibility of motion in a void, and of an intermediate or neutral
motion (neither natural nor violent) that can endure perpetually. One
can find too a rejection of the quies medius in reflex motion; a rejection
of Aristotle's dynamical laws of motion; a sophisticated discussion of
gravity, including the distinction between extensive and intensive gravity, similar to Benedetti's notion of specific gravity; a rejection of the
notion that air has weight in air based on Archimedian principles; and
detailed analyses of the factors that cause bodies to accelerate as they
fall. Not all these teachings are the same as Benedetti's, but one gains
the impression that, had the Venetian mathematician visited the Collegio in the years following the publication of his last work, he would
have found a compatible atmosphere in which to advance his researches
(Wallace 1987b, nn. 58-59).
THE

SPANISH

CONNECTION

This, then, brings me back to terminus ad quem with which I began
this discussion. Most of the ideas I have just sketched are to be found,
in various ways, in the lectures of Jesuits in Rome around 1590, in
Galileo's MSS 27, 46, and 71, likewise composed around 1590, and in
Benedetti's publications, probably known to Galileo through Jacopo
Mazzoni, with whom he studied in 1590. I suspect that it was a fusion

of ideas gleaned from Benedetti and the Jesuits that lay behind the
various drafts on motion in Galileo's MS 71. Yet I have found no
documentary evidence that would connect Benedetti directly with the
Jesuits, or the Jesuits with Benedetti, in the development of these
concepts. Was there a common source from which they could have
derived? I suspect that there might have been, and I would like to
speculate about this as the terminus a quo of my investigation - the
'Spanish connection' to which I have alluded above.
A plausible candidate for the origin of a mode of thought that would
allow mathematics to enter into an experimental study of motion is
none other than the Spanish Dominican who first proposed that the
motion of falling bodies is uniformly accelerated with respect to time
- uniformiter difformis is the expression he used - and who was seen
by D u h e m on this account to be a scholastic precursor of Galileo
(Duhem 1906-1913). I refer, obviously, to Domingo de Soto. Soto was
known to the Jesuits; indeed, Toletus had studied under him at Salamanca before joining the faculty of the Collegio, and Rugerius, as we
have seen, called attention to his superior treatment (along with Toletus's) of Aristotle's dynamic laws of motion. Now, in his commentary
and his questions on the Physics, Soto assimilated his doctrine on
impetus to his teaching on gravitas and taught that a falling body accelerates continuously because of the impetus being built up in it during its
travel - ideas very similar to.those found in Benedetti. These notions
are not fully developed in an incomplete edition of Soto's Physics,
published at Salamanca around 1545, but they are present in the edition
of 1551 as well as in the more widely diffused second edition of 1555,
both also printed in Salamanca. Between 1545 and 1550, moreover,
Soto was present at the Council of Trent, which took place just north
of Venice. As the most illustrious theologian in the Dominican Order,
he was surely known to Abbot Gabriel de Guzman and the two Spanish
Dominicans Benedetti praises so lavishly in his Resolutio of 1553 and
his two versions of the Demonstratio of 1554 and 1555, directed, as we
saw, "against Aristotle and all philosophers". While in northern Italy,
it is also possible that Soto became acquainted with experimental work
being done there on laws of fall, which would have buttressed his own
rejection of Aristotle's teaching on this subject. And finally, though I
have found no mention of Soto in Benedetti's Speculationes of 1585, it
may be no mere coincidence that Soto's Physics, both commentary and
quaestiones, was reprinted in Venice in 1582 with an introduction that

gives fulsome praise to his ability as a natural philosopher (Wallace
1987b, nn. 63-68). All bits of coincidental evidence, but all pointing to
Soto as a link that could ultimately tie together Benedetti, Galileo, and
the Jesuits of the Collegio Romano.

SOTO'S

SECOND ENIGMA

Earlier I remarked that Soto was an enigma for Koyr6, but I did not
elaborate on Soto's enigmatic status. Actually two enigmas can be
associated with Domingo de Soto. The first is how he came to know
that the motion of heavy bodies in free fall is uniformiter difformis with
respect to time, and the second is how this knowledge might have been
transmitted to Galileo. The first enigma was what puzzled Koyr6 and
served as the subject of an essay I published years ago with the title
'The Enigma of Domingo de Soto: Uniformiter Difformis and Falling
Bodies in Late Medieval Physics' (Wallace 1968). The second enigma,
to my knowledge, was not explicitly addressed by Koyr6, although it
posed the problematic on which much of his Etudes galil~ennes was
based. Let us address this second enigma now, for, if we can cast light
on that, we may additionally be able to fill a lacuna in Duhem's thesis
about Soto and his importance for Galileo's science. We can do so
through a study of books and manuscripts written by Jesuits in Italy and
Portugal in the century following Soto's publication of his uniformiter
difformis doctrine.
Galileo mentions Soto twice in MS 46, in a Tractatus de elementis
that occupies the last part of the manuscript. We now know that this
Tractatus, as well as other treatises written by Galileo at Pisa around
1589-1591, were based on lectures given by the Jesuits mentioned above
(Wallace 1977). Some of these lectures were published, but the majority
survive only in manuscript. They were based on scholastic and Renaissance authors, whom they cite extensively, and are otherwise prosaic
teaching notes. What makes them somewhat distinctive is the attention
they pay to nominalist teachings deriving from the Calculatores of
Oxford University and the Doctores Parisienses.
The development of these lecture notes took place in Rome at the
Collegio Romano over a period of some thirty years. There the introduction of calculatory thought is traceable to Toletus, himself a Span-

iard, who taught the course in natural philosophy in 1560 and imported
ideas he had learned from Soto at Salamanca. Some of this material
was taken up by two other Spanish Jesuits, Pererius, mentioned above,
who taught natural philosophy at the Collegio between 1558 and 1566,
and Francisco Suarez, who taught theology there between 1580 and
1585. Fortunately these authors published their materials, which have
been analyzed in some detail by Christopher Lewis (Lewis 1980). Lewis
picked out for examination the use by all three of calculatory language
in the following areas of natural philosophy: (1) when discussing problems of action and reaction; (2) when treating the intension of forms
in alteration and identifying distributions of qualities as uniform, uniformly difform, etc. ; and (3) when analyzing the ratios of motions
following the tradition of Thomas Bradwardine.
Of the three Jesuits, Toletus undoubtedly made fullest use of the
Calculatores in these areas, even referring to "the calculator Suisset"
(i.e., Swineshead) by name in his treatments of reaction and alteration.
He also had the clearest understanding of calculatory terminology,
although he frequently departed from positions held at Oxford and
favored instead those developed at Paris. In treating expressions such
as uniformiter difformis, moreover, Toletus made the interesting comment that "these [terms] should be very carefully considered in order
to understand many matters that are met with in physics". Suarez
likewise took up uniform difformity in some detail when analyzing the
action of natural agents in his Disputationes metaphysicae of 1597,
although he rejected the view (apparently subscribed to by Toletus)
that velocity could be viewed as an intensity of motion, which would be
expected of one subscribing to Mertonian developments in kinematics.
Pererius, predictably, showed the least acquaintance with, or interest
in, the calculatory tradition, although he was acquainted with some of
its terminology. In discussing the dynamical laws given by Aristotle in
the seventh book of the Physics, for example, Pererius accepted and
defended them without even a nod in the direction of Bradwardine,
thus showing little sympathy for the mathematical physics developed
two centuries earlier at Merton College, Oxford (Lewis 1980).
As already noted, partially because of his antimathematical bias Pererius was replaced after 1566 and succeeded by a series of other professors. Lecture notes survive from only two who taught between then
and 1585, viz., Hieronymus de Gregorio and Antonius Menu, but the
second of these, Menu, enjoyed the longer tenure and seems to have

had the greater influence. Menu revived the approach of Toletus and
had a notable effect on the Jesuits mentioned above who taught natural
philosophy at the Collegio between 1585 and 1592, namely, Vallius,
Vitelleschus, and Rugerius, all of whose lecture notes survive in whole
or in part. Although some details are lacking, these four professors
supplied the materials on which Galileo's early notebooks on the De
caelo and De generatione and the early versions of his De motu were
based, and so serve to explain Galileo's knowledge of the calculatory
tradition (Wallace 1987a, n. 14).
Menu is of particular importance for standing at the head of this
fifteen-year tradition, which used Mertonian terminology but usually
applied it in ways more consistent with teachings in vogue at Paris in
the fourteenth century and so associated with the Doctores Parisienses.
Indeed, Menu cites these doctors when treating the question whether
the world could have existed from eternity and when discussing the
ratios of the elements. He was also favorable to their adoption of
impetus, or virtus impressa, as necessary to explain the motion of
projectiles. Particularly striking are his arguments in favor of the proposition that "the motion of a simple or compound body through a void
will be successive, for granted that it would encounter no extrinsic
resistance, there would still be intrinsic resistance" to overcome. These
are clearly those of the Parisienses, adopting the calculatory stance of
the Mertonians but applying it to physical problems in the tradition of
Jean Buridan, Albert of Saxony, and others who worked in fourteenthcentury Paris (Wallace 1987a, nn. 15-16).
The lecture notes of Vallius, Vitelleschus, and Rugerius do not employ these particular arguments, but they nonetheless touch on all the
matters pertaining to the mathematical or calculatory tradition that are
to be found in Galileo's early writings. The latter's notes in MS 46 are
written in the form of a questionary based on Aristotle's De caelo
and De generatione. The questions wherein analytical languages in the
Mertonian and Parisian traditions occur most frequently are in the
treatises De alteratione and De elementis, where inquiries are made into
the intension and remission of forms, the parts and degrees of qualities,
and the number and quantity of the elements. There seems little doubt
that all of these materials are derived from lectures given at the Collegio
some time prior to 1591. The precise author is difficult to identify,
however, since correspondences can be found between Galileo's notes
and passages in Rugerius, Vitelleschus, Vallius, and Menu, and indeed

all the way back to Pererius and Toletus. At the present stage of
research Vallius seems to be the most likely candidate, for, although
his surviving lecture notes are incomplete, the portions that survive
show closest agreement with Galileo's text. There is excellent evidence,
moreover, to connect Galileo's MS 27, the one containing questions on
Aristotle's Posterior Analytics, with Vallius's lectures on logic, which
were completed in the summer of 1588 and manifest a good knowledge
of nominalist positions on science and demonstration (Wallace 1987a,
nn. 19-21).
My study of all these materials thus encourages me to go considerably
beyond Christopher Lewis in identifying likely sources of Galileo's
knowledge of the calculatory tradition. Suffice it to mention that citations from Walter Burley and William Heytesbury, as well as Bradwardine and Swineshead, are to be found in these Jesuit lectures. And
not only do such citations occur in discussions involving intension and
remission, latitudes of qualities, and maxima and minima, but they also
occur in discussions of local motion and of Aristotle's dynamical laws
involving ratios between forces, resistances, and velocities of motion.
Vitelleschus, for example, cites experimental evidence against the Aristotelian formulations in Book 7 of the Physics and refers his students
to Bradwardine's De proportione rnotuurn for an alternative view. Rugerius likewise discerns difficulties with Aristotle's rules and, as already
noted, sends his students to Toletus and Soto for more satisfactory
treatments of the ways in which velocity varies at the beginning,-middle,
and end of motion (Wallace 1987a, nn. 22-24).
Of the natural philosophers who taught physics at the Collegio Romano after Rugerius down to 1626, I have thus far located reportationes
of lectures by four other Jesuit professors: Robert Jones, an Englishman, who taught in 1592-93, Stefano Del Bufalo, who taught in 159697 and again in 1598-99; Andreas Eudaemon-Ioannis, who taught in
the intervening year 1597-98, while Del Bufalo had the course in metaphysics; and Fabiano Ambrosio Spinola, who taught in 1625-26. Of
these, the treatments of the first and the last, Jones and Spinola, show
less concern with the calculatory tradition. Del Bufalo, on the other
hand, has a rather full discussion of alteration, degrees of qualities,
intension and remission of forms, and action and reaction - in the last
of which he mentions the teaching of the Calculator and contrasts it
with those of Pomponazzi, Buccaferreus, Flaminio Nobili, Franciscus
Neritonensis, and Zabarella. In his discussions of gravitas and levitas,

moreover, he mentions the Parisienses and compares their teachings
with those of Geronimo Borro and Buonamici - and this in 1597, the
year in which Buonamici's De motu had just appeared. It is noteworthy
that all of Del Bufalo's notes located thus far are in the National Library
at Lisbon, where they had been taken from the Jesuit college at Evora,
having been sent there from Rome by October of 1603, as recorded in
one of the codices containing them (Wallace 1987a, nn. 25-28).
The other professor who deserves mention for his calculatory interests is Eudaemon, who, as already mentioned, had the course in natural
philosophy in 1597-98. In addition to his lectures on the Physics, De
caelo, and De generatione, he left a tractatus in two books on action
and passion and a quaestio on the motion of projectiles, both of which
are written in the calculatory manner. As I have pointed out in my
Galileo and His Sources, Eudaemon is of some importance for the fact
that he discussed "the ship's mast" experiment with Galileo at Padua,
and, along with Biancani, also teaching there, could have influenced
Galileo's use of calculatory terms in his De motu accelerato fragment
and later writings (Wallace 1984a; 1987a, nn. 29-30).
The first book of Eudaemon's work on natural agency, entitled simply
Tractatus primus, is prefaced by five definitions and nine suppositions;
it then develops twenty-one propositions, with proofs and corollaries,
all relating to the ways in which qualities come to be mathematically
distributed as a result of such agency, with occasional geometrical
diagrams in the margins illustrating the text. Noteworthy among the
definitions are the third and the fifth, the third stating that "something
is said to be distributed uniformly difformly when it diminishes in the
same ratio as the distance increases," and the fifth explaining how
quantitative attributes can be ascribed to a quality that is uniformly
difformly distributed. Following the definitions Eudaemon begins his
suppositions, which he prefaces with the note:
Because the matters with which we shall be concerned are physical, it is necessary to take
some propositions from our physical disputations that can be presupposed as principles in
this treatise. Things that are commonly conceded in physical science or are sufficiently
proved and explained m a y be seen in our disputations on De generatione and on the
Physics. A n d since this treatise is principally mathematical, it will not be necessary to
note and prove propositions that come from mathematics.

This notation, and the nine suppositions that follow it, are important
for the fact that they show Eudaemon adopting the stance of a mathe-

matician and attempting to develop a mathematical physics of natural
agency, even though he was a philosopher entrusted with the main
sequence of courses at the Collegio. Also noteworthy is Eudaemon's
first supposition, which reads as follows:
We presuppose that every natural agent acts uniforrniter difformiter on a quantified
subject when applied to it. Physicists commonly concede this, at least with respect to
some parts of the sphere of activity, because we see that when close the agent acts more
vehemently and when farther way less so; therefore, the closer the greater, the farther
the lesser; therefore, as the distance increases the action decreases; therefore the action
is uniformly difform.

Noteworthy here and throughout the treatise is the preoccupation with
the expression uniformiter difformis as applicable to natural agency
(Wallace 1987a, nn. 31-33).
The second book of this same treatise is titled De iis quae in actione
et passione physica contingunt and it begins, like the first, with definitions, ten in number, then notes a single supposition, and concludes
with proofs of thirty-one propositions, some of which contain substantial numbers of corollaries. The reason for this development is not
transparently clear at first reading, but it all becomes intelligible when
we get to the Quaestio de motu proiectorum that follows immediately
after the second book. The entire treatise on natural agency had occupied fifty-one closely written folios; that on the motion of projectiles
coming after it takes up seventy-two more. Divided into three articles,
it inquires first whether the projector moves the projectile immediately
at a distance, then whether the vis movens is within the projectile itself,
and finally whether the virtus movens is located in the medium, and if
so, how (Wallace 1987a, n. 34). Somewhat surprisingly, considering the
fact that his predecessors at the Collegio had all adopted the impetus
explanation of projectile motion, Eudaemon ends up by rejecting an
impetus in the projectile and by putting the virtus movens in the air. I
have not yet analyzed his arguments in detail, but I suspect that his
reason for doing so is to subsume projectile motion under natural
agency so as to show that it slows down uniformly difformly. This, we
may recall, was Soto's position, for he held that falling motion is
accelerated and projectile motion decelerated in the same quantitative
way, namely, uniformiter difformiter.
If such was Eudaemon's thesis in this manuscript, undated but proba-

bly written in 1599, his discussions with Galileo at Padua around 1604
take on special significance. At that time Galileo was looking for a
principle on which he could construct his new science of motion, as we
know from his letter to Paolo Sarpi. His telling Eudaemon that he had
experimented with a stone dropped from the mast of a ship first at rest
and then in motion shows that both were still interested in the problem
of impetus. Eudaemon could therefore have been a source that directed
Galileo's attention around 1604 to calculatory treatments of uniform
acceleration and deceleration, later to be reflected in the De motu
accelerato fragment on which the Two New Sciences would be based
(Wallace 1987a, nn. 35-37).
Let us look back, then, at the situation at the Collegio Romano from
the time of Pererius, say 1566, when he taught, or 1576, when his
textbook was published, to Eudaemon in 1599. In all of that time there
were many references to the Calculatores and Parisienses and how they
impacted on theses in natural philosophy. Not one, however, is to be
found in a printed text - all occur only in manuscript sources. It is not
surprising, therefore, that influences deriving from this tradition have
thus far been overlooked by scholars and so have not been seen as a
significant factor in the growth of mathematical physics among the
Roman Jesuits toward the end of the sixteenth century.
THE

JESUIT

TRADITION

IN PORTUGAL

To move now to the Iberian peninsula, a situation similar to that at
the Roman College existed in the Jesuit colleges there, particularly in
those at Evora and Coimbra. The Coimbran Cursus philosophicus was
a five-volume course, first published at Coimbra between 1592 and 1605
and reprinted often thereafter. My researches have shown that natural
philosophy in Portugal became less technical and mathematical from
the end of the sixteenth century onward, and this possibly explains why
there is no conspicuous use of calculatory terminology in the famous
Cursus. A goodly number of manuscripts from Evora and Coimbra
dating from the 1570s and 1580s are still extant, however, and these
show the same patterns deriving from the Calculatores and the Parisienses as do the lecture notes from the Collegio Romano.
Lectures on the Physics and De caelo for the years 1570, 1582,
1587, and 1588 by professors named Juan Gomez de Braga, Luis de
Cerqueira, Antonio del Castelbranco, and Manuel a Lima respectively

are all extant. Some of these Jesuits taught at Evora, others at Coimbra,
but the substance of their notes is all the same; in some cases the
wording is repeated almost exactly, suggesting a transmission of notes
from one professor to another. In addition, notes from a Trinitarian,
Marcus de Moura, who taught at Lisbon in 1588 are available, and his
lectures are substantially the same as those given by Manuel a Lima at
Evora in the same year. The same could be said of an anonymous set
of lectures on the Physics, De caelo, and Meteorology given at Coimbra
in 1580 (Wallace 1987a, nn. 40-42).
The anonymous lectures of 1580 are a good place to start, for their
author gives a key to the source of most of the materials the others
contain. The fifth chapter of his commentary on the seventh book of
the Physics begins with two questions: (1) whether the velocity of local
motion is to be ascertained from the quantity of space it traverses as
from an effect, and (2) whence the velocity of motion is to be judged
as from a cause. Following his replies to these queries the author writes:
"These last two questions are treated more fully by Domingo de Soto
and can be studied there. For this reason, and especially because of
limitations of time, we will pass over them quickly." And his reply to
the first question indicates the extent of his dependence on Soto, which
I give in the slightly clearer formulation of Cerqueira, who repeated
this material at Coimbra two years later, in 1582:
Sometimes the mobile is m o v e d so difformly with respect to time that, taken [any] part
of time in which it moves, the velocity it has at the middle instant will exceed the velocity
it had or will have at one terminal instant of that time by the same a m o u n t as it is
exceeded by the velocity it had or will have at another [terminal instant]. Such a motion
is said to be uniformiter difforrnis with respect to time, and it is found in heavy and light
bodies when they move naturally, since the more they depart from their starting point
the greater is the velocity with which they move.

This, of course, is the teaching developed by Soto around 1550, which
is reiterated in most of these lecture notes preserved in Portugal
throughout the 1570s and 1580s. It is further explained and extended
to projectile motion by Cerqueira, and by Manuel a Lima again in
1588, in the following terms:
It is customary to ask at this place why it is that things that are moved naturally in
rectilinear motion are moved more swiftly at the end than at the beginning of their motion,
whereas those that are moved violently are moved more swiftly at the beginning . . . . The
reason for this is that, just as the force that exists in the hand of the thrower when

separated from the hand of the thrower, so also gravity and levity, impelling the heavy
and light thing to its natural place, impresses by such motion a certain impulse through
whose agency the motion of the heavy and light thing is made swifter. And this impetus
gets more intense as the heavy and light objects come closer to their natural places,
which is to be understood in terms of the relation of each to the terminus a quo. For if
one and the same stone were now to descend from the middle of a tower and later from
its top, it would descend much more swiftly at the end of the later motion than at the
end of the earlier. For the longer the space that is traversed the greater is the impetus
impressed by levity and gravity throughout the motion, since it is continually intensified
until the thing arrives at its natural place. And since this impetus effects in the heavy or
light thing a motion similar to that which arises in it from gravity or levity, Aristotle
referred to it as an increase of gravity and levity; others, however, speak of it as accidental
gravity and levity, since it is lost as soon as the motion stops.

I give this as one example relating to the ratios of motions; similar
materials relating to action and reaction, wherein the opinions of Heytesbury and the Calculator are discussed, could also be mentioned. But
perhaps this is sufficient for present purposes to show evidences of a
Jesuit mathematical tradition on the Iberian peninsula in the latter part
of the sixteenth century (Wallace 1987a, nn. 43-46).
To return briefly to Italy, I would add that Biancani, who had studied
under Clavius at Rome in the 1590s, wrote detailed defenses and justifications of mathematics and mathematical physics as sciences in the
Aristotelian sense, wherein he shows considerable competence as both
a philosopher and a mathematician. These he explicitly directed against
Pererius and the authors of the Coimbran Cursus philosophicus. Biancani taught principally at Parma, where Giambattista Riccioli was in
turn his student. And Riccioli is of some importance for his verification
of Galileo's experiments on falling bodies. In his Almagestum novum
of 1651 Riccioli recounts that he had first started experimental work in
this field with two other Jesuits in 1629, and then with yet another in
1634. At that time he obtained permission, he says, to read Galileo,
whom he first thought to be in error but later found to be correct. Of
his early work Riccioli writes that
at that time I had not yet come to the better and more evident experiments manifesting
not only an inequality in the motion of heavy bodies but the true increment of their
velocity, increasing uniformiter difformiter toward the end of the motion.

What is interesting here is Riccioli's use of Parisian terminology deriving
from Soto when describing the results to which he had finally come.
This seems to me a fairly good indication that such terminology had

been part of his training too, and persisted in his mind to the middle
of the seventeenth century, i.e., to 1651 (Wallace 1987a, pp. 58-62).
CONCLUDING

REMARKS

From all these indications it would seem that the fourteenth-century
work at Oxford and Paris on calculationes, transmitted via Spain and
Portugal to Rome and other centers where Jesuits had colleges, figured
in the rise of mathematical physics at the beginning of the seventeenth
century. The circumstances of this transmission may help to clear up
two problems that have bothered historians of science. The first of
these is the disparity between Galileo's use of calculatory language and
that of the Mertonians, which has recently been analyzed by Edith
Sylla (Sylla 1986). Such disparity is readily understandable when one
considers that Galileo acquired that language at several removes from
its initial formulators. The second is the lack of a consistent attitude
on the part of the Jesuits toward the use of mathematics in the study of
nature. This becomes intelligible in terms of the tensions that developed
within the Order between the mathematicians and the philosophers,
and the censorship that was invoked to present a 'united front' to the
outside world. Vallius had difficulty with censors within his own Order
when he attempted to have his Collegio Romano lectures on logic and
natural philosophy published in the early 1600s, and we know that
Biancani ran into the same difficulty with censorship when he wrote in
1615 and 1620 in support of Galileo (Wallace 1984a, pp. 141-48).
Invariably the theologians and the leadership within the Order sided
with conservative confreres among their philosophers rather than with
progressive confreres among their mathematicians whenever Church
teaching was involved. As a result, the period between about 1560 and
1650 presents a somewhat ambivalent picture of the Jesuits' role in
the development of mathematical physics. But the manuscript record,
official positions aside, shows that solid progress was being made during
those decades, wherein foundations were laid for later important contributions to the sciences from within the Society of Jesus.
A yet more important result of these researches for this conference
is their vindication of Duhem, as contrasted with Koyr6, in the work
of these French historians on the origins of modern mechanics. Koyr6's
fortunes have declined in recent years with the discoveries by Stillman
Drake and others of the extensive experimental program on which

Galileo had embarked between 1604 and 1610. This has sounded the
deathknell for KoyrCs appraisal of Galileo as a Platonist or rationalis~l
who had no need of experiment to found his 'new science'. My own
work tarnishes KoyrCs image a bit more, for it shows that his neglec~t
of medieval and scholastic sources vitiated much of the reasoning be.hind his Etudes galildennes, the part relating to Benedetti alone ex.cepted. But if Koyr6 has been devalued, as it were, the same cannot
be said of Duhem. Duhem's emphasis on Soto, it turns out, was well
founded. One would no longer wish to maintain that Soto was the
proximate source of Galileo's science. But whether one traces Soto's
influence through the Jesuits in Italy or in Spain and Portugal, or by a
parallel route through Benedetti, there seems little doubt that Soto
played a pivotal role in promoting a mathematical analysis of local
motion?
NOTES
1 The further development of this essay is a conflation of two previously published
studies, the first focusing on the Benedetti-Jesuit relationship (Wallace 1987b) and the
second on influences on the Jesuits that derived from Domingo de Soto (Wallace 1987a),.
Neither of these studies, on the one hand, is readily available; both, on the other, are
heavily documented with references to source materials and to Latin texts. Since readers
of this journal are not primarily interested in history, I have pruned much of the docu~
mentation from my presentation here. However, to make available a detailed justification
of my thesis for those who might be interested, I have included parenthetical references
to the footnotes of the two studies in the body of the text.
2 The numbers here and following continue the page enumeration of the previous citation
in the text.
3 Preparation of this essay was supported in part by a grant from the National Endowment
for the Humanities, an independent agency of the U.S. government.
REFERENCES
Benedetti, G. B.: 1553, Resolutio omnium Euclidis problernatum aliorumque ad hoc
necessario inventorum, Apud B. Caesanum, Venice.
Benedetti, G. B.: 1554, Demonstratio proportionum motuurn localium contra Aristotelern
et omnes philosophos, Apud B. Caesanum, Venice.
Benedetti, G. B.: 1585, Diversarum speculationum rnathematiearum et physicarum liber,
Apud Haeredem Nicolai Bevilaquae, Turin.
Duhem, P.: 1906--1913, ~,tudes sur Ldonard de Vinci, 3 vols., Hermann et Fils, Paris.
Favaro, A. (ed): 1890-1909, Le Opere di Galileo Galilei, 20 vols. in 21, G. Barbera,
Florence.
Favaro, A.: 1916, 'L6onard de Vinci a-t-il exerc6 une influence sur Galil6e et son 6cole?',
Scientia 20,257-65.

Favaro, A.: 1918, 'Galileo Galilei e i Doctores Parisienses', Rendiconti della R. Accademia dei Lincei 27, 3-14.
Galilei, G. : 1988, Tractatio de praecognitionibus et praecognitis and Tractatio demonstratione, W. F. Edwards and W. A. Wallace (eds.), Editrice Antenore, Padua.
Giacobbi, G. C.: 1976, 'Epigone nel Seicento della "'Quaestio de certitudine mathematicarum": Giuseppe Bianeani', Physis 18, 5 4 0 .
Giacobbi, G. C.: 1977, 'Un gesuita progressista nella "Questio de certitudine mathematicarum" rinascimentale: Benito Pereyra', Physis 19, 51-86.
Koyr6, A: 1939, I~tudes galil~enes, Hermann et Fils, Paris.
Koyr6, A: 1964, "The Enigma of Domingo de Soto', in Rend Taton (ed.) and A. J.
Pomeranz (trans.), History of Science, 4 vols., Basic Books, New York, vol. 2, pp.
94-95.
Koyrd, A.: 1978, Galileo Studies, John Mepham (trans.), Humanities Press, Atlantic
Highlands, New Jersey.
Lewis, C.: 1980, The Merton Tradition and Kinematics in Late Sixteenth and Early
Seventeenth Century Italy, Editrice Antenore, Padua.
Maccagni, C.: 1967, Le speculazioni giovanili 'De motu" di Giovanni Battista Benedetti,
Domus Galilaeana, Pisa.
Maccagni, C.: 1983, "Contra Aristotelem et omnes philosophos', in Luigi Olivieri (ed.),
Aristotelismo Veneto e Scienza Moderna, 2 vols., Editrice Antenore, Padua, vol. 2, pp.
717-27.
Sylla, E.: 1986, 'Galileo and the Oxford Calculatores: Analytical Languages and the
Mean-Speed Theorem for Accelerated Motion', in W. A. Wallace (ed.), Reinterpreting
Galileo, The Catholic University of America Press, Washington D.C., pp. 53-108.
Wallace, W. A.: 1968, 'The Enigma of Domingo de Soto: Uniformiter difformis and
Falling Bodies in Late Medieval Physics', Isis 59, 384-401.
Wallace, W. A.: 1977, Galileo's Early Notebooks: The Physical Questions, The University
of Notre Dame Press, Notre Dame.
Wallace, W. A.: 1978, 'Galileo Galilei and the Doctoms Parisienses', in R. E. Butts and
J. C. Pitt (eds.), New Perspectives on Galileo, D. Reidel, Dordrecht, pp. 87-138;
reprinted and enlarged in 1981a, pp. 192-252.
Wallace, W. A. : 198la, Prelude to Galileo. Essays on Medieval and Sixteenth-Century
Sources of Galileo's Thought, D. Reidel, Dordrecht.
Wallace, W. A.: 1981b, 'Aristotle and Galileo: The Uses of Hypothesis (Suppositio) in
Scientific Reasoning', in D. J. O'Meara (ed.), Studies in Aristotle, The Catholic University of America Press, Washington D.C.
Wallace, W. A.: 1981c, 'Galileo and Scholastic Theories of Impetus', in A. Maieru and
A. Paravicini (eds.), Studi sul X I V secolo in memoria di Anneliese Maier, Edizioni di
Storia e Letteratura, Rome, pp. 275-97; reprinted in 198fa, pp. 320--40.
Wallace. W. A. : 1984a, Galileo and His Sources: The Heritage of the Collegio Romano
in Galileo's Science, Princeton University Press, Princeton, New Jersey.
Wallace, W. A.: 1984b, 'Galileo and the Continuity Thesis', Philosophy of Science 51,
504-10.
Wallace, W. A.: 1986, "Galileo's Sources: Manuscripts or" Printed Works?', in G. B.
Tyson and S. Wagonheim (eds.), Print and Culture in the Renaissance: Essays on the
Advent of Printing in Europe, University of Delaware Press, Newark, Delaware, pp.
45-54.

Wallace, W. A.: 1987a, 'The Early Jesuits and the Heritage of Domingo de Soto', History
and Technology 4, 301-20.
Wallace, W. A.: 1987b, 'Science and Philosophy at the Collegio Romano in the Time of
Benedetti', in Cultura, Scienze e Tecniche nella Venezia del Cinquecento, Istituto Veneto
di Scienze, Lettere ed Arti, Venice, pp. 113-26.
Committee on the History and Philosophy of Science
The University of Maryland
College Park, MD 20742
U.S.A.

THE DUHEMIAN

HISTORIOGRAPHICAL

PROJECT

ABSTRACT. Duhem regarded the history of physical science as carrying a twofold
lesson for the practicing physicist. First, history revealed the slow, groping, yet continuous
development of physical theory toward a true description of the relations among natural
entities. Second, history also unmasked false explanations and metaphysical beliefs that
might seduce the unwary scientist into following an unfruitful line of research. This paper
brings forth the central images underlying Duhem's historiographical project and uses
the papers by S. Menn and W. A. Wallace to ask what Duhem's enterprise actually
meant in practice. I argue that the main question is the following: What is to count as
the proper space of historical meaning and explanation? 'Strong' Duhemians, such as S.
Menn, purchase the longue dur~e at the cost of making historical agents into completely
passive transmitters of conceptual homologies; 'weak' Duhemians, such as W. A. Wallace, shorten the temporal distance between agents and permit thereby a modicum of
conflict and negotiation within physical theory while still seeking to preserve long-term
conceptual genealogies. Both positions, it is argued, allow insufficient room for actors'
categories to determine the space of cultural analysis.

If anyone doubts whether the spirit of Duhem is alive, these two papers
must put that hesitation to rest. Steven Menn and William A. Wallace
present similar stories of continuity. In each case, a genealogy has been
exhibited; hidden conceptual pathways have been documented and
exposed with skill; and in each account, a celebrated early modern
scientific achievement has been shown to be tied to a tradition, however
complex. History, and in this case, the history of science, is regarded
as a repository of conceptual traditions. Like Olympian runners passing
the torch, the conceptual complexes pass from one thinker to the next
not in a straight line, to be sure, for sometimes the lines of transmission are lost in the mists of the past. But, in the end, the torches are
brought home, the routes of transmission mapped, the concept or
method delivered safe and sound?
Both contributors believe that their histories, in some sense, vindicate
Pierre Duhem's historiographical project. But since they do not explicate Duhem's understanding of history,2 it seems appropriate to touch
briefly upon some of its central features, to ask N what way our contributors have construed the terms of that enterprise, and finally, to ask
why it is worth our while to rake through the somewhat neglected texts
-

Synthese 83: 261-272, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

of the distant past in search of resemblances - family ones or otherwise.
Along the way, I suppose that we shall need to ask just what might be
meant by an 'intellectual tradition'.
Duhem's notion of the history of physical theory had for him no
mere decorative role. In The Aim and Structure of Physical Theory he
subtitles one section, 'The Importance in Physics of the Historical
Method' (Duhem 1962, p. 268). There and in Physics of a Believer,
Duhem represents history as a "progressive evolution" (Duhem 1962,
p. 220f) both in the sense that "no physical theory has ever been created
out of whole cloth" (Duhem 1962, p. 221) and in the sense that logic
alone cannot justify the choice among physical theories. In a famous
formulation, Duhem writes: "It is not possible to compare an isolated
consequence of theory with an isolated experimental law. The two
systems must be taken in their integrity: the entire system of theoretical
representations on the one hand, and the entire system of observed
data on the other." This process of comparing entire systems of representation does not happen overnight. It is a slow, evolutionary movement guided by bon sens and characterized by "the hesitations, the
gropings and the gradual progress obtained by a series of partial retouchings". 3 One observes this movement both in the long history of
universal attraction and in the relatively short history of the formation
of electrodynamic doctrines between 1819 and 1823.
Given this involvement of science history in both discovery and justification, Duhem believes that certain beneficial consequences follow.
First, he thinks that history can assist the physicist broadly in avoiding
seductive explanatory fads - "the gossip of the moment", "unreasoned
exaggerations of the present time", "the mad ambitions of dogmatism
as well as the despair of Pyrrhonian scepticism". 4 Here Duhem was
undoubtedly influenced by the example of the history of philosophy in
the nineteenth-century French philosophy curriculum; history of
science, like its counterpart, could exhibit to the physicist the uncertainty spawned by differing opinions, systems, and philosophical sects
(Goldstein 1968; Fabiani 1983). But, history could also point the physicist toward something more stable and certain. Duhem believes that
the history of physical theory over the longue dur~e reveals an increasing
correspondence between idealized and actual relations among entities.
He reiterates this point using different images, but a morphological
analogy appears to govern his general sense. "The naturalist", he
writes,

swim-bladder - not in the particular and concrete forms they assume in each individual,
but in the abstract, general schematic forms which fit all the species of the same group.
Among these organs thus transfigured by abstraction he establishes comparisons, and
notes analogies and differences; for example, he declares the swim-bladder of fish analogous to the lung of vertebrates. These homologies are purely ideal connections, not
referring to real organs but to generalized and simplified conceptions formed in the mind
of the naturalist; the classification is only a synoptic table which summarizes all these
comparisons. (Duhem 1962, p. 25)

The zoologist naturalizes the homologies (i.e., shows that they "correspond to real relations among the associated creatures brought together
and embodied in his abstractions" [ibid.]) when he establishes that
general resemblances turn out to be actual blood-relationships. In Physics of a Believer Duhem provides another suggestive image:
Physical theory is neither a metaphysical explanation nor a set of general laws whose
truth is established by experiment and induction:.., it is an artificial construction manufactured with the aid of mathematical magnitudes;.., the relation of these magnitudes
to the abstract notions emergent from experiment is simply that relation which signs have
to the things signified;.., this theory constitutes a kind of synoptic painting or schematic
sketch suited to summarize and classify the laws of observation; it may be developed
with the same rigor as an algebraic doctrine, for in imitation of the latter it is constructed
wholly with the aid of combinations of magnitudes that we have ourselves arranged in
our own manner. (Ibid., p. 277)

One is tempted to regarct Duhem's evolutionist account of physical
theory as a kind of secularized theology of history - both providential
and redemptive - unveiling the Divine Plan as a directed scientific
tradition and redeeming the physicist who grasps the natural classifications toward which physical theory moves. Roger Ariew and Peter
Barker draw attention to an important image from Physics of a Believer
where Duhem articulates this directionality in a physicalist idiom:
It is not enough for the cosmologist to know very accurately the present doctrines of
theoretic physics; he must also be acquainted with past doctrines. In fact, it is not with
the present theory that cosmology should be analogous, but with the ideal theory toward
which present theory tends by continual progress. It is not the philosopher's task, then,
to compare present-day physics to his cosmology by congealing science at a precise
moment of its evolution, but rather to judge the tendency of theory and to surmise the
goal toward which it is directed. Now, nothing can guide him safely in conjecturing the
path that physics will take if not the knowledge of the road it has already covered.
(Duhem 1962, p. 303; Ariew and Barker 1986, p. 149)

As Ariew and Barker notice, Duhem provides in this passage a physicist's image of history - the trajectory of a ball. At any moment in its
flight, we cannot know the ball's end-point or, by analogy, no particular
artificial classification or 'synoptic painting' can show us the end-point
of a physical theory. For history is filled with attractive metaphysical
systems and mechanism builders, mere explanatory illusions that sustain
our faith in the ultimate discovery of natural law. Only by judging the
direction of physical theory over time can the physicist make successful
inductions toward natural classification that permit new and old laws
to be connected within a single account. Duhem thus appears to subscribe to the following slogan: the history of descriptive laws in science
is continuous and progressive; the history of explanatory schemata is
neither. 5
These are the briefest outlines of Duhem's historiographical project
as expressed in two of his most explicitly philosophical writings. Consider now how this enterprise was to be put into practice. In Aim and
Structure, Duhem makes much ado about the history of the "memorable
discovery of universal attraction" as an instance of the progressive
evolution of physical theory. This history, says Duhem, cannot possibly
include everything that the Ancients uttered about the heavy and the
light. "Let us retain", says he, " . . . only what prepared the way for the
Newtonian theory, by neglecting systematically everything not tending to
that goal" (Duhem 1962, p. 222; my italics). Later in the essay he
informs us that:
From the first half of the seventeenth century all the materials which were to be used in
constructing the hypothesis of universal attraction were assembled, cut, and ready to be
put into operation; but it was not yet suspected what an extension this work would have.
(Ibid., p. 246)

Duhem's historical method reminds us of the ball in flight. Like Aristotle's projectiles, there is no natural motion without a goal; yet, like
Galileo's idealized cannon ball, we must imagine away all terrestrial
hindrances. Duhem's method of classifying historical homologies is
possible only after all the textual underbrush has been removed.
This is not the place to pursue the reception of Duhem's historiographical project - interesting though that would be. From what we do
know at present, however, one conclusion seems clear: Duhem's greatest following came not from physicists and philosophers, but from
historians. 6 And from within the canon of general historical writings,

Duhem was perceived as having something strikingly new to say.
Duhem made medieval culture and 'the origins of modern science' into
significant topics of investigation. As the historian A. Dufourcq wrote
in 1913:
The origins of science are less known than its discoveries. We profit from its conquests,
enjoy its benefits without any concern about the source from which they derive. Yet
there is no more interesting study. In no domain is human progress secured by some
spontaneous and necessary evolution. It is important to know the conditions in which
science was born, the conditions in which its progress accelerates so that our future
procedures may be better oriented. For this reason the works of Duhem must be highly
esteemed. They establish on the basis of vast evidence that the principles on which
modern science rests were formulated before Newton, before Descartes, before Galileo,
before Copernicus, before Leonardo himself, by the masters of the University of Paris
during the 14th century. (Dufourcq 1913; quoted and translated in Jaki 1984, p. 409)

The rhetoric of origins, the humbling of Renaissance authority, the
implicit praise of Medieval Christianity, the allusions to Gallic pride all
must have carried with them important symbolic meanings within the
Republican politics of the fin-de-siecle French historical profession. Not
surprisingly, Duhem's work also met with excitement among certain
elements of the Church. Jaki cites an interesting review of the third
volume of Duhem's Leonardo studies by the Jesuit Father H. Bosmans:
I remember, many years have gone by since, I was then a student of theology and
philosophy, busy with things very different from the science of mechanics . . . . In order
to get respite from the metaphysics of the masters of the Middle Ages, or, to tell frankly,
to have a laugh for a moment, my camarades and myself read aloud a page from the
physics of those old scholastics. To laugh! And how right it seemed to be! The whole
world thought the same. We have long since had second thoughts about these outbursts
of hilarity. Duhem's book taught me how many prejudices still remain to be corrected.
(Bosmans 1914; quoted and translated in Jaki 1984, p. 410)

Duhemian historians praised the discovery of a new site of 'origins' and
exulted in the challenge to the autonomy of the Renaissance; but
significantly, they did so while ignoring Duhem's metaphysical and
epistemological theses. The search for conceptual continuities and homologies linking medieval and early modern science had become an
end in itself.
In this comment, I would like to suggest that the quest for continuities
and traditions still leaves open certain difficulties that belong squarely
on the doorstep of Duhem's account of physical theory.
Both of our papers begin by identifying a terminus ad quem. Wallace

identifies this as a certain conception of science - a "mathematical
physics" he calls it, characterized by a certain ideal of reasoning found
in the Posterior Analytics; a form of reasoning that Galileo displays in
a certain type of analysis of local m o t i o n . For Menn, the explanandum
is more limited. It is not an entire conception of science, but a specific
doctrine, namely, the conservation of motion and, even more specifically, that version of the conservation of motion formulated by Descartes. These termini are, presumably, what D u h e m would identify as
natural classifications.
Now, before we proceed further, we must ask why these termini
have been chosen and not others - for example, William Gilbert's
notion of "the magnetic substance common to loadstone and iron and
the earth itself" (Gilbert 1958, Bk. II, chap. 1, p. 72) or Giordano
Bruno's theory of natural magic. Duhem's own criterion is clear: the
terminus must be °'the reflection of an ontological order". That is
evidently not what we have here. Menn says explicitly: "Descartes is
an interesting case, both because he holds a strong and precise (though
false) principle of conservation, and because he justifies this principle
by an argument from natural theology." By this standard, Menn might
have chosen Kepler's solar force law or Kepler's polyhedral scheme for
ordering the planets and begun his story with Plato. On the other hand,
Wallace makes no reference to the truth status of his terminus in this
paper, but in his other writings it seems clear that he believes that
Galileo did discover certain truths about nature and that he arrived at
these truths from the use of a correct scientific method. 7
'So much for the problem of the ad quem; but where do we seek the
terminus a quo? Here, fortunately, D u h e m showed the way. For, as
we know, since D u h e m was the first to track down the conceptual
lineages and since he initiated this undertaking nearly a century ago in
quite a different context than our two authors, we can well understand
his biases, in part because we have the benefit of hindsight. Duhem's
termini a quo were all Parisian. This is because he believed that Paris
was the eternal city, that everything good came from Paris, 8 including,
of course, the famous Condemnations of 1277 and the method of hypothetical reasoning de potentia Dei absoluta. And, even in his own time,
D u h e m continued to look to Paris for all good ideas in physics - an
attitude not shared by our authors, although the attitude is not unknown
among many colleagues in literature, fashion design, and the culinary
scientiae mediae.

Thus, we cannot allege that our contributors suffer from Parisocentrism. Yet, in different ways, they wish to recommend to us the method
of filiations that led D u h e m to Paris. Professor Menn wishes to take us
back to Mecca via the medieval Arab Avicenna, while Professor Wallace has been edging further away from the High Middle Ages and now
focuses his gaze on the Scholastic presence in the Mediterranean Basin
from about 1550. 9 For Wallace, while the genealogies to medieval
Paris, Oxford and R o m e can still be made, his recent studies of Galileo's
sources concentrate principally on sixteenth-century materials that now
spread out from Rome to Jesuit academic outposts in Salamanca and
Coimbra. In short, Professor Menn is, in a sense, closer to the original
D u h e m in searching out causae rernotivae, while Professor Wallace's
causae are proxirniorae.
Does this make a difference? I think that it does. In my opinion,
Professor Menn is forced into a more difficult position because the
temporal and, I think, also the cultural distance is too great to sustain
a common space of meanings. Let me mention some of these difficulties.
First, we have no evidence that Descartes knew or understood Avicenna's notion of rnayl at all, let alone through a source discussed by
Menn. This leaves Menn arguing for a '°strong possible resemblance".
Second, Menn must explain why it is that Descartes's views differ or
diverge so much from Avicenna's. Avicenna, for example, denies that
heavenly bodies have an intrinsic source of motion and concludes that
they do not resist constant motion. Yet, writes Menn, ".Descartes claims
that any bodies have an intrinsic source of natural motion and concludes
that no bodies resist the constant motion". How and why does Descartes accomplish this? Professor Menn says that "it follows from Descartes' conception of body as pure extension, which is designed precisely to strip bodies of any natures, immanent forms or active powers".
Evidently, the notion of body as pure extension does not appear in
Avicenna. We are left to wonder, then, how it is that Descartes 'strips
down' bodies so completely that no medieval Aristotelian could recognize them. Finally, Menn tells us that, "at a sufficiently abstract level
Descartes' theory of the causes of motion is very close to Avicenna".
But surely if one pulls the 'historical camera' back far enough, one can
connect concepts from all times and places; and it might even be
tempting to follow Carl Gustav Jung into the realm of the collective
unconscious of seminal archetypes, Arthur O. Lovejoy into a realm
of 'unit-ideas' or Pierre D u h e m into a lineage of increasingly perfect

homologies. I am not suggesting that Menn would want to go this far,
but his tendency to read history for resemblances threatens to blend
into a search for conceptual identities.
Professor Wallace's attempt to vindicate D u h e m is, I think, more
successful because the termini of his analysis are much closer in time.
Galileo could, as it were, actually talk to and borrow 'software' from
some of his sources. Wallace wants to make sense of Galileo's commitment to a certain view of science and to make sense of fragments of a
scholastic calculatory vocabulary (especially the uniforrniter difformis
expression). In this kind of story, there are at least hints of a history
of science that moves away from Duhem's philosophical history of
disembodied concepts, one that acknowledges the integrity of particular
cultures within which specific forms of scientific life are discernible.
But, on such a view, notions of 'transmission', 'continuity', and
'source', as well as 'influence' and 'reception' all become deeply problematic. For what, after all, is a 'source'? If it is a text, then it can only
acquire specific historical meaning from being read. And since reading
is an active, time-bound process, we cannot say that any two people,
let alone any two groups, will read the same text in the same way
(Chartier 1987, pp. 183-239). Nor can we assume that practices of
reading in the seventeenth century, the Victorian age or today are quite
the same. Nor can we assume that Domingo de Soto had the same
theological objectives at the Council of Trent that Etienne Tempier had
in 1277. Nor can we assume that Galileo, who was neither a Dominican
nor a Jesuit, had the same objectives that de Soto had when he used
the expression uniformiter difformis.
At the end of his paper, Professor Wallace throws some illumination
on this problem. H e informs us that Galileo's use of calculatory language was not quite the same as the fourteenth century Mertonians
(see Sylla 1987). "Such disparity", writes Wallace, "is readily understandable when one considers that Galileo acquired that language at
several removes from its initial formulators" (my italics). But again,
what is a " r e m o v e " if not a different context of meaning that must be
understood in its own terms?
The second point that Professor Wallace makes in his conclusion is
that the Jesuits themselves did not hold a consistent attitude toward
the use of mathematics in the study of nature, that there were tensions
within the Order between the mathematicians and philosophers and
that the Order papered over these difficulties through censorship. Even

Paolo Valla at the Collegio Romano experienced difficulty in publishing
his lectures on logic and natural philosophy in the early 1600s and
Giovanni Biancani later encountered resistance when he supported
Galileo between 1615 and 1620. Here again we cannot assume that the
mechanisms and motives of post-Tridentine ecclesiastical censorship
had the same political meanings as Bishop Tempier's Condemnations
of 1277. Attention to such political and social factors shows promise of
righting an imbalance within Duhem's original account. For Duhem
analyzed conflicts between the faculties of theology and arts at the
University of Paris in the thirteenth century but failed to carry forward
his study along those lines into the sixteenth and seventeenth centuries. lo
Where, then, does this leave the Duhemian historiographical project?
As a practical resource for guiding physicists, it seems to have attracted
no significant audience. Even those few physicists who engaged in
historical work seem not to have followed Duhem's dicta; if anything,
the Quantum revolution encouraged the search for discontinuities. 11
To professional historians, on the other hand, Duhem presented a
corpus of texts that simply could not be ignored - however they might
be interpreted. And, in pressing for conceptual resemblances between
the 'well known' and the 'newly found' he succumbed to that malaise,
understandable and common among historians, of overestimating the
value of an archival find. Nowhere is this more evident than in his
notion of 'precursor'. If Alexandre Koyr6 undervalued Galileo's scholastic debts, Duhem, for his part, had an impoverished notion of
'source'. Too readily he was willing to regard the early moderns as
passive recipients of scholastic language and concepts. Thus, Duhem
pictures Osiander as a kind of receptacle who transmits unchanged a
Greek doctrine while omitting the rhetorical and polemical context of
his anonymous 'Letter to the Reader'. Similarly, Duhem's Copernicus
in To Save the Phenomena voices a 'misguided' methodological realism;
but Duhem ignored the way in which Copernicus tried to persuade the
Pope that correcting the calendar and the order of the heavens should
be part of a common agenda of Church reform (Duhem 1969, pp.
61-91; see also Westman 1987 and Westman 1990).
The Duhemian project, in other words, has tended to regard the
'learning of the schools', (Dear 1988) the inheritance of the universities,
as sources that influenced passive historical actors, rather than as resources that were actively used, altered, emended, believed and - dare

we use the term? - misunderstood and misrepresented by early modern
propagandists of natural knowledge. With great subtlety and erudition,
both of these papers have laid the groundwork for such an analysis. I
do not underestimate for a moment the philological, paleographical
and philosophical difficulties that they have had to conquer; indeed, I
doubt that we would be able to focus our problem quite so finely were
it not for their struggle with these texts. For having brought us to this
point, we are all in their debt.

NOTES
1 The image is consciously Duhemian: "By virtue of a continuous tradition, each theory
passes on to the one that follows it a share of the natural classification it was able to
construct, as in certain ancient games each runner handed on the lighted torch to the
courier ahead of him, and this continuous tradition assures a perpetuity of life and
progress for science" (Duhem 1962, pp. 32-33).
2 For an insightful discussion of Duhem's understanding of physics in relation to history,
see Martin (1990).
3 Duhem (1962), p. 253; On bon sens and logic, see Martin (1987).
4 Duhem (1962), p. 304; cf. p. 270: "By retracing for him the long series of errors and
hesitations preceding the discovery of each principle, it puts him on guard against false
evidence; by recalling to him the vicissitudes of the cosmological schools and by exhuming
doctrines once triumphant from the oblivion in which they lie, it reminds him that the most
attractive systems are only provisional representations, and not definitive explanations".
s It seems to have gone unnoticed that Thomas Kuhn adopts this position in Kuhn (1957),
pp. 264-65. I intend to develop this observation further in a retrospective review of
Kuhn's book to appear in a future issue of Isis.
6 Stanley Jaki has assembled a significant quantity of very useful information - much of
it in the form reviews of Duhem's books - that permits one to make this statement (Jaki
1984, chaps. 9-10). Unfortunately, Jaki's apologetic and defensive tone compromises
many of the judgments he makes about Duhem and his work.
7 See W. A. Wallace, 'Galileo and Reasoning Ex Suppositione', in Wallace (1981), p.
149.
s I owe this insight to my colleague Amos Funkenstein.
9 See his 'Pierre Duhem on Galileo', in Wallace (1981), pp. 303-19.
10 A. Funkenstein's important study Of the transition from medieval to early modern
forms of scientific and historical reasoning makes the problem of God's attributes the
fulcrum of the analysis in a consistent way such that Duhem failed to provide. Furthermore, Funkenstein explicitly disavows the thesis that medieval theological speculation
necessarily produced early modern science (see Funkenstein 1986, pp. 360-63).
11 See, for example, Pauli (1955) and Westman (1984); Fleck (1979); Holton (1973); also
De Broglie in Duhem (1962), pp. v-xiii.

REFERENCES
Ariew, R. and P. Barker: 1986, 'Duhem and Maxwell: A Case-Study in the Interrelations
of History of Science and Philosophy of Science', in A. Fine and P. Machamer (eds.),
PSA 1986, Proceedings of the 1986 Biennial Meeting of the Philosophy of Science
Association, vol. 1, Philosophy of Science Association, East Lansing, Michigan, pp.
145-58.
Bosmans, H.: 1914, 'Review of Pierre Duhem: 1906, Etudes sur Leonard de Vinci, A.
Hermann, Paris', in Revue des Questions Scient~fiques 76, 529-37.
Chartier, R.: 1987, The Cultural Uses of Print in Early Modern France, Lydia G.
Cochrane (trans.), Princeton University Press, Princeton, New Jersey.
Dear, P.: 1988, Mersenne and the Learning of the Schools, Cornell University Press,
Ithaca, New York.
Dufourcq, A. : 1913, 'Les origines de la science moderne d'apr6s les dccouvertes recentes',
Revue des deux monde 16, 349-78.
Duhem, P.: 1962, The Aim and Structure of Physical Theory, P. P. Wiener (trans.), with
a foreword by Prince L. de Broglie, Princeton University Press, Princeton, New Jersey;
first published in 1914.
Duhem, P.: 1969, To Save the Phenomena, An Essay on the idea of Physical Theory from
Plato to Galileo, E. Doland and C. Maschler (trans.), with an Introductory Essay by
S. L. Jaki, University of Chicago Press, Chicago; first published in 1908.
Fabiani, J.-L.: 1983, 'Les programmes, les hommes et les oeuvres: professeurs de
philosophie en classe et en ville au tournant du siecle', Actes de la Recherche en Sciences
Sociales 47-48, 1-20.
Fleck, L.: 1979, Genesis and Development of a Scientific Fact, F. Bradley and T. J. Trenn
(trans.), T. J. Trenn and R. K. Merton (eds.), foreword by T~ S. Kuhn, Chicago
University Press, Chicago; first published in 1935.
Funkenstein, A.: 1986, Theology and the Scientific Imagination from the Middle Ages to
the Seventeenth Century, Princeton University Press, Princeton, New Jersey.
Gilbert, W.: 1958, De Magnete, P. F. Mottelay (trans.), Dover, New York; first published
in London, 1600.
Goldstein, D. S.: 1968, 'Official Philosophies in Modern France: The Example of Victor
Cousin', Journal of Social History 1,259-79.
Holton, G.: 1973, Thematic Origins of Modern Science, Harvard University Press, Cambridge, Massachusetts.
Jaki, S. L.: 1984, Uneasy Genius: The Life and Work of Pierre Duhem, Martinus Nijhoff,
The Hague/Boston.
Kuhn, T. S.: 1957, The Copernican Revolution, Harvard University Press, Cambridge,
Massachusetts.
Martin, R. N. D.: 1987, 'Saving Duhem and Galileo: Duhemian Methodology and the
Saving of the Phenomena', History of Science 25, 301-19.
Martin, R. N. D.: 1990, 'Duhem and the Origins of Statics: Ramifications of the Crisis
of 1903-04', Synthese 83 No. 3 (next issue).
Pauli, W.: 1955, 'The Influence of Archetypal Ideas on the Scientific Theories of Kepler',
in C. G. Jung, The Interpretation of Nature and the Psyche, R. F. C. Hull and P. Silz
(trans.), Routledge & Kegan Paul, London; first published in 1952.

Sylla, E.: 1987, 'The Oxford Calculators in Context', Science in Context 1,257-80.
Wallace, W. A.: 1981, Prelude to Galileo, Essays on Medieval and Sixteenth-Century
Source of Galileo's Thought, D. Reidel, Dordrecht.
Westman, R. S.: 1984, 'Nature, Art, and Psyche: Jung, Pauli, and the Kepler-Fludd
Polemic', in B. Vickers (ed.), Occult and Scientific Mentalities in the Renaissance,
Cambridge University Press, Cambridge, pp. 177-230.
Westman, R. S.: 1987, 'La pr6face de Copernic au paiz~: esth6tique humaniste et r6forme
de l'6glise', History and Technology 4, 365-84.
Westman, R. S.: 1990, 'Proof, Poetics and Patronage: Copernicus's Preface to De Revolutionibus', in D. C. Lindberg and R. S. Westman (eds.), Reappraisals of the Scientific
Revolution, Cambridge University Press, New York, pp. 167-205.
Department of History and Science Studies Program
University of California, San Diego
La Jolla, CA 92093
U.S.A.

SCIENCE

AND THEOLOGY

CENTURY:
OXFORD

IN THE FOURTEENTH

THE SUBALTERNATE

COMMENTARIES

SCIENCES

IN

ON THE SENTENCES*

ABSTRACT. Both Pierre Duhem and his successors emphasized that medieval scholastics created a science of mechanics by bringing both observation and mathematical
techniques to bear on natural effects. Recent research into medieval and early modern
science has suggested that Aristotle's subalternate sciences also were used in this program,
although the degree to which the theory of subalternation had been modified is still not
entirely clear. This paper focuses on the English tradition of subalternation between 1310
and 1350, and concludes with a discussion of the theory advanced by Thomas Claxton
early in the fifteenth century.

In the second of the focal essays for this conference, Pierre D u h e m
provides a distillation of his celebrated punctuated continuity thesis:
" W h e n we see", he says, "the science of a Galileo triumph over the
stubborn Peripateticism of a Cremonini, we think, uninformed as we
are of the history of human thought, that we witness the victory of the
young, modern Science over medieval p h i l o s o p h y . . , whereas in fact,
we are contemplating the long-prepared triumph of the science born in
fourteenth-century Paris over the doctrines of Aristotle and Averroes,
restored to honour by the Italian Renaissance". 1 From his early work
in the history of statics to the magnum opus of the SystOme du monde,
it was Duhem's contention that the seeds of seventeenth-century science
could be found in the scholastic writers of the fourteenth century. And
while the thesis sustained much criticism and has undergone considerable revision, Duhem's contemporary rivals were forced to concede
limited recognition of the principle; as I have noted elsewhere, even
George Sarton observed that in the history of science, "there are no
unbegotten fathers except Our Father in H e a v e n " . 2
The particular aspect of Duhem's work that I should like to focus
upon here involves the application of mathematics - and particularly
geometry - to the effects of nature. Duhem's historical researches and
those of his successors have emphasized that medieval scholastics created a science of mechanics by bringing both observation and mathematical techniques to bear on natural effects. But while the successes of this
program were evident, the foundations were certainly not: in particular,
Synthese 83: 273-292, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

precisely what justified the extensive application of mathematics to
natural philosophy? Medieval readers of Aristotle's Posterior Analytics,
Ethics, Metaphysics, and Physics were well aware that the Philosopher
had cast a dim view on the unrestrained application of techniques of
one science in the domain of another. Whether this position was part
of an emerging theory of scientific method that Aristotle never brought
to full fruition, 3 or reflects fundamental contradictions in the historical
development of his thought is still unclear. 4 But the fact remains that
Aristotle's discussion presented medievals with an enormous methodological problem.
Aristotle's discussions of disciplinary autonomy carried with them a
significant exception, the so-called subalternate sciences. Autonomous
in their own right yet dependent upon other sciences for their first
principles, the subalternate sciences comprised a relatively small class
of disciplines, particularly between mathematics and natural philosophy. For a number of reasons, the medieval development of subalternation theory holds special significance in a reassessment of Duhem's
historical work. First, the initial object of Duhem's work - statics - was
included among these sciences, both by Aristotle and his medieval
readers. 5 A far more problematic step had been taken by the end of
the fourteenth century, for it seems clear that at least in some circles
the new techniques of dynamics and kinematics developed during the
course of that century were being associated with subalternation: in the
1380s, for example, H e n r y of Langenstein at Paris included the latitudines formarum among such sciences, adjacent in his arbor scientiarum
to the more traditional disciplines of astronomy and music. 6 Recent
research into Galileo's early thought also suggests that the subalternate
sciences were a source for his ideas about scientific method and the
correct reading of the book of nature, although it is still not entirely
clear whether the conception of the subalternate sciences upon which
Galileo was drawing was in fact the same as that which Aristotle had
prescribed, 7 and as Professor McMuUin has suggested, the subalternate
sciences in the sixteenth century were 'an ambiguous heritage', s Finally,
in the intervening period, during which according to D u h e m a 'superstitious archaism' was responsible for the rejection or at least neglect
of earlier theories of the moderni, 9 we find both Pietro Pomponazzi
and Galileo's teacher Francesco Buonamici lamenting the excessive
injection of mathematics into natural philosophy 1° - that is, precisely

the objection that Aristotle had made in the Posterior Analytics and
which the subalternate sciences had sought to overcome.
It is rather well known that D u h e m concentrated much of his historical research on the University of Paris, ignoring or at least deemphasizing the parallel achievements across the Channel. In spite of - or
perhaps because of - this, I should like to focus my attention on the
English and especially Oxford tradition of the subalternate sciences,
particularly during the crucial years between 1310 and 1350. The source
upon which I shall draw will not be commentaries on the Posterior
Analytics, the work in which Aristotle discussed his theory of subalternation most directly, but rather medieval commentaries on Peter Lombard's Sentences, in which subalternation was frequently discussed in
prologues. I have done so for several reasons. As a pragmatic consideration, while the Posterior Analytics remained a popular text in Europe
during the fourteenth century, it seems to have been less popular at
Oxford, where some of the most interesting scientific work was taking
place. In fact, during the period 1250-1400, Oxford scholars seem to
have produced fewer than half the number of commentaries on the
Analytics that orie finds at Paris during the same period. 11 Second,
commentators on the Sentences were generally older and perhaps more
mature than those in the Arts Faculty who commented on the Analytics.
And finally, in general, discussions of subalternation found in commentaries on the Sentences were divorced from Aristotle's text, and thus
open to considerably more interpretive latitude.12
At the outset, a concession is in order. Despite the considerable number
of commentaries on the Sentences produced at Oxford during the fourteenth century, and while many contain discussions of scientia, not all
commentators chose to discuss the subalternation of the sciences. About
1334, Robert Holcot, for example, produced a quodlibetal question
'Utrum theologia sit scientia', frequently a topos for discussion of subalternation, but Holcot's treatment omits any such material. 13 At Cambridge, Robert of Halifax (Franciscan, fifty-sixth lector at the Cambridge Convent, ca. 1336) included in his prologue the question, 'Utrum
scientia quam potest theologus h a b e r e . . , sit practica vel speculativa'.
Such questions frequently were sources for discussions of subalternation, in part because of Aristotle's reference in Posterior Analytics
in part because of Aristotle's reference in Posterior Analytics
though the latter is not formally subalternated to the former. Yet

Halifax's question likewise omits such material, t4 And finally, the
copy of Richard Fitzralph's commentary on the Sentences preserved
in Oxford, Oriel College MS 15 contains a prologue with a similar
discussion, 15 but which once again omits reference to subalternation. 16
When combined with the relative neglect of Aristotle's Posterior
Analytics, one might be inclined to suggest that it is slightly at variance
with the idea that periods of intense scientific change are both preceded
and accompanied by appeals to philosophical analyses of scientific
method. 17 In fact, however, I believe other factors are at work. First,
discussions of subalternation were frequently reserved for prologues to
commentaries, and as the fourteenth century progressed, such prologues often came to be reduced in length and eventually omitted
entirely) 8 Doubts about the scientific status of theology and the resulting reduction in the size of prologues seem to be responsible in part
for omissions of discussions of subalternation. As a result, when commentators chose to discuss the topic, they sometimes found room for
it in related questions in Book I, as Adam Wodeham did, for example,
in distinction I, question 3, in a reservation entitled, 'whether the same
conclusion can be demonstrated in different sciences' (Utrum eadem
conclusio possit demonstrari in diversis scientiis)) 9 Second, in the
thirty or forty years prior to 1330, the problem of subalternation had
been debated thoroughly in commentaries on the Sentences, and a
variety of positions were now available. As newer, more topically significant questions arose, subalternation passed from primary importance because it was already a topic on which a core consensus, if not
unanimity rested.
If we turn now to the elements of that consensus, we find several
rather interesting developments in the theory itself. The first, and
clearly most pronounced, is the tremendous influence exercised by
Robert Grosseteste; indeed, the extent to which fourteenth-century
scholars achieved a general consensus at all is attributable to Grosseteste's authority. In almost every commentary that discusses subalternation, he is cited repeatedly, sometimes more frequently than Aristotle
himself. Thus the Benedictine scholar Robert Graystanes cites Grosseteste's commentary on the Analytics nine times in a rather short question on subalternation, frequently quoting substantial sections of the
text, while citing Aristotle's text only three times. 2° He apparently
considered the commentary so important that he procured a copy for
the Durham College library? 1 Graystanes's contemporary, John of

Reading, cites Grosseteste's commentary twenty-eight times, Aristotle's
text only twelve times. 22 And even when commentators fail to cite
Grosseteste explicitly, as is the case for Robert Cowton and William
of Nottingham, it seems clear that Grosseteste's positions stood behind
their texts. 23
The reasons for this infatuation with Grosseteste's commentary are
not too difficult to determine. For Franciscans like John of Reading and
William of Ockham, Grosseteste's previous ties to the Order provided a
fraternal link and, as I have argued elsewhere, perhaps even an authoritative text in the convent library. But for the Benedictine Graystanes
and the Augustinian author of an anonymous commentary found in
Balliol College MS 63, and indeed for the Franciscans as well, the
motive was one of clarity and elucidation: where Aristotle's explanation
of subalternation was elliptical or incomplete, Grosseteste provided a
more complete mechanism. As subsequent readers saw it, Grosseteste's
contributions could be summed up under four ideas. The subalternating
and subalternate subjects were nonidentical, for otherwise there would
be no need to transcend the original science in demonstration, and
indeed one would fall victim to Aristotle's injunction against importing
the elements of other disciplines. Second, these two subjects were
distinguished by the so-called superadded condition that made the
middle term of the syllogism the nexus of subalternation. Third, subalternate sciences were subalternated simultaneously to two superior
sciences, each providing a critical element in the demonstration. 24 And
finally, because of the superadded condition imposed in subalternation,
the subalternate subject possessed an accidental rather than essential
unity. 25
All of these positions can be found to some degree in Aristotle's
text itself. What impressed fourteenth-century readers of Grosseteste's
commentary was the degree to which the latter could extend the former.
Thus, in an argument dependent on the superadded condition, Robert
Graystanes first quotes Aristotle, then follows with Grosseteste's elucidation:
This is confirmed by the Philosopher, in Posterior Analytics I: the subalternate science
always concerns being per accidens; whence in the same place, chapter 12, the Lincolnien
[says], 'It must be known that the inferior science superadds a condition through which
it appropriates to itself the subject and properties of the superior science. A n d there are
in the conclusion of the subalternate science, as it were two natures, viz. a nature which
it takes from the superior, and a proper nature which it superadds'. So far [Grosseteste]. 26

For Graystanes, as for many of his contemporaries, Grosseteste did
not replace Aristotle as much as extend the Philosopher's original
meaning.
Aside from Grosseteste, there was one other crucial context for
discussions of subalternation. Fourteenth-century commentators frequently affiliated their discussions of subalternation with discussions of
the unity of science. For example, John of Reading made subalternation
the subject of two questions in his prologue and balanced them against
a still more substantial question on the unity of science, referring back
to his discussions of subalternation no fewer than seven times. And as
I have already noted, Adam Wodeham likewise introduced an argument
from subalternation into a question on the appropriateness of the same
conclusions to diverse sciences. The reasons for this affiliation are not
difficult to ascertain. First, Aristotle himself had associated the two
topics, for it appears at least three times in Posterior Analytics I,
particularly because it is clear that when he discusses the relationship
between the subalternate and subalternating sciences, the underlying
assumption is that there are well-defined criteria that distinguish the
sciences. 27 Second, one should not underestimate the influence of Peter
Aureol's commentary on the Sentences for this aspect of the discussion.
Aureol had linked the two topics very closely, and his work became a
target for several subsequent readers, including both Ockham from one
side and Reading from another. 28 Finally, there seems to be a particular
link between this discussion and the original theological text of the
Lombard's Sentences. Fourteenth-century discussions of the unity and
subalternation of the sciences in particular were frequently cast in the
psychological language of the habitus of science. Briefly, medievals
argued that corresponding to each act of the intellect, there was a habit
residing in the soul that reproduced this act and thus allowed for such
things as recall and cogitation. As a result, discussion of the unity of
science and by extension subalternation was married to epistemological
discussions of the unity of habitus, topics that Aristotle had treated
separately in the Posterior Analytics and the Categories, respectively. 29
The broker for this marriage seems to have been, in part, Lombard's
text, for the opening chapter of distinction 1 draws upon Augustine in
maintaining that "every doctrine is of things or of signs" (Omnis doctrina de rebus vel de signis). 3° Clearly, the original intent of the
passage was exegetical, but the door was also open to discussions of the

relationships between names and things, and with them came discussions of science.
Aside from this association with discussions of unity of science, there
is some evidence to suggest that early fourteenth-century commentators
developed their positions on subalternation by drawing upon logical
techniques developed in the middle ages. This is perhaps best exemplified by drawing once again upon John of Reading. Reading begins
his discussion of subalternation by reviewing the now-familiar criteria
for subalternation that he has gleaned from Robert Grosseteste, and
in particular, the notion that the subalternate science must be subsumed
under two subalternating sciences. The requirement of the superadded
condition imposed on the subalternate subject precluded an inferior
science that was merely a contraction of the superior. This leads John
to an extended discussion of predication, in the course of which he lists
seven ways by which logical ascent and descent can occur in superior
and inferior sciences. It would take us too far afield to discuss each of
these, but the significant fact is that John concludes that only one of
them - descent under a quidditative concept that is p e r se one to a
concept that is one p e r accidens and that joins the higher subject with
an accidental property - produces subalternation? 1 It should, in fact,
come as no surprise that John concludes that these are Grosseteste's
criteria dressed up in more recent garb. But in fact, the purpose of
John's discussion and the reason for his reference to logical ascent and
descent was to distinguish between the descent and ascent of supposition theory and the doctrir/e of subalternation, for at least in John's
account, there seems to have been some conflation of these issues in
the years immediately preceding John's tenure at Oxford. 32
It is rather well known that D u h e m was often not kindly disposed to
medieval uses of logic, particularly at Oxford. On occasion, he was
inclined to see the use of logic as going beyond legitimate purpose and
becoming an artificial exercise, a 'logical acrobatics'. 33 But at least in
the case just cited, D u h e m probably would have agreed that Reading's
extensive logical discussion served the purpose of setting the theory of
subalternation on firm ground and avoiding unwarranted and illegitimate claims on the theory.
John's purpose, at least in this context, was to guard against unlimited
appeals to subalternation as a technique justifying cross-disciplinary
work. But at about the same time - that is, about 1320 - the association

of subalternation with discussions of the unity of science and with the
notion of scientific habits, seems to have produced some inclination to
expand the criteria for subalternation of one science to another. William
of Ockham, for example, called attention to a strict and broad sense
of subalternation, and in the first question of his prologue noted that
while Aristotle mentioned explicitly only a few pairs of subalternating/
subalternate sciences, he intended to permit cross-disciplinary work in
other sciences subordinated in other ways. 34 Likewise, despite John of
Reading's determination to hold a conservative line on the expansion
of subalternation, even he notes in his discussion of generic descent
under a subject that while the inferior is "not properly and completely
subalternated to the [superior s c i e n c e ] , . . , in a certain way perhaps it
can be said [to do s o ] " Y The anonymous author of a commentary in
Balliol 63, while discussing the relationship between two sciences, one
of which depends on the other for the certitude of its truths, notes that
this is "not properly subalternation, but n e v e r t h e l e s s . . , has a similarity
with subalternation". 36
Although to my knowledge, no one in the early fourteenth century
explicitly tied the expansion of subalternation to the new attempts to
quantify qualities, statements such as these may well have convinced
proponents that those attempts were legitimate. It is hardly surprising
that such ideas might be held implicitly rather than explicitly, for if
indeed there was consensus on the theory of subalternation, it was on
this issue of cross-disciplinary transmission that consensus was tested
most severely. I have already alluded to John of Reading's otherwise
conservative tendencies. His contemporary, Robert Graystanes, was
even more direct: speaking of the resolution of principles within the
subalternate and subalternating sciences, Graystanes notes that strictly
speaking, such resolution cannot occur except within the proper genus.
" F o r " , as he points out, "the geometer cannot resolve beyond what
his faculty permits; rather, it is proper that resolution should remain
primarily within its own limits...,,.37 Writing at approximately the
same time, but in London, Walter Chatton expressed much the same
sentiments in a direct response to Ockham's more liberal discussion? s
If fourteenth-century scholars found that subalternation provided room
for legitimate growth in new techniques, they retained a healthy caution
about extending it too far.
On several occasions in this paper, I have referred to a consensus about

subalternation. In doing so, I do not wish to imply that there was
agreement in every detail of the theory, for as we have seen, certain
aspects were open to continued discussion; the consensus rather extended to a core of material that I have tried to identify. In view of
that, I should like to conclude by discussing the ideas of a Dominican
scholar at Oxford from the early fifteenth century, Thomas Claxton. 39
Claxton's work has often been taken as the culmination of a revival of
Thomism at Oxford early in the fifteenth century, 4° but while this may
be true in general, it would seem that his ideas about subalternation
and the unity of science depend as much on his reading of subsequent
fourteenth-century sources as a review of Aquinas. The second question
to Claxton's prologue investigates the well-worn issue of whether the
theology that we possess in this life is in fact scientia, and in his own
autographed copy preserved in Cambridge, Gonville and Caius College
MS 370(592), he devotes some twenty-seven closely written folios to
the issue. He begins by proposing six principal arguments against the
view: it is not demonstrative, nor is it evident, intuitive, and abstract;
it is neither practical nor speculative; it is not numerically one; and
finally, it has no determinate subject. 41 He proposes to treat each of
the issues plainly, openly, and truthfully, so that his students should
understand, for, as he tells us, the theologians of old very often were
deficient in logic. And despite his long narration of these six arguments,
he maintains that he will not dwell on prior opinions excessively, since
only those which by merit of fame or nearness to truth must be treated.
Others, he trusts, will be refuted by apparent truths, since if a little
error in the beginning leads to a great one at the end, so also truth
always easily declares itself. 42
In his preliminary definitions, Claxton says that there are three genuine senses of science and one that is spurious. Science is first, the
evident assent of the mind to what is, was, or will be. Second, in the
strictest sense, it may also be evident assent that is caused syllogistically,
and this, he says, is what Aristotle had in mind when he referred to
science as the cognition of a conclusion in a demonstration. Third, it
may refer to a habit of the mind created from many assents collected
together, each having a certain coordination to the other by comparing
the first subject and predicate. This, he says, is the way Aristotle speaks
of natural science in the Physics, the Metaphysics, De caelo et rnundo,
and many other places. All three a r e equally valid ways of referring to
science. As for the spurious sense, Claxton says that some doctors of

theology suggest that science is merely true assent without vacillation,
whether evident or inevident. This allows them to call faith science,
but Claxton notes that this is false, because it does not make sufficient
distinction between opinion and science. And although Augustine
speaks in this way, he does so modo vulgaris loquendo, and this sort
of expression ought to be avoided by those in the s c h o o l s . 43
It is in his responses to the fifth and sixth principal arguments - on
the unity and subject of science - that Claxton discusses subalternation.
A science, or for that matter, anything can be one in several senses:
one numerically per se, one specifically, one generically, one per conclavationem (literally, being locked up together), or one by attribution
and coordination. 44 The latter he singles out for special consideration,
because he says this sense of unity is a bit more restricted and is in fact
the way sciences - he lists natural philosophy, ethics, arithmetic, and
music - are said to be one by attribution or coordination to one first
principle, that is, the first proposition in which the primary predicate
equally (although not really) is predicated. And in a reference to a
popular fourteenth-century analogy that derives ultimately from the
Metaphysics, he says this sort of unity is like that of the people of
England, since they have one king, one law, one polity. 45
Claxton then gives a more concrete example, the case of natural
philosophy and medicine. Both have the same first principle in which
the primary predicate (the so-called tertium adiacens) is predicated,
namely "Some body is mobile" ('Aliquod corpus est mobile'). But they
are not the same science, because the first predicate is applied to natural
philosophy and medicine through separate first principles: in natural
philosophy according to place, quantity, etc., in medicine according
to health and infirmity or the excesses of the humors and other such
things. Thus, in spite of their attribution to one first principle, the
coordination is held under different species, and they are not one
science. One science, says Claxton - echoing Aristotle - is of one
genus, that is, of one subject and the things joined to it by proper first
principles .46
This discussion of the unity of science leads Claxton to subalternation.
In subalternation, one needs not only the same subject in each science,
but also equally significant first proper principles whose subjects and
predicates are per se superior and inferior. For example, medicine, he
says, is subalternated to natural philosophy because under the latter's

first principle 'corpus est mobile', medicine has its own first principle,
'corpus animale est mobile ad infirmitatem vel sanitatem vel neutralitatern', in which both subject and predicate are related as superior and
inferior. The same thing is true of geometry and perspective, through
the respective first principles 'figura est terminata' and 'linea visiva
terminatur ad oculum faciens visionem'. But, Claxton adds, another
part of perspective is subalternated to natural philosophy under a different first principle, viz., 'animal est mobile ad visionem a corpore lucido
sibi obiecto'. 47 It is clear that what allows Claxton to speak in this way
about partial subalternation is once again the propositional notion of
science and a unity based on attribution and coordination, although
elsewhere it is clear that he takes issue with previously formulated
versions of such ideas, particularly those of Ockham and Holcot. 4s
Still later, Claxton elaborates on this subordination of principles. In
his response to the sixth principal argument of the question, concerning
the relationship between the theology of the wayfarer and the blessed,
he notes that no science is subalternated to another unless the principles
of the subalternating and subalternate sciences compare by means of
an addition (habet se ex additione) as plainly in the subject as in the
predicate. But clearly in the two theologies concerned, there are not
two such differentiated subjects, but an identical one. ~9 Although he
does not cite Robert Grosseteste anywhere in this question - perhaps
an indication of the distance between discussions in the opening years
of the fifteenth century and those of a century earlier - his ideas about
subalternation are consistent with the received tradition that derived
ultimately from the bishop of Lincoln. In this sense, Claxton's commentary represents still a further distillation of the late medieval tradition of subalternation.
It should be clear that this tradition was vitally dependent upon the
theological context in which it developed, an issue that returns us
once again to Duhem. As Stanley Jaki has reminded us in his recent
biography, 5° Duhem's ideas about medieval science were inseparable
from his understanding of medieval theology. The fuller treatment of
this theological tradition of subalternation would require equal consideration of positions developed at Paris and elsewhere during the
fourteenth century, for indeed in addition to native positions, Claxton
cites the imported ideas of Gregory of Rimini and other Parisians. 5~
But this must remain for another occasion.

NOTES
* I am especially grateful to the Fulbright Comission and the National Science Foundation, whose assistance made possible the research involved in this paper. I would also
like to thank the librarians of institutions listed in the bibliography to this paper, who
facilitated my research by permitting the use of manuscripts in their collections.
1 Duhem (1987), p. 341.
2 Livesey (1987), p. 365; Sarton (1959), p. 38.
3 McKirahan (1978).
4 Graham (1987). The structure of his thesis is set out at pp. 14-17.
s Posterior Analytics I. 13 78638. Version P of the so-called Liber Jordani de ponderibus,
which Duhem was particularly keen to attribute to Jordanus or at least suggest stood
behind Jordanus' work, begins, "Cure scientia de ponderibus sit subalternata tam geometric quam philosophie naturali, opertet in hac scientia qltedam philosophice, quedam
geometrice probari." See Moody and Clagett (1960), p.151. Duhem (1905-1906), vol. 1,
pp. 128-32.
6 Henry of Langenstein, Expositio prologi Bibliae; Vienna, C)sterreichische Nationalbibliothek CUP 3900, fol. 49vb. See Steneck (1975).
7 James G. Lennox (1986) attempts to tie Galileo to the tradition of the mixed sciences
and presents a stimulating discussion of Aristotle's position but fails to consider whether
the tradition received by Galileo was in fact developed further by medieval scholastics.
William Wallace's recent research (in particular [1981] and [1984]) has demonstrated that
Galileo's early work was heavily influenced by Jesuit scholars at the Collegio Romano.
But a glance at the sources cited by one of Galileo's chief Jesuit sources, Paulus Valla,
suggests that the tradition upon which Valla and perhaps his colleagues were drawing
was developed in medieval commentaries on the Sentences, not exclusively the Posterior

Analytics.
8 McMullin (1978), esp. at 211-12.
9 Duhem (1987), p. 340.
10 Pomponazzi (1525), fol. 6va, 9va-vb; Buonamici (1591), p. 525.
u By my own count, based on surviving commentaries listed in Lohr (1967-1974), there
were some thirty-six commentaries on thb Posterior Analytics produced at Paris during
the period, against only sixteen at Oxford.
12 Concerning this latitude, see Glorieux (1941) at 1863-1865.
13 Muckle (1958). The date of Holcot's work has been the subject of much discussion.
See Courtenay (1987), p. 252 n. 5 and 268-69.
14 Paris, BN lat. 15880, fol. 36ra-38vb; BN lat. 14514, fol. 277vb-280rb. Concerning
Halifax, see Courtenay (1987), p. 272.
is Oxford, Oriel College 15, fol. 3ra--4va. This prologue is best treated as an anonymous
one, since Fitzralph's authorship has been rejected by Left (1963), p. 176.
16 One might also add Stephen Patrington's Repertorium diversorurn auctorum (Florence, B. Laurenziana MS Plut. XVII sin. cod. 10) to this list. Patrington's work, written
before 1389, is a handy source for investigating particular topics discussed in the fourteenth century, since it is preceded by an index of topics which he excerpted. While it
contains a good deal of material on seientia (Sections 35a-36a; pp. 33-35) and especially
scientia large et proprie (Section 35b2; p. 34), Patrington does not seem to have included
subalternation.

In all such cases, however, an element of caution is in order. While such treatments
of scientia do not contain explicit references to subalternation, they are frequently valuable for ancillary materials. For example, in Halifax's treatment just mentioned, it is
clear that his position on the definition of speculative and practical sciences is somewhat
flexible, and thus coordinates with the flexibility in the definition of subalternation that
will be discussed below. The prologue in Oriel 15, fol. 3rb contains a definition of scientia
that might be compared with the one reviewed retrospectively by Thomas Claxton early
in the next century.
A somewhat more useful discussion is found in Walter Chatton's Reportatio from about
1322-23. See below, note 38.
17 Kuhn (1970), pp. 87-88.
18 Courtenay (1987), pp. 251-58.
19 Adam Wodeham: forthcoming, d. I, q. 3, pp. 226-50 at 246. I should like to thank
Dr. Wood for allowing me prepublication use of her edition. I have examined the section
of Cambridge, Gonville and Caius College MS 281(674) that contains this portion of the
text (fol. 137ra-rb), and one might note that the argument based on subalternation seems
to have been singled out in the margin for special attention by one reader.
20 Robert Graystanes, Questiones super Sententias, Prologue, q. 3; London, Westminster
Abbey MS 13, pp. 141b-143a. Like many of the questions in this commentary, question
3 contains a lengthy addition to article 2 which is to be found at pp. 156b-157b. Graystanes
lectured on the Sentences probably around 1322. For a description of the manuscript, see
Robinson and James (1909), p. 72. For a list of the questions contained in the text, see
Kennedy (1986). Concerning Graystanes's career, see Emden (1957-1959), vol. 2, p. 814
and Tachau (1988), pp. 161,209.
21 In the earliest catalogue of Durham College books, we find the record " . . . Lyncolnicrisis super librum posteriorum et expositio super metaphisica ex procuratione eiusdem",
where Graystanes is identified in the preceding record; Blakiston (1896), p. 37. The
volume was also included in the catalogue made ca. 1390: "Lincolniensis super libros
posteriorum et Fernandus super methephisicam in j volumine." See Salter et al. (1942),
p. 243. Given Graystanes's use of Grosseteste's commentary in his commentary on the
Sentences, it would be interesting to inspect this volume, and the further identification
of Fernandus de Hispania as the author of the second commentary would facilitate this.
But Fernandus's Metaphysics commentary survives in only one known copy, Oxford,
Merton College MS 281, which unfortunately seems never to have contained Grosseteste's
commentary on the Posterior Analytics.
22 Concerning Reading's career, see Livesey (1989), esp. chapter I. For a discussion of
Reading's use of Grosseteste, see chapter II.1.
29 Thus, for example, Cowton refers to the thing superadded to the object of the subalternating science, a feature of Grosseteste's theory that becomes virtually universal in the
fourteenth century. See In Sententias. Prologus, q. 2; Theissing (1970), p. 262, lin. 4-6.
William of Nottingham's discussion of subalternation occurs in q. 1, a. 3 of his commentary; Cambridge, Gonville and Caius College MS 300(514) fol. 4ra-5rb. At fol. 5ra, he
notes, "semper scientia subalternata addit aliquam rationem extraneam super subiectum
seientie subalternantis". Somewhat more perplexing is William of Alnwick's treatment
in Prologue, q. 5, a. 1 (Assisi, B. Communale 172, fol. 29v-34r). Alnwick neither cites
Grosseteste explicitly nor uses arguments suggesting familiarity with his commentary.
But the discussion occurs in response to Aquinas's position, and elsewhere, in question

1, it is clear that Atnwick's position on subalternation is governed by his underlying
contention that the real problem of faith and reason lay not in this or that mechanism
of subalternation, but in their compossibility at all. This question has been edited by
d'Souza (1973); note especially the brief discussion of subalternation there at p. 475.
24 Despite Grosseteste's authority, some aspects of the theory were open to modification.
The anonymous author of Merton College MS 103 (produced around 1300) cites Grosseteste in his treatment of subalternation (fol. 216ra-216va), but also gives four conditions
for subalternation, the second of which is (fol. 216ra-rb): "Secunda condicio est quod
principia scientie subalternantis descendant in principia scientie subalternate et in omnes
conclusiones eius, ita quod nulla sit conclusio in subalternata quin possit probari per
principia subalternantis, et propter hoc medicina non subalternatur geometric, quia non
quoad omnes conclusiones dependet ex principiis geometrie, licet quoad aliquas, ut quod
vulnera circularia tardius sanantur." But under such a condition, it is difficult to see how
a science should be subalternated simultaneously to two superior sciences.
25 Robert Grosseteste (1981), pp. 148-50. For a more complete discussion of Grosseteste's theory of subalternation, see Laird (1983), chapter II and Livesey (1989), chapter
II.2.
a6 Robert Graystanes, Questiones super Senentias, Prologue, q. 3; London, Westminster
Abbey MS 13, p. 142b: "Confirmatur per Philosophum I Posteriorum; scientia subalternata semper est de ente per accidens, unde Lincolniensis ibi et est c. 12, 'sciendum quod
scientia inferior superaddit condicionem per quam appropriat sibi subiectum et passiones
superioris scientie. Et sunt in conclusione scientie subalternate, sicud due nature, natura
scilicet quam accipit a superiori et natura propria quam superaddit.' Hec isti."
27 Note, for example, that the discussion of subalternation first appears at Posterior
Analytics 1.7, where Aristotle introduces the topic by appealing to the three elements of
demonstration: the conclusion, the axioms, and the underlying genus. And medieval
scholars, John of Reading especially, drew special attention to Aristotle's discussion in
1.28 on the unity of science and its cohesion. Much the same can be said of Aristotle's
discussion in 1.13, where the theory of subalternation is most elaborate.
2s It would take us too far afield to discuss Aureol's positions on both issues. I have
discussed them and the objections made by Ockham and Reading in Livesey (1989),
chapter III.4 and in Livesey (1985).
29 For the latter, see Metaphysics IV.2 1003b19-23 and especially Categories VIII 8b28-34.
3o Peter Lombard (1971), T. I, pars ii, p.55; Augustine (1962), I, c. 2, n. 2 (p.7).
3, John of Reading, Scripture in I librum Sententiarum, Prol. q. 6; Florence, BN Centrale,
Cony. Soppr. D.IV.95, pp. 86-87. I have edited the text of this question in Livesey
(1989).
32 For a more extensive discussion of this argument, see Livesey (1989), chapter II,
section 6.
33 Duhem (1913), p. 442: "La solution des sophismes se pr6sente donc comme un
16gitime exerciee de Logique, tant qu'elle demeure un exercice. Mais la gymnastique qui
ne se propose plus simplement de fortifier et d'assouplir te corps, la gymnastique qui
cesse d'6tre un moyen et se prend pour une fin, devient acrobatie; de m6me, en toute
6mde, l'exercice artificiel qui perd de rue l'objet r6el pour lequel il a 6t6 combin6 devient
une acrobatie; ainsi la casuistique morale ou juridique peut d6g6n6rer en acrobatie, ainsi
la solution des probl~mes peut prater h l'acrobatie math6matique et la solution des
sophismes h l'acrobatie logique.

Au temps de Guillaume Heytesbury, cette acrobatie logique 6tait le sport en vogue
l'l~cole d'Oxford."
34 William of Ockham (1970), Prol., q. 1 (pp. 14-15). William of Ockham (1974), III,
ii, chap. 21 (pp. 54142). The influence of Ockham's ideas on subsequent writers in the
fourteenth century has been a hotly debated topic. Duhem, of course, regarded Ockham
as a seminal figure for much of the scientific work of the fourteenth century, a position
that found a number of supporters in subsequent generations of historians. Weisheipl
(1968) in particular and Herman Shapiro (1957) attempted to show the relationship
between Ockham's positions on crucial physical and metaphysical issues and the calculatory tradition. But more recently, Courtenay (i987) and Tachau (1988) have called
attention to the fundamental differences between Ockham and his reputed followers,
arguing that the existence of an 'Ockhamist school' may have been assumed too quickly.
On the issue of subalternation, one can find early opponents of Ockham, such as Chatton
(see note 38 below), whose arguments seem to derive more from an underlying disagreement about metabasis than from the mechanism of subalternation. Such a fundamental
debate is one that very likely will be with us for some time, but certainly one additional
piece of evidence that needs to be considered in greater detail is the commentary on the
Sentences found in Merton College MS 284.
From the paper on which the text was written, it is clear that the commentary was
produced after 1340, and based on other considerations, probably before the mid-century.
The text seems to have been a notebook of some anonymous student, who selected
excerpts from other previous commentaries, perhaps as a way to prepare for his own.
But what is also clear is that Ockham's position figures prominently, and when other
positions are given, Ockham is granted the last word. The text itself closely resembles
the Ordinatio, although it differs in ways that led Gerard Etzkorn (1987) to suggest that
the author may have been using the lost Reportatio of book I.
Unfortunately, the sections of Prologue, qq. l, 11, and 12 that contained material on
subalternation were not excerpted by the author, leading one again to the fact that about
the middle of the century the topic seems to have suffered a decline in interest. But
question 2 of MS 284, corresponding to question 2 of Ockham's prologue, contains much
material on the definition of scientia and the distinction between quia and propter quid
demonstration, issues that were central to both Aristotle's and Ockham's ideas about
subalternation. In particular, at fol. 7v, an objection to Ockham's theory of cognition is
made, viz., if Ockham were correct, only one experience would be necessary to know a
principle of art and science; Ockham's resolution is likewise given, that if the principle
falls under the most specific species, then certainly only one experience suffices. But if
the principle falls under what is common to several species, several experiences are
required, following what Aristotle says in Posterior Analytics II on induction. Likewise,
at fol. 9v, Ockham notes the fundamental distinction between quia and propter quid
demonstration: the same thing is proved, but through different media. At fol. 10r, he
follows up what has been said about individual and universal cognition by defining
particular and universal demonstration, providing examples of each, the second of which
relies heavily on the temporal element in the demonstration. And Ockham's tendency
to reinterpret Aristotle is also exemplified shortly thereafter (at fol. 10r), when in the
context of Aristotle's statement that to know is to understand the cause of the thing,
Ockham notes that not every demonstrable should have a cause properly speaking:
rather, it suffices that there should be something prior to which the thing agrees primarily
in predication.

35 John of Reading, Scriptum in 1 librum Sementiarum, Prol. q. 6; Florence, BN Centrale,
Conv. Soppr. D.IV.95, p. 86: "Scientia ergo de superiori et inferiori nec est una nisi
sit genere relato, nec se habet sicud scientia subalternans et subalternata. Assumptum quod scilicet scientia de inferiori non subalternetur scientie de superiori, non sic proprie
subalternata illi et complete, lieet aliquo modo posset forte dici - patet."
36 Oxford, Batliol College MS 63, fol. 67r-85v at 70r: " U n d e si non sit hic proprie
subalternatio, est tamen hic quedam subalternatio que similitudinem habet cure subalternatione." F. Pelster (1955, at pp. 30-31) concluded that the author was an Augustinian
at Oxford, and while Roger Mynors suggested that MS 63 as a whole probably was
produced not long after 1330, it is somewhat difficult to determine the date of this
commentary. At fol. 69r, it refers to Peter Aureol, which places the text after 1317; but
other than William de Ware, whose commentary is still earlier than this, the other authors
cited in the text cannot be identified. It is clear that elsewhere the author was relying
upon Aegidius Romanus for his information about subalternation, although as I have
noted above, there is a heavy dose of Grosseteste in the commentary as well. The author
notes that there are three modes of subalternation: (1) in which the inferior science serves
(famulatur) the superior science, (2) in which the inferior science adds a condition to
the subject of the superior, and (3) in which the inferior and the superior sciences consider
the same truth, the former modo grosso, the latter modo subtili. (1) and (3) are mentioned
by John of Reading in question 7 of his prologue, immediately after discussion of Richard
Connington's theory (Florence, BN Centrate, Conv. Soppr. D.IV.95, p. 93); in the text,
the position is not attributed to a specific author, and may well have been a common
one at Oxford at the time.
37 Graystanes, Questiones super Sententias, Prologue, q. 3; London, Westminster Abbey
MS 13, p. 143a: "Respondeo negando hanc consequentiam. 'Visio linee in verbo est
perfectissima eius cognitio. Ergo subalternat sibi omnes alias notitias de verbo.' Sed
oportet addere quod visio in verbo esset causa aliarum cognitionum quod non est verum
in proposito. Unde eadem conclusio potest cognosci perfectius et imperfectius ut forte
methaphysicus, quia cognoscit per tres causas aliquam conclusionem, cognoscit perfectius
quam geometer, qui cognoscit per unam causam tantum. Ipsi enim considerant multas
easdem conclusionis cure scientia unius conclusionis; una non est subalternata alteri
eiusdem conclusionis, ut cognitio quam habet geometer de alia cognitione ad illam quam
habet metaphysicus de eadem, ut enim prius habitum est. Subalternans est principium
respectu subalternate, et eadem conelusio non potest esse principium respeetu sui ipsius.
Maior etiam non est verum nisi intelligitur sic, quod resolutio in cognoscentibus non stat
nisi ad perfectum cognoscibile vel perfectissimam cognitionem illius generis. Non enim
potest geometer resolvere ulterius quam permittit sua facultas, sed oportet quod resolutio
sua stet in prima limites suos".
38 In his Reportatio, Prologue, qu. 1, a. 3, Chatton refers to Ockham's view that while
the same proposition cannot be proven in distinct sciences when one defines science as
the habit of one conclusion, it can so pertain to different sciences when science is taken
as a collection of habits. Thereupon, Chatton divides his response into two parts, one
restricted only to theology, the other to sciences in general, and with respect to the latter,
he argues that such propositions proved in distinct sciences are not similar in essendo but
rather in significando. "For although by possessing several sciences, one can apply
premises which one forms according to concepts formed in the other, nevertheless the
practitioner in any s c i e n c e . . , will form the conclusion from cognitions of a different

ratio in being from the conclusion of any other science." And in direct response to
Ockham's argument, Chatton observes that even supposing that the conclusions are
subordinated (he does not use - here or elsewhere - the term subalternation), still the
conclusion is proved through middle terms of different rationes by different practitioners.
See the text edited by Reina (1970), at 296-302.
39 For details on Claxton's life, see Emden (1957-1959), vol. 3, p. 426. Claxton was at
the Oxford Convent by 1404 and a regent master in 1413. His commentary gives a
retrospective look at the previous century, and thus offers not merely a picture of current
views, but also fifteenth-century criticisms of the early fourteenth-century positions outlined in this paper.
4o Courtenay (1987), p. 363.
41 Cambridge, Gonville and Caius College, MS 370(592) fol. 10v-14r.
42 Ibid., fol. 14r: "In ista questione, sic procedam: primo enim declarabo materias tactas
in titulo questionis nude, aperte, et vere, ut studentes intelligant. Veteres enim theologi
sicut in loquendi logica plurimum defecerunt. Sic veritates inventas vel quas crediderunt
se invenisse in culto et imperito modo loquendi sequentibus se tradiderunt. Unde et
parvus error in principio in maximum dilatatus est, qua ex causa Philosophus III Metaphysice c. 11 in textu commenti 6. Veteres philosophos, theologos ut orpheum, ysiodum, et
philosophos etiam reprobat naturales qui adinventas veritates sub tegumentis poeticis vel
mathematicis a sequatibus suis velaverunt. Opiniones autem paucas tangam, quia solum
e a s q u e merito fame ant propinquitatis ad veritatem tangende sunt. Alie enim scita
veritate faciliter reprobantur, quia sicut falsitas inconveniens plurimis se involuit, ut patet
ex sententia Philosophi I Celi et mundi dicentis parvus error in principio maximus est in
fine, sic et veritas semper facile vincit et se declarat."
43 Ibid., fol. 16r-v.
44 Ibid., fol. 28v.
45 Ibid., fol. 28v.
~6 Ibid., fol. 28v-29r.
47 Ibid., fol. 29r: "Ex hiis patet quod ad hoc quod aliqua scientia sit alteri subalterna
son solum opertet quod sit de subiecto eodem de quo est scientia cui subalternatur sed
quod habeat equipollenter aliquod principium proprium primum cuius subiectum sit per
se inferius ad subiectum et predicatum per se inferius ad predicatum primi principii illius
scientie cui subaltcrnatur. Verbi gratia, philosophia medicinalis subalternatur philosophia
naturali quia sub isto principio eius primo "corpus est mobile' habet primum suum
principium proprium 'corpus animale est mobile ad infirmitatem vel sanitatem vel neutralitatem,' sicut perspectiva sub hoc principio geometrie, 'figura est terminata,' capit hoc
principium sibi proprium 'linea visiva terminatur ad oculum faciens visionem,' et ideo
perspectiva subalternatur geometrie, licet secundum aliquas eius partes subalternetur
philosophie naturali capiens istud principium suum sub primo principio eius dicto 'animal
est mobile ad visionern a corpore lucido sibi obiecto.' Similiter ars de ponderibus capit
proprium principium suum hoc, scilicet 'corpus gravius elevat levius' sub primo principio
philosophie naturalis, et ideo sibi subalternatur. Et sic de musica que capit hoc suum
principium, 'ex proportione 1 ad 4 fit diapason et plenus tonus,' sub hoc principio
arismetice, 'omnis numerus est alteri proportionalis' et ideo sibi subalternatur, et sic de
aliis".
48 Thus, at fol. 31v, Claxton resolves an objection that his notion of unity of science is
too strong, allowing all the sciences in the world to be one numerically in the way that

geometry is one; he replies that although all the sciences in the world might be one by
aggregation, this is not the way that geometry is one, since sciences are said to be one
not merely by aggregation, but by aggregation and coordination to one first principle,
and such coordination is not found in diverse sciences.
Claxton's objections to Holcot and Ockham occur in the response to the sixth principal
argument, at fol. 32r and 35v.
~9 Ibid., fol. 36r: "Sexta conclusio est hec: Viatorum theologia non est sanctorum theologic subalterna. Probatur ista conclusio sic. Nulla est facultas vel scientia alteri subalterna
nisi cuius principium habet se ex additione tam aperte subiecti quam aperte predicati vel
realiter vel equivalenter ad primum principium alterius vel cui subalternatur. Sed non sic
se habet theologia viatorum ad theologiam beatorum. Ergo non est sibi subalterna. Patet
consequentia et major ex premissis et minor sic probatur. Idem est subiectum theologic
viatorum et theologic beatorum, et utriusque theologic primum principium alteri equipollet. Ergo primum principium theologic viatorum non est inferius primo principio theologic
beatorum, scilicet ea inferiorite que requiritur ad subalternationem. Patet consequentia
et antecedens per hoc, quod utriusque theologic est primum principium ~Deus est summum bonum possibile.'" He then sums up his earlier remarks that subalternation is not
merely dependent on a simple relationship of superiority and inferiority of certainty:
"Septima conclusio est hec: licet viatorum theologia sit inferior id est imperfectior quam
beatorum theologia, non tamen est ei subalterna. Ista conclusio patet ex premissis".
5o Jaki (1984), pp. 393-400.
51 For example, at fol. 35v.

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St. Bonaventure, New York.
Department of the History of Science
The University of Oklahoma
Norman, Oklahoma 73019
U.S.A.

CHRISTOPHER

CLAVIUS

CLASSIFICATION

AND

THE

OF SCIENCES

ABSTRACT. I discuss two questions: (1) would Duhem have accepted the thesis of the
continuity of scientific methodology? and (2) to what extent is the Oxford tradition of
classification/subalternation of sciences continuous with early modern science? I argue
that Duhem would have been surprised by the claim that scientific methodology is
continuous; he expected at best only a continuity of physical theories, which he was
trying to isolate from the perpetual fluctuations of methods and metaphysics. I also argue
that the evidence does not support the conclusion that early modern doctrines about
mathematics and physics are continuous with the subalternation of sciences from Grosseteste, Bacon, and the theologians of fourteenth-century Oxford. The official and dominant
context for early modern scientific methodology seems to have been progressive Thomism, and early modern thinkers seem to have pitted themselves against it.

When considering the various historical doctrines relating science and
mathematics, we should keep in mind three important facts. (1) Early
m o d e r n science considered mathematics as the foundation of physics
or natural philosophy - witness Galileo's famous assertion that "the
great book of nature is written in the language of mathematics and its
characters are triangles, circles, and other geometrical figures" (1960,
p. 25). (2) It wasn't always that way. Aristotle in the Physics discussed
how the mathematician differs from the physicist (1930, II, chap. 2).
H e asserted that physicists deal with physical bodies and their essential
attributes; physicists treat of surfaces and volumes, lines and points,
but as the limits of physical bodies. Mathematicians also treat of surfaces and volumes, points and lines, but not as physical, separating them
from their essential attributes and from motion. G e o m e t r y investigates
physical lines, but not qua physical; the m o r e physical branches of
mathematics such as optics, harmonics, and astronomy, investigate
mathematical lines, qua physical, not qua mathematical. Instead of
mathematics being the foundation of physics, Aristotle conceived of
mathematics and physics as different sciences separated by their differ-'
ent objects. A n d (3) the medievals were not univocal in their support
of the Aristotelian position. T h e y interpreted' Aristotle's remarks so
variously that they can be considered as making up at least two distinct
Synthese 83: 293-300, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

traditions, roughly that of Thomas Aquinas and that of Robert Grosseteste.
Thomists standardly held that physics, metaphysics, and mathematics
are not part of one large science, but constitute three (or more) radically
different sciences, differing in their subject and method: metaphysics
considers being in common, physics considers natural being, and mathematics considers quantified being. Some such schema was adopted
widely, with many variations. What all such schemas had in common
was the rejection of a universal science (whether or not based on
mathematics). Mathematics usually filled the lowest rank in these classifications (typically, the least perfect of the speculative sciences). Mathematical sciences, such as astronomy, astrology, and optics were called
middle sciences because they were thought to occupy a middle position
between mathematics and physics; they were thought to depend on
mathematics, but also to consider the mathematical object as applied
to a physical object. The typical doctrine was that the middle sciences
were more mathematical than physical, since the mathematical object
was more essential to them than their condition of application. Thus,
the middle sciences would have been unfit to provide support for physics. Implicit in all this is the doctrine that a higher science cannot
derive its principles from a lower science, so that physics cannot derive
principles from mathematics or from any middle science.
The followers of Grosseteste, including Roger Bacon and scholars
from fourteenth-century Oxford, held a doctrine that could easily have
been derived from the writings of Aristotle, but that seems discontinuous with the Thomist line. While agreeing with the basic intuition that
the higher sciences provide the reason for the lower sciences (the
subalternated sciences), Grosseteste disagreed about the status of the
important composite sciences. He argued that composite sciences have
an additional nature about which the higher sciences say nothing; ultimately he asserted that only mathematics can provide the reason for a
subalternated science and even for natural philosophy. Roger Bacon
followed him in this. In the Opus Majus and Opus Tertium, Bacon
detailed a view of human knowledge as a hierarchy of knowledge in
which mathematics is antecedent to natural philosophy and to metaphysics: "without mathematics no science can be had" (1859, p. 35; also
1928, I, p. 109). Steven Livesey, in his paper, discusses this tradition in
fourteenth-century Oxford.

All three above facts can be subsumed under the heading of scientific
methodology and have relevance to the now-popular variation to
Duhem's thesis of the continuity of physical theory, namely, the thesis
of the continuity of scientific methodology. The questions I wish to
pose are: (1) would Duhem have accepted such a thesis? and (2)
to what extent is the Oxford tradition of classification/subalternation
continuous with early modern science? The answer to the first question
is relatively simple. Duhem would have been surprised by the claim
that scientific methodology is continuous; he expected at best only a
continuity of physical theories, which he was trying to isolate from the
perpetual fluctuations of methods and metaphysics. Duhem addressed
the issue of the classification or subalternation of sciences in medieval
science, though in bits and pieces, here and there. What he said allows
us to surmise his views. In the SystOrnedu Monde, Duhem spoke harshly
about Roger Bacon's arguments against infinite divisibility, which use
the certainty of geometry to oppose the existence of indivisibles. Duhem
then praised John Buridan's view, in which "the proposition, continuous magnitude is not composed of indivisibles, is not viewed by Buridan
as a corollary whose truth is assured by the necessity of not contradicting
geometry"; Duhem said that Buridan "sees in it a principle whose truth
the geometer is obliged to admit in order to construct his science . . . .
Far from geometry's certainty guaranteeing the truth of the proposition,
it is the truth of geometry that is subordinated to the correctness of the
proposition; and the corredtness of the proposition is not for geometry,
but for physics or metaphysics to establish" (1985, pp. 19-20). Duhem
detailed an interpretation of Buridan as keeping separate a geometry
which considers lines and surfaces as nothing but constructions of the
mind and a physical geometry, in conformity with reality, which only
treats bodies. By reasoning about the former, we achieve results in
conformity with measurements carried out on real bodies (1985, pp.
32-33). But Duhem recognized that Buridan's views were not accepted
by his successors: "Doubtless Buridan's notion was too profound since
it does not appear to have been adopted by even his most faithful
disciples. Albert of Saxony and Marsilius of I n g h e n . . . did not hesitate
to rely on geometry in order to refute the hypothesis [of infinite divisibility]" (1985, p. 20).
The answer to the second question is considerably more complex
(and controversial). Setting aside the general question of the continuity

of scientific methodology, I wish to ask specifically about the early
modern scholastic doctrines concerning the relations between mathematics and physics.
Now, the broad outlines of seventeenth-century Scholasticism were
Thomist. There was a renaissance in Thomistic philosophy during the
second half of the sixteenth century. This renaissance was felt most
strongly in Jesuit philosophy. Saint Ignacius of Loyola, founder of the
Jesuits, advised the Jesuits to follow the doctrines of Saint Thomas in
theology. Naturally, it would be difficult to follow Saint Thomas in
theology without also accepting much of Aquinas's and Aristotle's philosophy. Loyola's advice was made formal in the Jesuits' Ratio studior u m of 1586: "In logic, natural philosophy, ethics, and metaphysics,
Aristotle's doctrine is to be followed" (Rochemonteix 1889, vol. IV,
p. 8n).
The flavor of the advice can be captured through a circular from the
chief of the Order of Jesuits to the Superiors of the Order, written just
after the end of the Council of Trent and imbued with the spirit of the
Council and Loyola's advice. The circular announces specific doctrines
"that must be held in theology and in philosophy", for example, ;'Let
no one defend anything against the axioms received by the philosophers, such as: there are only four kinds of causes; there are only four
elements; there are only three principles of natural things; fire is hot
and dry; air is humid and hot" (Rochemonteix 1889, vol. IV, pp.
4n-6n). These 'axioms' are sufficient to banish Stoic, Epicurean, and
Atomist philosophies; moreover, the circular also rejects doctrines that
might have been accepted by non-Thomist scholastics - Ockhamists,
for instance: "Let no one defend anything against the most common
opinion of the philosophers and theologians, for example, that natural
agents act at a distance without a medium." The circular continues with
specific opinions that Jesuits must teach and hold as true - all in
conformity with Thomist doctrines and against Averroist and Franciscan
doctrines - but the crux of the matter seems to have been: "Let no
one introduce any new opinion in philosophy or theology without consulting the Superior or Prefect." The circular ends with: "Let all profes-,
sors conform to these prescriptions; let them say nothing against the
propositions here announced, either in public or in private; under no
pretext, not even that of piety or truth, should they teach anything
other than that these texts are established and defined. This is not just
an admonition, but a teaching that we impose."

L a t e r circulars r e a f f i r m e d t h e s a m e p o s i t i o n . F o r e x a m p l e , the Jesuit
T h o m i s t s t a n c e is u p h e l d e v e n in a discussion o f t h e t h o r n y q u e s t i o n of
d i v e r g e n t a u t h o r i t i e s . T h e f o l l o w i n g can b e r e a d in a c i r c u l a r f r o m
a n o t h e r G e n e r a l o f t h e Jesuits, to t h e S u p e r i o r s , w r i t t e n in o r d e r to
e x p r e s s c l e a r l y t h e basic t e n e t s u n d e r l y i n g t h e Ratio studiorum o f 1586:
No doubt we do not judge that, in the teaching of scholastic theology we must prohibit
the opinion of other authors when they are more probable and more commonly received
than those of Saint Thomas. Yet because his authority, his doctrine, is so sure and most
generally approved, the recommendations of our Constitutions require us to follow him
ordinarily. That is why all his opinions whatever they may be . . . . can be defended and
should not be abandoned except after lengthy examination and for serious reasons.
(Rochemonteix 1889, vol. IV, pp. lln-12n)
This i n t e r p r e t a t i o n of L o y o l a ' s a d v i c e d r a w s a fine line b e t w e e n following T h o m a s ' s o p i n i o n s ordinarily a n d a b a n d o n i n g t h e m for e x t r a o r d i n a r y r e a s o n s , a f t e r l e n g t h y e x a m i n a t i o n . B u t the circular c o n t i n u e s :
" O n e s h o u l d h a v e as t h e p r i m a r y goal in t e a c h i n g to firm up the faith
a n d to d e v e l o p p i e t y . T h e r e f o r e , no o n e shall t e a c h a n y t h i n g n o t in
c o n f o r m i t y with t h e C h u r c h a n d r e c e i v e d t r a d i t i o n s , o r t h a t can d i m i n i s h
the v i g o r o f t h e faith o r t h e a r d o r o f a solid p i e t y . " T h e i n t e n t o f t h e
c i r c u l a r is clear. T h e p r i m a r y g o a l in t e a c h i n g is t h e m a i n t e n a n c e o f
t h e faith, a n d n o t h i n g s h o u l d b e a l l o w e d to i n t e r f e r e with it. A n d since
the r e c e i v e d t r a d i t i o n s a r e k n o w n to c o n f o r m to t h e faith, t h e y s h o u l d
b e t a u g h t a n d n o v e l t i e s a r e to b e a v o i d e d . T h e c i r c u l a r c o n t i n u e s :
Let us try, even when there is nothing to fear for faith and piety, to avoid having anyone
suspect us of wanting to create something new or teaching a new doctrine. Therefore no
one shall defend any opinion that goes against the axioms received in philosophy or in
theology, or against that which the majority of competent men would judge is the common
sentiment of the theological schools . . . . Let no one adopt new opinions in the questions
already treated by other authors; similarly, let no one introduce new questions in the
matters related in some way to religion or having some importance, without first consulting the Prefect of studies or the Superior,
It is n o t s u r p r i s i n g t h a t t h e p h i l o s o p h y t e x t b o o k s w r i t t e n b y Jesuit
a u t h o r s - t h o s e o f P o r t u g u e s e Jesuits, the C o i m b r a n s , a n d such C o l l e g i o
R o m a n o Jesuits as F r a n c i s c u s T o l e t u s - t h o u g h n o t i d e n t i c a l with o n e
a n o t h e r , g e n e r a l l y p r e s e r v e d basic T h o m i s t i c d o c t r i n e s . T h e s a m e can
b e said a b o u t t h e q u e s t i o n o f t h e classification o f sciences as r e f l e c t e d
in the Ratio studiorum, i n c l u d i n g t h e k e y q u e s t i o n s a b o u t the utility o f
m a t h e m a t i c s to n a t u r a l p h i l o s o p h y a n d t h e status o f such m a t h e m a t i c a l
sciences as a s t r o n o m y a n d optics.

The extreme Jesuit view about mathematics and natural philosophy
can be represented by Ludovico Carbone (a non-Jesuit) (1599; cf.
Wallace, 1984, especially pp. 126-48). Carbone details eleven doubts
about the mathematical sciences. Some of these doubts concern the
type of abstraction characteristic of mathematics: mathematicians consider bare quantity without any connection to substance; the intelligible
matter they arrive at when they set aside sensible matter is merely
fictive and cannot be defined in terms of true genus and difference;
they abstract from being and the good; they abstract from motion and
the natural forces that produce it; they abstract from all kinds of cause
and so cannot use causal reasoning in any of their demonstrations.
(1599, pp. 240-43). Though Carbone was not a Jesuit, he studied at
the Collegio Germanico, annexed to the Jesuits' Collegio R o m a n o . His
works were influenced (perhaps overly so) by those of Collegio R o m a n o
professors. In any case, one can find similar views in the works of
some Jesuits, Piccolomini and Pereira, for example (see Crombie 1977.)
C a r b o n e ' s views about mathematics and the mathematical (or middle)
sciences fit very well with sixteenth-century scholastic doctrines, of
Thomist descent, about the order and classification of the sciences.
It is against this background that Christopher Clavius proposed his
reform of mathematics, arguing its importance to natural philosophy.
In an essay for the Ratio studiorum on the teaching of mathematical
disciplines he wrote:
Physics cannot be understood correctly without [the mathematical disciplines], especially
what pertains to that part concerning the number and motion of the celestial orbs, of the
multitude of intelligences, of the effect of the stars, which depend on the various conjunctions, oppositions, and other distances between them, of the division of continuous
quantities to infinity, of the tides, of the winds, of comets, the rainbow, halos, and
other meteorological matters, of the proportion of motions, qualities, actions, passions,
reactions, etc., concerning which the calculatores wrote much. (1901, p. 472)
In the same vein, Clavius disputed the c o m m o n opinions that the
mathematical sciences are too abstract and fictive:
It will contribute much to this if the teachers of philosophy abstained from those questions
which do not help in the understanding of natural things and very much detract from the
authority of mathematical disciplines in the eyes of the students, such as those in which
they teach that mathematical sciences are not sciences, do not have demonstrations,
abstract from being and the good, etc. (1901, p. 471)
Obviously Clavius has in mind the kind of views represented by Carbone and others. This is significant, since Clavius was responsible for

the training of Jesuit mathematics professors and the content of their
teaching.
Clavius concentrated on showing that mathematics and mathematical
sciences are useful and more certain than the other sciences. However,
a science's degree of certainty is not proportional to its degree of
perfection, so that, in spite of his pronouncement that physics cannot
be understood correctly without the mathematical sciences, his view
does not alter the basic Thomistic scheme. That scheme claims that the
subjects of the sciences are different, and more or less perfect; it is
consistent with it that a less perfect science, such as mathematics, might
have results that are certain, with respect to a particular subject, such
as abstract or quantified being. The difference between Clavius and
Carbone is not really a difference of theory but a difference of emphasis
within the same general theory. Clavius, the champion of mathematics
in the Collegio Romano, does not seem to appeal to the Oxford doctrine
of classification/subalternation in order to defend mathematics.
It would be pleasant to think that the early modern doctrines about
the relations between mathematics and physics are continuous with the
subalternation of sciences from Grosseteste, Bacon and the theologians
of fourteenth-century Oxford. Unfortunately, thus far the evidence
does not support such a conclusion. The official and dominant scholastic
context for early modern doctrines seems to have been progressive
Thomism, and early modern thinkers such as Descartes seem to have
pitted themselves directly against it. From his earliest writings, the
'Private Thoughts', for instance, we have Descartes's dream of a chain
of sciences that would be no more difficult to retain than a series of
numbers (1974, p. 214), and from Rule I of the Rules for the Direction
of the Mind, we have an explicit denial of the doctrine that the sciences
should be distinguished by the diversity of their subjects, "all the sciences being in effect only human wisdom, which always remains one
and identical to itself, however different are the objects to which it is
applied" (1974, p. 360).
REFERENCES

Aristotle: 1930, Physica, W. D. Ross (trans.), Oxford University Press, Oxford.
Bacon, R.: 1859, Opus terfiurn, in Opera Hactenus lnedita, J. S. Brewer (ed.), Kraus
reprint, London.
Bacon, R.: 1928, Opus rnaius, J. H. Bridges (ed.), Univ. of Pennsylvania Press, Philadelphia.

in Universam philosophiam, N. A. Zalterium, Venice.
Clavius, C.: 1901, 'Modus quo disciplinae mathematicae in scholis Societatis possent
promoveri', in Monumenta Paedagogica Societatis Jesu quae Primam Rationem Studiorum anno 1586 praecessere, A. Avrial, Matriti.
Crombie, A. C.: 1977, 'Mathematics and Platonism in Sixteenth-Century Italian Universities and in Jesuit Educational Policy', in Y. Maeyama and W. G. Saltzer (eds.),
Prismata, Naturwissenschaftsgeschichtlishe Studien, Franz Steinerverlag, Wiesbaden.
Descartes, R.: 1974, Oeuvres de Descartes, vol. X, C. Adam and A. Tannery (eds.),
Vrin, Paris.
Duhem, P.: 1985, Medieval Cosmology, Roger Ariew (trans.), Chicago University Press,
Chicago.
Galilei, G.: 1960, The Assayer, S. Drake (trans.), in The Controversy on the Comets of
1618, Univ. of Pennsylvania Press, Philadelphia.
Rochemonteix, C. de: 1899, Un CoIlOge des Jesuites au XIIe et XIlle si~cle le coll~ge
Henri I V de la Fl~che, Legvicheux, Le Mans.
Wallace, W.: 1984, Galileo and His Sources, The Heritage of the Collegio Romano in
Galileo's Science, Princeton, New Jersey.

Department of Philosophy
Virginia Polytechnic Institute and State University
Blacksburg, Virginia 24061
U.S.A.

THE REALISM

THAT

DUHEM

REJECTED

IN COPERNICUS

ABSTRACT. Pierre Duhem rejected unambiguously the strong version of realism that
he believed was held by Copernicus. In fact, although Copernicus believed that his theory
was clearly superior to Ptolemy's, he seems to have recognized that his theory was at
best only approximately true. Accordingly, he recognized that his arguments were not
demonstrative in the traditional sense but probable and persuasive. Duhem regarded
even the belief in probably true explanations as misguided. Nevertheless, Duhem recognized that, even if metaphysical intuition does not enter into the content of physical
theories, the rejection of hypotheses could be explained only by appeal to common sense.
Hence, Duhem held a qualified instrumentalism according to which physical theories are
not realist, but the terms of ordinary experience and empirical laws are realist. Accordingly, Duhem rejected the complete subordination of science to philosophy as well as the
complete separation of science from philosophy. Duhem's history of cosmological doctrines reflects his belief in the origin of the subordination of science to philosophy and
of the struggle to achieve the proper balance without being driven to the opposite extreme
of their complete separation.

1 . INTRODUCTION
The figures of Copernicus and Galileo hover over two of Pierre
Duhem's multi-volume historical studies like specters making timely
appearances as D u h e m discovered and uncovered a text that in some
way anticipated a concept found clearly for the first time in our modern
heroes (Etudes; Systdme). In Duhem's plan those earlier texts created
a possibility that with time became more probable and then was to
become certain as Copernicus and Galileo appear in full, adopting an
available and prepared conceptual space, defining its content and fulfilling an expectation. There was nothing inevitable about these developments; on the other hand, they did not emerge ex nihilo. As it turned
out, D u h e m never completed his most ambitious drama and, perhaps
worse, he did not live to produce a definitive, if you will, cinematic
version, leaving us instead with an often diffuse and repetitious series of
sketches in which the leading characters make only cameo appearances.
Be that as it may, these are the Copernicus and Galileo of Duhem's
histories, and it is with them that we must be content. In the works on
Synthese 83: 301-315, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

which this examination primarily rests, The Aim and Structure of Physical Theory and To Save the Phenomena, Copernicus and Galileo play
something of a symbolic role for Duhem as representatives of a commitment to a version of realism of which Duhem definitely disapproved.
Their cameo appearances in his major historical surveys occasionally
suggest a somewhat less stereotypical portrayal and a far more positive
evaluation, yet Duhem apparently believed that the childishly naive
realism of the commonsense view of science could be traced to Copernicus and Galileo. These authors require separate treatment; I will
focus on Copernicus even though Duhem made little distinction between them on the question of their realism. Moreover, the problems
concerning Duhem's positivism and realism are complicated even more
by the intricately tangled relations of his philosophy, science, and history, My aim is to define as precisely as possible Duhem's views on
realism. My procedure involves (1) identifying the realism that Duhem
rejected in Copernicus, (2) comparing Duhem's reading of Copernicus
with recent interpretations of Copernicus, and (3) projecting the result
into conditions that a realist interpretation of Duhem must meet if it
is to be consistent with his principles and practice. The risk in trying
to project how Duhem's account might look today is obvious, but I
trust that the distinction between explication and appropriation can be
made sufficiently clear so as to avoid misunderstanding and deception.
2.

THE

REALISM

THAT

DUHEM

REJECTED

IN COPERNICUS

The exposition follows the order in which the two works mentioned
above appeared. In Aim and Structure, Copernicus first appears in a
context where Duhem cites St. Thomas Aquinas approvingly for having
held that astronomical hypotheses that save the appearances are not
necessarily true nor are they sufficiently demonstrable, for it is possible
that the appearances might be better preserved by some other hypothesis yet unknown by men. Duhem points out that this opinion agrees
with a number of passages in Copernicus and Rheticus. Duhem explains
that in the Commentariolus Copernicus presents the fixity of the sun
and the mobility of the earth as postulates that the reader is asked to
concede. Of course, Duhem adds that in De Revolutionibus Copernicus
"professes an opinion concerning the reality of his hypotheses which
is less reserved than the doctrine inherited from Scholasticism and
expounded in the Commentariolus" (AS, pp. 41---42). After citing Osian-

der's 'Letter to the Reader', Duhem criticizes Kepler's disapproval in
the following words: "This enthusiastic and somewhat naive confidence
in the boundless power of the physical method is prominent among the
great discoverers who inaugurated the seventeenth century" (p. 42).
Duhem concludes the paragraph with a quotation from Cardinal Bellarmine's letter to Foscarini about speaking ex suppositione, and Duhem
comments: "In this passage Bellarmin [sic] maintained the distinction,
familiar to the Scholastics, between the physical method and the metaphysical method, a distinction which to Galileo was no more than a
subterfuge" (p. 43).
The passages and opinions to which I have just referred appear in
the second part of Chapter 3 on representative theories and the history
of physics. Here Duhem attempts to explain the role of natural classifications and explanations in the evolution of physical theory, and in the
second part of that chapter he contrasts the views of physicists and
philosophers on representation and explanation. Duhem makes it clear
that even the natural classifications towards which he sees physical
theory evolving are not explanations (pp. 31-32). Although the explanation of a theory yields to another explanation, it is in the representative
part that Duhem locates what appears as a natural classification.
Duhem's preference for the empiricist reading of Newton's law of
universal gravitation, a reading that Duhem commends to the physicists
of the nineteenth century, shows that he does not regard natural classifications as explanatory, nor is there any indication that he views physical theories as requiring the discovery of the causes of phenomena (pp.
47-49). On the contrary, Duhem complains that in the nineteenth
century, hypothetical theories offered as more or less probable explanations of phenomena led to an extraordinary multiplication of such
theories. He comments: "The noise of their battles and the fracas of
their collapse have wearied physicists and led them gradually back to
the sound doctrines Newton had expressed so forcefully" (p. 53). What
doctrines? Certainly not the inductive method without hypotheses,
which Duhem elsewhere deplores (pp. 190-200, 284), but deductive
and inductive procedures by way of hypotheses that lead to a condensed
representation. Such a representation is not explanatory, nor does it
lay bare the causes of phenomena. Duhem is wary not only of causal
explanation but even of probable explanation (pp. 37, 53). These he
expects to rise and fall, but that which corresponds to natural classification is found in the representative parts:

It is not to this explanatory part that theory owes its power and fertility; far from it.
Everything good in the theory, by virtue of which it appears as a natural classification
and confers on it the power to anticipate experience, is found in the representative part;
all that was discovered by the physicist while he forgot about the search for explanation.
On the other hand, whatever is false in the theory and contradicted by the facts is found
above all in the explanatory part; the physicist has brought error into it, led by a desire
to take hold of realities . . . .
When the progress of experimental physics goes counter to a theory and compels it to
be modified or transformed, the purely representative part enters nearly whole in the
new theory,.., whereas the explanatory part falls out in order to give way to another
explanation.
Thus, by virtue of a continuous tradition, each theory passes on to the one that follows
it a share of the natural classification it was able to construct,.., and this continuous
tradition assures a perpetuity of life and progress for science.
This continuity of tradition is not visible to the superficial observer due to the constant
breaking-out of explanations which arise only to be quelled. (pp. 32-33)
The remainder of Duhem's substantive comments about Copernicus
in Aim and Structure serves to s u p p o r t this d e p i c t i o n o f t h e e v o l u t i o n
of p h y s i c a l t h e o r i e s . T h e r o l e o f t h e C o p e r n i c a n R e v o l u t i o n in the
e v o l u t i o n o f t h e p r i n c i p l e o f u n i v e r s a l a t t r a c t i o n consists in t h e d e s t r u c t i o n o f t h e g e o c e n t r i c s y s t e m . W h a t survives o f C o p e r n i c u s ' s specul a t i o n s a b o u t a n a t u r a l a p p e t i t i o n o r s y m p a t h y in c e l e s t i a l b o d i e s is n o t
t h e c a u s e o f t h e p h e n o m e n o n , a n d n o t t h e a n a l o g y of the m o t i o n o f
i r o n t o w a r d a m a g n e t , b u t r a t h e r t h e i d e a t h a t follows a l m o s t as a
c o r o l l a r y to t h e r e j e c t i o n o f g e o c e n t r i c i t y , n a m e l y , t h a t o t h e r b o d i e s
m u s t b e like t h e e a r t h (pp. 225-31; c o m p a r e Syst~me, X, p. 320).
B e f o r e t r y i n g to d r a w c o n c l u s i o n s f r o m this s u m m a r y o f Aim and
Structure, we m u s t c o n s i d e r D u h e m ' s a p p e n d i c e s to t h e s e c o n d e d i t i o n
p u b l i s h e d in 1914. I n t h e p r e f a c e to t h e s e c o n d e d i t i o n , D u h e m claims
t h a t h e h a d n o t b e e n b r o u g h t to d o u b t his p r i n c i p l e s b u t t h a t t i m e h a d
given h i m an o p p o r t u n i t y to m a k e t h e m p r e c i s e a n d to d e v e l o p t h e m ,
r e f e r r i n g to o n e article p u b l i s h e d a b o u t a y e a r a f t e r t h e first a p p e a r a n c e
of Aim and Structure in serial f o r m a n d a s e c o n d article p u b l i s h e d in
1908 as " c l a r i f i c a t i o n s a n d a d d i t i o n s " (p. xvii).
I n a s m u c h as To Save the Phenomena, t h e n e x t w o r k to b e e x a m i n e d ,
d i d n o t a p p e a r until 1908, t h e c o n s i d e r a t i o n o f t h e articles a p p e n d e d
to Aim and Structure n o w will n o t d i s t u r b t h e o r d e r o f the e x p l i c a t i o n .
I n t h e first article, 'Physics o f a B e l i e v e r ' , D u h e m a c k n o w l e d g e s t h a t
in o r d e r to l e g i t i m a t e t h e a s s e r t i o n t h a t as p h y s i c a l t h e o r y p r o g r e s s e s ,
it b e c o m e s e v e r m o r e s i m i l a r to a n a t u r a l classification as its i d e a l e n d ,
h e m u s t a p p e a l to m e t a p h y s i c s (AS, p. 298). T h e l e g i t i m a t i o n of the
a s s e r t i o n a n d its f u r t h e r e l a b o r a t i o n e x c e e d the limits of his m e t h o d s

as a physicist. The propositions of cosmology and the theorems of
physics are radically heterogeneous, that is, they can neither agree
with nor contradict one another. "However, between two propositions
bearing on terms of different natures it is nevertheless possible that
there would be an analogy, and it is such an analogy which ought to
connect cosmology with theoretic physics" (p. 301). Duhem goes on
to explain that this analogy obtains only "between the metaphysical
explanation of the inanimate world and the perfect physical theory
arrived at the state of a natural classification" (p. 302). We do not and
never will possess this perfect theory. Duhem's severe restrictions here
are apparently intended to caution the philosopher that no proof is
possible, that his theoretic scaffolding is shaky, and that he must have
an accurate and minute acquaintance with physical theory (pp. 302--3).
In addition, he must know its history because his challenge is to understand theory and its development well enough to be able to perceive
trends, that is, to judge the tendency of theory and to surmise the goal
towards which it is directed. "So the history of physics lets us suspect
a few traits of the ideal theory to which scientific progress tends, that
is, the natural classification which will be a sort of reflection of cosmology" (p. 303). In the concluding section of this essay Duhem allows
himself to speculate about the analogy that he sees between general
thermodynamics and the essential doctrines of Aristotelian physics; "we
recognize in these two doctrines", he concludes, "two pictures of the
same ontological order, distinct because they are each taken from a
different point of view, but in no way discordant" (p. 310).
In the final essay, 'The Value of Physical Theory', Duhem adds the
following reflections. Only of propositions which claim to assert empirical facts can we say that they are true or false (AS, pp. 333-34). Of
propositions introduced by a theory we can say that they are neither
true nor false, but only convenient or inconvenient (p. 334). No physicist, however, is entirely satisfied with this state of affairs. Physical
theory confers on us a certain knowledge of the external world which
cannot be reduced to merely empirical knowledge nor to the utility of
the theory. Duhem concludes that it would be unreasonable to work
for the progress of physical theory unless this theory were the increasingly better defined and more precise reflection of a metaphysics, unless
physical theory tends to a natural classification, the nature of which
corresponds by analogy to a certain supremely eminent order (pp.
334-35).
On the assumption that these clarifications and additions are consis-

tent with Aim and Structure, these are the conclusions that can be
drawn. A natural classification is not causally explanatory and does not
appeal to causes as explanations of the phenomena ordered in physical
theory. Duhem consistently regarded physical theories as representations or condensations of laws and phenomena. The evolution of physical theory depends on hypothesis and experimentation, but no mechanical rules suffice to assure progress. The dangers that Duhem perceived
in metaphysics, metaphysical commitments, and the desire for explanation are typically empiricist: dogmatism, premature closure, and the
fact that metaphysical speculations are even more resistant to definitive
correction. Whereas a hypothesis or even a theory will be forever
abandoned, once-abandoned metaphysical conceptions are often rehabilitated. On the other hand, the drive to perfect physical theory, the
fact that hypotheses are rejected, and that over time there is progress
suggested to Duhem that there is a natural classification toward which
physical theory tends, but that the justification for this surmise could
be located only in a kind of metaphysical intuition. In Duhem's opinion,
Copernicus fit in the history of scientific progress, but his belief in the
absolute truth of his hypotheses was not only unnecessary and excessive
but might have been disastrous if not for Osiander's 'Letter'. Kepler's
view was naive, and Galileo's agreement with the pragmatic reading of
hypotheses was disingenuous.
In To Save the Phenomena, Duhem treats Copernicus more extensively and spells out in more detail his understanding of Copernicus's
arguments and beliefs. From Copernicus's dedication to the Pope in
De Revolutionibus, Duhem takes Copernicus to assert not only that
hypotheses should be true, but that Copernicus believed that he had
succeeded in proving demonstratively the truth of his hypotheses, that
is, demonstrative proof as understood by Duhem - only by way of
uniquely true hypotheses. In order to do so, Duhem objects, Copernicus
would have had to show that his hypotheses were not merely sufficient
but even necessary for saving the phenomena. Duhem admits that
Copernicus at best implied this larger claim, but Rheticus was quite
explicit on the point, namely that astronomy should be constructed on
hypotheses that are founded in the very nature of things as the causes
of the observed phenomena (pp. 61-65).
Now if we consider these claims along with Duhem's appreciation
for Osiander's opinions about hypotheses and with the fact that between
1571 and 1582 toleration of hypotheses was ebbing, it is clear that

Duhem's central concern is the freedom of hypotheses from philosophical and theological constraints. In other words, Duhem sees Copernicus's realism as a two-edged sword. If astronomy is subject to theory,
whether theological or physical, then the only hypotheses that will be
permitted are those that are in conformity with the prevailing theory
and the prevailing realism. Duhem's principal objection to realism is
that it requires absolute, apodictic certainty, and once someone believes
himself to be in possession of such certainty, he imposes this view on
other sciences. Hence, Duhem objects to the claim of absolute truth.
Such a claim closes off inquiry and places too many constraints on
imagination. Duhem deplores the philosophical-theological imperialism
of the prevailing realism of the second half of the sixteenth and the
first half of the seventeenth century when, in his view, a mistake was
made that was not corrected until the nineteenth century.
The conclusion of To Save the Phenomena, however, introduces an
important qualification and a significant twist (pp. 113-17). Duhem
takes the single assertion that astronomical hypotheses should be physically true and distinguishes two propositions: (1) that the hypotheses
of astronomy are judgments about the nature of heavenly things and
their real movements, or (2) that the experimental method can serve
as a control on the correctness of astronomical hypotheses and thereby
come to enrich our cosmological knowledge with new truths (p. 116).
Duhem retains the view that Copernicus held the assertion in the first
sense, a view which Duhem judges to be illogical, but manifest and
seductive. Then comes the new twist: Beneath this clear but false and
dangerous sense lay the idea of the unification of the theories of celestial
and terrestrial motions. This true but hidden meaning of the same
principle gave birth tO the scientific efforts of Newton whose dynamics
by means of a single set of mathematical formulae represents the motions of the stars, of the tides, and of falling bodies. The final paragraph
reads:
Despite Kepler and Galileo, we believe today, with Osiander and Bellarmine, that the
hypotheses of physics are mere mathematical contrivances devised for the purpose of
saving the phenomena. But thanks to Kepler and Galileo, we now require that they save
all the phenomena of the inanimate universe together. (p. 117)

Do these references to Kepler's and Galileo's efforts mean that metaphysical knowledge has entered into the content of physical theory? I

think not. Once the motions of the planets, tides, and falling bodies
have been represented successfully by Newton's dynamics, the true
idea of unification emerges from the false and dangerous sense which
Copernicus held. In other words, we have physical laws that are provisional and approximate and hence not true and that approach a natural
classification to which corresponds analogously and only analogously a
metaphysical order or cosmological knowledge to which alone we can
ascribe truth.
If there was any inclination to interpret Duhem's second reading of
the assertion about hypotheses as realist, Duhem's reference to Newton, his characterization of the result as a representation, and his continued insistence on physical hypotheses as mathematical contrivances
suggest that his view here is broadly consistent with the one presented
in Aim and Structure. In sum, the realism that Duhem attributes to
Copernicus and that he consistently rejects can be collected in the
following assertions: (1) Astronomical hypotheses must be true, and
(2) Astronomical hypotheses must be demonstrated to be true, that is,
the hypotheses must be sufficient and necessary to save the phenomena
as the causes of the phenomena. In other words, Duhem clearly attributes to Copernicus the view that hypotheses are not only convenient
and not merely possibly true, but are absolutely true. According to
Duhem, Copernicus believed in the absolute, infallible, and unrevisable
truth of his hypotheses, and that he believed himself to have demonstrated the truth of his hypotheses.

3.

RECENT

INTERPRETATIONS

OF C O P E R N I C U S

Duhem's instrumentalist interpretation of ancient astronomy has been
criticized clearly elsewhere (Lloyd, Mittelstral3). Duhem's account of
Copernicus does not seem to be consistent with recent interpretations
of Copernicus, even between two interpretations which are in some
respects hostile to one another. Edward Rosen rejected the exclusively
fictionalist interpretation of Ptolemaic astronomy, and he commended
Copernicus for remaining silent on the question of the reality of his
own epicycles and deferents (1984, chap. 3 and p. 59; 1961, pp. 93-94).
It might be added, however, that in either case the answer would have
constituted an embarrassment for Copernicus. Noel Swerdlow and Otto

Neugebauer (to whom I refer later briefly as 'Swerdlow' for reasons
stated by Neugebauer himself in his prefatory remarks) interpret Copernicus's truth-claims concerning hypotheses as probable, fallible, and
revisable in details if not in principles (I, pp. 19-21).
In view of Duhem's positivist inclinations, it is at least a little strange
that as he surveyed the development of cosmology, he did not see fit
to examine the empirical evolution of astronomy in more detail. What
few figures Duhem uses in Le SystOme are schematic and far too qualitative to permit any insight into the solution of mathematical-astronomical
problems. This observation provokes a number of doubts, but the
obvious answer is probably the correct one, namely, that Duhem's
history is not the story of the better representations, because these
were only approximate and could serve only as hints of later, more
adequate representations. Swerdlow's recent commentary, of course,
emphasizes the solution of technical problems, and he claims that it
was only with the appearance of Regiomontanus's Epitome in 1496 that
mathematical astronomy in Europe was reborn (I, p. 54).
Experts disagree on this last point, but whatever the difficulties with
Swerdlow's interpretation, he has provided at least one reason for
Copernicus's hesitation about publication that conflicts with Duhem's
account. If Copernicus had concluded that he had indeed demonstrated
the truth of the hypothesis of the moving earth, then why would he
have expressed doubt and fear about its reception? As Swerdlow so
incisively puts it, "Copernicus was no fool". (After that comment we
may imagine Swerdlow muttering, "So take that, Luther".) Copernicus
was convinced that he was right, claims Swerdlow, but he also knew
that his arguments and mathematical proofs were probable at best (I,
p. 20). When Copernicus asserted that the observations of the bounded
elongations of Mercury and Venus and of the retrogradations of all of
the planets followed directly and necessarily from the hypothesis of the
orbit of the earth around the sun, he concluded that all of these
phenomena proceed from the same cause. But the cause to which he
immediately refers is the motion of the earth, not the cause of the
motion of the earth nor the cause of any other motion for that matter
(De Revolutionibus I, 10). Copernicus had no demonstration, because
Copernicus could not demonstrate the cause of the motion of the
earth. Copernicus's argument, then, rests, first, on the fact that directly
observable consequences follow from the hypothesis of an orbiting
earth and, second, on assigning priority to the directness of these

observations over the observation of terrestrial motions, which he justified by reintroducing standard late medieval doubts about the supposed
simplicity of terrestrial motions (De Revolutionibus I, 8).
Why did Copernicus get no further? Kepler has provided the definitive answer in my opinion: Copernicus believed that Ptolemy's models
were correct and that his task was to preserve their effects (Swerdlow;
Hartner). Swerdlow appropriates Kepler's answer and adds that even
though Copernicus probably made far more observations than is usually
thought (another point on which there is disagreement among the
experts), he derived parameters for already invented models that were
slightly modified. It was not Copernicus's intention to construct models
that were actually appropriate to the motions of the planets, because
he believed that Ptolemy's descriptions of phenomena were correct and
that the models that represent them were at least theoretically accurate
(Swerdlow I, pp. 36-38, 77-85). Finally, we need to consider the
import of remarks made by Rheticus in 1551 in which he reports that
Copernicus complained about the accuracy of his own observations
and that he had come to question the accuracy and veracity of many
observations of the ancients. The remark probably refers to the period
of the late 1530s when Copernicus was altering his work to make it
numerically as internally consistent as possible. Such reservations are
not found in De Revolutionibus, but if the report is true, it would mean
that Copernicus had come to realize that his theory was not accurate.
There may well have been other problems that concerned Copernicus,
but we need not resort to speculation to confirm Copernicus's doubts
about the publication of his book or about the demonstrability of the
heliocentric hypothesis. The point is that Copernicus's confidence in
the truth of the hypothesis of an orbiting earth was unaffected, even
though he apparently realized that the perfection of the planetary
theory that his hypothesis required would have to be left to future
astronomers (Swerdlow I, p. 20).
What this means is that the realism that Duhem attributed to Copernicus is only partly correct. Copernicus believed that astronomical hypotheses should be true; he believed that the hypothesis of an orbiting
earth was true; but we have little persuasive evidence that Copernicus
believed that he had demonstrated, in any traditional sense, the truth
of his hypothesis. On the contrary, the evidence rather indicates that
Copernicus knew that his arguments were at best probable and only
more or less persuasive, and for that reason a dialectical-rhetorical

strategy (in the tradition of the Topics) was necessary (compare with
Westman). As for his belief in the absolute truth of his hypothesis, in
Duhem's view the consequences might have been disastrous if not for
Osiander. Consider the reply that had Copernicus not believed that
much, we have good reason to believe that he might not have published
his book at all. As to what he knew, however, Copernicus apparently
held the view that astronomical science could progress by postulating
hypotheses that were more rather than less probable and by making
ever more accurate observations. On the other hand, Duhem is correct,
in my view, that Copernicus saw the ultimate goal as the construction
of physically causal explanations of observed motions. But back to the
first hand again, even if it was only a provisional view in light of his
self-perceived failure to prove the heliocentric theory, Copernicus's
acquiescence to the probable truth of his theory means that Copernicus
himself believed that absolute truth is not a necessary condition of
progress. Alas, even this more modest view was rejected by Duhem.

4.

MINIMAL CONDITIONS FOR A REALIST
INTERPRETATION

OF DUHE M

Duhem consistently reserved the judgment of truth or falsity to empirical assertions, preferring to assess hypotheses as to their convenience
or inconvenience. None of his assertions about progress, natural classification, and a metaphysical order suggests that physical theory aims or
should aim at causal explanation or at causes of observed phenomena.
We do think in terms of causes, and although such an inclination
suggests some profound natural imperative, Duhem was very reluctant
to impart to this activity a role any more concrete than an attraction,
drive, or intuition.
According to some standard distinctions between the truth-claims of
various versions of scientific realism, if we focus on the theoretical
terms of science, we must conclude that Duhem rejected metaphysical
realism, semantic realism, and epistemic realism (Merrill):
Metaphysical Realism: The entities postulated by a (good or acceptable) scientific theory
really exist. Alternatively: the theoretical terms of science denote actually existing entities. Semantic Realism: We must interpret scientific theories realistically - i.e., we must
take the theoretical terms of science to function as denoting terms. Epistemic Realism:
To accept a theory is to believe that it is true, to believe that its terms denote existing

entities. Alternatively: to have good reason for holding a theory is to have good reason
for holding that the entities postulated by the theory really exist. (p. 229)

Had he supported any of these unambiguously, then surely Duhem
would have had no difficulty with assertions about the truth of theories,
the existence of causes and theoretical entities, literal interpretations
of laws and theories, or that evidence for a theory implies belief that
the theory is true or an accurate description of reality.
On the other hand, if we focus on the observation terms of a theory
and on all of the commonsense terms of our experience and on what
Duhem styled "empirical laws - meaning the laws of ordinary experience which common sense formulates without recourse to scientific
theories" (AS, p. 283), then Duhem approved realism in metaphysical,
semantic, and epistemic senses. Alternatively, we might represent
Duhem's view about physical theories as allowing him to accept semantic realism while rejecting metaphysical and epistemic realism (Merrill,
p. 232). But Duhem explicitly rejected the suggestion that laws may be
regarded as true without commitment to existence-claims about the
entities postulated in the theory, because physical laws are always
provisional and approximate (AS, p. 172). Hence, Duhem seems selfconsistent in maintaining a qualified instrumentalism as regards physical
theories and laws while holding a qualified, if regulative, realism as
regards our ordinary experience and deeper metaphysical intuitions.
This is, I believe, one of the sources of the confusion in discussions
of Duhem's positivism and realism. This distinction, that is, between
scientific theories and empirical laws, is the basis of Duhem's view that
physical theory and metaphysical doctrines have no common terms;
between judgments having no common terms but bearing on the same
subjects there can be neither agreement nor disagreement.
Although experimental facts are more refined, more theory-dependent, and more abstract than simple observation statements, physical
theory and metaphysical doctrines are connected in some fashion at the
level of observation, inasmuch as theories correlate abstract ideas with
the really observed facts (AS, p. 147). That there is at least some
connection at the level of observation and yet disparity in the correspondence between abstract symbol and concrete fact (p. 151) seems to
render adequation asymptotic and always incomplete (pp. 154-58).
These and other limitations led Duhem to his extraordinary caution.
In more general terms, Duhem was very sensitive to the problem that

the revisability of physical theories makes truth-claims paradoxical. On
the other hand, the inaccessibility of unobservable entities leaves the
analogy intuited by metaphysical doctrine unable to satisfy proof-conditions. Whatever the dangers, however, the connections are what
Duhem exploits to compensate for the limitations of physical theory
and metaphysics. The logical problem concerning crucial experiments,
for instance, does not mean that hypotheses are never rejected on
rational grounds, but rather that logic and the rules of experimental
method do not possess the resources for justifying conclusively the
abandonment of a hypothesis (Ariew, pp. 322-23). The analogy between physical theory and cosmology can aid the philosopher in his
selection of cosmological doctrine as it seems to correspond to the
natural classification towards which he sees the arrangement of experimental laws advancing.
Earlier I characterized Duhem's account of Copernicus as consistent
with his philosophical views. But inasmuch as the account of Copernicus
is only partly correct and, furthermore, the fact that Duhem's history
of fictional hypotheses is questionable, the correction demands a reformulation of Duhem's judgments. The truth-claims or judgments of
probable truth made by the astronomer or physical theorist are mistaken only if made qua astronomer or physical theorist. But, as Duhem
himself recognized, even the astronomer and physical theorist make
judgments that can be justified only by appeal to metaphysics. Duhem's
history of cosmological doctrines is the history of the correct positivist
philosophy of science and the history of its relation with metaphysics
(compare with Paul). There were two extremes that Duhem rejected:
(1) the complete subordination of science to philosophy and (2) the
absolute and total separation of science from philosophy.
As a consequence, Duhem's history unfolds in the following stages:
(1) In the most ancient speculations known to us, philosophy was linked
inseparably with the science of nature and with the science of number
and figure. (2) During that period and certainly by the time of late
antiquity, the exact sciences became more detailed and difficult, leading
to a distinction, b u t no separation, between science and metaphysics.
(3) During the Renaissance, however, occurred an overreaction to this
distinction that made science subordinate to theological and philosophical realism. (4) Subsequently, much of philosophy developed independently and, emptying itself of the content to which it owed its
solidity, appeared to fly off with the slightest effort. In other words,

the subordination of science to philosophy contributed to the independence of philosophy. Hence, by the nineteenth century the picture
looked like this: Most of philosophy was unsupported and unnourished
by science; science remained for some subordinate to philosophy and
for others completely separate from philosophy; and finally there were
some bold individuals who were taking up the task of once again linking
science with philosophy and mathematics without the subordination of
science to philosophy (AS, pp. 312-13).
For Duhem, then, the history of the continuity that he had traced
and the history of a continuing tradition that he was making constituted
the story of the gradual rectification of two extremes and the story of
the restoration of the delicate balance between representation and
explanation, a balance that Duhem believed was essential to the advance of physical theory, metaphysics, and history itself. The extent of
Duhem's positivism and of his fear of premature closure and dogmatism
is revealed in his rejection of even probable explanation, but Duhem
clearly believed that his view was the balanced one. The problem and
tension recognized and experienced by Duhem remain as the principal
obstacles to the reconciliation of empiricism with scientific realism.

REFERENCES
Ariew, R.: 1984, 'The Duhem Thesis', The British Journal for the Philosophy of Science
35, 313-25.
Copernicus, N.: 1949, De Revolutionibus orbium caelestium libri sex, I, 10, F. and C.
Zeller (eds.), R. Oldenbourg, Munich, II, p. 26, I1. 24-25.
Duhem, P.: 1954, The Aim and Structure o f Physical Theory, Philip Wiener (trans.),
Princeton University, Princeton, New Jersey. This translation is referred to as AS in
this paper.
Duhem, P.: 1954, 'Physics of a Believer', AS, pp. 273-311.
Duhem, P.: 1954, 'The Value of Physical Theory', AS, pp. 312-35.
Duhem, P.: 1909 and 1913, Etudes sur L~onard de Vinci, 2e and 3e s6rie, A. Hermann,
Paris; referred to as Etudes in this paper.
Duhem, P.: 1969, To Save the Phenomena, E. Dolan and C. Maschler (trans.), University
of Chicago Press, Chicago, Illinois.
Duhem, P.: 1913-1959, Le Systdme du monde, 10 vols., A. Hermann, Paris; referred to
as Systdme in this paper.
Hartner, W.: 1973, 'Copernicus, the Man, the Work, and its History', Proceedings of the
American Philosophical Society 117, no. 6, 413-22.
Lloyd, G. E. R.: 1978, 'Saving the Appearances', The Classical Quarterly, n.s. 28,
202-22.

Martin, R. N. D.: 1976, 'The Genesis of a Mediaeval Historian: Pierre Duhem and the
Origins of Statics', Annals of Science 33, 119-29.
Merrill, G. H.: 1980, 'Three Forms of Realism', American Philosophical Quarterly 17,
229-35.
Mittelstral3, J.: 1962, Die Rettung der Phginomena, Walter de Gruyter, Berlin.
Paul, H. W.: 1972, 'Science and the Historian's Craft', Journal of the History of Ideas
33, 497-512.
Rosen, E.: 1984, Copernicus and the Scientific Revolution, Krieger, Malabar, Florida.
Rosen, E.: 1961, 'Renaissance Science as Seen by Burckhardt and his Successors', in
Tensley Helton (ed.), The Renaissance, University of Wisconsin, Madison, pp. 77-103.
Swerdlow, N. and O. Neugebauer: 1984, Mathematical Astronomy in Copernicus's De
Revolutionibus, 2 vols., Springer-Verlag, New York.
Westman, R.: 1987, 'La Pr6face de Copernic au pape: esth6tique humaniste et rfiforme
de l'6glise', History and Technology 4, 365-84.
Program of Liberal Studies
University of Notre Dame
Notre Dame, Indiana 46556
U.S.A.

COPERNICUS,

THE

ORBS,

AND

THE

EQUANT

ABSTRACT: I argue that Copernicus accepted the reality of celestial spheres on the
grounds that the equant problem is unintelligible except as a problem about real spheres.
The same considerations point to a number of generally unnoticed liabilities of Copernican astronomy, especially gaps between the spheres, and the failure of some spheres
to obey the principle that their natural motion is to rotate. These difficulties may be
additional reasons for Copernicus's reluctance to publish, and also stand in the way of
strict realism as applied to De Revolutionibus, although a realistic astronomy may be
envisioned as a goal for Copernicus's research program.

In the previous p a p e r Andr6 G o d d u presents D u h e m ' s views on the
progress of science, connecting his views on Copernicus with some
recent scholarship and examining the varieties of realism this renders
possible. I want to suggest that this recent work on Copernicus misses
certain important considerations by unduly emphasizing mathematical
astronomy over cosmology and physics. The same issues have consequences for realism, and display valuable features of D u h e m ' s image
of science.
W h e n Copernicus explains his motives, in the preface to D e R e v o l u tionibus addressed to Pope P a u l I I I , he contrasts his views with two
other schools of thought but he criticizes these alternatives on different
grounds. The homocentric models revived by Amico and Fracastoro
fail to show numerical a g r e e m e n t with positional data. On the other
hand, although the eccentric models of the Ptolemaic tradition do show
numerical agreement, they " c o n t r a v e n e the first principle of regularity
of m o t i o n " (Copernicus 1976, p. 25). As this objection is not raised in
the case of the homocentric models, we may conclude that they do not
contravene this principle, which concerns motion, the basic subject
matter of physics as defined by Aristotle, not just astronomy or the
motions found in astronomy.
The objection to the Ptolemaic tradition concerns the nature of the
motion required by the equant. T h e r e seems to be no difficulty with
the equant, regarded as a constraint on the motion of a point in a twodimensional mathematical construction used for calculating planetary
Synthese 83: 317-323, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

longitudes. If there is a difficulty it is because of the connection of the
motions with physics, and the "first principle" invoked by Copernicus
is an attempt to express the difficulty. Modern commentators have not
quite got hold of the problem. Swerdlow for example describes the
equant as an offense against "simple mechanical sense" (1972, p. 36).
In the work cited by Goddu, Swerdlow and Neugebauer describe the
objection to the equant as being on "physical or mechanical rather than
on merely philosophical grounds" (1984, p. 290). These remarks must
be understood ahistorically. There was no canonical mechanics for early
modern scientists to draw upon for such judgments. To understand the
equant problem, then, we need to examine the physics of motion
employed by Copernicus.
Copernicus evidently expected his audience to be familiar with Aristotle's account of motion. 1 The aspects of the account relevant for
understanding Copernicus's objections to Ptolemy are: all bodies move,
either because they are subject to their own internal source of motion,
or because they are moved by something else, which in its turn moves
on account of an internal source. Further, a body may only produce
motion in another body when the two are in contact. Copernicus is
attempting to give an account of the motion of the planets, which are
not themselves endowed with a source of motion. 2 Therefore planets
are moved by something else.
In De Revolutionibus, Book I, Chapter Four, Copernicus discusses
stations and retrogressions as apparent irregularities in the paths of the
planets. Planets also appear sometimes nearer and sometimes farther
from the earth. "Nevertheless", he goes on, "it mUst be admitted that
their motions are circular, or compounded of a number of circIes,
because they pass through irregularities of this kind in accordance with
a definite law and with fixed returns to their original positions, which
would not happen if they were not circular" (1976, p. 39). But planets
do not move themselves; they are moved by something else. What
other object is capable of moving a planet in indefinitely repeating
circles? Chapter Four begins, "The next pointis that the motion of the
heavenly bodies is circular. For the m o v e m e n t o f a sphere is a revolution
in a circle, expressing its shape by the very action, in the simplest of
figures, where neither beginning nor end is to be found, nor can the
one be distinguished from the other, as it moves always in the same
place" (1976, p. 38, emphasis added). Hence we are to understand that
the planets move in circles because they are moved by spheres. Their

motion is uniform for the same reason: "Circular motion always goes
round evenly, for its cause is unfailing" (1976, p. 45), this cause being
for Copernicus the natural tendency of spheres. 3
Tounderstand Copernicus's position we need to concentrate not on
the circles generated by the spheres, or their mathematical properties,
but on the nonmathematical concepts of motion and the perfection of
the heavens. If we are to locate these concerns according to the dichotomy of mathematical astronomy versus cosmology, then these are
clearly cosmological concerns. We are obliged to conclude that Copernicus's main announced criticism of Ptolemy, the inadmissibility of the
equant, is a cosmological objection, and in this respect it is identical to
the criticisms of the homocentric theorists. The equant is only a problem
because planets have to be moved by uniformly rotating spheres.
Spheres may rotate uniformly only about axes which are diameters, but
the motion required by the equant could be created only by a sphere
rotating uniformly about an axis that is not a diameter, a condition
impossible to satisfy.
It is a matter of current controversy whether Copernicus believed in
the reality of the celestial spheres familiar in the Ptolemaic tradition. 4
There is admittedly no unequivocal statement in De Revolutionibus, a
point usually counted in favor of those who deny that Copernicus
accepted spheres, although the passages I have already quoted (among
others) are difficult to interpret in any other way. But the most telling
point is that the equant problem is not intelligible except as a problem
about real spheres. General historical evidence tends to the same conclusion. Whatever his personal views, Copernicus must have expected
his audience to accept the reality of the spheres. Throughout his lifetime
the only major astronomical traditions (the Ptolemaic tradition as developed by Puerbach and Regiomontanus, and the less developed alternative tradition of homocentrics) assumed the existence of celestial
spheres, s Both the text and the context of Copernicus's work suggest
that he accepted the reality of the celestial spheres, and this commitment suggests additional reasons for his reluctance to publish, in addition to those adduced by Goddu.
If Copernicus's system is interpreted by means of the physical construction familiar in the Ptolemaic tradition, a major problem appears
- the spherical shells are no longer in contact. 6 There are huge gaps
between them. There is an even larger gap between the spherical shell
of Saturn and the fixed stars. And there is a discontinuity at the center

of the system. In the Ptolemaic system as developed in the Planetary
Hypotheses, or the Theorica tradition, or even in the rival homocentric
models of Fracastoro and his contemporaries, the innermost sphere of
the heavens is continuous with the uppermost sphere of the terrestrial
elements. The terrestrial elements form a further series of nesting
spheres which is continuous all the way to the center of the system.
There is no empty space. Once the center is moved to the Sun, 7 the
first of the spheres of the heavens, counting outward from the center,
is the sphere of Mercury. The size of the Sun is known to be much
smaller than Mercury's sphere. What fills the region between?
Copernicus's cosmological model has gaps. These difficulties are
independent of the success of the model in calculating planetary positions, and to that extent are conceptual rather than empirical. They
are no different in kind from those that motivated Copernicus to seek
an alternative to Ptolemy. And in fact there are other similar difficulties. s For Copernicus, the natural motion of a sphere is to rotate, but
the Moon is a sphere, and it does not rotate. 9 The fixed stars are also
confined to a sphere, and that sphere does not rotate. The same problem arises for the Sun, although whether or not it rotates may be an
open question. Adding all these potential difficulties to the problem of
the gaps between the spheres provides considerable additional grounds
for Copernicus's reluctance to publish. ~0
Copernicus's lack of a detailed (as we would say) physical model for
heavenly motion makes his realism hard to appraise. Perhaps we need
to see realism not as a global requirement which must be satisfied by
any theory, but rather as a goal to be reached if a series of related
theories succeeds. The hope is that more and more of these difficulties
will be resolved by later work, as Galileo resolved the problem of
brightness variation for Venus by demonstrating the phases.l~ Sometimes, of course, the resolution takes the theory in a new direction, as
in the case of Kepler's solution to the problem of the gaps between the
spheres. We might say that Kepler's work made a realist interpretation
of Copernicus's theory untenable.
Contemporary philosophers and historians are too likely to treat
science as an activity in which most of the time things go right, as the
paradigm of rationality or an activity so successful that its success needs
explaining. Much contemporary concern with realism in science is, I
think, a consequence of tfiis underlying conception, as is the persistent
tendency to ignore or underemphasize the anomalies which are as much

for the current theory. It would be as great a mistake to describe
science, as a historical phenomenon, without anomalies, as it would be
to describe monarchies, as an historical phenomenon, without succession problems, or democracy, as an institution, without faction fights.
The assumption of success is fatal as an approach to understanding the
history of science.
D u h e m saw that the history of science is largely the history of error,
of failed theories and abandoned positions. The history of science is
like the history of life on earth - extinct theories outnumber the survivors. D u h e m accommodated scientific failure by relegating realism to
the realm of metaphysics. As Goddu shows, D u h e m allowed realism
only when science and metaphysics coincide at a theoretical endpoint.
Interestingly this coincidence is to be recognized by 'bon sens' a nonlogical faculty of judgment. It is salutary to be reminded by D u h e m that
there are sources of knowledge that resist logical analysis. I would even
locate some of them inside science itself (e.g., tacit knowledge). If we
are unable to endorse Duhem's solution to the problem of scientific
failure, the response need not be a global realism, but a historically
relativized realism - the realism of medium term theoretical success,
which may be withdrawn in the long term. But even in locating the
problem, Duhem's history and philosophy of science is more sophisticated than much of what has passed for historical and philosophical
analysis of science during the twentieth century.

NOTES
He refers, for example, to Aristotle's threefold division of simple motions as if he
expects his audience to already understand the doctrine (Copernicus 1976, p. 45).
2 Although ancient Stoics took the contrary view, and there was new interest in their
scientific ideas during the sixteenth century (Barker 1985; Barker and Goldstein 1984,
1988). The possibility that each sphere was endowed with an intelligence capable of selfmovement was also debated in the Middle Ages (Weisheiphl 1985, chap. 7).
3 For a very different reading of these passages, see Jardine (1982).
4 Swerdlow (1973, 1976) had very much the best of an exchange with Rosen (e.g., 1975),
in which he affirmed the reality of Copernicus' spheres against Rosen's denials. Other
important points appear in Jardine (1982) and Westman (1980), the latter taking a middle
position. I propose modifying Westman's position in the direction of Swerdlow.
5 For Puerbach see Aiton (1987); on the homocentric theorists see Swerdlow (1972).

edge of the model see Van Helden (1985). On Copernicus's calculations of planetary
distancescompare Van Helden (1985) with Neugebauer (1968).
7 Strictly speaking the center is moved to the mean Sun.
s Other difficulties are more plainly empirical. Copernieus's theory accounts for the
observed pattern of variation in brightness for Mars, but also requires a similar variation
in brightness for Venus - and this is not apparent to a naked eye observer. This problem
was eliminated by Galileo's "discovery' of the phases of Venus (Ariew 1987). Similarly,
although Copernicus avoids the dramatic variation in the apparent size of the Moon
predicted by Ptolemy's theory, his own theory employs not one but two epicyclic motions
and will not keep the same face of the Moon always turned towards the earth.
9 This seems to have been the majority position prior to Copernicus. A minority of
cosmological commentators recognized that a rotation o f the moon might compensate
for the kind of epicyclic motion mentioned in the previous note (Gabbey (forthcoming);
Grant 1987).
m Although these defects of the Copernican theory seem compelling to the modern
reader, considerably more argument would be needed to establish that Copernicus himself
would have seen either these difficulties or the empirical problems mentioned in note 8
as major defects. In particular, it would be important to consider whether Copernicus
saw his astronomy as a system in the modern sense. For more on this problem see Barker
and Goldstein (1988).
11 See note 8 above.

REFERENCES
Aiton, E. J.: 1987, 'Peurbach's Theorica novae planetarum', Osiris 3, 5-44.
Ariew, R.: 1987, 'The Phases of Venus Before 1610', Studies in History and Philosophy
of Science 18, 81-92.
Barker, P.: 1985, "Jean Pena and Stoic Physics in the Sixteenth Century', in R. H. Epp
(ed.), Recovering the Stoics, Southern Journal of Philosophy, 23 Supplement, 93-107.
Barker, P. and B. R. Goldstein: 1984, "Is Seventeenth Century Physics Indebted to the
Stoics?', Centaurus 27, 148-64.
Barker, P. and B. R. Goldstein: 1988, kThe Role of Comets in the Copernican Revolution', Studies in History and Philosophy of Science 19, 299-319.
Copernicus, N.: 1976, On The Revolutions of the Heavenly Spheres, A. M. Duncan
(trans.), Barnes & Noble, New York.
Gabbey, A. : forthcoming, 'Newton and the Libration of the Rotating Moon' in P. Barker
and R. Ariew (eds.), Revolution and Continuity, Catholic University of America Press,
Washington.
Goldstein, B. R.: 1967, 'The Arabic Version of Ptolemy's Planetary Hypotheses', Transactions of the American Philosophical Society 57, part 4, 3-55.
Grant, E.: 1987, "Eccentrics and Epicycles in Medieval Cosmology', in E. Grant and J.
E. Murdoch (eds.), Mathematics and Its Applications in Science and Natural Philosophy
in the Middle Ages, Cambridge University Press, Cambridge, England, pp. 189-214.
Jardine, N.: 1982, "The Significance of the Copernican Orbs', Journal for the History of
Astronomy 13, 168-94.

Neugebauer, O.: 1968, ~On the Planetary Theory of Copernicus', Vistas in Astronomy
10, 89-103.
Rosen, E.: 1975, 'Copernicus' Spheres and Epicycles', Archive Internationale d'Histoire
des Sciences 25, 82-92.
Swerdlow, N.: 1972, 'Aristotelian Planetary Theory in the Renaissance: Giovanni Battista
Amico's Homocentric Spheres', Journal for the History of Astronomy 3, 36-48.
Swerdlow, N.: 1973, 'The Derivation and First Draft of Copernicus's Planetary Theory:
A Translation of the Commentariolus with Commentary', Proceedings of the American
Philosophical Society 117, 423-512.
Swerdlow, N.: 1976, ~Pseudodoxia Copernicana', Archives Internationales d'Histoire des
Sciences 26, 108-58.
Swerdlow, N. and O. Neugebauer: 1984, Mathematical Astronomy in Copernicus's De
Revolutionibus, Springer, New York.
Van Helden, A.: 1985, Measuring the Universe, University of Chicago Press, Chicago.
Weisheiphl, J. A.: i985, Nature and Motion in the Middle Ages, Catholic University
Press of America, Washington.
Westman, R. S.: 1980, 'The Astronomer's Role in the Sixteenth Century: A Preliminary
Study', History of Science 18, 105-147.
Center for the Study of Science in Society
Virginia Polytechnic Institute and State University
Blacksburg, VA 24061-0247
U.S.A.

HOLISM

A CENTURY

AGO: THE ELABORATION

OF DUHEM'S

THESIS

ABSTRACT. Duhem first expounds the holistic thesis, according to which an experimental test always involves several hypotheses, in articles dating from the 1890s. Poincar6's analysis of a recent experiment in optics provides the incentive, but Duhem
generalizes this analysis and develops a highly original methodological position. He is
led to reject inductivism. I will endeavor to show the crucial role history of science comes
to play in the development of Duhem's holism.

The claim that our knowledge confronts the tribunal of experience as
a whole, which is known as the holistic thesis, has spurred much debate
and, in consequence, has received a good deal of attention. Yet it is
not at all obvious that the historical origin of this idea has been
thoroughly studied. It is generally acknowledged that Pierre Duhem
was the first to expound the thesis in 1906 in the first edition of The
Aim and Structure of Physical Theory. But how he arrived at the idea
and why he adopted it are questions which are most often neglected.
Tracing the holistic thesis back within Duhem's work, one discovers
that it originated in the 1890s, that is, almost a century ago. The
initial context shows that the philosophical claim is intimately related to
ongoing scientific discussions; it also reveals more clearly Duhem's
motives. An analysis of the elaboration of holism and its impact on
Duhem's thought yields some noteworthy results. First, a remarkable
evolution is brought to light. D u h e m came to reject inductivism; this
shift occurs after he began to philosophize. Secondly, Duhemian holism
does not reduce to a single narrowly interpreted thesis: generalizing
the thesis, the French philosopher endeavors to formulate a holistic
methodology. Thirdly, new significance is given to some inductivist
remarks, which commentators have noted in The Aim and Structure:
Duhem maintains several ideas developed within his earlier inductivist
approach; in this respect, his philosophy is not free from inconsistencies.
Finally, a clue is provided for Duhem's conversion to history of science,
for the second half of the French physicist's career is devoted almost
exclusively to history. External factors and even factors lying within
Synthese 83: 325-335, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

the province of history alone do not explain why, from 1903 on, Duhem
undertook to rewrite the history of science, especially the pre-Copernican period, an ambitious program, which culminated in his monumental Syst~me du Monde.
.
Some twelve years before synthesizing in The Aim and Structure his
reflections on the methodology of physics, Duhem announced in
'Quelques r6flexions au sujet de la physique exp6rimentale' the basic
idea of holism: "an experiment in physics can never condemn an isolated hypothesis but only a whole theoretical group" (Duhem 1894a,
p. 187).1 In 1894 this claim was truly novel. Not only was it absent in
the earlier articles, but it even appears to conflict with the initial conception set forth there. In his first philosophical article, 'Quelques r6flexions au sujet des th6ories physiques', Duhem recommended an
inductive method for selecting hypotheses, and he did not point out the
shortcomings of such a method (Duhem 1892, pp. 146f, for example). In
support of this contention, let us simply note that in an autobiographical
passage of 'Physics of a Believer' Duhem acknowedges such an evolution of thought, which implies the rejection of an earlier inductivism
(Duhem 1905, pp. 275-78).
A contemporary experiment in physics provided the incentive for
philosophical reflections: Otto Wiener's experiment on the direction of
vibration of polarized light, whose results were published in 1890. This
experiment created a stir at the time, not because it revealed a yet
unknown property of light, but because it seemed to make it possible
to decide between two competing theories. For a good number of
years physicists had been hesitating between Fresnel's theory and F. E.
Neumann's and MacCullagh's theory. The customary interpretation of
these theories yielded two diametrically opposed predictions: if light,
following the classical view, is taken to be a vibration in an ether
medium, according to the first theory, the vibration is normal to the
plane of polarization; according to the second theory, the vibration is
parallel to the same plane. By verifying the first prediction, Wiener's
experiment infirmed Neumann's theory and confirmed Fresnel's theory. Some scientists did not fail to take the experiment as an example
of a crucial experiment. Thus, for example, Cornu in his appraisal of
the experiment:

This beautiful experiment deserves to mark the beginning of a new era in the history of
optics: it decisively overthrows theories which place the vibration in the plane polarization
of light, like those of MacCullagh and Neumann; on the other hand, it confirms in a
spectacular manner the ideas of Fresnel and his pupils . . . . This experiment reveals by
a palpable fact the dynamic character of the vibration of light, which had begun to
be considered, by ~ome mathematicians, as an abstract conception, a symbolic entity
indifferently reducible to many different kinematic equivalents. In the light of this experiment in which the experimentator directs as he wishes the mechanical action of light
vibration like sound vibration, one can no longer assert that optical vibration is a mere
geometrical abstraction. (Cornu 1891a, p. 187; italics mine)

An exceptional situation warrants a strong conclusion: because two
competing theories which lead to contradictory predictions are involved, Wiener's experiment, indeed, enforces the truth, the reality, of
the surviving theory. Cornu seizes the opportunity to attack abstract
nonrealist conceptions, like those already presented by Poincar6 and
Duhem in several branches of physics. His interpretation of Wiener's
experiment constitutes a challenge for such conceptions.
Duhem rebuts such an interpretation in 'Les th6ories de l'optique',
citing the intricacy of experimenting: "What Mr. O. Wiener's experiment condemns is not the particular hypothesis that the vibration is
parallel to the plane of polarization; what it condemns is the group of
hypotheses which constitute MacCullagh's and Neumann's theory; his
experiment teaches us to abandon some part of it, but it does not tell
us what to change; we can for example give up placing the motion of
the ether molecule in the plane of polarization of the ray; but we can
also let the ether molecule vibrate in the plane of polarization as long
as we change some other hypothesis of the theory, for example the
hypothesis which explains the mechanical sense ascribed to light intensity" (Duhem 1894b, p.l12). One need only adopt another interpretation of one of the fundamental concepts of optics in order to provide
an entirely different situation. Nothing prevents such a move, as the
concepts involved admit of several interpretations.
Here Duhem is following Poincar6, this being one instance of the
latter's influence. The famous mathematician gave an account of
Wiener's experiment in 1891 in front of the Paris Academy of Sciences;
he held that this experiment in itself is not crucial (Poincar6 1891a). 2
Poincar6 took up again this view the following year, in the second
volume of his Thdorie mathdmatique de la lumi~re, in a passage which
Duhem did not fail to call attention to in his review of the book (Duhem
1893, p. 257). For both authors the philosophical question is in the

foreground. Neither Poincar6 nor Duhem are interested in rescuing
Neumann's theory; in their scientific research, they both favor Fresnel's
theory (Poincar6 1891a, p. 325; Duhem 1896).
Where does Duhem's originality lie? Should Poincar6 be given the
credit for formulating the holistic thesis? If Poincar6 may have been
the first to advance a critical interpretation of Wiener's experiment,
from his analysis he never inferred a general conclusion concerning the
nature of experimental testing. It is true that he writes in 1902: "In
o p t i c s . . . Fresnel believed the vibration to be perpendicular to the
plane of polarization; Neumann considered it to be parallel to this
plane. An 'experimentum crucis' which would make it possible to decide
between these two theories was sought for some time, but it was not
possible to find one" (Poincar6 1968, p. 224; this remark appeared in
his 1890, vol. 2, p. xiv). But this passage of La science et l'hypothOse,
is very ambiguous; in fact, Poincar6 is reproducing here a text published
in 1890, most likely before he learned of Wiener's experiment. Why
does Poincar6 not recall here his interpretation of Wiener's experiment?
He not only passes over this interpretation in silence, but he even
continues to speak of decisive experiments as well as crucial experiments (for example, in Poincar6 1968; pp. 158, 165). Poincar6 neglects
Duhem's early formulation of holism, which had been noticed right
away by Milhaud, another member of the loosely structured critique of
science movement, which Le Roy characterizes as a "new positivism".
Unlike Poincar6, Duhem generalizes the critical interpretation of
Wiener's experiment into a philosophical thesis: "What we have here
is not a particularity of the experiment carried out by Mr. O. Wiener
but a general characteristic of experimental method; it is never possible
to subject an isolated hypothesis to the test of experiment, but only the
group of hypotheses" (Duhem 1894, p. 112). Duhem perceives the
importance of this result, and he pursues his analysis in his next article,
'R6flexions au sujet de la physique exp6rimentale', where he chooses
a new example to illustrate his claim, Foucault's experiment. This
experiment shows that light travels faster in air than in water, thereby
infirming a prediction of the corpuscular theory of light, while confirming a prediction of the wave theory. Duhem demonstrates that this
experiment in itself is not, any more than Wiener's, a crucial experiment, that is, an experiment that imposes decisively one theory. Now,
this experiment was considered as a classic example of crucial experiment. 3 By giving another view of Foucault's experiment, Duhem challenges the methodology of crucial experiment, one of the dogmas of

traditional philosophy of science. What was merely a critical interpretation of a recent experiment becomes a full-fledged thesis. This thesis
implies an entirely new conception of experimental method.

.
Retrospectively, 'R6flexions au sujet de la physique exp6rimentale'
appears to be a complement to the first article, but this should not
conceal the novelty of the text. To subject experimental method to an
exacting analysis after Claude Bernard, whose aim was to introduce
experimental reasoning in physiology, must have seemed like a superfluous endeavor. The opening remark of the article is not a rhetorical
device: "What is an experiment in physics? This question will undoubtedly astonish more than one r e a d e r . . . ; is there any need to raise
it, and is not the answer self-evident? ''4 It is not the importance of
experimental method which Duhem questions, but the soundness of
the classical conception. He is conscious of contradicting traditional
methodology: "By declaring that the interpretation of facts by means
of theories is an integral part of a physical experiment . . . . we will
perhaps scandalize more than one mind concerned with scientific rigor;
more than one will bring up against us the rules framed hundreds of
times by philosophers and observers from Bacon to Claude Bernard. ''5
Duhem explicitly challenges Bacon's idea of crucial experiment; he
rejects Bernard's account when applied to a highly developed theoretical science like physics. In The Aim and Structure he will come to
condemn the inductive or Newtonian method.
Up to this point Duhem has shown that, because multiple theoretical
choices are involved, there are no experiments which are truly decisive
in themselves. But so-called crucial experiments were considered exceptional. Duhem goes a step further and gives us a general analysis of
physical experiments; he emphasizes here the importance of theoretical
interpretation: "An experiment in physics is the precise observation of
phenomena accompanied by an interpretation of these phenomena;
this interpretation substitutes for the concrete data really gathered by
observation abstract and symbolic representations which correspond to
them by virtue of the theories admitted by the observer" (Duhem
1894a, p. 182 and again in his 1914, p. 221f; 1954, p. 147; Duhem's
italics). Theoretical interpretation separates and distinguishes the practical fact, the brute evidence, and the theoretical fact, the evidence

incorporated into the theory. One example Duhem chooses for illustrating these remarks is Regnault's series of experiments on the compressibility of gases, which had become a paragon of experimental research.
This is an ordinary experiment in the sense that the experimental
procedure is straightforward;6 Regnault's results are not controversial,
that is, within a certain degree of approximation and pending some
minor corrections, they are definitive.7 Let us take the simplest measurement involved, the volume occupied by the gas: "In a sighting
device Regnault saw the image of a certain surface of mercury become
level with a certain line; is that what he recorded in the report of his
experiments? No, he recorded that the gas occupied a volume having
such and such a value . . . . " The operation involves concepts of several
different areas of physics, namely, general mechanics and celestial mechanics, s The volume occupied by a gas is not only an abstract idea but
also a theoretical idea. An experiment always involves a theory as a
whole and even brings in several different chapters of physics. Duhem's
interpretation of experimental method is thus intimately connected with
the holistic thesis.
It is not necessary to dwell on this point, which has received much
attention. Let us simply register that Duhem's conception of experimental testing is acquired, in the main, as early as 1894. In fact, the
article is almost identical with the text found in The Aim and Structure,
chapters four, five, and six of part two. What is striking, however, is
the omission in the article of the two paragraphs concerning Newtonian
method. Let us follow up this clue. From his analysis of experiment
Duhem draws some conclusions; for example, he rejects a particular
method of construction or presentation of a theory, according to which
"one would like the professor to arrange all the hypotheses of physics
in a certain order, to take the first one, enounce it, expound its experimental verifications, and then when the latter has been recognized as
sufficient, declare the hypothesis accepted; he would begin this operation again on the second hypothesis, on the third, and so on until all
of physics was constituted . . . . This idea is a false idea" (Duhem 1894a,
p. 196). Such a method clearly contradicts the holistic thesis: it is not
possible to test an isolated hypothesis. The Aim and Structure takes up
almost word for word this sentence, inserting a highly revealing clause:
"One would like [the professor] to formulate the first hypothesis by
inductive generalization of a purely experimental law" (Duhem 1914,
p. 304; 1954, p. 200; italics mine). What is being referred to is the

inductive method, which The Aim and Structure condemns unambiguously; "The teaching of physics by the purely inductive method such as
Newton defined it is a chimera" (Duhem 1914, p. 309; 1954, p. 203;
italics mine). What is true of teaching is all the more so of theory
construction. Apparently, in 1894 Duhem did not attempt to deduce
all the consequences of his analysis of experimental method, since the
same analysis will lead him, twelve years later, to declare the inductive
method impracticable. It is true that only two years before Duhem
recommended this method against the excesses of mechanism.
Duhem's criticism of the inductive method raises a question: how to
choose the principles on which to build a theory? In the first article
this choice appeared in fact to be determined, guided, in some way, by
the inductive method. By what to replace this method? The pedagogical
hints given in 'R6flexions au sujet de la physique exp6rimentale' are
obviously an insufficient answer. In The Aim and Structure the difficulty
is no longer avoided; the author sends the reader on to the following
chapter on the selection of hypotheses, where recourse is made to
history of science. History of science thus appears in Duhem's methodological treatise; it has its place in the construction as well as in the
teaching of physical theories: "The legitimate, sure, and fruitful method
of preparing a student to receive a physical hypothesis is the historical
method" (Duhem 1914, p. 408f; 1954, p. 268). In 1894 Duhem does
not yet perceive the role that history of science should play; this is
undoubtedly the deep reason why he hesitated to criticize explicitly the
inductive method.
.
How does history of science come to provide a solution? It is by
no means accidental that after rejecting the inductivist schema of the
transition from Kepler's laws to Newton's principle in part two chapter
six of The Aim and Structure, Duhem gives a long account of the
historical genesis of the principle in the next chapter. This account is
clearly intended as an alternative to the inductivist reconstruction. The
author places the principle of gravitation in the history of scientific
thought. Duhem integrates some material from his erudite Origines de
la statique, which he is working on simultaneously. Duhem no longer
leaves out the Middle Ages; he has an inkling of his famous thesis:
many major ideas of modern science have their origin in the thirteenth

and fourteenth centuries. Already Duhem criticizes the classic idea of
scientific revolution, a drastic and sudden change: "In the course of
this long and laborious birth, we can follow the slow and gradual
transformations through which the theoretical system evolved; but at
no time can we see a sudden and arbitrary creation of new hypotheses"
(Duhem 1914, p. 384; 1954, p. 252). The slowness, the gradualness of
scientific evolution is a sign of its continuity. Duhem explicitly links
continuism with his idea of natural classification: "By virtue of a continuous tradition, each theory passes on to the one that follows it a
share of the natural classification it was able to construct" (Duhem
1914, p. 44; 1954, p. 33; italics mine). History of science then provides
the missing link for Duhem's rejection of inductivist methodology.
Let us test this idea by attempting a final comparison between one
of the early articles and The Aim and Structure. It is not a coincidence
if the text in which the holistic thesis first occurs is Duhem's first article
pertaining to history of science. 'Les throries de l'optique' offers a
rapid overview of optical theories since the seventeenth century. During
the second half of the seventeenth century, Huygens formulated a wave
theory of light. This theory inspired by Cartesian physics, in turn, was
rejected by Newton and his successors in favor of a corpuscular theory
based on an attractionist model. Toward the middle of the nineteenth
century, in the light of new discoveries, scientists took up again the
wave hypothesis. This evolution is quite astonishing: the rehabilitation
of a hypothesis which had been rejected and was believed to have been
refuted.
Duhem uses the history of optics to illustrate a general thesis concerning the nature of physical theories. Theories are fragile and temporary
constructions. Historical distance shows that many of the pretensions
of traditional mechanism concerning the value of its hypotheses are
unfounded. Duhem foretells the imminent decline of mechanism: "Mechanical hypotheses have disappeared, broken up by experimental contradictions or carried away by the torrent which has, for three centuries,
turned over and over metaphysical systems" (Duhem 1894b, p. 124).
These critical remarks serve to justify abandoning realistic and mechanistic conceptions. Physical theory is to be conceived as a convenient
representation of laws and not an explanation of reality. History serves
to justify this view.
Skepticism is not however the final lesson of Duhem's history. Behind
the succession of theories and hypotheses, he perceives an evolution,

a direction of history. Old theories disappear, while contributing to the
evolution of science. First of all, the experimental laws which were
discovered with the help of these theories remain. But if theories merely
serve to suggest experimental laws, their usefulness would seem slight;
one might even propose to do away with them altogether. Yet theories
appear to play an essential role. This is how Duhem sees the legacy of
hypotheses which have been discarded: "Huygens' hydrodynamic ideas
are outmoded; but they have given to mathematical optics the notion
of wave surface, the form of this surface for isotropic and uniaxial
media. Newton's light particles have disappeared, with their access of
easy reflection and easy transmission; but optics has continued to represent light phenomena by means of a magnitude which varies periodically
in time and whose period, very short, characterizes color. Young assimilated the ether of the ray of light with a column of vibrating air; this
assimilation is no longer accepted, but it led to ascribe a direction to
the magnitude represented by light phenomena and to compose these
magnitudes with one another like forces or speeds. Fresnel's ether and
its motions seem about to disappear; but through them it has become
known in optics that the magnitude representing light phenomena is
governed by the same equations as the transversal motions of elastic
solids" (Duhem 1894b, p. 125). In this series of examples some of the
fundamental concepts of modern optics are to be found. The contribution of a theory is, in the final analysis, quite different from what its
creator foresaw. The elements of a theory are altered and incorporated
in a new context. The scientist is surprised by the strange origin, and
the historian by the unexpected evolution. Even when they prove to
be false, theories can add something to the language of science. This
language is refined and enriched, progressively becoming a more and
more efficient instrument.
In The Aim and Structure Duhem often calls on the history of optics
in order to illustrate his argumentation; he draws heavily on 'Les thdories de l'optique'. But the ideas of the article undergo an interesting
modification. Duhem relates in the article Arago's experiment so as to
explain the acceptance of Fresnel's theory. The same example in The
Aim and Structure shows that theory can anticipate experiment and
serves to introduce the idea of natural classification, which is absent in
the article: "[Physical theory] assumes, while being completed, the
characteristics of a natural classification. The groups it establishes permit hints as to the real affinities of things. This characteristic of natural

classification is marked, above all, by the fruitfulness of the theory
which anticipates experimental laws not yet observed, and promotes
their discovery" (Duhem 1914, p. 40; 1954, p. 30; italics mine). Duhem
thus expands his idea of a progressive development of the languages of
science and expounds a continuist philosophy, which has both methodological and historical implications.
An analysis of 'R6flexions au sujet de la physique exp6rimentale' and
'Les thdories de l'optique' shows that the first formulation of the holistic
thesis is unaccompanied by an explicit criticism of the inductive method;
it also indicates the bearing history of science has on the author's
evolution of thought. What I suggest is that methodology and history
of science are intimately connected in Duhem's philosophy and that
this connection deserves careful attention. Going back a century, returning to the initial context, also helps us to understand better the
meaning of holism. Holism is not an abstruse idea framed only by
philosophers; it originates in a precise scientific setting and becomes a
general philosophical thesis, in an attempt to break with traditional
methodology. Holism thus lies at the origin of contemporary philosophy
of science.
NOTES
1 The same remark is taken up again in his (1914), p. 183, translated by P. Wiener as
Duhem (1954), p. 278; I give throughout the pagination of the original with that of the
translation. In places I modify the English translation.
2 A. Cornu replied in his (1891b); Poincar& nevertheless, maintained his position in his
(1891b).
3 As Duhem says, in his (1894a), "An experiment regarded as one of the most decisive
ones in optics", p. 190. This remark is taken up in his (1914), p. 282; (1954), p. 186.
4 Duhem (1894a), p. 179. The same remark occurs in his (1914), p. 218; (1954), p. 144.
Duhem foresees the reader's astonishment again in another passage of his (1914), p. 231;
(1954), p. 153.
5 Duhem (1894a), p. 182. This passage does not occur in The A i m and Structure, but
Bacon and Bernard are mentioned in Part II, chap. 6, section 1.
6 Duhem (1894a): "What Regnault did is what every experimental physicist necessarily
does", p. 182. "Let us take any experiment whatever for example, Regnautt's experiment", p. 185. Only the first passage appears in his (1914), p. 221f; (1954), p. 147.
7 Duhem (1894a): "In his experiment on the compressibility of gases Regnault let exist
a cause of systematic error which he did not perceive and which has since been pointed
out: he neglected the action of weight on the gas under pressure", p. 206. Also in his
(1914), p. 239; (1954), p. 158.
s Duhem (1894a), p. 181. Also in his (1914), p. 220f.; (1954), p. 146. In The A i m and

Structure, Duhem adds hydrostatics and optics to the list, before concluding: "The
knowledge of a good many chapters of physics necessarily precedes the formation of that
abstract idea, the volume occupied by a certain gas."

REFERENCES
Brenner, A.: 1990, Duhem: science, rdalitd et apparence, Vrin, Paris.
Cornu, A.: 1891a, 'Sur une experience rEcente, determinant la direction de la vibration
de la lumi~re polarisEe', Comptes Rendus des Sdances de l'AcadOnie des Sciences 112,
186-89.
Cornu, A.: 1891b, 'Sur les objections faites ~ l'interprEtation des experiences de M.
Wiener', Comptes Rendus 112, 365-70.
Duhem, P.: 1892, 'Quelques rEflexions au sujet des theories physiques', Revue des Questions Scientifiques 34, 139-77.
Duhem, P.: 1893, 'ThEorie mathEmatique de la lumi~re', Revue des Questions Scientifiques 33,257-58.
Duhem, P.: 1894a, 'Quelques rEttexions au sujet de la physique expErimentale', Revue
des Questions Scientifiques 36, 179-229.
Duhem, P.: 1894b, 'Les theories de l'optique', Revue des Deux Mondes 123, 94-125.
Duhem, P.: 1896, 'Fragments d'un cours d'optique', Annales de la Socigtd Scientifique de
Bruxelles 20.
Duhem, P.: 1905, 'Physique de croyant', In Duhem (1981), pp. 413-72, translated in his
1954, pp. 417-21.
Duhem, P.: 1914, La thgorie physique, son objet et sa structure, Chevalier et Rivi~re,
Paris. Reprinted by Vrin, Paris, 1981.
Duhem, P.: 1954, The Aim and Structure of Physical Theory, P. Wiener (trans.), Princeton University Press, Princeton, New Jersey.
Duhem, P.: 1981, La thdorie physique, son objet et sa structure, Vrin, Paris.
Poincard, H.: 1890, Electricitd et optique, Carr6, Paris.
Poincar6, H.: 1891a, 'Sur l'experience de M. Wiener', Comptes Rendus des Sdances de
l'Acaddrnie des Sciences 112, 325-29.
Poincar6, H.: 1891b, 'Sur la rEflexion mEtallique', Compres Rendus 112, 456-59.
Poincar~, H.: 1968, La science et I'hypothdse, Flammarion, Paris.
Wiener, O.: 1890, 'Stehende Lichtwellen und die Schwingungsrichtung polarisierten Lichtes', Wiedmann's Annalen 40.
DEpartment de Technologic et Sciences de l'Homme
Centre Benjamin Franklin
Universit6 de Technologic de Compi~gne
BP 649- 60206 Compi~gne Cedex- France

DUHEM

AND THE ORIGINS

RAMIFICATIONS

OF THE

OF STATICS:

CRISIS

OF 1903-04"

ABSTRACT. Much speculation on the sources of Duhem's historical interests fails to
account for the major shifts in these interests: neither his belief in the continuous development of physics nor his Catholicism, when his Church was encouraging the study of
generally Aristotelie.n scholastic thought, led to any interest in mediaeval science before
1904. Equally, his own claim that he was merely testing his views on the nature of physical
theory is easily squared only with earlier work with no trace of mediaeval science. Behind
this discontinuity lies a major crisis. Though not a positivist, Duhem had based all his
work on assumptions acceptable to positivists. One of these, the sterility of the Middle
Ages, was refuted by his chance discovery of evidence of genuine mediaeval science in
the autumn of 1903, but that left the doctrine of scholastic sterility intact.

1. I N T R O D U C T I O N : I N T E R P R E T I N G D U H E M AND THE 1913
ACADEMY DOCUMENT

Since it covers both the history of science and its philosophy, the
work of Pierre D u h e m provides a suitable test case on which to focus
discussions of the mutual interaction of these two studies? To what
extent, we may ask, did Duhem's philosophical writing control his
historical investigations? To what extent were the historical investigations a main source for his distinctive philosophical positions? Like
Agassi (1963) and Lakatos (1971), D u h e m fully expected that the mutual relationship would be close, but the outcome of his labours was
not what he or anyone else would have expected. A study of that
outcome can tell us a good deal about Duhem's other concerns.
In 1913 D u h e m authorized one interpretation of his historical work,
in his submission to the Acadrmie des Sciences at the time of his
election as a nonresident member. 2 His attempt to present his philosophical and historical studies as ancillary to his physics bears all the
marks of the occasion for which it was drafted: it was as a physicist
that he was up for election, and it was as a physicist he was going to
present himself. Whatever other interests he may have had, they were
not relevant on that occasion or, if they were relevant, it was for the
light they shed on his career as a physicist.
Synthese 83: 337-355, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands,

The picture he presented then lies behind one school of Duhem
interpretation, of which Armand Lowinger with his Columbia thesis
(1941) is perhaps the most prominent representative. Duhem the physicist had developed a scientific programme to reduce the whole of physics
to the laws of heat via a general thermodynamics or Energetics; in
defence of that programme he had developed a philosophy, a critical
analysis of scientific knowledge, and set this out in a number of writings
up to the Thdorie Physique. But to the good scientist, theories, including
theories of scientific knowledge, require testing, and for the facts to
test this theory he turned to history. On this showing, the historical
writings are apologetics for the Energetic method.
This interpretation of Duhem's philosophical and historical interests
aligns him with the common practice of late positivism, and makes of
him a practitioner of the rigidly internalist critical history for which
perhaps Mach 3 is best known (and which some latter day positivists
are still trying to keep alive in the face of the flood of externalist
historiography), a practitioner of a type of 'history' in which the only
factors allowed to appear are those which the logic of the philosopherhistorian accepts as relevant. This account represents also a highly
integrated rigid view of Duhem with no room for development, with
all the parts interconnected, and no joins showing. Most obviously, it
makes no allowance for Duhem's undoubted and never concealed religious and political concerns.
There is much to be said for this view of Duhem's philosophy and
historical interests. Both his love of and dedication to theoretical physics, and his commitment to his Energetic programme are beyond doubt,
and apologetics for his Energetic method seems a reasonable description for the brilliant classic short works he wrote before and up to
about the turn of the century, works like Les Theories Electriques de
J. Clerk Maxwell (1900-1901), Le Mixte et la Cornbinaison Chimique
(1902) and the Evolution de la Mgcanique (1903). Nonetheless, it is a
nonsense: the detailed discussions in the Syst~me du Monde (1913-59)
of the philosophy and theology of Aquinas and of the condemnations
of 1277 have no conceivable connection with Duhem's Energetic programme. The Academy document and the school of Duhem interpretation springing from it would have been a pretty fair description up
to 1903. It was not in 1913.
At this point, readers may be tempted to appeal to Duhem's doctrine
of continuity. 4 According to this much-discussed doctrine, good physics

builds on what came before instead of seeking to destroy it, usually
also claiming that the appearance of revolutions in the history of physics
conceals an underlying continuity discoverable by closer analysis. It is
commonly supposed that the idea of a seventeenth-century scientific
revolution offended against this doctrine and so drove Duhem into
seeking the mediaeval antecedents of modern science. Duhem's belief
in continuity is beyond question, but as Malocchi has shown, it was
common among late nineteenth century positivists, and it will not do
the work required of it. If his continuism is an adequate explanation
of Duhem's work on mediaeval science it is remarkable that it did not
have that effect before 1904.
2.

MEDIAEVAL

SCIENCE

AND THE ~NEO-SCHOLASTIC'

ALTERNATIVE

There is another theory of the origin of Duhem's philosophical and
historical interests which is even more implausible: that it was an outgrowth of late nineteenth century and early twentieth century neoscholasticism, s This programme for reviving scholastic thought is particularly associated with Pope Leo XIII, 6 and as a Catholic Duhem must
be supposed to have been aware of it. The ultimate source of this
theory is a little unclear, though it seems to have been current in the
Vienna Circle, 7 and it also got publicity from Antonio Favaro. s In
epistemology it seems to rest on superficial resemblances between
Duhem's doctrine of the autonomy of physics, 9 its independence of all
metaphysical and extra-physical considerations, and scholastic theories
of the classification of the sciences. In history of science its basis seems
to be Duhem's interest in the Middle Ages, and his many publications
in neo-scholastic journals such as the Brussels Revue des Questions
Scientifiques, 1° and the Paris Revue de Philosophie. u
It depends Oil what counts as scholastic. If all that is meant is taking
mediaeval thought seriously, Duhem is included; he is also included if
it means no more than a genuine attempt on the part of Catholics to
grapple with modern science, and he may have seen the Revue des
Questions Scientifiques in that light. 12 In the eyes of the Catholic authorities, however, it meant very specifically the revival of the thought
of Thomas Aquinas, and his supposed reconciliation of Christian
thought with Aristotle. 13 It was a definite ecclesiastically sponsored
movement with definite ideas, forwarded by particular people. Duhem

could, the evidence is, tolerate some of these, like Jean Bulliot, the
editor of the Revue de Philosophie, but many of them could rouse him
to express his disgust in extremely violent terms. 14 They in their turn
found him an embarrassment: the lengths Jacques Maritain went to
refute him 15 is evidence of that, and equally symptomatic is the way
l~tienne Gilson avoids citing the passages from Duhem's Systgme du
Monde 16 this Thomist must have found particularly uncongenial.
But the most obvious difficulty facing any kind of 'neo-scholastic'
theory of the origin of Duhem's interests in the history of mediaeval
science in particular is the discontinuity, discussed above, in the career
of the continuist philosopher of physics. Duhem's mediaeval interests
came so very late in his life: all the works on which Duhem's reputation
as a historian of mediaeval science rests are later than 1904.17 The
'neo-scholastic' theory of Duhem's philosophical and historical interests
could have had some plausibility in 1913, but it has none for the D u h e m
of 1903, whose works showed no interest in or knowledge of mediaeval
science. In the first part of his career D u h e m seems to have been totally
immune to all ecclesiastical pressures in favour of mediaeval thought,
while in the second part, his researches were increasingly controlled by
concerns outside physics. A serious account of the various interests of
the historical D u h e m has to take account of this discontinuity, and pay
attention to just what was happening at the watershed of 1903-1904
and in the years that followed.
3. THE DISCOVERY OV 1903--1904
In 1974, I began examining systematically those of Duhem's works
deriving from that crucial period. I found what had not to my knowledge
been documented before: Duhem's discovery of mediaeval science took
him completely by surprise in the winter of 1903-1904 while he was
working on Les Origines de la Statique. In a paper published by Annals
of Science, 18 I documented the surprise and sought to interpret the
evidence: I saw the discovery of mediaeval science as provoking a crisis
of a far-reaching kind, some of whose ramifications I attempted to
indicate. It is now clear to me that I did not see anything like the full
picture, but, nevertheless, a very brief summary is in place here. In
what follows I do not speak of a crisis in the Kuhnian 19 sense of an
interregnum between paradigms, when nobody can understand each
other, but in the Biblical sense of a judgement, a time when one's acts

and one's doings are in question, under judgement, and it is unclear
what will stand or fall.
In the autumn of 1903 Duhem had just completed his Evolution de
la Mdcanique, of which a principal theme had been the dynamics of
Lagrange, a theory of moving bodies and of the forces that moved
them built on a principle (virtual velocities) having to do with bodies,
not in motion, but at rest. This principle of the theory of forces at rest,
or statics, had a long history, and Duhem now set out to write a work
on the origins of that theory, under the motto title Les Sources des
Thdories Physiques. Like much else that he wrote, he published this
work in serial parts in a journal, in this case the quarterly Revue des
Questions Scientifiques. The first instalment of four chapters, appeared
in the October 1903 issue, and in the ordinary course of events, the
next would have appeared in the January 1904 issue. It did not: when
it did appear in April it was flagrantly inconsistent with the first. The
first instalment~ unusual though it was for the emphasis it placed on
Leonardo's ideas and their influence, otherwise broke little new ground,
and in particular flatly announced that the commentaries of the scholastics on Aristotle's Mrlxo~wx& ~pol3k'Cllx~'ro~ (actually there were no
such commentaries: the work was unknown in the Middle Ages 2°) had
added nothing to our knowledge. The second, however, started with
the admission that Duhem had so far given only a crude sketch of the
early development of the subject, and now needed to gather up the
Alexandrian sources of mediaeval statics. He was also now laying heavy
emphasis on the previously unmentioned thirteenth century figure of
Jordanus de Nemore.
What brought Duhem to this volte face is even now not clear. He
seems, in late October or early November 1903, to have become bothered by the inadequacies of his sources and asked Paul Tannery for
help in locating a certain Euclid text. Tannery's postcard reply of
December 1903, 21 volunteers the following additional information:
There is also, under the name of Euclid, another piece on statics, Euclidis de Ponderibus,
sometimes confused with the work Jordanus Nemorarii de Ponderibus (see Rose's Anecdora Graeco-Latina II, 291). I have seen this treatise in manuscript, but don't really know
it - it seems of Arabic origin. Woepcke (Journal Asiatique XVIII, 1351, p. 217) has given
the translation of a Euclid piece 'on the balance' connected with it. Maurice Gallien,
retired artillery commander (Toulouse, 5 rue Traversi6re) was going to make a special
study of these writings, so that I have not concerned myself with them, but I have not
heard from him since 1900.

That postcard seems to have set him off: at any rate, in 1905, in his
preface to the book form of his work (otherwise a verbatim reprint of
the articles, including the inconsistencies), he told the world that the
only thing for it was to get hold of and analyse everything relating to
mediaeval statics in the Bibilioth6que Nationale and the Bibiloth6que
Mazarine. Duhem's response, it might be felt, was perhaps a little
extreme: did he really need to go that far to fill in the gaps in his
sources? For a critical historian, Duhem had always been unusually
careful with his sources, making sure he got his facts right before his
critical analysis got going, but this is going beyond even ordinary care.
It is hard to resist the conclusion that for Duhem important issues were
at stake.
4. THE C O N S E Q U E N C E S OF THE D I S C O V E R Y

My 1976 paper attempted to say what these issues were. I suggested
that in Duhem we had to do with a physicist, with the prejudices
physicists imbibed in their training, and among these prejudices, I
suggested, was the doctrine, in all his sources from Lagrange 22 to
Dtihring 23 and Mach, that the mediaeval period was scientifically sterile.
In Jordanus, however, he encountered evidence, which his training as
a physicist compelled him to recognize as evidence, of worthwhile
mediaeval science. I also suggested that the refutation of the doctrine
of mediaeval sterility had knock-on effects in other areas of Duhem's
thinking: it called in question his historiographical assumptions and the
methodological principles that guided these assumptions, particularly
the autonomy of physics. As he had explained in the Thdorie Physique, 2 4 the kind of history of interest to the physicist, was one bare of
all personal details, containing only the occasions in which an important
new fact was discovered, a principle clarified or false idea refuted, and
in this he was advocating a 'critical' approach to the history of physics
rather like the 'rational reconstruction' method advocated by Imre
Lakatos.
Duhem was, however, conscious of the limitations of this 'historical'
method. In 1903, in an extended essay review of the French translation
of Mach's Mechanik, 2s he discussed Mach's exclusion of nonscientific
ideas from his story, and remarked that this was acceptable for recent
physics, since it was now generally agreed that physics was and should
be separate from religion and metaphysics. This general agreement,

however, did not obtain in earlier periods, and the historian who wanted
to bring the past to life had to take account of such ideas. Bringing the
past to life again was what Duhem was certainly not doing in 1903. In
the following year, however, he was doing it, and because he was doing
it, he could no longer assume the autonomy doctrine in his analysis.
But equally, he had nothing to replace it with, and the lack of such a
principle shows in the chaotic nature of much of his work over the next
decade. With To Save the Phenomena in 1908, 26 however, he had the
outline of a replacement, in which the problem of autonomy replaced
autonomy: the standing of physics and its degree of independence from
other disciplines was now the central issue.
Thus far this is the account of my 1976 paper. With qualifications, it
still seems generally correct, though something would need to be added
about the positivistic atmosphere in which the physicist had been
trained, as has been so admirably done by Roberto Maiocchi, but a
great deal more needs to be said about the crisis of those years.
5.

WIDER

RAMIFICATIONS

OF A CRISIS

What I did not see in 1976 was that bringing into question the historiographical applications of Duhem's methodology had much wider effects
on the whole orientation of a man in an extremely sensitive political
and religious position. I did not then see these wider effects, nor see
it for what it was, a crisis imperilling his whole life strategy, I did not
see that beyond the time invested in a particular approach to the history
of science, founded on a particular set of historiographical assumptions
linked to a particular methodology, lay a particular way of coping
with the political and religious conflicts all around him. Duhem had
developed an integrated strategy for coping with these conflicts, and
this strategy was now at risk. I have no time or space here for a detailed
account of the pressures Duhem as a Catholic scientist in the Third
Republic was exposed to, and in any case the job has been very well
done by Harry Paul, 27 but some understanding of these is essential for
understanding the religious motifs in his writing, and for making any
kind of sense of his later output, and I give a brief summary here.
The France Duhem grew up in and in which he made his career was
deeply unstable, its instability marked by a succession of crises that
split the country from top to bottom. 28 The most famous of these was
the Dreyfus affair of the closing years of the nineteenth century and

early years of the twentieth century. This concerned the Jewish army
colonel, Albert Dreyfus, who was imprisoned in 1894 on Devil's Island
after being falsely found guilty of espionage, and the long political
campaign for his rehabilitation that finally succeeded only in 1906. The
Third Republic was in practice the constitution imposed by one party
on another, imposed by people who were atheists on Catholics who
hankered after a restored Bourbon monarchy, imposed by people
whose ideological inspiration was positivist 29 on Catholics who had
every reason to resist that ideology, imposed by people who appealed
to the authority of science as the counterweight and answer to the
authority of religion. The educational system was the key to the strategy
against the religious enemy: a schoolmaster in every parish was to
undermine the authority of the priest. It was an all-embracing system,
from the elementary school to the university, unless you opted for
mostly underfunded Catholic schools and universities of low prestige.
Duhem made his career as a Catholic in the state system, and was not
alone in this even if he was perhaps the most visible, and the obvious
question is what strategy he adopted to ensure his survival and protect
his integrity. That strategy will throw light on the rationale behind the
nonsense of the 1913 Academy document discussed in my opening
paragraphs.
In a like political situation the founders of the Royal Society of
London responded to it by forbidding all discussion of politics and
religion at its meetings. The strategy is common in conflict-ridden societies, and was available to Duhem; if, for example, as a Catholic (and
therefore drawn to the side of the reactionary opponents of the campaign for Dreyfus's release from the Devil's Island) he wanted to stay on
good terms with his friend and colleague, the left-leaning mathematician
Jacques Hadamard 3° who just happened to be the brother-in-law of
Albert Dreyfus and organiser of the campaign for his release. The
correspondence with Hadamard continues right through the Dreyfus
affair, and after Duhem's death Hadamard contributed to the memorial
volume on his work 31 and spoke at the 1936 memorial meeting in Paris
organized by Aldo Mieli? 2 He also referred to him in friendly terms
in his Psychology of Invention (1945) many years afterwards. It is no
surprise that letters from Hadamard at the time of the affair are on
purely technical matters (the stability of the solar system 33) and do not

refer to politics. Duhem's strategy is the obvious one: make your stand
on your scientific excellence, and let your work speak for itself: never
ever appeal to your faith or politics in your scientific work. The French
Catholic who made his career as a scientist within the Third Republic
at no point appealed to his religion: his work, acceptable to the positivists on their own terms, was to be its own argument. The thing was
to seek truth and broadcast what he found to the winds, 34 avoiding
unnecessary religious or political polemic.
Duhem was thus involved in a strategy of defeating the enemy from
within using the assumptions and methods of the positivists, excelling
at the science and using only the methods of the science that was their
paradigm of knowledge and rationality. Only by thus presupposing
physics as a neutral ground for debate, valid in its own terms, could
Duhem attempt to expose the limitations of claims to authority based
on that science. Hence the rigorous analysis of the bases of physical
theory, underpinning a particularly abstract approach to the problems
of theoretical physics, in which all that counted were just those things
the positivists said counted: agreement with observation and experiment. Hence also the brilliant historical sketches of the 1890s and
early 1900s in which alternative less abstract approaches to physics and
physical chemistry based, for example, on atomic hypotheses were
shown as leading into contradictions and dead ends while the abstract
approaches Duhem favoured triumphantly overcame these obstacles.
Hence finally the brilliant attempt to show that within its own terms an
account of physical theory relying on nothing but observation and
experiment was incomplete, unable to explain its own goals and procedures. 35
Duhem's strategy had only partial success. Close colleagues like Hadamard often came to make allowances for his combative disposition
and respect his integrity, but those who controlled his career and wrote
reports on him saw him as something of a Trojan horse who had to be
neutralized: they held back his professorial grading as long as they
could and made sure that he never got the Paris job that was the normal
expectation of an academic of his standing. As Harry Paul has shown,
to them~he was a dangerous enemy to be dealt with at arm's length.
That may be no surprise, but it is more surprising that Duhem's strategy
was hardly more acceptable to his fellow Catholics.

6.

NEO-SCHOLASTICISM

AGAIN

Duhem's neutralizing strategy can be contrasted with the neo-scholastic
alternative. This offered an alternative philosophy, based on the work
of St. Thomas Aquinas, and an alternative rationality in which the
authority of science was to provide an independent rationale for the
authority claims of the Catholic hierarchy, its right to command obedience both in the religious sphere and the political. Thomist scholasticism
offered a philosophical environment that facilitated the elaboration of
a natural theology offering proofs of God's existence to underpin the
teaching of the Christian revelation and assist the articulation of that
revelation. At the same time it facilitated the erection of a system of
natural law underpinning Catholic moral theology, giving it a solidity
that it might have lacked if it had to rely on the teachings of the New
Testament and its tradition. Such claims to authority were very much
at issue when Duhem was writing, as the Catholic community descended
worldwide into its so-called modernist crisis, 36 of which France was the
principal focus. The principal document of that crisis, the encyclical
Pascendi Dominici Gregis of 1907, 37 specifically pointed out the dangers
'modernism' posed to natural theology, and went on to identify a
distrust of scholasticism as a principal symptom of the 'heresy' so
named. Through the 1890s Duhem did not object to the idea that a
rationale for the method of physics might be found in a metaphysics of
generally scholastic type, but he did not encourage it, and in the meantime ensured, to neo-scholastic protests, 3s that any such metaphysics
would have no power whatever to dictate the contents of his autonomous physics.
Duhem did not, moreover, do anything to encourage any suggestion
that there was a mediaeval science, scholastic in form, worthy of attention in his own time. Such suggestions could have been very welcome
to the ecclesiastical authorities: a constant theme of Catholic apologetics
has been to show how the Church supported education and learning in
the Middle Ages, and to show the beneficence of the church's control
in matters intellectual. Moreover, a plausible scholastic science would
have made easier the job of the natural theologian wanting to update
the proofs of God's existence. But a science under scholastic auspices
was not a likely prospect for Duhem's apologetic purposes: what he
needed was one under nonscholastic auspices. There should be no
difficulty in seeing why: it was and is a commonplace that the seventeenth century scientific revolution was at heart the replacement of

scholastic sterilities by experimentally controlled mathematical precision, 3 9 and that received wisdom meant that the Church that was
supposed to have encouraged these stefilities could make no convincing
claim to the attention of scientific intellectuals. There was a high price to
pay for taking pride in just that feature of mediaeval thought universally
agreed to have been overcome by the rise of modern science. Duhem's
strategy had no room for mediaeval science, or at least for what was
then known of it, and little room for a synthetic programme of absorbing science into metaphysical framework of scholastic inspiration.
But that strategy had serious consequences: Duhem was now in effect
sitting on the fence in the midst of his Church's battle for survival,
refusing it the weapons it needed to win the war. His difficulties were
now more severe than they had been in the early 1890s. Then, when
his early near-Machian assistance to the memory account of physical
theory4° had come under scholastic attack, he had responded with a
theory of natural classification, according to which the classifications
imposed on the world by his purely mathematical abstract systems
approached the truth asymptotically. He was even prepared to hazard
the guess that reality might be truly describable by a metaphysics of
scholastic type. The concession cost him little, for he had never doubted
that there was a real world out there, and he had not conceded metaphysics any right to dictate the contents of his physics. He seems to
have thought that such partial concessions to scholasticism, welcomed
as they were by Belgian friends associated with the Revue des Questions
Seientifiques, would be enough to fulfill his obligations as a loyal Catholic, but the events of the following decade proved otherwise.
After the death in 1916 of his student friend, the historian of philosophy Victor Delbos, Duhem, who had himself only a couple of m o n t h s
left to live, remarked to Blonde141 that he had sometimes heard him
accused, particularly by priests, of not being open and forceful enough
in his Catholicism: to be insufficiently strident was to leave oneself
open to suspicions of treason. Astonishing as it may now seem, Duhem
was exposed to just this suspicion, that in his philosophy he had compromised with the enemy. In this he was in a like position to those other
Catholics, increasingly accused by their opponents of modernism, who
sought intellectual and political dialogue with non-Catholics. Throughout the 1890s and into the beginning of the following decade, Duhem
had avoided aligning himself either with such Catholics or against them.
He was now to be forced to take sides. In 1905 his student friend

Maurice Blondel invited him to collaborate with the Annales de Philosophie Chrdtienne, 42 which he had just acquired on the death of its previous owner and editor Charles Denis. D u h e m hesitated: he was not
prepared tO give up his previous collaborations and rather wished that
Catholics would unite against the common enemy instead of shooting
at each other. H e did, however, agree to collaborate with it and it
carried both his 'Physique de Croyant' ( O c t o b e r - N o v e m b e r 1905) and
To Save the Phenomena. But in due course it also carried Maurice
Blondel's long attack (1909-10) on the reactionary politics of Action
Frangaise 43 and those Catholics, mainly neo-scholastic, who hoped for
an alliance with this atheistic positivist-led monarchist movement.
When, as a result of that campaign, it was denounced to Rome and
condemned in 1913, 44 Duhem's sympathies were only too clear. He
had made his choice.
7. CONCLUSION

The reason for Duhem's mediaeval interests and the discontinuity in
his career should now be clear. In October 1903 he stumbled on what
he did not know he was looking for: a nonscholastic mediaeval science.
It seems that, much as he distrusted many of the scholastics of his
acquaintance, he had assumed that the story they told of the Middle
Ages was factually correct: the 'science' of the period was indeed
scholastic and (therefore) sterile. Loyal to his Church as D u h e m wished
to be, his loyalty did not go so far as to proclaim the fertility of that
sterile nonsense. But now, it seems, impressions had been mistaken
and D u h e m went in search of more of the newly discovered gold. He
discovered that the scholastics could not be relied on to give an account
of mediaeval thought, of its science, of its philosophy, or even of its
theology. H e discovered that when first stated the doctrines now being
made normative for Catholics had actually been condemned by the
ecclesiastical authorities of their day in the name of Christian orthodoxy, in his view rightly so. H e discovered that the famed synthesis of
Christianity and Aristotle was no synthesis at all, merely incoherent,
for Aristotle's philosophy, like much else from the ancient world, was
irrevocably vitiated by the pagan principles on which it was built, and
so he was able to satisfy himself that the system of thought needing to
be discarded if modern science was to make its appearance was equally
inimical to Christian orthodoxy.

Duhem pursued these discoveries with all the persistence and energy
of a detective on the trail of a fraud, for fraudulent was certainly how
he regarded it, and the massive results of his industry were the Etudes
sur Ldonard de Vinci, To Save the Phenomena, and the monumental
incomplete Systdme du Monde. Without the crisis of 1903-1904 nobody
would now be remembering Duhem the historian of science, and without it his work would lack its special flavour and interest. The ramifications of this major upset need to be borne in mind by readers of any
of his writings of these years. Duhem took a while to establish the new
directions in which his thought would go, but while the argument of
this paper has concentrated on his historical work, it is a safe bet that
no area of his work was left untouched.

NOTES
*Drafted for the Btacksburg conference, versions of this paper were also presented at
colloquia at the University of Harvard Department of the History of Science and the
University of Toronto Institute for the History and Philosophy of Science and Technology.
I am grateful to all those who responded to earlier versions, but particularly to Phillip
Quinn, the commentator on my paper at Blacksburg, and Jamil Ragep.
1 Useful general accounts of Duhem are D. M. Miller's (1971) DSB article, and S. L.
Jaki's (1984) biography.
2 See P. Duhem, 'Notice' (1971), a translation of the relevant part of which was circulated
with the preparatory papers for this conference.
3 See Mach, Geschichte und Wurzel and Mechanik.
4 Heavily emphasized by Agassi in his Historiography. Maiocchi, Chimica e Filosofia,
gives a very full treatment of this aspect of Duhem's work and its antecedents among his
late nineteenth century predecessors.
5 The only full presentation of this common interpretation I know of is that of Paul,
Contingency (1979), chapter 5, pp. 136-78. For a detailed discussion of it with full
references see my essay review 'Darwin and Duhem' (1982).
6 See his encyclical Aeterni Patris. There are full discussions of the movement in McCool,
Catholic Theology (1972), and Thibault, Savoir et Pouvoir (1972). The relevant articles
in the New Catholic Encyclopedia ('scholasticism', 'thomism', 'sciences, classification of')
give something of its intellectual commitments.
7 See Philipp Frank's reiterated but unargued claims in his 'Introduction, Historical
Background' (pp. 1-51) to his Modern Science and its Philosophy (1949).
8 See his 'Galileo...' (1921).
9 See Thdorie, parr: I, chapter I.
70 On this journal see Nye, 'Moral Freedom' (1976).
11 On this journal and Duhem's role in its foundation see Paul, Contingency, pp. 177-8,
and H61~ne Pierre-Duhem, Savant, p. 105.
1: See his letter of 3 July 1897 to Paul Tannery.

13 Dom David Knowles, Evolution of Mediaeval Thought, offers one version of this
theme, and Gilson, Christian Philosophy, a more sophisticated version.
14 Solicited by Maurice Blondel to collaborate with the Annales de Philosophie Chr~tienne
of which Charles Denis was then the editor, he replied (12 January 1896) thus (translation
mine):
The Abb6 Denis may be a decent man, but as for the Socirt6 St. Thomas d'Aquin,
whose organ his journal is, it too may well contain some decent people, but it also
contains some beings puffed up with vanity - Count Domet de Vorges for example
as well as some dirty poisonous beasts, like the individual who hides in the Annales
de Philosophic Chrdtienne as well as in Le Monde, behind the name 'Congressist' I have no desire to mix my prose with people of that ilk, who think they are
authorized to tell lies because they wear a cassock.
Moreover I will confess to you that such people have put me off the Catholic
world - not Catholics, which isn't the same thing - more than I can say. The Lille
Catholic University had already given me the measure of the degree of sincerity in
that world when the Brussels congress completed my education: scribes and Pharisees, hypocrites!
-

The congress referred to was the third in a series of international meetings of Catholic
Academics. The congress report (vol. 1, 1895) prints the text of Duhem's interventions
and the Thomist A. Gardeil (1894) gives a highly suggestive account of events.
15 See his Distinguer pour Unir (1932, pp. 84-90, 123-5, 385).
16 His Christian Philosophy (1955) cites the chapter of volume v of the Syst~me dealing
with Albertus Magnus but not the equally extensive adjacent chapters on Thomas Aquinas
and Siger of Brabant.
17 The Origines (1905-6), the t~tudes (1906, 1909, 1913), and Systdme (1913-59).
18 My 'Genesis' (1976), which analyses the chronology of this episode in detail.
19 According to P. L. Rose, and S. Drake (1971). I owe this reference and much else to
the late Dr. Charles Schmitt, then the member of the editorial board of Annals of Science
responsible for handling my paper.
2o See his well-known Structure and Essential Tension.
21 So dated by the editors from the postmark.
22 See Lagrange, Mechanique Anatitique (sic) (1788, 1811-15, 1853-55).
23 Kritische Geschichte... (1873, 1877). Diihring actually states explicitly that the mediaeval period was a historical desert.
24 Theorie, Part II, Chapter VI, Section VI.
25 This twenty-page essay review (1903) of Mach's Mdcanique (1904) has all the marks
of an inside job done on advance proof copy. The translation was only published the
following year, and Duhem got the title wrong, reading Etude for Expose. See also
Hentschel (1988).
26 This is a natural interpretation of Duhem's preface (pp. 1-2).
27 See particularly his 'Crucifix and Crucible' (1969), and 'Quest of Kerygma' (1969).
28 Bury's France 1814-1940 (1949-1976) gives a useful general history of the period,
while Adrien Dansette's Boulangisme (1938) gives a fascinating account of one of the
crises.
29 On nineteenth century positivism see Gouhler, Jeunesse d'Auguste Comte (1933-41);
Hayek, Counter-Revolution of Science (1952); and Simon, European Positivism (1963).

30 The Encyclopedia Judaica has a useful account of him.
3i 'L'Oeuvre de Duhem darts son aspect math6matique' (1917).
32 Hadamard (1937).
33 Thdorie, part II, chapter III, sections III and IV, citing an article by Hadamard, are
largely the fruit of this correspondence.
34 With Catholic critics in mind, the letter to Blondel cited above continues:
My firm intention is never to get mixed up with these people: seek the truth, and
when I think I've found a particle of it, throw the news of it to the four winds and
let the crows caw.
Cf. this response from Lucien Laberthonni6re (9 January 1909):
The stuff of yours that I've read and the conversations I've had with you have
considerably clarified, by confirming it, the idea I had of the intellectual apostolate.
I am very grateful. Yes you are right: what matters and counts is to work away
believing in the value of the truth
I haven't been able to see the other side of this correspondence.
35 See Th~orie, part I, chapter IV, section X and elsewhere.
36 The essential secondary source on modernism is l~mile Poulat's Histoire Dogme et
Critique (1962, 1979).
37 On the analysis of this encyclical (1907) and its origins see Vidler, Variety (1970), and
Daly, Transcendence and Immanence (1980).
38 See e.g., Vicaire, 'Valeur Objective' (1893); Paul, Contingency, presents a mass of
evidence of neo-schotastic criticism of Duhem.
39 See e.g., Burtt, Metaphysical Foundations (1924, 1932); Butterfield, Origins of Modern
Science (1949, 1957, 1962); Hall, Scientific Revolution (1954, 1962); Koyr6, Etudes Galildennes (1966); Westfall, Construction of Modern Science (1971, 1977).
4o See his 'R6flexions' (1892).
41 Letter of 8 August 1916.
42 Blondel's letter seems to have been lost, but Duhern's reply is dated 25 July 1905.
Laberthonni~re's response to Duhem's offer of the article that became 'Physique de
Croyant' is dated 16 August 1905. Both the published Blondel-Wehrl6 (1957) and Blondel-Valensin (1969) correspondences contain material relating to this journal implying
that Blondel was at least financing or had actually bought it.
43 The standard work is Eugen Weber's classic study (1962), but see also Paul, Second
Raillement (1967).
44 Index (1948). Laberthonni6re was forbidden to publish anything at all or say anything
about this further ban. There are full letters from Duhem to Blondel dated 27 June and
20 July, and from Blondel dated 16 July 1913. I thank Donald G. Miller for copies of
letters from Duhem when on loan to him, and G. Mosseray for copies of letters from
Blondel. I hope to make a fuller study of this important correspondence in the future,
and I thank Duncan McGibbon for discussing its significance with me. Extracts from
Duhem's second letter are published in L. Lecanuet (1930), pp. 478-9, and the BlondelWehrl6 correspondence.

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Questions Scientifiques 31, 139-77.

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Cambridge.
Philosophy Dept.
London School of Economics
Houghton Street
London WC2A 2AE

DUHEM

IN DIFFERENT
ON BRENNER

CONTEXTS:

COMMENTS

AND MARTIN

ABSTRACT. These comments consist of reflections on the papers Anastasios Brenner
and R. N. D. Martin presented at the Conference on Pierre Duhem: Historian and
Philosopher of Science. I argue they present nicely complementary accounts of Duhem's
turn to history of science: Brenner emphasizes reasons internal to Duhem's philosophical
concern with scientific methodology while Martin highlights reasons derived from the
broader context of Duhem's engagement with religious controversies of his culture. I go
on to suggest that seeing Duhem in this broader perspective can help us cope with the
conflicts between science and religion in our own culture.

At first glance the papers by Anastasios Brenner and R. N. D. Martin
seem quite diverse in their preoccupations, but a bit of reflection on
them reveals a common theme.1 Both papers raise questions about the
role of history of science in Duhem's thought. What larger purpose, if
any, did he mean to use the history of science to serve? And, in
particular, why was he especially interested in late medieval science?
As I shall argue, the two papers return answers to such questions that
are in some ways nicely complementary. Moreover, it seems to me that
this complementarity is a consequence of the fact that Brenner and
Martin situate Duhem's thought in different intellectual contexts. This
leads me to wonder about how to specify a context for the study of
D u h e m that will enable us to learn as much as we can from the legacy
of his thought. Anglophone philosophers have, for the most part, focused on the context of Duhem's concerns with science and philosophical reflection on its methodology. But, as I shall suggest, there may
be much of philosophical value to be learned from locating D u h e m in a
broader context that includes his religious concerns and the theological
problems of his culture and ours.
Brenner's paper concentrates its attention on the context of Duhem's
developing philosophy of science and reveals reasons for Duhem's historical turn internal to his methodological thinking. As Brenner's narrative presents the development of Duhem's holism, it begins in an analysis of Wiener's experiment on the direction of vibration of polarized
light and is later generalized into a philosophical account of experimental method. Duhem's general analysis of experiment is meant to
Synthese 83: 357-362, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

support holism by showing that, in order to bring experience and scientific theory into contact with one another, observed fact must be transformed into theoretically interpreted fact and that whole theories are
presupposed in making such transformations. Consequently, theoretical
principles cannot be established seriatim by induction. And this, as
Brenner emphasizes, leaves Duhem facing a problem about how to
choose among theoretical principles.
Readers of The Aim and Structure of Physical Theory will recall that
Duhem invokes good sense to solve this problem. We test whole groups
of theoretical principles experimentally. When such a group fails to
square with experimental results, logic alone does not dictate which of
its members are to be rejected. But at this point good sense may
intervene to yield a choice. Duhem himself describes good sense rather
dramatically in terms of Pascalian reasons of the heart. It might also
be characterized less grandly, following Polanyi, in terms of tacit craftknowledge of communities of scientific practice or, following Maclntyre, in terms of the local rationality of historical traditions of inquiry.
The point is that good sense embodies a kind of informal rationality
and so its choices are generally rational. If the good sense of scientists
can itself be shaped by knowledge of the history of science, there will
be a role for history of science to play in the constitution of scientific
rationality.
I think it quite plausible to suppose that Duhem envisaged a role of
this sort for history of science. After all, he writes history of science
with the didactic aim of supporting his instrumentalist philosophy. If
history could be made to teach scientists that their enterprise does best
when it concentrates on saving the appearances, then it would make
good sense for scientists to rally in support of the research program in
energetics Duhem himself favors, even if logic alone does not dictate
that they should do so. As Brenner points out, the main lesson a history
of scientific theories written from a Duhemian point of view teaches is
that experimental laws accumulate, the language of science grows ever
richer, and science progressively becomes a more and more efficient
predictive instrument.
Duhemian history of science is, of course, partisan history. Scientific
realists can and do write history of science in support of their philosophical predilections. This is a game both sides in the controversy between
instrumentalism and realism can play, and neither side has yet emerged
from play a clear winner. Some historical episodes seem to be grist for

the instrumentalist mill; others appear to be powder for the realist
cannon. So I think it would be wise to remain skeptical about whether
the entire history of science or a consensus of its practitioners can be
made to speak unambiguously in favor of one side or the other in the
great philosophical debate between instrumentalism and realism.
Near the end of his paper Brenner draws attention to the somewhat
surprising fact that D u h e m did not ultimately rest content with mere
instrumentalism. In The Aim and Structure of Physical Theory, he
claims that the growing predictive success of science serves to indicate
that science is making progress toward a natural classification, a classification system that, so to speak, carves nature at the joints. Though
my own opinion is that this claim has a status in Duhem's thought
closer to a pious hope than to a demonstrated conclusion, I think it is
a bit puzzling that D u h e m considered it important to advance such a
claim. After all, a thoroughgoing instrumentalist does not have to take
a stand on the vexed question of whether science is approaching or will
converge on a natural classification. Why is D u h e m unwilling to engage
in skeptical suspense of judgment on this issue? Why, in other words,
does D u h e m think that successfully saving the appearances is not, in
the last analysis, success enough for science? Some interesting but
rather speculative answers to such questions emerge from considerations emphasized in Martin's paper.
Martin's account of Duhem's engagement with medieval science invokes a broad intellectual context that includes Duhem's religious concerns and those of his cultural environment. H e situates D u h e m in the
thought-world of the Dreyfus affair in politics, the modernist controversy in theology, and the revival of Thomistic scholasticism in French
Catholic philosophical circles. As he s~ces it, D u h e m was not moved to
study medieval science by disinterested historical curiosity; Duhem's
agenda went beyond a simple desire to test his instrumentalism against
another part of the historical record. Nor is his interest in medieval
science to be explained by attributing to D u h e m as a Catholic intellectual a desire to support the neo-scholastic movement. Prominent in
that movement was the ambition to constrain science by insisting that
it be grounded in a Thomistic philosophy of nature, and D u h e m had
ample reasons, both personal and professional, to resist this attempt to
subordinate science to philosophy by mounting a defense of the autonomy of science. Since he had an interest in maintaining that science
fares badly if it is subordinated to philosophy or theology, it would

have suited Duhem quite well to think that the Middle Ages were,
scientifically speaking, dark ages.
According to Martin's narrative, Duhem discovered almost by accident that there had been good science done in the Middle Ages, and
this discovery precipitated an intellectual crisis. The pressing question
was whether the historical record could be used to show that science
had done well enough, or even especially well, when subordinated to
scholastic theology or philosophy. If it could, the historical case for the
claim that science must be autonomous if it is to make progress would
be undermined. So Duhem's project in the history of medieval science
was, Martin argues, to show that good medieval science was not in
fact grounded in or based on Aristotelian or Thomistic theology or
philosophy. And there is indeed evidence that such a concern shapes
the way Duhem thinks about medieval science. He assigns a pivotal
and liberating role in his own narration to the condemnation of various
Aristotelian theses by Etienne Tempier in 1277, and he makes much
of the connection between philosophical nominalism and scientific progress in the fourteenth century.
No doubt it is in principle possible for a thoroughgoing instrumentalist to mount a philosophically interesting defense of the autonomy of
science. One way to proceed is to demarcate the spheres of authority
of science and religion by means of an appeal to some version of the
Kantian distinction between phenomenal and noumenal realms. Science
concedes to religion exclusive cognitive access to the things in themselves of the noumenal realm; in return, religion yields to science
exclusive cognitive access to the appearances of the phenomenal realm.
The writ of science runs no farther than saving the appearances, but
within the phenomenal realm science is the supreme cognitive authority.
If this division of labor could be enforced, the protracted warfare
between science and religion could be brought to an end.
The trouble with such a defense of the autonomy of science is that,
in practice, some of the partisans of religion will not accept peace on
these terms. They are not willing to settle for coexistence with science
but instead demand that it submit to religious control. Neo-scholastic
thinkers of Duhem's day often insisted that it is Thomistic philosophy
of nature and not science that tells the real truth about the observable
natural order. It is easy to see how such a view can lead to a devaluation
of or even contempt for science, and such attitudes have not been
unknown in Catholic intellectual circles. These days we hear ominous

talk of Islamic science coming from the Islamic fundamentalists of Iran.
Closer to home, there is so-called 'creation science', allegedly based
on biblical revelation, and many Christian fundamentalists claim that
it rather than evolutionary biology is on the right track in accounting
for life on earth. If a strong defense of the autonomy of science is to
be mounted against such practical threats as those I have mentioned,
it seems to me of strategic importance to insist that science in its own
right can, at the very least, aspire to become an independent source of
cognitive access to the final truth about the natural order. I think it
makes sense to suppose that the whiff of realism in Duhem's talk about
approach to a natural classification is part and parcel of such a strong
defense. Even if there is a religious way of knowing that has exclusive
access to truth about supernatural things, Duhem is in a position to
maintain that it does not have exclusive access to the truth about nature
and so cannot on that account legitimately claim to control or preempt
scientific inquiry.
But if it is granted that autonomous scientific inquiry is an independent source of cognitive access to the natural order, there is no guarantee of perpetual peace between science and religion. Even if it does
not have exclusive cognitive access to the natural order, traditional
Christian theology has been committed to claims that have implications
for our understanding of nature. The Augustinian account of Adam's
fall, if taken literally in broad outline, makes some sort of historical
claim about a catastrophe in the remote human past. The Catholic
doctrine of Transubstantiation is framed in terms of concepts drawn
from an Aristotelian metaphysics of substance and accident. The most
distinctive of Christian doctrines, the Incarnation, places constraints
on the ways in which traditional Christians can consistently formulate
accounts of human nature. Though it may be hoped that in the long
run science and Christian theology will independently converge on a
unified account of nature, in the short run conflict between the best
science at a given time and the best theology of that time cannot
be ruled out in advance. If a realistically interpreted science were to
undermine the historical claim, the metaphysical framework or the
theories of human nature alluded to above, then traditional Christians
would come under increasing pressure to choose between backing off
to mere instrumentalism in philosophy of science and making deep
and perhaps unwelcome revisions in theology. If the retreat to mere
instrumentalism is precluded for the sake of maintaining a strong de-

fense of the autonomy of science, a delicate balancing act may be
required in order to negotiate successful resolutions to episodes of
conflict between science and theology. In such negotiations, it cannot
be assumed a priori that science has to be the fixed point, for scientific
conceptual schemes and ontologies have changed in the past and are
likely to do so in the future. But neither can it be assumed a priori that
theology has to be the fixed point, since ecclesiastical doctrine has
developed over the centuries and will doubtless continue to do so. And,
of course, the whole enterprise of conflict resolution is only made more
complicated by the fact that Christianity is not the only religion whose
theology has implications for our understanding of nature and so can
claim to be a source of cognitive access to the natural order.
So when we locate Duhem in the larger context of the theological
controversies of his culture, some problems emerge that are not merely
of antiquarian interest to those of us who take the cognitive claims of
both science and religion seriously. One moral I would draw from
considering Duhem in this context is that a strong defense of the
autonomy of science may carry with it an unpredictable theological
price. But I do not think this exhausts what Duhem has to teach us
about how to cope with the conflicts between science and religion that
persist in our own culture, and so it seems to me there is much to be
learned from studies of Duhem which, like Martin's, situate his thought
in its religious context.
NOTE
, These comments are based on the versions of their papers that Brenner and Martin
presented at the Conference on Pierre Duhem: Historian and Philosopher of Science and
do not take into account any subsequent revisions they may have made in those papers.
Department of Philosophy
University of Notre Dame
Notre Dame, Indiana 46556
U.S.A.

EINSTEIN AND DUHEM*

ABSTRACT. Pierre Duhem's often unrecognized influence on twentieth-century philosophy of science is illustrated by an analysis of his significant if also largely unrecognized
influence on Albert Einstein. Einstein's first acquaintance with Duhem's La Thgorie
physique, son obfet et sa structure around 1909 is strongly suggested by his close personal
and professional relationship with Duhem's German translator, Friedrich Adler. The
central role of a Duhemian holistic, underdeterminationist variety of conventionalism in
Einstein's thought is examined at length, with special emphasis on Einstein's deployment
of Duhemian arguments in his debates with neo-Kantian interpreters of relativity and in
his critique of the empiricist doctrines of theory testing advanced by Schlick, Reichenbach,
and Carnap. Most striking is Einstein's 1949 criticism of the verificationist conception of
meaning from a holistic point of view, anticipating by two years the rather similar, but
more famous criticism advanced independently by Quine in 'Two Dogmas of Empiricism'.

The typical story of the influence of Pierre Duhem's philosophy of
science outside of French philosophical circles begins with Otto Neurath
and ends with Willard V. O. Quine. There is more than a little truth
to this story. Duhem's influence on Neurath was significant, direct,
and generously acknowledged. 1 His influence on Quine was equally
significant, though indirect (Neurath was the principal intermediary),
with Quine himself having been unaware of the parallel between his
and Duhem's views until it was pointed out to him by others. 2 And it
is primarily through Quine's writings that Duhem's ideas have retained
what currency they have in contemporary debates in the philosophy of
science.
But the story is far from complete, and it leaves one with the clear
impression that Duhem's holistic variety of conventionalism has been
far less influential than the views of other thinkers like Mach, Poincar~,
Russell, Wittgenstein, Schlick, and Carnap. I think that this impression
is misleading. I think that we have, for years, and for a variety of
reasons, underestimated Duhem's influence on twentieth-century philosophy of science. 3 And I will defend this thesis by exhibiting what I
regard as the pronounced 'Duhemian' features of Albert Einstein's
mature philosophy of science. I do not claim that Einstein's philosophy
of science is through and through Duhemian; no such simple description
can adequately characterize the views o f a thinker like Einstein, who
Synthese 83: 363-384, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

aimed, deliberately, not to be a systematic philosopher and who took
the philosophical turn only when driven that way by problems arising
in his scientific work. Instead, I want to argue (1) that recognition
of the 'Duhemian' features is essential for understanding Einstein's
philosophy of science, and (2) that the central place of the 'Duhemian'
elements in Einstein's thinking is evidence of the profound and pervasive, if not always well-recognized influence of Duhem's ideas within
twentieth-century philosophy of science.
1.

EINSTEIN'S

FIRST
LA

ACQUAINTANCE

THI~ORIE

WITH

DUHEM'S

PHYSIQUE

Let us begin by exploring the context of Einstein's first acquaintance
with Duhem's major work in the philosophy of science, La Th4orie
physique, son objet et sa structure (1906), which appeared in a German
edition in 1908 under the title Ziel und Struktur der physikalischen
Theorien. It was translated by Friedrich Adler, an ardent follower of
Ernst Mach, who himself contributed a sympathetic foreword. In at
least two respects, the involvement of Adler and Math is significant for
understanding Einstein's acquaintance with the text.
From the point of view of intellectual history, the involvement of
Adler and Math tells us something about the contemporary reception
of Duhem's views at least among German-speaking philosophers of
science, namely, that many thinkers saw no serious conflict between
the views of Mach and Duhem, that both were seen as part of a larger
anti-metaphysical movement in the philosophy of science emphasizing
the economical and descriptive side of scientific theorizing. Mach's own
characterization of Duhem's main thesis is instructive:
The author shows how physical theory gradually transforms itself from a presumptive
explanation on the basis of a vulgar or more or less scientific metaphysics into a system
resting on a few principles, a system of mathematical propositions that economically
describe and classify our experiences. In this process the explanatory picture changes
many times, until finally it falls away entirely, while the descriptive part passes over into
the new, more complete theory almost u n c h a n g e d . . . Duhem regards the model, like
the picture, as a parasitic growth. (Math 1908, pp. iii-iv)

And Adler's characterization echoes Mach's: "The elimination of all
metaphysics constitutes the fundamental tendency of thework, and the
principle of the economy of thought, which Math first formulated, is
consistently maintained" (Adler 1908b, p. vi). There were, of course,

some issues about which Mach and Duhem disagreed, as Adler dutifully
and carefully indicated. Duhem, for example, did not consider any
foundation for scientific concept formation like Mach's "elements of
sensation" (Adler 1908, p. vi); such crude 'atomistic' reductionism,
vesting not only each admissible proposition but each admissible concept with its own, individual empirical content, would be incompatible
with Duhem's holism. Nor did Duhem require, as Mach would, that
'hypotheses' have an empirical basis and serve merely as tools for
organizing experience (Adler 1908, pp. vi-vii); Duhem rejected such
constraints also on the basis of his holistic conception of theories,
arguing that entire theories must have empirical content, but that individual hypotheses could not (Duhem 1906, pp~ 215-16). 4 With hindsight, we might regard these as serious and fundamental disagreements,
as they indeed turned out to be, but the point is that Mach and contemporary Machians like Adler did not; they minimized the differences
and stressed the broad areas of agreement.
Further evidence of Duhem's friendly reception by Mach and his
followers is easily assembled. Thus, for example, the just-published La
Thdorie physique receives high praise from Mach in the foreword to
the second edition (1906) of Erkenntnis und Irrtum, Mach's last systematic work on epistemology and the philosophy of science, 5 and it is
cited numerous times in the annotations. Especially noteworthy are
Mach's seemingly approving mentions of the characteristically 'Duhemian' theses of the theory-ladenness of observation, 6 and the holistic
character of all~ hypothesis testing. 7 There is also Mach's gracious acknowledgment of Duhem's role in "the epistemological discussions"
and of Duhem's "valuable" critical remarks in the foreword to the
seventh edition of his Mechanik (1912, p. ix). S And there is, finally,
the fact that another one of Duhem's major works, his L'Evolution de
la mdcanique (1903a), was translated in 1912 by Philipp Frank, also an
enthusiastic follower of Mach's. 9 As Frank explained some years later,
he and many of his contemporaries regarded the views of Duhem and
Mach as being quite compatible, both examples of what the philosopher
Abel Rey dubbed the "new positivism".s° Like Adler and Mach himself, Frank stressed the common anti-metaphysical tendency of Mach's
and Duhem's theories of scientific method, but he also emphasized
theoretical holism as one of the principal features of Duhem's position
of interest to him and his contemporaries (Frank 1949, pp. 25-28). 11
The sympathetic reception by Mach and his followers may not reflect

a wholly accurate reading of Duhem. The one thesis that has proven
to be D u h e m ' s major contribution to discussions of scientific method his theoretical h o l i s m - i s simply incompatible with the reductionistic
and atomistic empiricism in Mach's epistemology. But that does not
change the fact crucial for the story I want to tell here, which is that
the Machians' public sympathy for D u h e m would have prepared the
ground for a similarly sympathetic reading by other thinkers, like
Einstein, already favorably inclined toward Mach. 12
Perhaps even m o r e important for my story, however, is specifically
the involvement of Friedrich Adler as the translator of La Thgorie
physique. It is important because of the personal relationship between
Adler and Einstein.
Einstein and Adler were both students of physics in Zurich around
the turn of the century, Einstein at the E T H , Adler at the University
of Zurich.13 Both completed dissertations under Alfred Kleiner at the
University of Zurich, 14 and, finally, both were candidates for the Extraordinary Professorship in physics at the University of Zurich to which
Einstein was appointed in 1909.15 They had been acquainted with one
another from their student days, Einstein apparently having first sought
out Adler upon hearing that he was working on a dissertation on specific
heats. They reportedly met often to discuss questions of physics, and,
together with their future wives, who were also physics students, they
audited lectures at the E T H ? 6
When Einstein returned to Zurich in the fall of 1909 to assume his
new position at the university, he and his wife happened to rent an
a p a r t m e n t immediately upstairs from the Adlers at Moussonstraf3e 12.
The old relationship between the families, both now with children,
was quickly resumed. But more importantly, the renewed personal
relationship led to a renewal of the intellectual relationship between
Einstein and Adler. In order to escape the noise of the children, they
would retire to the attic, where they could work and carry on their
discussions in relative quiet. 17 Adler described their relationship in a
letter to his parents of 28 October 1909:
We stand on very good terms with Einstein, who lives above us, and indeed as it happens,
among all of the academics, we are on the most intimate terms precisely with him. They
have a bohemian household similar to ours, one boy of Assinka's age, who is very often
at our place... The more I speak with Einstein - and that happens fairly often - the more
I see that my favorable opinion of him was justified. Among contemporary physicists he
is not only one of the clearest, but also one of the most independent minds, and we are

of one mind about questionswhose place is generallynot understoodby the majorityof
other physicists. (Ardelt 1984, p. 166)
The Adlers and Einsteins lived as neighbors until the spring of 1911.18
Einstein and Adler shared more than an address and a profession.
They shared also the interest in the philosophy of science in general,
and in Mach's work in particular, that was typical of many students in
Zurich at that time, Zurich being as it were the Swiss second home of
positivism, owing to the fact of Richard Avenarius's having taught at
the University of Zurich from 1877 to his death in 1896. Einstein was
introduced to Mach's writings by his friend Michele Besso during their
student days at the ETH and quickly developed an appreciation for
Mach's style of conceptual criticism? 9 Adler also first read Mach during
his student days (Ardelt 1984, p. 98). Having started out as a follower
of Friedrich Engels's brand of materialism, he was slow to warm to
the anti-metaphysical Mach, but by 1905, when he published a paper
criticizing the epistemological assumptions underlying Ostwald's energeticist program from the point of view of Mach and Avenarius (Adler
1905), he had been won over to the cause (Ardelt 1984, pp. 98-99,
125-37). 2o Adler and Mach began corresponding in 1903 (see Blackmore and Hentschel 1985, pp. 30-31), meeting personally for the first
time in May 1905 (Ardelt 1984, p. 136), after which Adler went on to
become a frequent public spokesman for Mach. 21
So by the time when Einstein became the fellow bohemian Adler's
upstairs neighbor and companion in attic conversation in the fall of
1909, Adler was a close colleague and prominent supporter of Mach's.
It was that very autumn when Adler wrote his spirited defense of Mach
against Planck's widely-discussed criticisms. 22 Just a few months earlier,
in July or August, Einstein's own correspondence with Mach had
begun, apparently with the help of Adler. 23
And it had been just one year since the publication of Adler's translation of Duhem's La Thdorie physique (1908). 24 Under these circumstances, it seems to me highly likely that Einstein's first acquaintance
with Duhem's work can be dated to no later than the fall of 1909.
There is no documentation of his having read La Thdorie physique at
this time, but given the nature of his relationship with Adler, given
their mutual interests in Mach and the philosophy of science, and given
Adler's role in translating La Thdorie physique, it is hard to imagine

that Einstein would not at least have learned about the work through
discussion with Adler. A n d my guess is that he probably also then read
it for the first time. But whether he read La Th~orie physique at this
time or merely discussed it with Adler, his acquaintance with D u h e m
would have been conditioned by the context, a context in which the
community of interest between Mach and D u h e m as proponents of the
'new positivism' would have been featured, a context that would have
predisposed Einstein to sympathy with Duhem.
When exactly Einstein did read La Th~orie physique for the first time
is not clear. That he did read it and had a favorable opinion of it is
evident, however, from the one and only apparent reference to the
b o o k that I have found in his writings and correspondence. It is in a
letter of September 1918 from Einstein to the Bonn mathematician
Eduard Study. Einstein had written to Study on 17 September ( E A
22-301) praising Study's book, Die realistische Weltansicht und die
Lehre vom Raume (1914), but suggesting that he did not agree with all
of Study's views. In his reply of 23 September ( E A 22-304), Study
asked Einstein to elaborate on his criticism, and Einstein answered on
25 September ( E A 22-307) with a three-page letter setting out his
reaction in detail.
The main thrust of Einstein's criticism concerns Study's defense of
scientific realism, the principal aim of the book. Einstein says that the
proposition " T h e physical world is real" appears to him "meaningless"
(sinnIos), as if one were to say " T h e physical world is cock-a-doodled o o " (Die KOrperweh ist kikeriki); he adds that to him the "real" is
"an in itself empty, meaningless category". A n d he concludes, "I concede that the natural sciences concern the 'real', but I am still not a
'realist'"
B u t then, as if to balance his criticism of the realist, Einstein offers
this criticism of the positivist:
The positivist or pragmatist is strong as long as he battles against the opinion that there

[are] concepts that are anchored in the "A priori." When, in his enthusiasm, [he] forgets
that all knowledge consists [in] concepts and judgments, then that is a weakness that lies
not in the nature of things but in his personal disposition/just as with the senseless battle
against hypotheses, cf. the clear book by Duhem/. In any case, the railing against atoms
rests upon this weakness. Oh, how hard things are for man in this world; the path to
originality leads through unreason (in the sciences), through ugliness (in the arts)-at
least the path that many find passable. (EA 22-307)
That the interlineated remark about D u h e m is joined to a criticism of

the positivist attack on hypotheses makes it clear that the book intended
is La Thdorie physique, and that Einstein had in mind specifically
sections 8 and 9 of chapter 6, along with the whole of chapter 7. 25 This
is where Duhem defends the role of hypotheses against overly restrictive
empiricist demands that every admissible scientific proposition possess
its own empirical content, arguing, again, that while whole theories
must have empirical content, the individual hypotheses constituting
those theories cannot.
Given Einstein's relationship with Adler, and my conjecture that he
first learned about Duhem through Adler, it is striking that he emphasizes here as a principal virtue of La Thdorie physique vis h vis the
positivism of Mach one of the two differences between Mach and
Duhem that Adler had pointed to in his preface to the translation of
La Th(orie physique. But whereas Acller downplayed the significance
of such differences between Mach and Duhem, Einstein stresses them.
As we shall see later, it was precisely this thesis about the lack of
empirical content of individual hypotheses that proved to be Duhem's
main legacy to Einstein and that constituted the crucial difference
between Einstein's empiricism and that of the Vienna 'and Berlin empiricists.
2.

UNDERDETERMINATION,
IN

EINSTEIN'S

HOLISM,
PHILOSOPHY

AND
OF

CONVENTIONALISM
SCIENCE

Conventionalism first emerges as an explicit theme in Einstein's thinking in the mid- to late 1910s, partly in response to certain conceptual
problems encountered in the development of general relativity, and
under the significant influence of Moritz Schlick, himself then still the
realist and conventionalist of his pre-Vienna days. 26 Einstein and
Schlick most often brought out their conventionalist arguments in reply
to attempts by various neo-Kantians to defend Kant against general
relativity's threat to the claimed a priori character of Euclidean geometry. 27
In a series of essays and reviews during the early 1920s, 28 Einstein
and Schlick agreed with the neo-Kantians that empirical evidence
underdetermines theory choice, especially the choice of deep theoretical
principles like the axioms of geometry; but whereas the neo-Kantians
exploited the fact of underdetermination to insulate cherished principles
from empirical refutation, and insisted that our choice among the alter-

native theories equally compatible with experience is d e t e r m i n e d by a

priori considerations, Einstein and Schlick argued that no principle is
i m m u n e to rejection or revision in the light of experience, and insisted
that the choice a m o n g alternative theories is a m a t t e r of convention,
guided at most by considerations of simplicity. I n d e e d , this is one of
the roots of Einstein's frequent talk of theories being "free creations
of the h u m a n intellect" (for example, Einstein 1921, p. 5).
The kind of conventionalism that Schlick and Einstein d e p l o y e d in
response to the n e o - K a n t i a n s o w e d at least as m u c h to Poincar6 (1902,
1905) as to D u h e m . But the distinctively D u h e m i a n themes of holism
and u n d e r d e t e r m i n a t i o n often came to the fore, especially in Einstein's
writings o f the period.
Consider, first, the t h e m e of u n d e r d e t e r m i n a t i o n . In a r e m a r k a b l e
letter to Schlick of 21 M a y 1917, Einstein wrote:
If two different peoples pursue physics independently of one another, they will create
systems that certainly agree as regards the impressions ('elements' in Mach's sense). The
mental constructions that the two devise for connecting these 'elements' can be vastly
different. And the two constructions need not agree as regards the "events'; for these
surely belong to the conceptual constructions. (EA 21-618)
(By " e v e n t s " Einstein means the points of the space-time manifold
constituting a t h e o r y ' s f u n d a m e n t a l ontology.) A n d in his address on
the occasion of Planck's sixtieth birthday (26 April 1918), Einstein
wrote:
The supreme task of the physicist is... the search for those most general, elementary
laws from which the world picture is to be obtained through pure deduction. No logical
path leads to these elementary laws; it is instead just the intuition that rests on an
empathic understanding of experience. In this state of methodological uncertainty one
can think that arbitrarily many, in themselves equally justified systems of theoretical
principles were possible; and this opinion is, in principle, certainly correct. But the
development of physics has shown that of all the conceivable theoretical constructions a
single one has, at any given time, proved itself unconditionally superior to all the others.
No one who has really gone deeply into the subject will deny that, in practice, the world
of perceptions determines the theoretical system unambiguously, even though no logical
path leads from the perceptions to the basic principles of the theory. (Einstein 1918, p.
31)
This passage is especially interesting for the way it contrasts the logical
fact of u n d e r d e t e r m i n a t i o n with the practical fact of u n a m b i g u o u s determination, exactly the same ironic contrast having b e e n stressed by
D u h e m . 29

Perhaps the most definitive statement of the underdeterminationist
t h e s i s is f o u n d in a l i t t l e - k n o w n n e w s p a p e r a r t i c l e o f E i n s t e i n ' s , e n t i t l e d
' I n d u k t i o n u n d D e d u k t i o n in d e r P h y s i k ' , t h a t a p p e a r e d o n C h r i s t m a s
d a y 1919 in t h e Berliner Tageblatt. E i n s t e i n w r o t e :
A theory can thus be recognized as erroneous if there is a logical error in its deductions,
or as incorrect if a fact is not in agreement with its consequences. But the truth of a
theory can never be proven. For one never knows that even in the future no experience
will be encountered that contradicts its consequences; and still other systems of thought
are always conceivable that are capable of joining together the same given facts. If two
theories are available, both of which are compatible with the given factual material, then
there is no other criterion for preferring the one or the other than the intuitive view of
the researcher. Thus we may understand how sharp-witted researchers, who have command of theories and facts, can still be passionate supporters of contradictory theories.
(Einstein 1919, p. 1)
N o t i c e h e r e E i n s t e i n ' s c a r e f u l d i s t i n c t i o n b e t w e e n n o r m a l H u m e a n ind u c t i v e u n c e r t a i n t y - t h e s t a n d i n g p o s s i b i l i t y t h a t n e w facts will arise
that are incompatible with accepted theories - and Duhemian underdetermination - the necessary existence of alternative theories equally
c a p a b l e o f e x p l a i n i n g t h e s a m e facts.
H o l i s m is i m p l i c i t l y a s s u m e d at e v e r y m e n t i o n o f u n d e r d e t e r m i n a t i o n
- there are empirically equivalent alternative theories precisely because
it is t h e o r i e s as a w h o l e , n o t i n d i v i d u a l h y p o t h e s e s , t h a t s t a n d t h e test
o f e x p e r i e n c e . B u t e x p l i c i t l y h o l i s t i c a r g u m e n t s a r e n o t c o m m o n in
E i n s t e i n ' s w r i t i n g s f r o m t h e 1910s a n d 1920s. T h e o n l y e x a m p l e I h a v e
f o u n d is in o n e o f E i n s t e i n ' s r e v i e w s o f a n e o - K a n t i a n w o r k o n r e l a t i v i t y ,
A l f r e d E l s b a c h ' s K a n t u n d Einstein ( E l s b a c h 1924), w h e r e , a f t e r a s s e r t ing t h a t r e l a t i v i t y t h e o r y is i n c o m p a t i b l e w i t h t h e K a n t i a n d o c t r i n e o f
t h e a priori, E i n s t e i n w r o t e :
This does not, at first, preclude one's holding at least to the Kantian problematic, as,
e.g., Cassirer has done. I am even of the opinion that this standpoint can be rigorously
refuted by no development of natural science. For one will always be able to say that
critical philosophers have until now erred in the establishment of the a priori elements,
and one will always be able to establish a system of a priori elements that does not
contradict a given physical system. Let me briefly indicate why I do not find this standpoint
natural. A physical theory consists of the parts (elements) A, B, C, D, that together
constitute a logical whole which correctly connects the pertinent experiments (sense
experiences). Then it tends to be the case that the aggregate of fewer than all four
elements, e.g., A, B, D, without C, no longer says anything about these experiences,
and just as well A, B, C without D. One is then free to regard the aggregate of three of
these elements, e.g., A, B, C as a priori, and only D as empirically conditioned. But
what remains unsatisfactory in this is always the arbitrariness in the choice of those

elements that one designatesas a priori, entirely apart from the fact that the theory could
one day be replaced by another that replaces certain of these elements (or all four) by
others. (Einstein 1924b, pp. 1688-89)
This passage deserves careful attention. For one thing, it anticipates
the still more sophisticated holistic arguments we will find Einstein
advancing in the late 1940s in opposition to the empiricist theories of
meaning. More immediately, however, it points up the reasons for the
parting of the ways that was shortly to occur between Einstein and
Schlick in their respective understandings of the role of conventions in
science.
By 1925, when the second edition of the Allgemeine Erkenntnislehre
appeared, Schlick had adopted the more refined interpretation of the
conventionalist thesis we now associate with the members of the Vienna
Circle and its allies like Hans Reichenbach. More clearly than in the first
edition of the Erkenntnislehre, Schlick now insisted on a fundamental
distinction between two types of propositions constituting a theory:
analytic coordinating definitions and synthetic empirical propositions.
He argued that only the former are conventional and that once they
are fixed by convention the truth or falsity of the individual empirical
propositions is unambiguously determined by experience - quite the
contrary of Duhem's position (Schlick 1925, pp. 89-101). 30 Schlick and
the other defenders of this position, like Reichenbach, 31 seem to have
been driven to it by the logic of their argument with the neo-Kantians.
As Einstein noted in his review of Elsbach, merely asserting that a
theory as a whole possesses empirical import is logically not sufficient
to force the hand of the neo-Kantian, who can always then protect
cherished, allegedly a priori principles from empirical refutation by
electing to abandon other elements of the theory when confronted
with empirical evidence incompatible with the theory's predictions.
Presumably not satisfied with Einstein's subtle criticism that the choice
of which propositions to protect is entirely arbitrary, Schlick and Reichenbach seem to have wanted a more decisive reply to the neo-Kantian,
one that would logically imply the empirical corrigibility of each individual synthetic proposition the neo-Kantian might want to defend, such
as Euclid's fifth postulate. Hence the distinction between coordinating
definitions and empirical propositions, and the claim that only the
definitions are conventional.
The Schlick-Reichenbach conception of conventionalism stands or
falls with the analytic-synthetic distinction, which provides the only

basis for distinguishing between coordinating definitions and empirical
propositions. Consistent Duhemians do not endorse the analyticsynthetic distinction, but that was not how Einstein criticized Schlick
and Reichenbada. Instead, he used the same argument he used against
the neo-Kantians, namely, that such distinctions among the propositions
constituting a theory - whether between a priori and a posteriori propositions or between coordinating definitions and empirical hypotheses is arbitrary, and hence, presumably, of no fundamental epistemological
significance. One finds this argument in Einstein's classic 1936 essay,
'Physik und Realit~it', where Einstein ever so gently qualifies what might
appear to be an endorsement of the Schlick-Reichenbach position:
We shall call 'primary concepts' such concepts as are directly and intuitively connected
with typical complexes of sense experiences. All other concepts are - from the physical
point of view - meaningful only insofar as they are brought into connection with the
'primary concepts' through statements. These statements are partly definitions of the
concepts (and of the statements logically derivable from them) and partly statements that
are not derivable from the definitions, and that express at least indirect relations between
the 'primary concepts' and thereby between sense experiences. Statements of the latter
kind are 'statements about reality' or 'laws of nature', i.e., statements that have to prove
themselves on the sense experiences that are comprehended in the primary concepts.
Which o f the statements are to be regarded as definitions and which as laws o f nature
depends largely upon the chosen representation; in general it is only necessary to carry
through such a distinction when one wants to investigate to what extent the whole conceptual
system under consideration really possesses content from a physical standpoint. (Einstein
1936, p. 316; emphasis mine)

See how the holistic viewpoint is insinuated at the end: We need
only make a distinction between definitions and empirical propositions
when we desire to determine the empirical content of the "whole
conceptual system", and even then, where we draw the line "depends
largely upon the chosen representation".

3. E I N S T E I N ' S
CONCEPTIONS

'DUHEMIAN'

CRITIQUE

OF

OF M E A N I N G AND T H E O R Y

EMPIRICIST
TESTING

Over the years, Einstein grew ever more impatient with the failure
of Schlick, Reiehenbach, Carnap, and their allies to understand his
reservations about their view of the structure of theories and the relation between theory and evidence. His summary opinion was stated
clearly, and with acid sarcasm, in a letter to Paul Schilpp of 19 May
1953, declining Schilpp's invitation to contribute a paper to the Carnap

v o l u m e of the Library of Living Philosophers:
It is a good idea to devote a volume of your collection to Carnap's life's work. But I
cannot comply with your request. That is to say, I have come to terms with this slippery

material from time to time only when my own problems made it urgently necessary. But
even then I have studied only a little literature, so that I cannot do justice to the swarm
of incessantly twittering positivistic little birds . . . . Between you and me, I think that
the old positivistic horse, which originally appeared so fresh and frisky, has become a
pitiful skeleton following the refinements that it has perforce gone through, and that it
has dedicated itself to a rather arid hair-splitting. In its youthful days it nourished itself
on the weaknesses of its opponents. Now it has grown respectable and is in the difficult
position of having to prolong its existence under its own power, poor thing. (EA 42-534)
Some of the reasons for Einstein's growing d i s e n c h a n t m e n t with positivism e m e r g e in his reply to R e i c h e n b a c h ' s contribution to the Library
of Living Philosophers v o l u m e on Einstein himself. A n d it is clear
f r o m this exchange that the p r o b l e m c o n c e r n e d precisely the failure
of R e i c h e n b a c h and his colleagues to appreciate the implications of
D u h e m i a n holism.
R e i c h e n b a c h had d e f e n d e d a view of the empirical character of geo m e t r y not unlike that which Einstein himself had d e f e n d e d years
earlier in his influential Geometrie und Erfahrung (Einstein 1921), 32
with the exception that R e i c h e n b a c h invoked explicitly the distinction
b e t w e e n coordinating definitions and empirical hypotheses, interpreting
Einstein's identification of the g e o m e t e r ' s 'rigid b o d y ' with the physicist's 'practically rigid rod' as an instance of a coordinating definition
(the definition of ' c o n g r u e n c e ' ) :
The choice of a geometry is arbitrary only so long as no definition of congruence is
specified. Once this definition is set up, it becomes an empirical question whichgeometry
holds for physical space . . . . The conventionalist overlooks the fact that only the incomplete statement of a geometry, in which a reference to the definition of congruence is
omitted, is arbitrary. (Reichenbach 1949, p. 297)
AS one might expect, Einstein did not agree. But instead of just saying
so, he c o u c h e d his criticism in the amusing f o r m of an imaginary dialogue b e t w e e n ' R e i c h e n b a c h ' and 'Poincar6'.
A crucial step in the dialogue has ' R e i c h e n b a c h ' grudgingly agreeing
with 'Poincar6' that, since there are no perfectly rigid bodies in nature,
and since we must therefore e m p l o y o u r physics to correct for deform a t i o n s resulting f r o m things like changing t e m p e r a t u r e , we really wind
up testing the whole b o d y of t h e o r y consisting of g e o m e t r y plus physics,
and not just g e o m e t r y alone. A t this point, Einstein has an ' a n o n y m o u s

nonpositivist' takeover for Poincar6, out of respect, he says, "for Poincar6's superiority as thinker and author" (Einstein may also have realized that the view attributed to Poincar6 was more Duhem's than
Poincar6's). The nonpositivist observes that, in agreeing that geometry
and physics are tested together, Reichenbach has contravened one of
his own fundamental positivist principles - the equation of meaning
with verifiability:
Non-Positivist: If, under the stated circumstances, y o u h o l d distance to be a legitimate
concept, how then is it with your basic principle (meaning = verifiability)? Must you not
come to the point where you deny the meaning of geometrical statements and concede
meaning only to the completely developed theory of relativity (which still does not exist
at all as a finished product)? Must you not grant that no 'meaning' whatsoever, in your
sense, belongs to the individual concepts and statements of a physical theory, such
meaning belonging instead to the whole system insofar as it makes ~intelligible' what is

given in experience? Why do the individual concepts that occur in a theory require any
separate justification after all, if they are indispensable only within the framework of the
logical structure of the theory, and if it is the theory as a whole that stands the test?
(Einstein 1949, p. 678)33
Not only is this a strikingly clear statement of the implications of
Duhemian holism for our understanding of the empirical content of
scientific concepts and theories, it is also a remarkable anticipation of
the more famous criticism of the verificationist theory of meaning that
Quine advanced independently two years later in his well-known essay,
~Two Dogmas of Empiricism' (Quine 1951). 34

4. CONCLUSION
A sympathy for Duhemian conventionalism, with its emphasis on
underdetermination and theoretical holism, was an abiding and central
feature of Einstein's mature philosophy of science. It is one of the keys
to an understanding of his attitude toward neo-Kantianism as well as
his attitude toward logical empiricism. And it is a measure of the
significant (if sometimes almost subterranean) influence that Duhem's
philosophy of science has exerted throughout our century.
Let me offer now a final anecdote showing clearly where Einstein's
sympathies lay. It concerns not D u h e m directly, but the wonderful
image that Otto Neurath introduced for representing the Duhemian
ideas of holism and underdetermination, where he compares theory
choice to o u r having to reconstruct a ship not on firm footing in a dry

dock, but at sea, one plank at a time (Neurath 1932, p. 206). The story
is found in Rudolf Carnap's diary. On the 16th of November 1952,
Einstein's longtime friend Paul Oppenheim brought him to visit Carnap,
who was then staying in Princeton. The conversation touched upon
several topics, turning eventually to the subject of reality. Carnap records this exchange:
(2) On reality. I say that only Mach advanced such formulations according to which the
sense data are the only reality. He says that the positivists nevertheless want to start
from something securely given, and that there is no such starting point. I agree: there is
no rock bottom, Neurath's reconstruction of the ship afloat. With that he emphatically
agreed. (RC 025-80-01) 35
NOTES
* I wish to thank the Hebrew University of Jerusalem, which holds the copyright, for
permission to quote from the unpublished letters of Einstein. Items in the Einstein
Archive are cited by giving their number in the control index after the following format:
EA nn-nnn. Similar formats are employed for citing other archival material. Thus 'AA'
refers to material in the Adler Archive at the Verein ffir Geschichte der Arbeiterbewegung, Vienna; and 'RC' refers to material in the Rudolf Carnap collection at the
Archive for Scientific Philosophy, Department of Special Collections, Hillman Library,
University of Pittsburgh. The research for this paper was supported in part by a grant
from the National Science Foundation, No. SES-8420140, as well as by grants from the
Deutscher akademischer Austauschdienst, the American Philosophical Society, and the
University of Kentucky Research Foundation.
1 See Neurath 1916, p. 27, 1932, pp. 213-14, and the numerous references to Duhem in
Neurath's collected philosophical papers, Neurath (1983).
2 "When I wrote 'Two Dogmas of Empiricism', I had not read Einstein's reply to
Reichenbach, nor did I know of Duhem. My holism there was just my own common
sense, plus perhaps some influence from Neurath's congenial figure of the boat. After
'Two Dogmas' appeared, January 1951, both Hempel and Philipp Frank told me about
the kinship of my view to Duhem's; so I added the footnote citation of Duhem when 'Two
Dogmas' was reprinted in From a Logical Point o f View, 1953." (Private communication, 9
October 1986.) On the connection to Einstein, see below, note 34.
3 There are many reasons for the neglect. Foremost among them must be the fact that
Neurath, whose thinking most clearly reflected the influence of Duhem and who would
have been Duhem's foremost advocate, died immediately after the second world war
(1945), and never had the same opportunity as Reichenbach or Carnap to represent
Viennese philosophy of science to an English-speaking public. As it turned out, Neurath's
views were not often fairly represented, being interpreted to us primarily by the bornagain physicalist, Carnap, who never really appreciated how different were his and
Neurath's views. English-speaking philosophers - most of whom did not read Poincar~
or Duhem in the original - came to know conventionalism only in the form in which it
was presented by Schlick, Reichenbach, and Carnap. But as is explained below in Section
2, this version of conventionalism differs significantly from that of Duhem.

4 Mach also worried that the Catholic Duhem had an ulterior motive: "Given the power
and influence that scholasticism and Catholicism still have in France, it is nevertheless
possible that Duhem is nurturing some kind of devil in the background; he is after all
an admirer of Thomas Aquinas, something of which he makes no secret at all. But of
what consequence is that, as long as he does not turn the devil loose? Perhaps he wants
to free physics of metaphysics only in order to win elbow-room for the latter over against
physics. Philosophers and theologians can do what they will with metaphysics. If by that
the physicists, physiologists, and psychologists accustom themselves to making do without
metaphysics, then all is won". He concluded: "For the time being I am quite content
with the degree of agreement with Duhem". (Mach to Adler, 22 April 1908, in Blackmore
and Hentschel 1985, p. 50.)
s Mach writes: "I was very pleased by Duhem's work, 'La Throrie physique, son objet
et sa structure' (1906). I had not yet hoped to find such thoroughgoing agreement on the
part of physicists. Duhem repudiates any metaphysical conception of questions in physics;
he views the conceptually-economical determination of the factual as the aim of physics . . . . The agreement between us is all the more precious to me, since Duhem arrived
at the same results wholly independently". (1906, p. x.)
6 "Claude Bernard advises us to disregard all theory in experimental investigations, to
leave theory at the door. Duhem rightly objects that this is impossible in physics, where
experiment without theory is incomprehensible . . . . In fact, one can only recommend
that attention be given to whether or not the experimental result is on the whole compatible with the assumed theory. Cf. Duhem (La Throrie physique, pp. 297f)". (Mach 1906,
p. 202, n. 3.)
7 "Duhem (La Throrie physique, pp. 364f) explains that hypotheses are not so much
chosen by the researcher, arbitrarily and at will, but rather force themselves upon the
researcher in the course of historical development, under the impress of facts that are
gradually becoming known. Such a hypothesis usually consists of a whole complex of
ideas. If a result then arises, e.g., through an 'experimentum crucis', that is incompatible
with a hypothesis, then for the time being one can only regard it as contradicting the
entire complex of ideas. On this latter point cf. Duhem, l.c., pp. 311f". (Mach 1906, p.
244, n, 1.)
8 What form these 'epistemological discussions' took is not clear. There was a modest
correspondence between Duhem and Mach, lasting from 1903 to at least 1909, but as
Stanley Jaki puts i~:, the letters 'contain only generalities' (1984, p. 380). The 'valuable'
critical remarks were presumably those contained in Duhem's review (1903b) of the
French edition (1904) of the Mechanik, remarks for which Mach thanked Duhem in a
letter of 15 May 1904 (published, along with the rest of the Mach-Duhem correspondence,
in Hentschel 1988, p. 78).
9 See Frank (1917) for a summary of Frank's views on Mach. For more on the relationship
between Mach and Frank, see Frank (1941), pp. 18-30, Blackmore (1972), and Wolters
(1987) (which corrects a number of errors in Blackmore).
lo Rey (1907), pp. 392ff; cited in Frank (1949), p. 21. In one essay Frank called Duhem
the "most important representative of the Machian line of thinking in France" (Frank
1917, p. 66).
11 For more on the relationship between Mach and Duhem, see Paty (1986), Jaki (1984),
pp. 319-73, and Blackmore (1972), pp. 196--7. For different reasons, the latter two

discussions should be read with care. Blackmore exaggerates the extent of Mach's influence on Duhem, whereas Jaki too quickly dismisses the "stereotype classification of
Duhem as representative of positivism" (p. 358), arguing that it ignores the significant
realistic and metaphysical strain in Duhem's thinking. Jaki does not stress sufficiently
the distinction - absolutely necessary for understanding the contemporary reception of
Duhem's views - between Duhem's broader philosophical, metaphysical, and theological
commitments (clearly recognized by Mach, as shown by the letter to Adler quoted above
in note 4) and his more restricted views on the methodology of physics. It was the latter
that excited the interest of contemporary philosophers of science, and it would be seriously misleading to describe Duhem's views on scientific methodology as a version of
scientific realism; the Duhemian thesis of underdetermination is inherently antithetical
to a realistic conception of scientific method. Some of the most insightful comments on
the relationship between Duhem and Mach and on Duhem's influence on the members
of the Vienna Circle are found in the work of Rudolf Haller; see especially Hailer (1982,
1985, 1988).
Another implication of Mach's sympathy for Duhem should not be overlooked. The
Mach who is so enamored of Duhem cannot be the niggardly positivist often presented
to us in the secondary literature. In particular, the Mach who reads La Thdorie physique
with enthusiasm must have a more liberal attitude toward the role of hypotheses in
physics than many of his critics grant him. One scholar who has already argued for this
more liberal interpretation of Mach on other grounds is Gereon Wolters; see Wolters
(1987), pp. 101-20, and (1988).
12 For more on Einstein's attitude toward Mach, see Blackmore (1972), pp. 247-85 and
Wolters (1987), pp. 11-171, which corrects some errors in Blackmore's treatment of these
topics.
13 Einstein studied at the ETH from 1896 to 1900; for documentation on Einstein's years
at the ETH, see Einstein (1987). Adler was at the University of Zurich from 1897 to
1901; see Ardelt (1984), pp. 71-111.
14 Adler's dissertation was completed in 1902 (Adler 1902); for background, see Ardelt
1984, pp. 101-11. Einstein's was completed in 1905 (Einstein 1905) after an abortive
earlier attempt at about the same time Adler finished his dissertation; for background
on both the 1905 dissertation and the earlier attempt, see Einstein (1989), pp. 170-82.
15 Einstein, of course, had been working since 1902 as a clerk in the Swiss Federal Patent
Office in Bern (see Seelig 1960, pp. 89-160). Adler had been a Privatdozent in physics
at the University of Zurich for the previous two and one half years, having received on
13 December 1906 the Venia legendi for "experimental and theoretical physics, as well
as their history and epistemological foundations" (Ardelt 1984, p. 157--66).
16 For background on the relationship see Seelig (1960), pp. 162-4. The lectures they
attended were either Minkowski's lectures on 'Analytische Mechanik', winter semester
1898/1899, or his lectures on ~Anwendungen der analytischen Mechanik', summer semester 1900 (Einstein 1987, pp. 367,369). See also Adler to Heinrich Braun, 22 January
1919, EA 6-013: "I have been well acquainted with Einstein from our time together as
students in Zurich".
17 See Seelig (1960), p. 165. Adler himself recalled these conversations in the first letter
he wrote to Einstein after his imprisonment for assassinating the Austrian MinisterPresident, Count Stiirgkh; see Adler to Einstein, 9 March 1917, EA 6-001.
18 In March 1911, Einstein moved to Prague to take up the chair in physics at the Charles

University (Seelig 1960, p. 203). At the end of May, Adler moved to Vienna to take up
a position as secretary to the Austrian social democratic party, one of whose founders
was Adler's father, Viktor (Ardelt 1984, p. 215).
19 For more on Einstein's first acquaintance with Mach, see Wolters (1987) and the
introduction to Einstein (1989). Einstein frequently expressed his debt to Mach; see for
example Einstein (1916).
2o Ardelt (1984) is also a good source to consult on the interesting role played by Mach's
philosophy of science in debates over the interpretation of Marxism that pitted Adler
and many of his Austrian colleagues, who were influenced by Mach's anti-metaphysical
arguments, against doctrinaire materialist Marxists like Lenin. Adler is one of the targets
of criticism in Lenin's Materialism and Empirio-Criticism (see, for example, Lenin 1909,
p. 46).
21 See, for example, Adler (1908a). For more on the relationship between Adler and
Maeh, see Ardelt (1984), Blackmore (1972), and Wolters (1987).
22 Adler (1909), Planck (1909). Adler's paper appeared on 26 December 1909. Mach
himself replied the following year (Mach 1910), eliciting a final rejoinder from Planck,
in which Adler's reply is cited (Plank 1910, p. 1188).
23 Near the end of a letter to Adler of 26 July 1909, Mach asks: "Is Einstein still in
Bern? I want to send him a copy also". (Mach was referring to a copy of the new second
edition of his Erhahung der Arbeit, 1909.) Einstein's first letter to Mach of 9 August 1909
(EA 1%410) indicates that he received the book sometime during the intervening fourteen
days. In that letter, Einstein too expressed sympathy for Mach in the debate with Planck
(Einstein to Mach, 9 August 1909, E A 17-410). The mentioned letters are reprinted in
Blackmore and Hentschel 1985, pp. 58-59.
24 It was Adler who first suggested the project to Mach in the fall of 1906 after reading
the second edition of Mach's Erkennmis und lrrtum (1906), in which, as noted above,
Mach had praised the book. As it turned out, Mach had already recommended translation
of the work to the publisher Barth, who then recruited Adler for the task. See Adler to
Mach, 19 October 1906 (AA 130), Mach to Adler, 20 October 1906 (AA 130), and Adler
to Macb, 10 November 1906 (AA 130). These details are provided in Ardelt (1984), p.
293, n. 16.
25 The only other serious candidate for 'the clear book by Duhem' is L't2volution de la
mdcanique (Duhern 1903a), which appeared in the German translation by Philipp Frank
in (1912). But not much in this book would bear directly on the positivist critique of
hypotheses, whereas the latter is an important theme in La Thdorie physique.
26 See Schlick (1915, 1917, 1918). For further discussion of these issues, see Howard
(1982, 1984, 1987, 1988).
27 Between 1919 and 1925 there was a floor of books and articles of this kind coming
both from critical realists in the tradition of Oswald Kfilpe and Alois Riehl and from
critical idealists in the Marburg tradition of Hermann Cohen and Paul Natorp. See, for
example, Sellien (1919), Cassirer (1921), Schneider (1921), Winternitz (1923), and
Elsbach (1924). For a helpful survey of the neo-Kantian reaction to relativity theory, see
Hentschel (1987).
2s See especially Schlick (1921, 1922), and Einstein (1924a, 1924b).
29 Duhem wrote: "Contemplation of a set of experimental laws does not, therefore,
suffice to suggest to the physicist what hypotheses he should choose in order to give a
theoretical representation of these laws; it is also necessary that the thoughts habitual

with those among whom he lives and the tendencies impressed on his own mind by his
previous studies come and guide him, and restrict the excessively great latitude left to
his choice by the rules of logic . . . . On the other hand, when the processes of universal
science have prepared minds sufficiently to receive a theory, it arises in a nearly inevitable
manner and, very often, physicists not knowing each other and pursuing their reflections
at a great distance from each other generate the theory at the same time. One would say
that the idea is in the air, carried from one country to another by a gust of wind, and is
ready to fertilize any genius who is disposed to welcome it and develop it, as with pollen
giving birth to a fruit wherever it meets a ripe calyx . . . . Logic leaves the physicist who
would like to make a choice of a hypothesis with a freedom that is almost absolute; but
this absence of any guide or rule cannot embarrass him, for, in fact, the physicist does
not choose the hypothesis on which he will base a theory; he does not choose it any more
than a flower chooses the grain of pollen which will fertilize it; the flower contents itself
with keeping its corolla wide open to the breeze or to the insect carrying the generative
dust of the fruit; in like manner, the physicist is limited to opening his thought through
attention and reflection to the idea which is to take seed in him without him". (Duhem
1906, pp. 255-56)
30 See also Schlick (1936).
31 Reichenbach's books on relativity are even better known sources for essentially the
same conception of the role of conventions; see especially Reichenbach (1924, 1928).
32 This essay is often misread as a repudiation of conventionalism, since Einstein's
principal aim was to criticize Poincar6's conventionalist defense of Euclidean geometry,
arguing that when geometrical primitives ('rigid body') are given physical interpretations
('practically rigid rod') geometry becomes an empirical science. But all Einstein denies
is that one would always choose to save Euclidean geometry owing to its simplicity
relative to alternative geometries. He still asserts that our choice of a total theory geometry plus physics - is conventional, determined primarily by considerations of simplicity, and he concludes: "In my opinion, Poincar6 is correct, sub specie aeterni, in this
conception" (Einstein 1921, p. 8).
33 I have corrected the translation on the basis of Einstein's original German text, which
was published in Einstein (1954), p. 503, the German edition of Schilpp (1949).
34 Quine was unaware of Einstein's criticism when he wrote 'Two Dogmas': 'I never met
Einstein, and I saw him only once - fifty years ago [1936], when he addressed the Harvard
tercentenary . . . . When I wrote ~Two dogmas of empiricism'. I had not read Einstein's
reply to Reichenbach". (Private communication, 9 October 1986). Quine does acknowledge his possibly having been influenced by Neurath (see above, note 2), who may also
have been a source for Einstein's ideas, though I have found no reference to Neurath by
Einstein. It is more likely that Paul Oppenheim discussed these questions with Einstein
during the 1940s. See below, section 4.
3s Quoted here from the transcription made by Richard Nollan from Carnap's original,
which is in Stolze-Schrey shorthand. Quoted by permission of the University of Pittsburgh. All rights reserved.

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Philosophy Department
University of Kentucky
Lexington, KY 40506-0027
U.S.A.

PIERRE DUHEM'S

THE A I M A N D S T R U C T U R E

OF P H Y S I C A L T H E O R Y :
A BOOK AGAINST CONVENTIONALISM

ABSTRACT. I reject the widely held view that Duhem's 1906 book La Thgorie physique
is a statement of instrumentalistic conventionalism, motivated by the scientific crisis at
the end of the nineteenth century. By considering Duhem's historical context I show that
his epistemological views were already formed before the crisis occured; that he consistently supported general thermodynamics against the new atomism; and that he rejected
the epistemological views of the latter's philosophical supporters. In particular I show
that Duhem rejected Poincard's account of scientific language, Le Roy's view that laws
are definitions, and '~heconventionalist's use of simplicity as the criterion of theory choice.
Duhem regarded most theory choices as decidable on empirical grounds, but made
historical context the main determining factor in scientific change.

Duhem's famous book La Th(orie physique is almost universally considered one of the most significant documents of that cultural movement
addressed against positivist optimism. Reflecting on the crisis of nineteenth-century mechanism, at the beginning of our century, this movement generated an instrumentalistic conception of scientific knowledge.
Duhem's text has always been considered one of the most brilliant and
vital - perhaps the most vital - of the conventionalist movement, the
skeptical, philosophical answer to the difficulties of classical science.
The study of Duhem's intellectual biography (Maiocchi 1985) has led
me to reach conclusions in many ways diametrically opposed to traditional judgments. These may be synthesized in a formula which is
only apparently paradoxical: the main intent of the Thgorie physique
was to oppose instrumentalism, subjectivism, and the devaluation of
the cognitive power of science.
The first observation to be made, apparently a point of chronology,
but of decisive importance, is that the epistemological theses contained
in the Th(orie physique of 1906 were clearly and fully expressed by
Duhem in a series of articles written between 1892 and 1894 (Duhem
1892a, 1892b, 1892c, 1893a, 1893b, 1893c, and 1894a). Thus Duhem's
epistemology predates the discovery of radioactive phenomena, Gouy's
experiments on Brownian motion, and Kaufmann's experiments on the
variable mass of the electron, as well as the introduction of quantum
Synthese 83: 385-400, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

hypothesis and the first relativistic hypotheses. In short, Duhem presented his epistemological theses before the "undoing of all principles",
to use Poincar6's ill-timed expression, and before the explosion of the
'crisis' of the sciences.
In fact, the thematics of crisis are totally absent in Duhem. On the
contrary, all of Duhem's historical and epistemological reflections, all
of his scientific work, as a researcher reveals the conviction that science
was not only undergoing a period of great splendor during the late
nineteenth century, but was getting rid of the errors that had accompanied it through the last three centuries! Duhem's criticism of
mechanism never attacks the trust in mechanics as a theory of mathematical physics, but always and only rejects attempts to extend mechanics into a nonscientific, metaphysical sphere. Above all, his criticism of
mechanism is based upon the fundamental assumption that there is a
better theory than rational mechanics, i.e., generalized thermodynamics. It is the success of thermodynamics that imposes the necessity of
constructing a new mechanics, not the failure of the old one. Thanks
to the new generalized mechanics, the dreams of the boldest mechanists, such as Berthollet, seemed to be on the verge of coming true.
The new mechanics did not reject classical mechanics, but enlarged
and generalized it. Classical mechanics became the model for rigor as
well as for method (Newton's, obviously, not Descarte's), and for the
form given to one's own principles, which were required to maintain
the closest possible analogy with the classical ones. The new mechanics
stayed close to its classical model, rather than opposing it, following
the original program of energetics formulated by Rankine and carried
on by the mechanist William Thomson, before the latter became what
Duhem called a "modelist" (see Duhem 1893d).
In Duhem's opinion, the developments in nineteenth century science
confirm the positivist belief in a continuous progress of scientific knowledge from other methodological bases: "In our days, many are being
swept by a wave of skepticism", but those who force themselves to find
in science "the continuation of a tradition of a slow but steady progress", will see "that a theory that disappears, never disappears completely" (Duhem 1894b, p. 124). It is not the crisis of science, but its
successes which impose upon Duhem the necessity of epistemological
reflection.
Duhem's interpretation of scientific theories as simple instruments of
classification does not appear as an answer to a supposed crisis of

mechanism. Not only is his epistemology free of such a 'crisis', but such
instrumentalistic conceptions had already been present in the French
milieu for several decades. Diffidence toward hypotheses, a phenomenalist view of science, and an instrumentalistic, manipulative interpretation of theories were widely diffused ideas, and dominant among the
French scientists of the positivist age. The French scientists' ideal was
personified by the likes of Regnault, Bertin, Berthelot, Sainte-Claire
Deville, Jamin, Cornu, Violle, and Le Chatelier - all fundamentally
experimenters. They sporadically showed an ideological belief in the
supreme value of mechanics, although in fact they produced 'antimodelist' physics. In many cases, their work was mathematically poor,
deaf to the calls of theoretical physics and insensitive to nuances of
experiment. Even more clearly than contemporary physics, the milieu
of chemistry, in which Duhem was trained, showed a general mistrust
of the idea that scientific theories might yield explanations, in the
sense of revealing hidden truths behind phenomena. These objections
appeared most clearly in the case of the atomic theory. Atomism was
interpreted in the first place as a classifying tool, even by its supporters
like Wurtz. Duhem's understanding of science and epistemology was
fundamentally influenced by Henri Sainte-Claire Deville. In the work
of this French chemist-physicist, Duhem found, even before Mach, the
very clearly stated idea that every scientific theory is simply a classifying
tool (see Sainte-Claire Deville 1866).
Unlike Mach in Germany, Duhem did not have to fight against
dogmatic belief in the nascent cognitive power of mechanics or against
a tendency to objectify models. The cognitive devaluation of theories
and models was already extensively employed as a criticism by French
positivism. As criticism it was not particularly discerning, but certainly
historically effective. Duhem had to fight a battle in exactly the opposite
direction: contrary to the flattening out imposed by the empiricist
method of his predecessors, he had to avenge the rights of theory,
showing how the ineliminable theoretical components present in every
observation gave meaning to the scientist's experimental work.
Duhem's epistemology was a defense of theories against positivist pretenses to eliminate them by strictly reducing science to pure experience.
The positivists considered theories as secondary tools when compared
to experience, even as superfluous and therefore, eliminable. Duhem
endeavored to show that theories are the heart of a scientific venture.

His was a radically anti-inductivist, antiempiricistic epistemology, a
'praise of theories', and in that sense it was opposed to Mach's.
Even Duhem's m6st renowned battle against Anglo-Saxon physics
cannot be understood as a fight against the identification of models and
reality, denying cognitive value to the models. Duhem never identified,
but rather, he always underscored the distinction between Cartesian
mechanism and that of Kelvin and Maxwell: in British mechanism,
Duhem immediately recognized the model had only heuristic functions;
it was a working tool for the physicist who needed to 'illustrate', satisfying the need of concrete interpretation (see Duhem 1893b). The fundamental charge against the British was not the fact that they used models,
but their use of models in an incoherent way, conceiving them precisely
as simple instruments. Even Laplacian physics was 'modelist', and yet,
on repeated occasions, Duhem referred to it as one of the great examples of a theory in physics. Anglo-Saxon 'modelism', propagated in
France by Poincar6, seemed to Duhem the most dangerous variant of
instrumentalism, and he fought it by taking an explicitly anti-instrumentalistic position: if theories were simple classifying tools, it would be
perfectly normal to adopt various criteria for different classifications,
introducing incoherence in physics by using different models to represent the same object, as the British did. Incoherence, (i.e., British
physics as supported by Poincar6) can be fought only by admitting that
theories are classifying tools, being neither arbitrary nor subjective, but
leaning rather not toward the construction of a 'natural classification',
namely, one having objective significance.
Theoretical coherence obsessed Duhem's research. He sought the
rigorous structuring of scientific terms in a deductive, hypothetical system which conceded nothing, in matters of rigor, to intuition or common sense. Generalized thermodynamics was the perfect answer to
these requirements (and where it fell short, Duhem took great pains
to make the necessary corrections). Anglo-Saxon 'modelism' instead
proposed an uncoordinated physics, a gallery of images that, due to
lack of coherence, could not be judged a theory. But coherence was
sustainable and justifiable only by admitting that theories, inasmuch as
they are constructed to organize mathematically the world of phenomena, are also capable of reflecting an ever-perfectible and always 'more
perfect' real arrangement, rather than a subjective one. We know with
certainty - according to Duhem in 1893 - that relations among material

substances are "neither undetermined nor contradictory". Therefore,
when faced with physics proposing two irreconcilable theories:
We are certain that the classification proposed by such physics is not in conformity with
the natural order of 'the l a w s . . , making the incoherence disappear, we will have some
probability of bringing it closer to that order to make it more natural, thus, more
perfect . . . . (Duhem 1893c, pp. 369-70)

The idea of 'natural classification' was judged an extrinsic ideological
addition, and even contradictory with Duhem's epistemology. Yet this
idea was enunciated from 1893 as the methodological axis carrying the
fight against British physics and in favor of generalized thermodynamics. Without it, all of Duhem's scientific work would be meaningless.
Not only that, but the whole of his epistemology and his historical work
was an effort to sustain this notion. The pivotal problem around which
all of the Thdorie physique hinges is just that: how to reconcile an
unprejudiced, pitiless and extremely acute Critique of the scientist's
work with the idea of a science that has cognitive value. How does one
criticize the dogmatic empiricism of positivism without falling into the
subjectivity of instrumentalism? In order to understand why this problem had become so important in Duhem's eyes during the first few
years of the new century, we should remember the genesis of the
Thdorie, and the framework within which it was generated.
During the years 1892-94, Duhem took up the fight against the
basic positivist empirical notion of science and against Anglo-Saxon
'modelism', which was still encountering noticeable diffidence among
the French. From those years to the year 1906, the year of publication
of the Thdorie, a number of riotous overlapping events considerably
changed the French scientific and cultural scene. A series of upsetting
experimental discoveries and an equally surprising sequence of theoretical elaborations (especially tied to Lorentz's theories) imposed a realistically interpreted atomic theory, together with Maxwell's electromagnetism, upon the younger French scientists such as Perrin and Langevin.
These events diffused the theme of scientific crisis.
The victory of atomism and electromagnetism meant victory - or at
least seemed to - for that modelism Duhem thought already defeated.
These scientific events accompanied and even favored changes of great
importance in the French philosophical panorama, which was characterized by the ever-increasing success of instrumentalistic, anti-intellectual,

and subjective concepts. Beginning in the 1890s, with the explosion of
the celebrated debate on the 'bankruptcy of science', French philosophy
was deeply marked by an impetuous blossoming of anti-intellectual
currents, such as Bergsonianism and modernism, radical conventionalism, and varied forms of spiritualism. To use Fouill6e's famous words,
this period saw the "revolt of the heart against the intellect". Modelism
and instrumentalism, English physics, atomism and exasperated conventionalism, the crisis of science, anti-materialism and spiritualistic
skepticism seemed to form a thick web destined to surround and suffocate the model of scientific rationalism elaborated by Duhem in the
1890s.
To fight these foes, Duhem published a series of works in the early
1900s. The Th~orie represents the ultimate battle of this campaign. In
1902, he criticized electromagnetic theory very harshly in Les Theories
~lectriques de J. Maxwell. During the same year he attacked atomism
with Le mixte et la combinaison chimique. In 1903, with L'~volution de
la m~canique, he confronted the more generalized critique of the 'modelist' approach in its diverse historical variants. And finally, in 1904,
Duhem started publishing for the Revue de Philosophie a series of
articles which were eventually collected (with some additions) in 1906
to form La Th¢orie physique. Here he fought the conventionalism
then in style on the epistemological level. The Th¢orie physique was,
therefore, not at all a book opposing the positivism of the 1800s, in the
name of the new century's revolution in physics. It was a work against
the emerging novelties intended to demonstrate that the criticisms
brought a decade earlier against the positivist conception of science
need not give way to the skeptical conclusions that seemed to follow
directly from these novelties.
An analysis of the text of the Th~orie confirms the interpretation
which has led me to give the history of this work's genesis. For reasons
of space, it is impossible to carry out a detailed analysis here, but some
indications may be given: on all the key problems of epistemology
(what is a scientific fact? what is a law? how does one choose
theories?), Duhem clearly takes a position critical of the main conventionalists, primarily Poincar6 and Le Roy, and fights against their
supposed solutions. I will briefly consider some examples.
Le Roy had given a rather strong subjectivist interpretation of the
'scientific fact', starting with the analyses made by Duhem in the 1890's
and maintaining that, due to the ineliminable theoretical components

present in every experience, the 'scientific fact' is to a certain extent
'created' by the subject (Le Roy 1899, p. 516). Poincar6 had retorted
by trying to subdue this radical subjectivism, maintaining that what the
scientist creates is the language with which we ask nature questions,
and it is then nature's task to give the answers (Poincar6 1905, p. 266
et seq.).
Duhem argues at length even against Poincar6's mitigated version
of conventionalism. The theme of science understood as a well-made
language is certainly not new: from Condillac and Lavoisier, through
the Ideologues, it had gone through positivism and had almost become
commonplace. ]k was directly connected to a depreciation of theories,
reducing them to the role of dictionaries which, through obviously
conventional rules, allowed the scientist to translate experience into
language. The view had, in fact, been emphasized by radical conventionalists like D'Adh6mar (D'Adh6mar 1904). Against these general
positions Duhem emphasizes (Duhem 1906, p. 266) that science differs
from other languages as to its terms, just because they are defined
within a theoretical context, stabilizing multiple interconnections in a
network of relationships between term and term, concept and concept,
not to mention :relationships among some terms and groups of phenomena. A scientific fact is not differentiated from a nonscientific fact only
because it is expressed in a language resulting from customs known only
by a small group of people (Poincar6's thesis). Its main characteristic is
that of belonging, by virtue of the theories that we use to express it,
to an intricate network of relationships with theoretical terms and with
a multitude of other scientific facts. When we translate a raw fact into
a scientific fact, we do not simply construct a proposition using the
expressions of a language provided with conventional rules known by
a small group of people (the scientists), we do much more. We insert
that fact in a sequential scheme, including other facts, and we recognize
relationships among phenomena. However, the linguistic translation of
the raw fact to the scientific fact is not simply made by choosing the
rules of translation freely and conventionally. It is guided by the theories allowed at a given historical moment, and the result of the translation work is, therefore, not invented by the scientist; it is the result
of history. It de,pends upon the level that science has reached at a given
historical moment. Science as a means of human expression is, in fact,
a language, but a language radically different from all others.

Duhem contributed more than anybody else to the criticism of positivism's dogmatic concept of science's empirical basis. His analysis of
the impossibility of crucial experiments is famous, but his criticism is
not limited to the denial of the notion of the empirical basis of science.
The distinction between the theoretical and the observational is unsustainable for Duhem from the logical point of view, because, in the
mature sciences, every observation is impregnated by theories. Positivism taught (just as neopositivism would in the future) that such a
distinction was logical, and therefore absolute. For an absolute distinction between theoretical physics and experimental physics, Duhem substituted an historical distinction: there exists at every historical moment
the heritage of previous history; a body of 'trusted' theories which
guarantees the experimental physicist the possibility of making 'observations' without having to doubt every concept used. Thus science may
progress, constantly increasing the theories it trusts (the 'background
knowledge' in modern terms). It makes statements which, from the
logical point of view, are unavoidably 'theoretical'. They are theoretical
at the moment they are proposed, but they become increasingly more
'experimental' as they are provided with increasingly more guarantees
of their validity.
Even on the notion of scientific law Duhem's views are opposed to
Poincar6, Milhaud, and especially Le Roy. His critique centered upon
the typically conventionalist affirmation that laws are used as definitions: in the presence of an experiment which seems to falsify the
law, we do not reject it, but we say that the present case does not fit
those for which the law was defined, that there are upsetting causes
that the conditions of the applicability of the law did not foresee.
Experiments, therefore, will never be able to force us to reject the
laws; they are not falsifiable (Le Roy 1899, p. 523). Evidently, this
approach empties scientific laws of any empirical content. It makes
the rigorously required comparison with experience useless for the
development of science, since any problem may be resolved by exercising an inventive activity which saves a law by placing it beyond experience. For Duhem, the stern comparison, the refutation of experience,
has a result which is only apparently identical to Le Roy's rescue of
law thanks to the addition of new perturbing causes, but actually has
diametrically opposed objectives to that of instrumentalism. For
Duhem, in fact, when confronted with a denial of experience we save a
law by specifying its conditions of validity, and that constitutes cognitive

progress. It is true, we use the law as a criterion to establish whether
or not the conditions under which it is considered valid are respected;
but it is experience which allows us to establish the conditions of
validity. Not every refutation falsifies the law. Some give us information
about its limits of validity, and this constitutes progress. Difficulties are
not resolved in a clever, intellectual game of rescue. They are resolved
in a symbolic representation by adhering more closely to reality. Each
one of our laws is necessarily a poorer scheme than the reality it wants
to represent. The failures, the falsifications, force us to refine the
theoretical scheme and to complete it in order to "make it more suitable
to represent reality" in an unending process of perfection (Duhem
1906, p. 285; 1954, p. 174). In this process it is the falsifying experience
that teaches us the conditions of the law's validity and the restrictions
to which the primitive terms of law are submitted. Experience is not
an enemy from which, with more or tess astute devices, one must seek
protection, it is the source of the perfecting process of the theoretical
scheme: "The necessity of these restrictions didn't appear at all in the
beginning, it was imposed by experience." (Duhem 1906, p. 287; 1954,
p. 176). The work of continuous minor repairs, through which the laws
of physics avoid the denials of experience, does not have the function
of saving a law by petrifying it into the limbo of conventionalism, but
it plays an "essential role in the development of science" (Duhem 1906,
p. 288; 1954, p. 176). What is important from Duhem's point of view
is not the rescue of the law, but the progress of the theoretical scheme,
which is realized in the attempt to resolve the issues raised by a falsifying
experience:
It is through the unending struggle of this work which continually completes the laws to
the end of includir,tg exceptions, that physics is able to progress.., it progresses because
without interruption, experience is forever causing the explosion of new contradictions
among the laws and the facts and without interruption, physicists rectify the laws so that
they may represent facts more accurately. (Duhem 1906, pp. 289-90; 1954, p. 177)

Even the problem of choosing the basic hypotheses of a theory, which
Poincar6 and Le Roy had resolved in terms of a conventional choice,
receives in the Thgorie a solution that decidedly finds fault with the
main lines of subjectivism. Moreover, it is just in this respect that the
most important and significant variation between the articles of the
1890s and the book of 1906 should be considered. The problem of the
choice of hypotheses had been dealt with in Quelques rdflexions au suiet

des thdories physiques (1892), in criticisms of the positivist dogmatism
extolling the creative freedom of the researcher. In this article, D u h e m
had maintained that hypotheses are chosen freely and that choices are
guided by subjective criteria, mostly that of simplicity. The Thdorie
physique repeats almost to the letter all of that article's criticisms of
positivism, but the paragraph dedicated to the choice of hypotheses is
completely ignored, together with all those passages containing rather
excessive conventionalism!
In the Thdorie, Duhem shifts the problem from the field of logic,
of metahistorical methodological criteria, to the field of history. The
subjective criteria of choice so dear to instrumentalistic conventionalism
are no longer given space because D u h e m is convinced of the fact that
even if they are possible from the abstract point of view, the scientist,
in reality, does not use them to make his own choices. He does not
use them because in the concrete cases of historical evolution, the
scientist does not make choices of any kind. The theory or hypothesis
germinates within him without his concurrence. This means, in a less
paradoxical form, that logical criteria are altogether insufficient to guide
theory choice and, relying only upon them, the scientist would remain
paralyzed in his progress by excessive freedom. This had been the
objection which, in a ferocious attack, the neo-Thomist Vicaire had
addressed to Duhem's article of 1892 (Vicaire 1893, p. 79). Duhem, in
the following year had rectified his own position, maintaining in L'dcole
anglaise et les thdories physiques that in the choice of hypotheses, a
scientist is never guided by logic alone:
The particular inclination of his spirit, his prevailing faculties, the diffused doctrines in
his environment, the tradition of his predecessors, the habits he has adopted, the education he has received, will be his guide, and all of these influences will be found again
in the form of the theory he will conceive. (Duhem 1893b, p. 377)
In the Th(orie, this idea is extensively developed and represents one
of the basic theses of the whole work: the historical context, in which
every scientist moves, guides the choice of hypotheses; these are the
concrete influences that every stage of development of the historically
determined scientific thought exerts upon the researcher, resulting in
the generation of new ideas. These ideas are the product of all of the
foregoing evolution, without which they could not be created; they are
'the last stage of a long development'. Since whoever contributes to
scientific progress is so immersed in his contemporary historical context

that he cannot move freely, every new hypothesis can only be a modification of already-stated hypotheses. The history of science must be a
continuous development (Duhem 1906, pp. 364 et seq. and 416 et seq.).
The thesis of historical continuity is one part of his epistemology
with which Duhem attempts to resolve the problem of the choice of
hypotheses. And it is a thesis which has a very important result: if in
1892, relying upon logical criteria of choice, such as simplicity, Duhem
had not been able to avoid the acceptance of an instrumentalistic vision
of science, now, leaving the problem of choice to the thesis of historical
continuity he can sustain a realistic and cognitive vision of the scientific
enterprise.
Showing the physicist the continuing tradition through which science of every age is
nourished by the previous century's systems, through which it is pregnant with the physics
of the future, citing to the physicist the prophecies that theory has formulated and that
experience has confirmed; it creates and strengthens in him the conviction that a physical
theory is not at all a purely artificial system, useful today and useless tomorrow, that it
is an always more natural classification; an always clearer reflection of reality that the
experimental method could never bear in a face-to-face contemplation. (Duhem 1906,
p. 445; 1954, p. 270)

What can be said then about the historiographical scheme, that makes
Duhem (and conventionalism in general) the advocate of a vision of
science proceeding on the basis of choice and decided by a criterion of
simplicity? In my opinion, the only possible answer is that the scheme
is completely wrong. Except for the paper of 1892, Duhem never
admitted that simplicity could be a sufficient criterion for choice. Obviously, like every reasonable person, he considered the simplicity of a
theory part of its merit, but he certainly didn't use it as a guideline.
Duhem's vaslE historiographical work clearly shows that the case of
empirically equivalent rival theories is in his opinion extremely rare,
and that for the vast majority of cases it is empirical factors that supply
a clear criterion of nonsubjective choice. Great theoretical disputes
were resolved, according to Duhem, by the superiority of one theory
over a rival one in 'saving the phenomena', without any necessity at all
to resort to criteria such as simplicity. For example, this is the case
of the clash between Ptolemy and Copernicus. It is a very wretched
historiographical thesis that, according to conventionalism, the heliocentric system won over the geocentric system because it was simpler.
In To Save the Phenomena, where Duhem confronts the problem, the

sixteenth-century victory of the Copernican system, intended as a calculating instrument, is always explained on the basis of the greater precision that the system allowed in the construction of astronomical tables.
There are times (although few) that simplicity is also mentioned along
with precision, but this attribute never appears by itself. It is always an
additional quality which certainly does no harm to the Copernican
system, but that certainly can not explain its victory just for its sake.
When commenting on sixteenth-century astronomers following Copernicus, from Reinhold to Peucer, from Schreckenfuchs and Piccolomini
to Giuntini, Duhem uses the term of simplicity along with 'precision'
only once, when referring to Reinhold. In all other cases, what is always
and only considered is the calculating precision obtainable starting from
the Copernican hypotheses. Duhem concludes his analysis of the victory
of Copemicus's theory with the astronomers thus:
The spirit of the greater part of the astronomers, during the 20 or 30 years following the
publication of Copernicus' book is very clear. The work of the astronomer from Thorn
attracts their attention very strongly because it appears to be suited for the construction
of precise astronomical tables. (Duhem 1908, p. 509; 1969, p. 8)

In the first place, therefore, the criterion of simplicity turns out to be
irrelevant and superfluous for the vast majority of theoretical disputes.
But even when facing those cases where we are in the presence of
equivalent empirical ranges in two rival theories, Duhem never considers simplicity a decisive element, capable of generating a choice
endowed with any solidity. The only example of empirically equivalent
theories contained in Le syst~me du monde is made up of two different
astronomical representations. Appolonius of Perga had proved epicycles and eccentrics to be equivalent with respect to observational
effects; in 244 B.C., Hipparchus, when faced with this surprising discovery, refused to make a decision in favor of either representation. Now,
in Duhem's opinion, this attitude was not due to the astronomer's
uncertainties or inability but, on the contrary, it was the attitude of
one who follows the correct scientific method; when confronted with
theories equivalent from the observational point of view and in the
absence of other references capable of guiding the choice (which could
be other already accepted theories), he refuses to choose. Although
using one theory because it is judged simpler, the astronomer does not
condemn the other and does not discard it as a possible alternate tool
(Duhem 1913-59, Vol. I, pp. 455--60). It is clear in this case that Duhem

does not consider simplicity the only criterion sufficient in founding a
definitive theoretical choice. In other cases of empirically equivalent
theories examined in detail by Duhem in his various works, the notion
of simplicity is always relegated to the background. That is the case,
for example, with the contrast between Lagrange's M(canique analytique and Poisson's Mdcanique physique where the fundamental criterion for evaluating the superiority of one over the other is seen in
the relationship between the type of mathematics used and the model
upon which such mathematics are applied (Duhem 1905, p. 83 et seq.).
The fact that the criterion of simplicity takes on a completely secondary historical role in Duhem should not surprise us, if we remember its
previously stated position in the historical dynamics of the relationship
between abstract and concrete, which is apparent in scientific laws.
According to Duhem, the symbolic schemes produced by the scientist
are always impoverished when compared to the reality they are
supposed to symbolize. The modification of the theoretical scheme
always happens through its increasing complication as it attempts to
represent all the richness of the experience. This is also the case for
theories: in Duhem's opinion historical progress generally creates an
increasing complexity of theoretical physics and only in some particular
cases (for example with Copernicus's theory) do we have a simplification which, in any case, cannot by itself justify the acceptance of a
theory. At this point, consider once more Le systkme du monde. Here
all of the ancient and medieval history of astronomy is recounted as a
progressive increase of complexity in function, to create a better adaptation to observational data (Duhem 1913-59, vol. I, pp. 129 and 201).
And in To Save the Phenomena Duhem advises that the complication
of a theory cannot be considered the sole motive for rejecting it:
The exact representation of celestial movements may force the astronomer to gradually
complicate his hypotheses, but the complexity of the system where he will have stopped
cannot be a reason to reject such system if it is in full accord with the observations.
(Duhem 1908, p. 129; 1969, p. 17)

The most conclusive demonstration of how much Duhem considered
scientific progress to be substantially characterized by an increase of
complexity is found in considerations regarding the relationship between mechanics and general thermodynamics. Just because it is a more
limited theory, capable of covering a lesser number of observational
data compared to general thermodynamics, mechanics is much simpler.

Conversely, because it is a better-suited to phenomena, general thermodynamics or energetics is even more complex than the theory it wants
to replace.
The new mechanics founded on thermodynamics has not at all imposed upon its essential
hypotheses the exaggerated simplicity required by the old mechanics: it has tolerated
their being more numerous and more varied allowing them to express themselves with
more complex formula. This greater amplitude left to the choice of principles proved to
be a happy and fruitful one. (Duhem 1905, p. 343)

Here then, is a rather difficult historiographical problem for the supporters of Duhemiam simplicity: the new mechanics, that to which
Duhem dedicated all of his work as a researcher, is considered more
complex than the old mechanics. The revolution brought about to
thermodynamics in the chemical and physical sciences proceeds from
the simpler to the more complexF
In the Thgorie Duhem intended to show how to avoid skepticism
without abandoning any of the criticisms of dogmatic positivist empiricism he had made over a decade before. The attempt is rather risky:
it is a question of constantly maintaining a balance on a metaphorical
thread with the recurring risk of falling on the one side into dogmatism,
on the other side into skepticism. It is clear that it is this second danger
that Duhem fears most because, as a matter of fact, his juvenile theses
had been interpreted as skeptical. And it is here that Duhem develops
a constant and tight polemic against Mach, against Poincar~ and against
Le Roy. It is astounding how the critics have not taken into account
these extremely clear Duhemian passages which represent the most
lucid, articulate and effective polemic against conventionalism with a
skeptical note. On all fundamental epistemological questions (what is
experience? what is a law? what is a theory? what is the nature of
science?), Duhem both reproposes and confirms his own juvenile theses; moreover, he is concerned to show how from those theses one
doesn't necessarily have to reach the depreciative conclusions of his
false friends. If all its pages are to be taken seriously, and not just those
on the critique on positivist dogmatism which in 1906 were the most
worn-out for Duhem's readers, the total vision of science that emerges
from the Thdorie is evidently a vision that is rather far from any trust
in science void of criticism. But it is also a realistic conception of a
science in constant movement, a science made by human beings, and
as such always revisable. It proceeds by continuously retouching its

own conceptual schemes, modifying them, and generally complicating
them, in view of an ever better adjustment between the scientific image
of reality and reality itself, a reality that has certainly not been completely reached but that becomes always more approachable.

REFERENCES
AdhNmar, R. de: 1904, La philosophie des sciences et le probl~me religieux, n.p., Paris.
Duhem, P.: 1892a, 'Quelques rNflexions au sujet des thNories physiques', Revue des
Questions scientifiques, 31,139-77.
Duhem, P.: 1892b, 'Notation atomiques et hypotheses atomistiques', Revue des Questions
scientifiques 31, 394-457.
Duhem, P.: 1892c, 'Commentaires aux principes de la thermo-dynamique', Journal de
Mathdmatiques Pures et Appliqudes 8, 269-330.
Duhem, P.: 1893a, Introduction ?t La mdchanique chimique, George CarrN, Paris.
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54-83.
Duhem, P.: 1893c, 'L'Ecole anglaise et les tMories physiques', Revue des Questions
scientifiques 34, 345-78.
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physique de Platon ?l Galilge, Hermann, Paris.
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?~ Copernic, Hermann, Paris.
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Duhem, P.: 1969, To Save the Phenomena: An Essay on the Idea of Physical Theory
from Plato to Galileo, University of Chicago Press, Chicago.
Le Roy, E.: 1899, 'Science et philosophie', Revue de Mdtaphysique et de Morale 7, pp.
375--425; 503-62.
Maiocchi, R.: 1985, Chimiea e filosofia, Scienza. epistemologia, storia e religione hell'opera di Pierre Duhem, La Nuova Italia, Firenze.
PoincarN, H.: 1905, La valeur de la science, Flammarion, Paris.
Sainte-Claire Devilte, H.: 1866, Lefons sur la dissociation, professdes devant la Socidtd
Chimique le 18 mars et le ler avril 1864. Hermann, Paris.

Vicaire, E.: 1893, 'De la valeur objective des hypotheses physiques', Annales de la
Philosophie Chrdtienne 126, p. 79.
Dipartimento di filosofia
Universita degli studi di Milano
Milan, Italy

M A I O C C H I ON D U H E M , H O W A R D ON D U H E M
AND EINSTEIN: HISTORIOGRAPHICAL

COMMENTS

ABSTRACT. These comments center on the methodological stance that Howard and
Maiocchi recommend to us when we are doing history of philosophy. If Howard and
Maiocchi are right, both Duhem and Einstein developed closely related versions of
conventionalism and realism, and in both of their philosophies the conventionalist and
realist moments were mutually compatible. Duhem's holism and, arguably, Einstein's as
well, denies the need for across-the-board literalism, and both of them had important
reasons for denying that convergence was required or even desirable for realism. Thus, for
those who are caught up in the current disputes, serious consideration of the discrepancies
between the standard current versions of realism and conventionalism and the positions
that contextualist analyses reveal to have been advocated by Duhem and Einstein may
uncover some of the tacit assumptions that impede the resolution or advancement of our
disputes.

It is some fifteen years since I read both Duhem and Einstein seriously,
the latter with particular attention to his arguments regarding the conventional character of spatio-temporal metrics. Since then, my professional preoccupations have been directed elswhere. The texts of the
masters are, therefore, not freshly in my mind. These comments, accordingly, center on the methodological stance that Howard and Maiocchi recommend to us when we are doing history of philosophy rather
than the interpretation of the particular texts they discuss. I shall point
out some of the virtues of their historiographical styles and provide
some extensions and corroborations of the general approach to the
texts that they both support.
To begin, let me characterize the similarities in the historical methodologies manifested in the papers of Maiocchi and Howard. They both
maintain that the proper understanding of philosophical texts and controversies requires a rather full understanding of the intellectual situation and cultural setting of the protagonists in question, most especially
of the specific content and character of the positions which they inherited, debated, and/or opposed. Thus the position of Duhem is not that
of Quine, and it will not be properly understood through the eyes of
those of us who are familiar with Quine but not with Deville, Rankine,
Mach, Poincar6, and Le Roy. Similarly, although Einstein's response to
Synthese 83: 401-408, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

turn-of-the-century positivism and the neo-Kantianism of the Marburg
School blends components of what we would call conventionalism and
what we would call realism, precisely because it was directed to specific
issues raised in that setting, the resultant doctrine cannot be mapped
onto any current version of conventionalism or realism.
Howard and Maiocchi, in short, insist on a sort of historicity that is
seldom found in standard histories of philosophy and relatively infrequent even in specialized treatments by historians of philosophy of
the major figures in the grand tradition. Their attention to the historical
setting greatly enriches our understanding of Duhem, of Einstein, and
of the devious pathways by means of which the former's influence
spread, particularly into corners of the German-speaking world during a
period when many have thought it relatively uninfluential. Both papers
produce some surprising findings - e.g., about the special importance
of theoretical coherence in the thought of Duhem and about Duhem's
influence on Einstein. These findings rest on close attention to the
scientific and the philosophical preoccupations of Duhem and Einstein.
They demonstrate the value of the contextualist historiographical approach.
Let us explor e some advantages of the historiographical stance I am
attributing to Howard and Maiocchi. It seems obvious, and hardly
needs to be said in the context of this symposium, that it offers better
hope than the usual methods of historians of philosophy for understanding the work of our philosophical ancestors. I shall argue that, in
addition, it can sometimes shed useful, if indirect, light on current
disputes when the usual methods are not much help. But I shall also
complicate matters a bit by trying to refine the historiography of our
speakers a bit, going slightly beyond what can be safely justified by a
literal reading of their texts.
For these purposes, it is expedient to articulate the historical methodology in question more clearly than I have as yet. To a first approximation, it distinguishes at least two ways in which one might interpret
a figure whose philosophical views are of interest. The first is very
natural to us, living as we do in an ahistorical culture, especially if,
like many philosophers and contemporary historians of philosophy, we
believe in some form of perennial philosophy. From such a starting
point, it is all too easy to trust our own formulations of a standard
philosophical problem or position and ask of a great (or not so great)
figure's texts what light they shed on the issues as thus conceived. This

is what I call the standard method of history of philosophy. It is by
such a route that we often come to quarrel about, for example, how
best to understand Einstein's realism or conventionalism, or that we
come to see Duhem's holism as so allied to Quine's that their two
rather different problematics are melted together under the misleading
label of 'the Quine-Duhem problem'.
The standard approach mines the work of the ages for positions and
for insights bearing on our problems - surely a useful and constructive
task, but surely also a way to fall prey to easy misunderstandings of
the positions of our predecessors and the issues that preoccupied them.
Real history, according to our speakers (and they are surely right) is
far more interesting and far more revealing philosophically - though it
often speaks less directly than we might wish to the philosophical
difficulties that tie us and our contemporaries in knots.
The second mode of doing the history of philosophy, in contrast,
looks to the local context in which a thinker was working - i.e., to the
positions taken by those with whom he or she was engaged, the distinctions employed at the time, the specifics of the disputes in which
the thinker was embroiled. It is this context that gives slippery technical
terms and concepts their proper meaning. Knowledge of this context
helps us to understand what has gone wrong when, employing current
labels in their current acceptation, the thought of the individuals being
studied seems, at least occasionally, to run skew or even counter to
our expectations. Thus it is that, if we employ such terminology with
current meanings, Duhem and Einstein are both misdescribed as 'realists' or 'conventionalists'. The subtle shifts since their day in the content
of the doctrines and the meanings of the labels involved account for
the fact that it was possible, perhaps even easy, for them to be both
realists and conNentionalists, a constellation that is very difficult, if
not conceptually incoherent, today. If Duhem and Einstein combined
realism and conventionalism in their philosophies, and our speakers
are very persuasive in arguing that they did, the likelihood of arriving at
a satisfactory understanding of their positions by means of the standard
method of the history of philosophy is very small indeed. What is
needed in order to properly grasp the philosophies here investigated is
a sound understanding of what Duhem and Einstein opposed, of the
issues they had to solve in developing their views. And those issues are
not the issues or our day.
Lest you think I am misascribing a foreign method to our speakers,

let me quote from a related paper by Professor Howard on 'Einstein's
Conventionalism'.
We cannot do justice to the philosophical opinions of a thinker like Einstein if [we] go
to him looking for answers to our questions. What is required, instead, is a genuinely
historical approach, that takes account of all available resources, and that subjects those
sources to the kind of critical scrutiny practised in other areas in the history of ideas.
(Howard 1987, p. 44)

It is obvious that Professor Maiocchi, who insists that a proper understanding of Duhem rests on setting his views into the context of his
disagreements with Mach, Poincarr, Le Roy, D'Adhemar, Milhaud,
and others, shares this stance with Professor Howard.
The time has come to complicate matters a bit. Both Duhem and
Einstein were engaged in scientific as well as philosophical controversies. While it would be a mistake to draw a hard-and-fast line between
science and philosophy - indeed, contextualism requires that we recognize that any such line changes with time and place - it is important to
recognize that the philosophical positions that our protagonists took up
were colored at least as much by their scientific as by their philosophical
concerns. Professor Howard claims, in the reading version of his paper,
that the case of Einstein shows that "the philosophy of science is
essential to good science, but only if it places the problems of the
scientist in the forefront, not if it attempts to impose its own agenda,
not if it pretends to instruct the scientist". It seems clear that this
portrays Einstein's own view and practice correctly, for reasons that
Howard develops in that paper. Like Howard, I would like to believe
that this claim is true of philosophy of science quite generally. But it
is not clear how widely such a position has been held by those who
have written what we would count as the philosophy of science from
the nineteenth century on, and it is not clear whether a parallel claim
about Duhem will withstand serious scrutiny.
Einstein's conventionalism was won, in part, by hard wrestling with
the interpretation of coordinates assigned to empty space, i.e., to places
occupied by no objects and in which no light rays or objects traversing
geodesic paths actually interested - and it solved the problem of interpreting the seemingly conflicting curvatures of space that result from
different coordinatizations of such empty regions. Duhem's conventionalism (reinforced by Maiocchi, if I understand him rightly), played
a less internal role in his science. Rather, it provides external philosophical arguments opposing the initially discredited, but later ascendant,

atomism against which he sought to secure his own brand of nonpositivist energeticism. To quote Duhem's Titres et Travaux, "it would be
irrational to work towards the progress or physical theory [in light
of the difficulty of directing experimental refutations against isolated
theoretical claims] if that theory were not the increasingly clear and
precise reflection of a metaphysics. The belief in an order transcending
physics is the sole reason for the existence of physical theory" (Duhem
1917, p. 156, as translated in this volume). Thus metaphysics served
Duhem as an external constraint on the proper outcome of scientific
reasoning as, I believe, it did not for Einstein.
Whether this imterpretation can be sustained in detail or not, it
illustrates the point that as long as there is a useful working distinction
in the relevant context between science and philosophy, it is necessary
for contextualist historians of the philosophy of science to work out the
interplay of the scientific and the philosophical influences on the positions in which they are interested - for the aims and the content of an
individual's philosophy will, at least sometimes, be crucially affected
by whether it is directed in the first instance to a scientific or to a
philosophical question. Indeed, in at least some cases (perhaps, for one,
in Einstein's) the,re will be nothing like a coherent closed philosophy
to be uncovered precisely because philosophical considerations were
pursued only as far as was needed to deal with the scientific problems
in hand, without great concern for the coherence of the resulting philosophical fragments. There need not be anything wrong with such an
eclectic use of philosophy in spite of the fact that it often results in a
misuse of philosophy as a rhetorical club employed in special pleading
in favor of whichever theory it is that one prefers. In any case, the fact
that such eclectic uses and misuses of philosophy are quite common
makes the contextualist's task of reconstructing philosophical views of
many particular figures extremely difficult.
A particularly interesting issue posed by Duhem's and Einstein's
philosophies of science, especially as they were presented by our symposiasts, is what to make of the notion of a natural classification, of the
notion that even though "two different peoples" would come up with
quite different descriptions of the events underlying the surface of some
domain of phenomena, nonetheless for the working scientist "the world
of perceptions determines the theoretical system unambiguously" (Einstein's Festrede for Planck, Einstein 1918, p. 31, as quoted by Howard).
The problem in question is quite general in the sciences and by no

means restricted to physics. Thus in my own work in history and philosophy of biology, I encounter parallel issues and intuitions regarding
the conflicts between Darwinian and anti-Darwinian interpretations of
evolution around the turn of the century and regarding instrumentalistic
versus realistic interpretations of Mendelian genetics from 1900 clear
through to the 1950s. What is of particular interest is the importance of
coherence of theories, which Maiocchi describes as a central Duhemian
obsession, crucial to his argument against the English-style use of models and to his argument that physics sought and might reasonably expect
to approach something like a natural classification.
To illustrate the point that parallel considerations play a crucial role
in the evaluation of work in other sciences than those with which
Duhem and Einstein were concerned, consider the gulf between embryology and genetics from the twenties through (at least) the fifties of
this century: all higher organisms have the same genes in virtually all
of their cells. Yet some system of hereditary controls causes the cells
to differentiate systematically (in the fight places and at the fight times)
into nerve, muscle, bone, liver, and kidney cells. Mendelian models
could not explain how the same cells could yield such different results
and embryological models and descriptions could not provide a serious
ous account of an extra-Mendelian system of heredity. Within fairly
circumscribed limits, both Mendelian genetics and descriptive/experimental embryology were in pretty good shape. But as soon as one
posed Duhemian questions about theoretical coherence, about the natural classification for the hereditary controls governing what an embryo
would become, the situation looked unsatisfactory indeed. As it happens, this complex of issues was taken particularly seriously in France,
where the debate over the status of Mendelism on these grounds was
particularly lively (Burian, Gayon, and Zallen, 1988). I have no idea
at this point whether there was any indirect influence of Duhem on
these debates, but it surely is a matter worth further exploration.
The complications that I have introduced can be summarized rather
neatly. There are at least four perspectives which a contextualist historian of philosophy of science may employ in working out the views
of a particular figure. These concern
1. the philosophical setting and disputes in which she or he was
engaged,
2. the scientific issues to which the philosophical considerations were
primarily addressed and the interpretation of those considerations

within the scientific as well as the philosophical context of the
day,
3. the application of those philosophical considerations in novel settings, scientific as well as philosophical, including the pathways by
which they became influential, and
4. the application of those philosophical considerations in later philosophical contexts.
Let us turn, to close these comments, to the last perspective on my
list. One particularly valuable philosophical use of the products of
contextualist studies of first-rank figures is to be found here. If Howard
and Maiocchi are right, both Duhem and Einstein developed closely
related versions of conventionalism and realism, and in both of their
philosophies the conventionalist and realist moments were mutually
compatible. If ][ am right, current versions of conventionalism and
realism are mutually incompatible. Most contemporary realisms have
been saddled with one or both of two commitments foreign to Duhem
and Einstein. These concern the need for science to converge on the
one true theory or, perhaps, the one true account of the phenomena
in a particular domain, and the need to be able to provide a literal
semantics across the board for the individual terms and concepts of a
true theory. Duhem's holism and, arguably, Einstein's as well, denies
the need for across-the-board literalism, and both of them had important reasons for denying that convergence was required or even desirable for realism. Thus, for those who are caught up in the current
disputes, serious consideration of the discrepancies between the standard current versions of realism and conventionalism and the positions
that contextualist analyses reveal to have been advocated by Duhem
and Einstein may uncover some of the tacit assumptions that impede
the resolution or advancement of our disputes.
Contextual studies of the sort that Maiocchi and Howard have executed here may not provide an Archimedean fulcrum for resolving
philosophical disputes, but they certainly offer a rich panoply of alternatives. In so doing, they provide us not only with vastly improved understanding of our philosophical predecessors,, but also with significant
leverage for making progress in our own disputes as well. For these
reasons, we should be grateful to them and, indeed, to many of the
other contributors to this conference.

REFERENCE.S
Burian, R., J. Gayon and D. Zallen: 1988, 'The Singular Fate of Genetics in the History
of French Biology, 1900--1940', Journal of the History of Biology 21,357-402.
Duhem, P.: 1917, 'Notice sur les titres et travaux scientifiques de Pierre Duhem', Mdmoires de la Soci(t~ des Sciences physiques et naturelles de Bordeaux series 7, 1, 40-169
(translated in part in this issue).
Howard, D.: 1987, 'Einstein's Conventionalism', paper delivered at the Department of
Philosophy, Johns Hopkins University, 25 February 1987,
Howard, D.: 1989, 'Duhem and Einstein', this issue.
Maiocchi, R.: 1989, 'Pierre Duhlem's The Aim and Structure of Physical Theory: A Book
Against conventionalism', this issue.
Department of Philosophy
Virginia Polytechnic Institute and State University
Blacksburg, VA 24061
U.S.A.

PIERRE DUHEM'S

CONCEPTION

OF N A T U R A L

CLASSIFICATION*

ABSTRACT. Duhem's discussion of physical theories as natural classifications is neither
antithetical nor incidental to the main thrust of his philosophy of science. Contrary to
what is often supposed, Duhem does not argue that theories are better thought of as
economically organizing empirical laws than as providing information concerning the
nature of the world. What he is primarily concerned with is the character and justification
of the scientific method, not the logical status of theoretical entities. The crucial point to
notice is that he look the principle of the autonomy of physics to be of paramount
importance and he developed the conception of natural classification in opposition to
accounts of physical theories that contravened it.

Pierre Duhem's view that physics aims to establish a 'natural classification' of phenomena is generally treated as something o f an embarrassment, so much so in fact that it is frequently dismissed as an aberration
or passed over in silence. Taking his official view to have been that
the sole purpose of theorizing in physics is to facilitate discussion,
commentators have tended to think that he must have regarded theories
as 'artificial classifications'. Duhem could not, they suppose, reasonably
have taken the theoretical physicist's aim to be both one of summarizing empirical laws in a compendious fashion and one of providing
insight into the realities behind the appearances. Indeed some commentators have gone so far as to argue that he introduced the idea of
natural classification because he could not bring himself to deny what
physicists instinctively believe and some have even argued that he meant
something quftte different by the idea from what he seems to have
meant.
This line of argument is tempting if only because Duhem devoted
considerable effort to arguing that theories should be regarded as economical classifications. However, it also labours under the difficulty
that Duhem frequently stresses that physical theories provide information ,about the nature of the world and it strains the imagination to
suppose that he did not appreciate the difference between artificial
and natural classification. While Duhem certainly thought that theories
summarize empirical laws, this did not prevent him from arguing
throughout his career for the view that they are converging on natural
Synthese 83: 409-420, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

classifications and he seems never to have doubted the consistency of
his position. 2 In fact we would seem far better advised to take Duhem's
remarks about physics converging on a natural classification at face
value and to attempt to figure out how they can be reconciled with the
rest of his philosophy.
Undoubtedly much of what Duhem says in La Th~orie physique
needs careful interpretation, but what he says about natural classification seems clear enough. Consider for instance his view that "physical
theory is not merely an artificial system, suitable today and useless
tomorrow, b u t . . , an increasingly more natural classification".3 Better
still, consider his explicit contention that "the aim of physical theory is
to become a natural classification, to establish among diverse experimental laws a logical coordination serving as a sort of image and reflection of the true order according to which the realities escaping us are
organized". 4 In these and similar remarks Duhem distinguishes natural
classifications for artificial ones, rejects the view that physical theorizing
is restricted to the logical classification of experimental laws, and suggests that the classifications that physicists provide are becoming increasingly natural.
In fact Duhem's picture of science is the familiar one of a selfcontained evolutionary enterprise in which less good theoretical classifications are replaced by better ones. In his view physicists make
progress by replacing classifications that are partly 'representative' and
partly 'explanatory' with ones that are more 'representative' and less
'explanatory'. 5 More specifically, he holds that clashes between theory
and experiment result in "the purely representational part" of the
theory (i.e., the part obtained using the methods of theoretical physics)
being taken up "nearly whole" by the new theory and "the explanatory
part" (i.e., the part not so obtained) giving way to "another explanation". We are to think of each theory as passing on to its successor "by
virtue of a continuous t r a d i t i o n . . , a share of the natural classification
that it was able to construct".
True, Duhem takes consistency, unity and agreement with experimental laws to be the only 'logical conditions' on physical theories. 6
He does not however take these conditions to be the only ones that
theories should satisfy, still less regard theories that satisfy them as
equally acceptable. In his view 'logically acceptable' theories are all too
easy to come by and it is essential that new theories also be transformations of those already in place. To be acceptable a theory must, he

argues, be "the slow and progressive result of an evolution"; it must
not be "the sudden product of a creation". 7 In other words we should
prefer theories that naturally extend flourishing traditions to ones involving new concepts all other things being equal. It is only when a
tradition falls short on experimental or logical grounds that it is appropriate to contemplate the introduction of new theoretical principles.
Here it is important to keep in mind that Duhem's view of theories
as converging on natural classifications is closely allied with his insistence on the autonomy of physics and its historical continuity. Given
his conception of physics as an essentially autonomous enterprise, it is
entirely unsurprising that he should appeal to the history of physics
(rather than something external to it) to supplement the logical constraints on classifications. And given his commitment to the principle
of historical corttinuity, there is nothing particularly remarkable about
his rejection of the view that physical theories are artificial classifications
in favour of the view that they are becoming increasingly natural. One
can well imagine him thinking that physical theories can be reasonably
regarded as natural classifications just to the extent that they are obtained by methods that are strictly autonomous and are appropriately
continuous with what went before, s
It might be thought that such an interpretation runs foul of Duhem's
conception of 'explanation' as radically at variance with 'logical classification' of his criticism of arguments to the effect that physical theories 'explain' experimentally established laws. But this is far less clear
than it might appear. For what Duhem's attack on explanation is actually directed against is not explanation as such but 'metaphysical explanation'. Even in the first chapter of La Th~orie physique, which is often
taken to clinch the issue, Duhem does not deny that theories tell us
something about the world. Here his main point is the negative one
that it is neither desirable nor possible to derive physics frcm metaphysics. In the terminology of a later chapter, the butt of his criticism is the
view that physics provides "definitive explanations"; he was not against
thinking of physics as directed toward the discovery of "provisional
representations".9
Far from wishing to show that theories should be thought of as
artificial classifications, Duhem was mainly concerned to combat attempts on the part of some of his contemporaries to subordinate physics
to metaphysics. What he rejected was not the usual conception of
physical theorizing as culminating in 'nonmetaphysical' explanations but

rather the view of it as resting in one way or another on metaphysical
assumptions, as subject to a priori restrictions. The main point that he
wanted to emphasize was that the methods of physics are our sole means
of investigating the world, that they are all that we can reasonably rely
on, that they alone provide us with 'representations'. It is, he tells us,
central to his conception of physical science that it "proceeds by an
autonomous method absolutely independent of any metaphysical opinion,,.lo
Similarly it is a mistake to trace Duhem's hostility to atomism and
mechanism to his rejection of the conception of physical theories as
explanations. The reason that he regarded Energetism as deserving
special consideration was not that it happened to have a particular form
but that he was of the opinion that "the means of knowledge available
to Physics justifies the course it takes", his view being that physicists
were - "the gossip of the moment" notwithstanding - in the process of
securing the "complete realization of [the] ideal [of an abstract theory]".l~ For him the problem with scientific inquiry based on atomistic
and mechanistic assumptions was that it violated the requirements of
the autonomy and continuity of physics. He did not think that atomism
and mechanism could not possibly be made good, only that they have
not been (and that there was a better alternative available).12
Undoubtedly part of the explanation of why commentators misunderstand Duhem's position is that they fail to appreciate that he held his
primary task to be one of delineating how the scientific method is
deployed in practice. It is a mistake to assume - as is usualiy done that he aimed to show that the methods of theoretical science are less
robust than normally thought or that he believed that progress in physics
occurs exclusively at the observational level or that thought of physical
truth and theological truth as having to do with different 'ontological
orders'. As he himself put it at the beginning of La Thdorie physique
his object was to provide "a simple logical analysis of the method by
which physical scienc e makes progress'.13 The question of the theoretical progress of physics was never an issue for him; even at his most
philosophical he remained true to his scientific and historical convictions.
To appreciate Duhem's stance it is helpful to remember that he took
the positivism of his day (its important merits notwithstanding) to be
no less flawed than the metaphysical approaches against which it was
then being pitted. He agreed with Ernst Mach and like-minded thinkers

concerning the autonomy of physics and he took attempts to ground
physics in metaphysics (including contemporary neo-scholastic attempts
to integrate it into a general theological cosmology) to be subject to
positivist criticism. Yet he was also convinced that the positivists were
wrong to relegate the aim of physical theorizing t o t h e development of
an economical summary or artificial classification of empirical laws.
Indeed he can perhaps best be regarded as attempting to appropriate
the positivist's criticisms without embracing positivism itself,
Duhem virtually states as much when he observes that "the history
of science alone can keep the physicist from the mad ambitions of
dogmatism as well as the despair of Pyrrhonian skepticism". TMA sensitivity to history and the method by which physical science progresses
is, he insists, an effective antidote both to dogmatic claims about the
subservience of physical theory to metaphysical speculation and to
skeptical counterclaims to the effect that such theory tells us nothing
whatsoever about the world. In his view a study of the history of physics
highlights both the "vicissitudes of cosmological schools" and the inadequacy of picturing "physical theory [as] an artificial system [rather
than as] an increasingly clearer reflection of realities", Whenever physicists are "on the point of going to [either] extreme", such a study can,
he avers, be relied on to provide the 'appropriate correction'.15
What is less clear - and with this we come to the nub of the issue - is
how Duhem can hold that physical theories gradually approach natural
classifications. It would seem that all that he should believe in this
regard is that theories are artificial classifications, this being all that is
warranted by considerations of logic and history. To Duhem's way of
thinking however such a conclusion would be premature. For while he
certainly believes that nothing stronger can be justified on the basis of
the logical and historical arguments appropriate to physical inquiry, he
is also of the view that there are additional nonlogical, nonhistorical
arguments that need to be considered. As he states the matter, "no
scientific method carries in itself its full and entire justification [and]
we s h o u l d . . , not be astonished that theoretic physics rests on postulates which can be authorized only by reasons foreign to physics". 16
Once again Duhem accepts some of the positivists' principles and
rejects others, He agrees with them concerning the character of the
methods of physics and the particular theories that can be obtained
using these methods. But he disagrees concerning the nature of the
theories and what these tell us about the world. In particular he takes

the positivists to err in supposing that scientific justification is the only
sort of justification that counts. The fact that physics is an autonomous
enterprise in which an attempt is made to devise economical classifications of phenomena is, he insists, no reason to believe that all that a
proper application of its methods can yield are economical classifications. As he sees the matter, physics is capable of establishing far more
than it itself can establish that it has established. 17
In support of this central point Duhem argues that it is taken for
granted - albeit surreptitiously - even by positivists. One cannot, he
argues, accept the positivist's assumption that physical theorizing results
in unified classifications without admitting that such theorizing goes
well beyond what can be justified in its own terms, hodgepodges of
empirical laws being perfectly compatible with pure logic and economy
of thought. Indeed Duhem explicitly states that "neither the principle
of contradiction nor the law of economy of thought permits us to prove
in an irrefutable manner that a physical theory should be logically
coordinated", is If one takes physics to be a well-founded enterprise
one must, he concludes, admit the existence of another "source [from
which] an argument [can be drawn] in support of this opinion".
To avoid misunderstanding I should stress that I am not arguing that
Duhem took the positivists to be right about physics and wrong about
what lies beyond it. He did not hold that physicists stray beyond the
confines of physics strictly understood when they assert that their theories are becoming increasingly natural, nor did he believe that they are
- in their capacity as physicists - obliged to think of their theories as
artificial classifications. To the contrary Duhem held that physicists are
even in this capacity entirely justified in taking their aim to be the
establishment of natural classifications and their theories to be even
now natural (at least to a certain extent). In his view what lies beyond
physics are only the arguments that warrant physicists believing what
they happen to believe? 9
Duhem himself devotes considerable effort to spelling out arguments
for these beliefs; he does not simply state that arguments are required.
Thus he points out that "it is impossible for us to believe that [the
order and organization revealed by our theories] are not the reflected
image of a real order and organization" and he argues in some detail
that physicists are best thought of as "yielding to an intuition which
Pascal would have recognized as one of those reasons of the heart "that
reason does not know". 2° In his view we are entirely justified in believ-

ing that theories tell us something about the world since it is entirely
natural to do so. We should not be misled by the fact that such belief
requires an intuitive judgement involving a 'reason of the heart'; this
does not mean that it is unimportant or unreliable.
In addition Duhem would have us believe that physicists are justified
in thinking of theories as natural classifications to the extent that they
are able to use them to obtain novel predictions. The possibility of
obtaining information about new situations would in his view be exceedingly remote were physical theories not at least roughly in accord with
how the world actually is. If a "theory [were] a purely artificial system",
its confirmation by a "hitherto unknown law" would, he stresses, "be
a marvelous feat of chance" and we should be quite unwilling to "bet
fearlessly in its favour". 21 Of course this is not a deductively valid
argument, it being impossible to derive a conclusion having to do with
the nature of theories (namely that they are natural classifications) from
a premise having to do with how theories have actually been used
(namely that the best of them successfully anticipate the future). But
for Duhem it is none the worse for that; he has no objection to this
type of nondeductive ('transcendental') argument. 22
In this connection it is helpful to recall that Duhem takes theoretical
physics and "spiritualistic metaphysics" to be both "radically heterogeneous" and "approach[ing] each other in their perfect form". 23 It is,
he reminds us, one thing to deny that metaphysical conclusions can be
derived solely from physical premises, quite another to hold that they
cannot be derived from physical premises in conjunction with other
reasonable (nonphysical) assumptions. What Duhem wishes to stress is
not that theoretical physics has no bearing on theological cosmology,
only that its bearing is never direct. One can, he insists, see that such
heterogeneous viewpoints are (or are not) analogous given "reasons
foreign to physics"; what is totally divorced from metaphysics is physical
theory "in itself and by its essence". 24
Thus I would dispute the widely-held view that Duhem contradicted
himself when he took general thermodynamics to approximate a natural
classification analogous to Aristotelian cosmology. In arguing this way
he was not compromising the principle of the autonomy of physics nor
was he going back on his views about the separability of physical
findings from metaphysics. While general thermodynamics "in itself
and by its essence" neither accords nor conflicts with Artistotelian
cosmology, we have every reason to hold that the two views are in

substantial agreement given the direction in which physics is tending and
certain extrascientific considerations. "Aristotle's cosmology reduced to
its essential affirmations" is indeed plausibly taken to be analogous to
"the teachings of thermodynamics" and it is not difficult to appreciate
Duhem's insistence that this is "all the more striking" for not having
been planned in advanceY
Be this as it may, it should be clear that Duhem stands foursquare
against instrumentalistic conceptions of physical theories. 26 He meant
what he said when he spoke of theories as "permit[ting] hints as to the
real affinities of things" and stated that natural classification serves as
"a sort of image and reflection of the true order according to which
the realities escaping us are organized". 27 For him it would have been
quite implausible to maintain that physical theories tell us nothing
except that certain experimental laws are logically coordinated. While
physics is (and always will remain) incomplete, we are well within our
rights to think of theories associated with traditions tending in definite
directions as reliable indicators of the realities behind the appearances.
In particular I should emphasize that it is not only those who regard
Duhem's philosophy as instrumentalist through and through who are
at fault. If the present interpretation is correct, it is just as wrong to
describe his view as 'mitigated' o r 'qualified' instrumentalism or to
classify it as 'semantic realism' or to think of it as a species of 'commonsense realism'. Duhem was not attempting to straddle the fence, nor
did he merely believe that physical theories should be regarded as true
or false, nor was he any less committed to the reality of scientific objects
than to the reality of everyday ones. Quite the reverse. If anything he
espoused a version of what is nowadays called convergent realism. As
we have seen he held that physics - left to its own devices - yields
information about the nature of the world and that we are entirely
justified in believing that its ontological claims are for the most part
close to the truth. 28
Admittedly it is not difficult to cobble together quotations from
Duhem's writing that make him sound as though he was uncompromisingly opposed to realism of any kind. 29 It is also true, however, that
we omit an important part of his story when we read him this way. His
general strategy is to argue first that theories are classifications (as
opposed to metaphysical explanations) and then to provide considerations for the view that they are more or less natural (rather than
artificial). Far from regarding physics as aiming at logical classification,

he takes this view of the matter to be the unsatisfactory outcome of an
overly narrow conception of what physics can achieve. For him "physical theory confers on us a certain knowledge of the external 'world
which is irreducible to merely empirical knowledge" and there is no
avoiding the fact that a purely instrumentalistic physics would be of
"meager importance". 3°
NOTES
* I have benefited from discussions with Howard Duncan concerning Duhem's philosophy, and from Roger Ariew's and Michel Stack's criticisms of an earlier version of the
paper. Also I would like to thank Ernan McMullin for his comments at the Blacksburg
Conference.
a Compare L. de Broglie's suggestion that Duhem "mitigate[d] the rigor" of his view
because he felt that physical theory must be accorded "a deeper bearing than that of
mere methodical classification of facts already known" (1962, p. x) and R. Poirier's claim
that "[Duhem's] expression 'natural classification' is roughly equivalent to 'language'"
(1967, p. 403).
2 Duhem invokes the conception of natural classification not only in La thdorie physique
of 1906 but also in 'L'rcole anglaise et les throries physiques' of 1893 and in 'Notice sur
les titres et travaux scientifiques' of 1913.
3 Duhem (1914/1962), p. 270.
a Duhem (1914/1962), p. 31. Also compare Duhem's view that "we can and we m u s t . . .
attempt to make [our] classifications as little artificial and as natural as possible"
(1893b/1987, p. 137) and his claim that "physical theory may attain a certain knowledge
of the nature of t h i n g s . . . [as] the goal of [its] progress, the limit it constantly approaches
without ever reaching" (1917/1987, p. 338).
5 Duhem (1914/1962), p. 32; see also pp. 204-5 and p. 221.
6 Duhem (1914/1962), p. 220.
7 Duhem (1914/1962), p. 221; see also p. 295. A good example is Duhem's criticism of
Maxwell's introduction of the notion of displacement current (see pp. 78-79 and Ariew
and Barker 1986, pp. 140-50). Also it should be remembered that Duhem argues that
"the physicist does not choose the hypothesis on which he will base a theory" but rather
draws on "the thoughts habitual with those among he lives and tendencies impressed on
his own mind by his previous studies" (1914/1962, pp. 255-56).
s The importance of t h e autonomy of physics for Duhem can hardly be overstated, it
being one of his "constant" concerns (1914/1962, p. 274). Compare Martin (1976), p.
127, where Duhem is said to have regarded the autonomy of physics as "an essential
regulative principle". In emphasizing this point I do not of course mean to belittle the
importance of Duhem's critique of the "Newtonian method of induction from observation" (see also Ari~w 1984, pp. 319-20).
9 Duhem (1914/1962), p. 270; see also Duhem (1893a/1987). In addition note that the
title of the first chapter of the La Th~oriephysique is "Physical Theory and Metaphysical
Explanation" and that explanation and classification are introduced as the two main
answers that "logicians" have given to the question of the aim of physical theory (p. 7).
Moreover Duhem is not in the least averse to speaking of other possible aims (see, e.g.,

p. 81). It is, I suggest, wrong to suppose that his discussion rests on a "dogmatic and
unsupported presupposition about the nature of explanation" (compare Alexander 1967,
p. 423).
ao Duhem (1914/1962), p. 274. Contrast Karl Popper's suggestion (1969, p. 104) that
Duhem "seems to think t h a t . . , there are essences but they are undiscoverable by human
science (although we may, somehow, move towards them)". As I read Duhem, his view
was not that "essences.,. are undiscoverable by human science" but that they are only
discoverable this way. Incidentally there are many striking parallels between Popper's
own philosophy and Duhem's (see e.g., Duhem (1914/1962), pp. 23, 27, 53, 177, and
277).
11 Duhem (1917/1987), p. 334 and Duhem (1914/1962), p. 304.
12 Significantly Duhem argues that atomism and Cartesianism are plagued by faulty
reasoning and at variance with important experimental laws; he does not challenge them
on philosophical grounds (compare his (1914/1962), pp. 80-86, 280, and 304), While
Duhem agrees with Hertz that "Maxwell's theory is the system of Maxwell's equations"
(p. 80), he no more takes the theory to be an artificial classification than does Hertz, his
main point being that it should not be encumbered with mechanical models. Also compare
Duhem's criticism of the atomist and the Cartesian for placing "hypothetical knowledge
of the nature of things at the starting point of physical theory" (1917/1987, p. 338).
13 Duhem (1914/1962), p. 3. Also note that Duhem believed that "to give the history of
a physical principal is at the same time to make a logical analysis of it" (p. 269).
14 Duhem (1914/1962), p. 270.
is Also compare Duhem's rejection of the complaint that his view "opens the door to
skepticism" and "makes a concession to positivism" (1893a/1987, p. 97). In this paper I
do not consider Duhem's historical work but it is worth noting that here too one of his
major themes is that physical theories are neither subordinate to metaphysics nor merely
'artificial'.
16 Duhem (1914/1962), p. 293; see also p. 298. In arguing this point I part company with
R. N. D. Martin, who holds that Duhem was concerned with the possibility of logically
justifying the requirement that physical theories be "logical and coherent" (see his 1987,
p. 306). As I read Duhem his point was that certain scientific procedures cannot be
established given logic (and history); he did not think of logic (or history) as being in
need of justification.
17 See also Duhem (1893a/1987), p. 99.
is Duhem (1914/1962), p. 102; see also pp. 293--4 and 334, and Duhem (I893b/1987), p.
134, The same point can be made about the common positivist demand - defended, e.g.,
by Mach - that later theories connect up with earlier ones.
19 If this is right, Duhem did not hold that "the scientist qua scientist must work with
theories as if they are only instruments [i.e. mere classifications]" (Joy 1975, p. 197). In
the terminology of Bas van Fraassen (see his 1980) Duhem maintained that physicists are
justified in believing their theories as well as in accepting them as empirically adequate. As
Michael Stack has pointed out to me there is an interesting analogy between physical
theories (as I take Duhem to conceive them) and perceptual beliefs in that both provide
information the reliability of which can be vouchsafed only by invoking 'external considerations'.
2o Duhem (1914/1962), pp. 26 and 27. Significantly Duhem also speaks of the physicists's
concern with unity as being "a legitimate one because it results from an innate feeling"

(p. 102). "The aspiration towards a theory whose parts all agree logically with one
another is", he insists, "the inseparable companion of [the] aspiration.,, towards a
theory which is a natural classification of physical laws" (pp. 103-4).
2i Duhem (1914/1962), pp. 28; see also pp. 195 and 297. In the same context Duhem
states that "the wonderful order [that] classification . . . brings about in the tremendous
arsenal of chemistry already assures us that the classification is not a purely artificial
system" (pp. 28-29; see also p. 300).
22 Thus I reject N. Cartwright's contention (1982, p. 112) that Duhem is antipathetic to
"theoretical laws because he does not countenance inference to the best explanation".
On my reading, Duhem espoused a version of what has come to be called "the miracle
argument" and he was opposed neither to theoretical laws nor to inference to the best
explanation.
23 Duhem (1914/1962), pp. 301 and 299.
24 Duhem (1914/1962), p. 285. It is irrelevant that there are normally disanalogies as
well as analogies between physics and metaphysics (p. 303). The crucial point is that we
can on occasion legitimately step beyond physics and "recognize in [physics and metaphysics] two pictures of the same ontological order, distinct [only] because they are each
taken from a different point of view" (p. 310). When Duhem speaks of his view as being
positivist in both "its origins" (p. 275) and "its conclusions" (p. 279), what he means is
that he developed his ideas without appealing to metaphysics and without having had
any specific conclusion in mind.
25 Duhem (1914/1962), pp. 310 and 307. I might note in passing that Duhem's discussion
of refutation rests on considerations similar to those just outlined. Duhem's basic idea is
that it often makes "good sense" to reject a theory rather than an auxiliary assumption
and that while decisions based on good sense cannot be justified scientifically they are
nonetheless perfectly reasonable (see p. 217).
26 Compare, e.g., Alexander (1967), p. 425, Popper (1959), p. 78, and van Fraassen
(1980), p. 86.
27 Duhem (1914/1962), pp. 30 and 31. It should not be forgotten that Duhem took
his preference for Energetism over atomism to have important consequences for our
understanding of the nature of the world and that he recognized the existence of "microscopic nuclei" (see p. 221).
28 For the views criticized in this paragraph see Joy (1975), p. 199 and Martin (1987), p.
309, Giedymin (1976), p. 184, and Jaki (1984), p. 320.
29 Compare Duhem (1914/1962), pp. 8, 19, 21, 115, 124, 144, and 180.
30 Duhem (1914/1962), p. 334.

REFERENCES
Alexander, P.: 1967, 'Pierre Duhem', in P. Edwards (ed.), Encyclopedia of Philosophy,
Macmillan, New York, Vol. 2, pp. 423-5.
Ariew, R.: 1984, 'The Duhem Thesis', British Journal for the Philosophy of Science 35,
313-25.
Ariew, R. and P. Barker: 1986, 'Duhem on Maxwell', PSA i986, Philosophy of Science
Association, East Lansing, Michigan, pp. 145-56.
de Broglie, L.: 1962, 'Forward' to P. Duhem 1914/1962, pp. v-xiii.

Cartwright, N.: 1982, 'When Explanation Leads to Inference', Philosophical Topics 13,
111-22.
Duhem, P.: 1893a/1987, 'Physique et mdtaphysique', reprinted in S. L. Jaki (ed.), Pierre
Duhem: prdmices philosophiques, E. J. Brill, Leiden, pp. 84-112.
Duhem, P.: 1893b/1987, L'6cole anglaise et les theories physiques', reprinted in S. L.
Jaki (ed.), Pierre Duhem: prdmices philosophiques, E. J. Brill, Leiden, pp. i13-46.
Duhem, P.: 1914/1962, La thgorie physique: son objet, sa structure, 2rid ed., translated
by P. P. Wiener as The Aim and Structure of Physical Theory, Atheneum, New York.
Duhem, P.: 1917/1987, 'Notice sur les titres et travaux scientifiques', translated in part
by Y. Murciano and L. Schramm in Science and Context 1, pp. 333-48.
Giedymin, J.: 1976, 'Instrumentalism and Its Critique: A Reappraisal', in R. S. Cohen
et al. (eds.) Essays in Memory of lmre Lakatos, Reidel, Dordrecht, pp. 179-207.
Jaki, S.: 1984, Uneasy Genius: The Life and Work of Pierre Duhem, Nijhoff, The Hague,
The Netherlands.
Joy, G.: 1975, 'Instrumentalism: A Duhemian Reply to Popper', Modern Schoolman 52,
194-99.
Martin, R. N. D.: 1976, 'The Genesis of a Mediaeval Historian', Annals of Science 33,
119-29.
Martin, R. N. D.: 1987, 'Saving Duhem and Galileo', History of Science 25, 301-19.
Poirier, R. : 1967, 'L'~pistemologie de Pierre Duhem et sa valeur actuelle', Etudes philosophiques 22, 300-419.
Popper, K. R.: 1959, Logic of Scientific Discovery, Hutchinson, London.
Popper, K. R.: 1969, Conjectures and Refutations, 3rd revised edition, Routledge and
Kegan Paul, London.
van Fraassen, B.: 1980, The Scientific Image, Oxford University Press, Oxford.
Department of Philosophy
University of Ottawa
Ottawa, Ontario, KIN 6N5
Canada

C O M M E N T : D U H E M ' S M I D D L E WAY

ABSTRACT. Duhem attempted to find a middle way between two positions he regarded
as extremes, the conventionalism of Poincar6 and the scientific realism of the majority
of his scientific colleagues. He argued that conventionalism exaggerated the arbitrariness
of scientific formulations, but that belief in atoms and electrons erred in the opposite
direction by attributing too much logical force to explanatory theories. The instrumentalist
sympathies so apparent in Duhem's writings on the history of astronomy are only partially
counterbalanced by his view that science is progressing toward a 'natural classification'
of the world.

In Duhem's writings about the nature of science, there is an ambivalence that even the most casual reader can scarcely miss. His account,
in consequence, does not fit into the usual categories of the philosopher
of science. He was, it seems, quite consciously trying to thread a middle
way between two positions he regarded as extremes. One was what
would today be called scientific realism, in the most usual sense of that
much-distinguished phrase, that is, the view that the explanatory success
of a scientific theory gives one valid (even though rarely conclusive)
reason to believe in the existence of the underlying entities postulated
by the theory. Duhem strongly rejected what has come, by a clumsy
phrase, to be called 'inference to best explanation', holding on both
historical and logical grounds that the explanatory power of a structural
theory cannot serve as a testimony of its truth.
On the other hand, he was equally unhappy with the conventionalism
of Poincar6 and the inductivism he found in the physics textbooks of
his day, because he thought that they unduly limited the truth-claims
of science either by exaggerating the arbitrariness of the scientific formulations, as in the case of conventionalism, or by undervaluing the
symbolic character of physical theory and the holistic character of its
associated warrant, as he held inductivism to do. His distinctive notion
of natural classification expresses his attempt to separate himself from
the skepticism he saw as inherent in the two dominant fashions of the
day in French philosophy of science, without at the same time embracing the model-realism he liked to associate with the 'broad but weak'
English mind.
Synthese 83: 421-430, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

By intention at least, then, he was neither a realist nor a skeptic
about physical theory, in the most usual senses of those two elastic
terms. In a move reminiscent of Arthur Fine's recent attempt to find
a middle way between realism and instrumentalism, he proposed a
definition of physical theory that allowed him conclude that:
What is lasting and fruitful [in physical doctrines] is the logical work through which they
have succeeded in classifying naturally a great number of laws by deducing them from a
few principles; what is perishable and sterile is the labor undertaken to explain these
principles in order to attach them to assumptions concerning the realities hiding underneath sensible appearances. (1914, p. 38)

The 'natural ontological attitude' he advocated, to appropriate a phrase
coined by Fine, is to suppose that even though physical theory is
incapable of itself of discovering entities that do not belong among the
sensible appearances:
The more complete it becomes, the more we apprehend that the logical order in which
theory orders experimental laws is the reflection of an ontological order, the more we
suspect that the relations it establishes among the data of observation correspond to real
relations among things, and the more we feel that theory tends to be a natural classification. (1914, pp. 26-27)

Notice the language Duhem uses when he describes how we come to
this belief: "the more we a p p r e h e n d . . , the more we s u s p e c t . . , the
more we f e e l . . . " . Even though the convergence of physical theory on
the relational structure of the world cannot be demonstrated by the
methods of physical science itself, it is the natural attitude for scientists
to adopt, and is supported by philosophic consideration of the history
of specific theories.
Duhem walked a tightrope, to be sure. On the one hand, he found
himself in disagreement with the most illustrious French exponents of
the new discipline of philosophy of science, Henri Poincar6, Eduard
LeRoy, and Abel Rey, who seemed to want to reduce science to a set
of practical prescriptions for action, depriving it of its status of objective
knowledge, as Duhem understood that phrase. On the other hand, he
was scornful of the attempts of the most distinguished physicists of the
day to construct theories involving unobservable entities like molecules,
atoms, and electrons. Despite the fact that such theories "would undoubtedly be regarded as prophetic forerunners of the theory destined
to triumph in the future", despite the 'almost universal assent' favoring
them among working scientists themselves, he urges his readers to set

them aside and to learn from the study of "the errors of past centuries"
to be on guard against those "efforts of the mind that wishes to imagine
what ought to be merely conceived" (1905, p. 304).
But Duhem did not want to appear entirely out of step. He tried to
put the best face on his disagreement with Poincar6 and Mach, claiming
to find a tension, amounting at times indeed to logical contradiction,
in their work. Besides their usual stress on scientific law as convention
or as convenient summary, he reminds us that they also on occasion
allow, indeed insist, that physical theory leads to the discovery of the
real relations of things with one another (1908b, pp. 327-35). He traces
this tension in their thinking to the complex character of the question
itself. A logical analysis of the experimental method can never of itself
warrant anythir~g more than the claim that physical theory serves an
instrumental function as a predictive device. It could not, for example,
forbid the simuJtaneous use of incompatible theories, provided they
served the purposes of prediction. Working scientists could never be
content with this; yet their conviction that such incoherence must be
eliminated cannot be justified merely by an appeal to convention or to
instrumental convenience.
It derives, he argues, from an intuition which clearly transcends the
limits of science. Those who subscribe to a generally positivist ideal of
knowledge face a dilemma, then. If they allow progressive unification
of laws as a requirement of good science, they seem to violate the
positivist canon; if they do not, they are likely to "shock most of those
working for the advance of physics" (1905, p. 294). This is how Duhem
excuses those whom he criticizes so gently: their heart is in the right
place, he tells us. When they err, it is by understatement, it is only
because they fail to realize that they do not need to take positivism
quite so literally. He is not nearly so tolerant of the other extreme, of
the 'atomists', as he calls them generically, those who believe that the
explanatory power of theory allows us to penetrate beneath the level
of sensible appearance, Their imaginative excess is more dangerous
than positivist defect because of its allure, to scientists and nonscientists
alike.
In his essay, 'Duhem's Conception of Natural Classification', Andrew
Lugg focuses on Duhem's doctrine of natural classification in order to
argue two theses, first, that despite appearances to the contrary, Duhem
was not an instrumentalist, and second, that equally despite appearances to the contrary, he was a realist, advocating a version of conver-

gent realism. I would agree with him on the first of these theses, with
some reservations, but would deny the second.
The instrumentalist thrust of To Save the Phenomena is well known.
Duhem traces the debates in astronomy between the 'mathematicians'
whose aim was merely to find a formalism that would fit the phenomena
and the 'physicists' who wanted to explain the planetary motions in
causal terms.1 His sympathies are clearly with the former in the period
prior to Galileo, when the explanatory schemes of the 'physicists' drew
their warrant mainly from metaphysical principles in regard to causal
action and hardly at all from their ability to save the phenomena. The
concluding sentences of the book are worth pondering:
Despite Kepler and Galileo, we believe today, with Osiander and BeUarmine, that the
hypotheses of physics are mere mathematical contrivances devised for the purpose of
saving the phenomena. But thanks to Kepler and Galileo, we now require that they save

all of the phenomenaof the inanimate universe together. (1908a, p. 117)
Duhem leaves us in no doubt that he believes Copernicus and Galileo
were wrong, in principle, to suppose that their astronomy could allow
them to claim that the earth is in motion. Their contention that their
hypotheses bear on 'real movements' was 'false and harmful', and
Osiander, Bellarmine and Urban VIII were right in viewing it as 'contrary to logic' (p. 116). There is no suggestion here (as there is elsewhere in his work) of a 'higher logic' that could later reverse this
judgment. 2 Insofar as Kepler and Galileo are given credit, it is for their
unification of earth and heavens in a single mathematical scheme, a
unification that Newton carried to completion. This overcame the sharp
dichotomy between the instrumentalism and the realism of earlier astronomy, and was thus the first major step to a natural classification.
So despite Duhem's insistence that it was the 'mathematics' and not at
all the 'physics' of that earlier period that would bear fruit, he still
manages to find a precarious middle way, one that leans, however,
rather more in one direction than the other?
Duhem criticized the overly instrumentalist tendencies he detected
in the conventionalism of Poincar6 and the positivism of Mach, because
they fail to account for the progressive unification to which the history
of science gives unequivocal testimony. Though there are discontinuities
in the history of physical theory, Duhem insists that these are on the
side of explanation; the metaphysical fashions controlling such explanation come and go, like the ebb and flow of the tide (1914, p. 39). On

the side of representation, however: "each theory passes on to the one
that follows it a share of the natural classification that it was able to
construct" (pp. 32-33).
One is reminded here of Kuhn, who stresses the discontinuity that
characterizes the development of explanatory theories (and is led, like
Duhem, to reject scientific realism on that account) but still wants to
insist on the overall progress in puzzle-solving and the cumulative
character (in one sense at least) of experimental laws. Like Duhem, he
insists also on the objectivity of scientific knowledge, despite his rejection of explanatory ontologies. Kuhn bases this claim on the fact that
theory-appraisal is guided by values, over and above predictive accuracy, that are themselves relatively "permanent attributes" of science;
again, the resemblance to Duhem's argument is striking. Kuhn would
no more want to be thought an instrumentalist than did Duhem, but
his defenses against the charge might be thought less secure, since he
could not call on so ontological a ground as Duhem's natural classification.
Lugg notes Duhem's criticisms of the two doctrines from which the
instrumentalism he questioned might derive. Yet Duhem's differences
with the two seem at times more of the nature of family quarrels. He
argues that Poincar6's conventionalism makes him unable to account
for the part played by theoretical interpretation in the statement of
experimental facts. Yet he also describes the principles of his own
energetics as "pure postulates or arbitrary decrees of reason" (Duhem,
1917, p. 1), validated only by the conformity of their consequences with
experimental law. The conventionalist emphasis on the arbitrariness of
symbolic formulations is not without virtue in his eyes, it would seem,
though it is in the end qualified, of course, by the doctrine of natural
classification.
Duhem is even gentler with positivism. He opens section 2 of 'Physics
of a Believer' with the words:
We should like to prove that the system of physics which we propose is subjected in all
its parts to the most rigorous requirements of positive method, and that it is positivist in
its conclusions as well as its origins. (1905, p. 275)

It is true that this essay, preoccupied with showing that he did not,
as his critics charged, make his physics subservient to a metaphysics, is
more emphatic- about the virtues of positivism than anything else he
wrote. Nevertheless, his insistence on the "essentially positivistic"

character of his account of physics (p. 279) was genuine. He could
applaud positivism for its exclusion from science proper of metaphysics
in any form. He could identify with the positivist denial of "any ability
[on the part of physical theories] to penetrate beyond the teachings
of experiment or any capacity to surmise realities hidden under data
observable by the senses" (p. 274). By arguing that physics was both
autonomous and yet in a fundamental sense incomplete, he could retain
positivism in one area while flatly contradicting it in another. Because,
of course, his insistence on the legitimacy of a metaphysics violated the
fundamental principle of Comte in regard to positive knowledge.
Duhem plays down this disagreement; the alliance with positivism was
crucially important to him. Though Lugg is clearly right to maintain
that in the end Duhem was in the strict sense neither a positivist nor a
conventionalist, it is important to stress how strong his affinity was with
both doctrines.
Lugg's second thesis, cannot, I think, be sustained. He takes Duhem
to be a realist, in the sense of holding that "the furniture of the world
is more or less what our latest theories pronounce it to be". Further,
he takes Duhem's opposition to atomism and mechanism not to be one
of epistemological principle; it is only, he thinks, a matter of the
inadequacy of the evidence as yet available in their favor. The trouble
with them "is not that they cannot (in principle) be made good but that
they have (as a matter of fact) never been made so".
Here I find myself in strong disagreement, though I realize that the
matter is not cut and dried. Duhem's objections to the use of retroduction within physics itself to infer to the existence and nature of entities
that lie beneath the level of sensible appearance, are assuredly a matter
of principle for him. Lugg argues that Duhem's often-repeated view
that physical theory cannot penetrate beyond the sensible appearances
has to be read in the light of his distinction between the physicist's
viewpoint, taken narrowly, and the larger perspective afforded by intuition and philosophical argument. But all that the distinction warrants
in this case is the claim about natural classification: that physical theory,
considered as a set of abstract laws, mirrors the underlying relations
between things more and more exactly. Does Duhem envisage that
molecules, atoms, electrons, and the like may one day become part of
the natural classification? Quite clearly not, it seems to m e . 4 If this
were to be even a possibility, his arguments against mechanism would

fail, and his strictures on explanatory models would have to be discounted as referring only to their use up to the time at which he wrote. I
can find no basis in his text for such a construal.
The only kind of realism that we can claim for him (and it is, of
course, a crucial one for him) is that of the relationships he found in the
laws of mechanics or, more generally, in what he called "energetics°'. It
is not a realism of explanatory theory. The distinction between law and
theory which is common today he did not make. For him, the explanatory aspects of the physical theories of his day, those involving unobserved entities causally responsible for the data of experiment, were
excess baggage~ illegitimate indulgences of the imagination. Would
he have allowed retroduction in areas other than the microworld, in
astrophysics or geology, for example? It is not clear. Is he, to speak
very loosely, in the early lineage of van Fraassen or of Laudan? Is he
prompted by an empiricism that would disallow any attempt to postulate
entities that are in principle unobservable? Or is he motivated by a
distrust of the ontological significance of explanatory models in any
domain of science, whether micro or macro?
Lugg notices that the arguments Duhem employs for the ontological
significance of the classifications found in physical theory are remarkably similar to one set of arguments used by contemporary defenders
of scientific reafism. Duhem notes the fertility and the unifying power
of the abstract laws of physics, and urges that these cannot possibly be
an "accident"; they are best explained by supposing these laws to
reflect "realities whose essence cannot be grasped by [the] methods [of
science] . . . . arranged in a certain order which physical science cannot
directly contemplate" (1905, p. 297). Here (as Lugg remarks) is inference to best explanation at the meta-level, more problematic in
Duhem's use of it than in that of the contemporary realists who do not
(as he does) implicitly question its validity at the object level. Why did
it not occur to him that the sort of argument he uses for his realism of
relations could just as easily be used for a realism of micro-entities?
Perhaps it was because these hidden entities seemed to him so remote
from human modes of perception and conception; they could be
reached only in imagination, and he distrusted imagination. But as he
scrutinized the historical record, the role played by metaphysics seems
to have bothered him even more. Only by drawing upon a cosmology
that legislated the acceptable sorts of entity and the permissible modes

of interaction could the theorist (it seemed) construct a causal account
of what supposedly goes on beneath the accessible surface of appearance. Not only are the facts of science theory-dependent, but explanatory theories have always been metaphysics-dependent. And this second
sort of dependence has not been beneficial; atomists, Cartesians, and
others have imposed their own notions of mechanism, and none have
found any lasting success. A theme to which he returns again and again,
one to which he clearly gave emotional as well as intellectual weight,
is the importance of recognizing the basic autonomy of physics. The
progressive unification which has gone on since Galileo's day has
proved, he asserts, to be in no need of the imaginative dress of cosmology.
Duhem clearly thinks of metaphysics as a contaminant in the earlier
story of physical theory. Because the physicist wrongly aspires to penetrate to bodies beyond the level of perception:
He no longer has the right to shut his ears to what metaphysics wishes to tell him about
the real nature of matter; hence as a consequence, through dependence on metaphysical
cosmology, his physics suffers from all the uncertainties and from all the vicissitudes of
that doctrine. (1917, p. 1)

His theories are thus "condemned to perpetual reformulation", and
cannot assure the consensus and progress of which science is capable.
Duhem's attitude to metaphysics is puzzling. 5 On the one hand, in
passages such as this one, he appears skeptical of the insights it claims
into the true nature of physical things. On the other, he is careful not
to deny its legitimacy as an autonomous mode of inquiry: "Our inquiry
concerning physics has not led us either to affirm or deny the existence
and legitimacy of methods of investigation foreign to this science"
(1905, p. 280). Indeed, he argues that metaphysics and physics ought
ultimately converge on the same natural classification, and suggests that
the cosmology towards which his favored science of energetics is tending
is the Aristotelian one, rid of its "fossilized doctrines" (1954, p. 308).
What might give cosmology access to the structure of the physical
world independently of scientific inquiry he never discusses. Are we to
suppose he is speaking here as a Catholic apologist? And if we are,
must this be thought to be merely a strategy on his part or a founded
belief? Difficult but important issues, ones that cannot be addressed in
short compass.
From the standpoint of contemporary scientific realism, Duhem appears to have seriously undervalued the resources of retroduction.

Imagination is not as dependent on prior cosmological commitment as
he supposed, and the criteria of fertility and unification that he valued
can direct imagination more effectively than he allowed. It is true that
in the historical cases he studied, the warrant for ethers and atoms lay
not so much in their contribution to a predictive model as in a prior
philosophy of nature. It is also true that his focus was on mechanics
where the purchase of realism has for quite specific reasons always been
precarious. Had he looked more closely at the structural sciences of
his own day, he might not have been quite so pessimistic about the
ability of the theorist to divine the shapes of entities that escape the
contingent modes of human perception.
NOTES
1 Historians have been critical of Duhem's instrumentalist reading of the Platonic tradition of 'saving the phenomena'. The commitment to circular motions and uniform
speeds of rotation would of itself suggest that the mathematical formalism was not chosen
on merely pragmatic grounds; the circular motions were in some appropriately qualified
sense regarded as real. And Duhem too easily ascribed straightforwardly instrumentalist
views to writers such as Ptolemy whose real views were undoubtedly much more mixed.
See G. E. R. Lloyd, 'Saving the Appearances', Classical Quarterly 28 (1979), 202-22.
2 R. N. D. Martin is at pains to argue that Duhem's apparent support for Bellarmine
and Urban and his criticism of Galileo must not be taken as an attempt on Duhem's part
to vindicate the action of the ecclesiastical authorities in 1616 ('Saving Duhem and
Galileo', History of Science 25 (1987), 301-19). Martin recalls Duhem's dictum that "pure
logic is not the sole guide of our judgements", and suggests that the fact that Galileo is
criticized here for his faulty logic ought alert us that "reasons of the heart" might (in
Duhem's view) have been operating under the surface, and that it was Galileo in consequence who was on the right track after all.
Martin may well be right about Duhem's relation to the ecclesiastical authorities of his
own day. But it is important to note that the insights Duhem finds hidden in Galileo's
work are (as Martin himself goes on to point out) cosmological ones about the unity of
earth and sky. Indeed, Duhem is explicit in saying that the truth Galileo was, all unknowingly, introducing was that "one form of dynamics, by rleans of a single set of mathematical formulae, must represent the movements of the s t a r s . . . (and) the fall of heavy
bodies" (1908, pp. 116-7). But this was not the issue between Galileo and Bellarmine.
On that issue, the Copernican claim about the reality of the earth's motion, Duhem never
qualifies his original claim that Galileo was wrong and that his critics were right. They
had, in this respect, understood the limitations of the experimental method better than
Galileo did (p. 13); see also 1914, p. 43. They realized (he alleges) that the hypotheses
of the astronomer are not, in fact, "judgements about the nature of heavenly things and
their real movements" (1908, p. 116). On this point, Duhem was entirely in agreement
with them, and not with Galileo. The limited realism of the 'natural classification' later
disclosed in Newtonian dynamics would undermine the simple instrumentalism they

imposed on mathematical astronomy. But it would not validate the realism of Galileo's
original position.
3 Instrumentalists might not find the theme of unification as congenial as Duhem assumes;
nor would the 'natural classification' imposed by a mechanics that prescinds from causal
explanation appear all that oppressive to them. It is in the end not clear what the notion
of classification amounts to in the domain of mechanics (by contrast with biology or
chemistry). What is being classified, if inference to unperceived entities is forbidden?
4 He never did (so far as we know) relax his opposition to a realist construal of atoms,
even in the light of the new arguments from Brownian motion which convinced Poincar~
and Ostwald, and even perhaps Mach. In his last published writing, La Science Allernande
(1915), he criticized the physics of electrons as a typical product of the esprit g(ometrique
so characteristic of the German mind (pp. 131-4). He rejected the theory of relativity
on the same grounds, deploring its disdain for common sense (pp. 134-9).
5 It is worth noting that metaphysics plays a dual role for him, first as cosmology or
philosophy of nature, and second, as reflection on the aims and limitations of science,
i.e., as philosophy of science. The argument for the convergence of physics on a natural
classification transcends the unaided resources of the physicist; it requires a ~metaphysical
assertion', but one whose validity is nevertheless crucially important to Duhem's entire
,position. He is obviously much more comfortable with "metaphysics' in this second sense
than in the first.

REFERENCES
The date of original publication will be used in the text to identify each work, but the
page references will be to the English translations noted below.

Duhem, P.: 1905, "Physique de croyant', Annles de Philosophie Chr~tienne 77. Translated
as an appendix in The Aim and Structure o f Physical Theory, 1954, pp. 273-311.
Duhem, P.: 1908a, Sozein ta Phainomena, Paris, Hermann. Translated by E. Doland
and C. Maschler as To Save the Phenomena, 1969, University of Chicago Press,
Chicago.
Duhem, P.: 1908b, "La valeur de la th~orie physique', Revue Gdndrale des Sciences Pures
et A'ppliqudes 19, %19. Translated as an Appendix to The Aim and Structure o f Physical
Theory, 1954, pp. 312-35.
Duhem, P.: 1914, La Th~orie Physique, son objet et sa structure, Paris, Chevalier et
Rivi~re, 1906. Second edition, Rivi6re, 1914. Translated by P. Wiener as The Aim and
Structure o f Physical Theory, 1954, Princeton University Press, Princeton, New Jersey,
Duhem, P,: 1915, La Science Allemande, Paris, Hermann.
Duhem, P.: 1917, 'Notice sur les titres et travaux scientifiques de Pierre Duhem" (Mai
1913), Memoires de la Soci(td des Sciences Physiques et Naturelles de Bordeaux, series
7, 1, 151-7. Translated by Peter Barker and Roger Ariew as 'Logical Examination of
Physical Theory'.
Department of Philosophy
University of Notre Dame
Notre Dame, IN 46556
U.S.A,

DUHEM

AND HISTORY AND PHILOSOPHY
OF MATHEMATICS*

ABSTRACT. The first part of this paper consists of an exposition of the views expressed
by Pierre Duhem in his Aim and Structure of Physical Theory concerning the philosophy
and historiography of mathematics. The second part provides a critique of these views,
pointing to the conclusion that they are in need of reformulation. In the concluding third
part, it is suggested that a number of the most important claims made by Duhem
concerning physical theory, e.g., those relating to the "Newtonian method', the limited
falsifiability of theories, and the restricted role of logic, can be meaningfully applied to
mathematics.

It is an interesting but rarely noted fact that Pierre Duhem included a
number of claims concerning the history and philosophy of mathematics
in his Aim and Structure of Physical Theory as well as in his other
writings (Duhem 1954; 1909; 1915). 1 Although these claims may at
times appear to be digressions, careful examination shows that they
function in a significant manner in Duhem's exposition of his philosophy; in particular, Duhem in many cases formulated his main positions
regarding physical theory by contrasting it with mathematics. In the
three parts of the present paper, I shall suggest answers to the following
three questions:
(1) What views did Duhem express in his Aim and Structure of
Physical Theory concerning the nature and development of mathematics?
(2) Are these views correct?
(3) Can any of Duhem's ideas concerning the nature and development
of physical theory be applied to mathematics?
The surprising result that has emerged from my efforts to answer
these questions is the recommendation that the second question be
answered negatively, but the third affirmatively. It is hoped that the
analysis in this paper will simultaneously contribute to a deeper understanding of Duhem's thought and also shed light from a Duhemian
direction on the search by historians and philosophers of mathematics
for patterns of conceptual change in mathematics. 2
Synthese 83: 431-447, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

PART

ONE

What were Duhem's views about the history and philosophy of mathematics? The following three claims are probably among the most
important:
(1) The method of mathematics is 'profoundly different' (Duhem
1954, p. 265) from that of physics. In support of this claim, Duhem
asserted that mathematicians begin with axioms, which are universally
accepted, whereas physicists repeatedly alter their theories in response
to new empirical information. Moreover, whereas mathematicians must
follow logic, physicists in the process of formulating theories have the
freedom at times to set logic aside.
(2) The development of mathematics has been very different from that
of physics. For example, mathematics grows in a linear and cumulative
fashion and has avoided the controversies that have beset physics.
(3) A knowledge of the history of physics is vitally important to
physicists, whereas mathematicians need have no knowledge of the
history of their discipline.
Allied to these claims are some less central points, for example,
that mathematicians make extensive use of the reduction to absurdity
method, v~hereas physicists are barred from employing this powerful
technique (Duhem 1954, p. 188).
Let us now examine some passages in Duhem's Aim and Structure
where he articulated these claims. The first claim is embodied in
Duhem's warning that:
The plan to obtain from common-sense knowledge the demonstration of hypotheses on
which physical theories rest is motivated by the desire to construct physics in imitation
of geometry; in fact, the axioms from which geometry is derived with such perfect rigor.
the "demands' that Euclid formulated at the beginning of his Elements are propositions
whose self-evident truth is affirmed by common sense. But we have seen on several
occasions how dangerous it is to establish an alliance between mathematical method
and the method that physical theories follow; how, underneath their entirely external
resemblance . . . . these two methods reveal themselves to be profoundly different.
(Duhem 1954, p. 265)

Shortly thereafter, Duhem contrasted the clarity and simplicity of
mathematical ideas with the confusion and complexity of concepts in
physics:
[T]he mathematical sciences are very exceptional sciences; they arc fortunate enough to
deal with ideas which emerge from our daily perceptions through the spontaneous work
of abstraction and generalization, and which still appear afterwards as clear, pure. and
simple.

This good fortune is refused in physics. The notions provided by the perceptions with
which it has to deal are infinitely confused and complex notions, the study of which
requires long and painful work of analysis. (Duhem 1954, p. 266)

In describing the methodology of physics, Duhem also warned against
excessive reliance on logic and, moreover, stressed the limitations of
what Duhem, following Pascal, called the 'geometrical mind'.
Pure logic is not the only rule for our judgments; certain opinions [in theoretical physics]
which do not fall under the hammer of the principle of contradiction are in any case
perfectly unreasonable. These motives which do not proceed from logic yet direct our
choices, these 'reasons which reason does not know' and which speak to the ample "mind
of finesse" but not to the ~geometrical mind', constitute what is appropriately called good
sense. (Duhem 1954, p. 217)

Duhem's stress on the dissimilarities between the methods of mathematics and of physics was no doubt linked to his conviction that the
patterns of development characteristic of these two disciplines have
also been very different. Regarding the pattern of development of
mathematics, Duhem remarked:
The propositions that make up purely mathematical sciences are. to the highest degree.
universally accepted truths. The precision of language and the rigor of the methods of
demonstration leave no room for any permanent divergences among the views of different
mathematicians: over the centuries doctrines are developed by continuous progress without new conquests causing the loss of any previously acquired domains.
There is no thinker who does not wish for the science he cultivates a growth as calm
and as regular as that of mathematics. But if there is a science for which this wish seems
particularly legitimate, it is indeed theoretical physics, for of all the well-established
branches of knowledge it surely is the one which least departs from algebra and geometry,
(Duhem 1954, p. 10)

Nonetheless, theoretical physics, according to Duhem, has enjoyed
no such "calm" and "regular" development. In fact, he described it as
having been beset throughout most of its history by "perpetual, sterile
disputes" (Duhem 1954, 107). Duhem attributed many such disputes
to the tendency of physicists, when formulating their theories, to have
recourse to metaphysics; as he stated: "to make physical theories depend on metaphysics is surely not the way to let them enjoy the privilege
of universal consent" (Duhem 1954, p. 10).
Elsewhere in his book, Duhem elaborated on this point in more
detail, contrasting the linear and cumulative character of the development of mathematics with the organic pattern of growth he attributed
to physics.

Physics makes progress t h r o u g h . . , continually supplementing laws in order to include
the exceptions. It was because the laws of weight were contradicted by a piece of amber
rubbed by wool that physics created the laws of electrostatics, and because a magnet
lifted iron despite these same laws of weight that physics formulated the laws of magnet i s m . . . Physics does not progress as does geometry, which adds new final and indisputable propositions to the final and indisputable propositions it already possessed . . . .
(Duhem 1954, p. 177)

Duhem later repeated this point, drawing implications from it for the
pedagogy of physics:
Instruction [in physics] ought to get the student to grasp this primary truth: Experimental
verifications are not the base of theory but its crown. Physics does not make progress in
the way geometry does: the latter grows by the continual contribution of a new theorem
demonstrated once and for all and added to theorems already demonstrated: the former
is a symbolic painting in which continual retouching gives greater comprehensiveness and
unity, and the whole of which gives a picture resembling more and more the whole of
the experimental facts, whereas each detail of this p!cture cut off and isolated from the
whole loses all meaning and no longer represents anything. (Duhem 1954, pp. 204-5)

It was no doubt because he felt these points were so significant that he
stressed the importance for the physicist of a knowledge of the history
of physical theory, even while denying that the history of mathematics
has a comparable role to play in mathematics. He asserted:
This importance which the history of the methods by which discoveries are made acquires
in the study of physics is an additional mark of the great difference between physics and
geometry.
In geometry, where the clarity of deductive method is fused directly with the selfevidence of common sense, instruction can be offered in a completely logical manner. It
is enough for a postulate to be stated for a student to grasp immediately the data of
common-sense knowledge that such a judgment condenses: he does not need to know
the road by which this postulate has penetrated into science. The history of mathematics
is. of course, a legitimate object of curiosity, but it is not essential to the understanding
of mathematics.
It is not the same with physics. There. we have seen. it is forbidden to be purely and
completely logical in teaching. Consequently, the only way to relate the formal judgments
of a theory to the factual matter which these judgments are to represent, and still avoid
the surreptitious entry of false ideas, is to justify each essential hypothesis through its
history.
To give the history of a physical principle is at the same time to make a logical analysis
of it. (Duhem 1954, p. 269)

PART

TWO

With this information as background, let us examine the validity of
Duhem's claims about the history and philosophy of mathematics. The

theses that I shall attempt to develop are (1) that the above cited claims
of Duhem are all seriously defective, and (2) that a number of Duhem's
most famous claims about physical theory can shed light on the history
and philosophy of mathematics.
It is an interesting fact that Duhem's claims about the calm inevitability and the linearity of the development of mathematics were made
at a time when mathematics was undergoing major changes and was
beset by a variety of controversies. To see evidence of these alterations
and altercations concerning mathematics, one needs look no farther
than the philosophical writing of Duhem's contemporary Henri Poincar& One wave of controversy began with the creation during the 1840s
by William Rowan Hamilton and by Hermann Gfinther Grassmann of
nontraditional algebras, for example, algebras in which the commutative law for multiplication is not obeyed, that is, where A x B does not
equal B x A. The broadened view of algebra that resulted included the
realization that mathematicians can create new and useful algebraic
systems very different from that single system that had been central
to mathematics before 1830 (Crowe 1985). One example of the rich
opportunities that were opened up by this new view of algebra is
Benjamin Pierce's Linear Associative Algebra of 1870 in which Pierce
delineated 162 different algebraic systems. Another embodiment of this
result was a debate that raged from about 1870 to about 1900 over the
various systems of vectorial analysis. Duhem, from the beginning of his
scientific training, must have encountered this controversy concerning
which vectorial system - the Hamiltonian, the Grassmannian, or the
Gibbs-Heaviside system - should be employed in physics and geometry,
or whether no vectorial methods should be employed. Aspects of this
debate surfaced in Duhem's Aim and Structure of Physical Theory,
where he somewhat disparagingly dismissed the British penchant for
vectorial methods as another example of the British passion for concrete
representations of physical quantities (Duhem 1954, pp. 77-79).
The shock experienced by the mathematical community at the creation of nontraditional algebras was far surpassed by the tremor that
gradually began to spread after 1829 when Nicolai Lobachevsky published the first non-Euclidean geometry (Bonola 1955; Gray 1979; Trudeau 1987). Four years later and independently of Lobachevsky, Johann
Bolyai published his essentially identical system. In 1851, Bernhard
Riemann presented his famous 'Ueber die Hypotheses, welche der
Geometrie zu Grunde liegen', in which he introduced a second major

non-Euclidean system. Among the French, it was above all Jules Hotiel
who introduced his countrymen to these radically new and different
geometrical systems. The spread of non-Euclidean geometries in France
can be dated from 1866 when Hotiel published a French translation of
one of Lobachevsky's presentations along with selections from Gauss's
correspondence with Schumacher. The publication of Gauss's letters
was crucially important because they revealed that this eminent mathematician had endorsed these geometries before his death in 1855.
Although Duhem made no mention of non-Euclidean geometry in
his Aim and Structure, 3 the philosophical implications of the new geometries were noted by a number of French authors, particularly Poincar6, who in his Science and Hypothesis of 1902 put forth the radical
assertion that "The geometrical a x i o m s . . , are neither synthetic a priori
intuitions nor experimental facts. They are conventions" (Poincar~
1952, p. 50). The changes in geometry went substantially beyond this.
Not only was geometry forced to expand so as to be capacious enough
to include both the Euclidean and the non-Euclidean systems as well
as geometries of more than three dimensions, but also Euclid's paradigmatic Elements was seriously challenged. In this regard, C. S. Peirce
asserted in 1892:
Euclid's treatise was acknowledged by all kinds of minds to be all but absolutely perfect
in its reasoning, and the very type of what science should aim at as to form and m a t t e r . . .
The truth is that elementary geometry, instead of being the perfection of human
reasoning, is riddled with fallacies, and is thoroughly unmathematical in its method of
development. (Peirce 1975, pp. 136-7)

As Joan Richards has recently documented in detail, a major controversy erupted in England during the final decades of the nineteenth
century concerning not only the non-Euclidean geometries, but over
Euclidean geometry itself (Richards 1988). One major culmination of
this controversy was the publication in 1899 by David Hilbert of his
Grundlagen der Geometrie in which he reformulated the axioms of
Euclidean geometry in a strikingly new and more rigorous manner.
The third major branch of mathematics, analysis, was also beset by
changes. The very foundations of the calculus were repeatedly reformulated by various mathematicians during the nineteenth century, most
notably Cauchy and Weierstrass (Boyer 1968, chaps. 23, 25; Hahn
1956; Kline 1980, chaps. 8-9). The realization of the necessity for this
was linked to such results as the violation of traditional intuition by

such discoveries as that of functions that are everywhere continuous
but nowhere differentiable. By 1900, probably the greatest controversy
surrounded the issue of what to make of the introduction by Georg
Cantor of transfinite numbers - which involved the acceptance of orders
of infinite quantities within mathematics.
The list of such fundamental changes in mathematics could be substantially extended, for example, by a discussion of the work commencing in the 1890s by Whitehead, Russell, Peano, and Frege on the
logical foundations of mathematics. Moreover, much could be said
about the problems evident in Duhem's description of mathematical
propositions as "universally accepted truths'" and of mathematical theorems as "demonstrated once and for all" in light of his statement in his
La Science allemande that "The great men who, from the XVIIth to
the middle of the XIXth century, have created Algebra, Integral Calculus, and Celestial Mechanics, have often justified their most important
discoveries with the aid of defective arguments or even by flagrant
paralogisms" (Duhem 1915, p. 7). But enough has already been noted
to suggest that Duhem's characterization of mathematics as, unlike
physics, enjoying a "calm a n d . . , regular" development in which progress is made by the adding of "new final and indisputable propositions
to the final and indisputable propositions it already p o s s e s s e d . . . " is
beset by problems.
PART

THREE

It seems unnecessary to elaborate further at this point on the questionable character of Duhem's claims about mathematics. What I shall do
now is investigate whether any of the central theses in Duhem's analysis
of physical theory can be applied to mathematics and its development.
If it can be shown that this is in fact the case, it will emerge as a
secondary result that Duhem's explicit contrast between physical theory
and mathematics should be viewed as flawed. In other words, if it can
be shown that the methodology and aevelopment of mathematics fit
with some of Duhem's fundamental theses about the nature and development of physical theory, then it will be evident that these disciplines are not as 'profoundly different' as the previously cited quotations
from Duhem would lead one to believe.
What are Duhem's most important claims about physical theory?
Although not complete, the following list includes a number of them.
(1) The so-called Newtonian method of doing physics in which each

of the fundamental laws of physics is built up directly from experiment
is not the method that physicists have followed (whatever their claims
to the contrary may be), nor is it the method physicists should invariably
pursue in attempting to develop theories. One aspect of this claim is
Duhem's assertion that experiments, rather than being the basis of
physics, are its crown. I shall call this first claim the 'Newtonian method
as myth claim'.
(2) According to Duhem, theories in physics, rather than being isolated entities that can be directly tested, are bound together in clusters.
Moreover, he asserted that when confronted with a contradiction, theories can in many cases be rescued by modifying another element in the
cluster. In short, this claim concerns the ability of theories to resist
falsification.
(3) The role that logic has played and should play in physical theory
is substantially more limited than is commonly assumed. The physicist
must in a fundamental way rely on good judgment, on 'bon sens'.
Correspondingly, physical theories must be judged as wholes. The
physicist, rather than being like a watchmaker who examines a watch
by taking it apart, is like the physician who, prevented from dissecting
patients, must examine them as entire entities, attempting to postulate
causes of disease that explain the symptoms afflicting patients (Duhem
1954, p. 188). In this sense, Duhem stressed the human quality of the
work of the theoretical physicist. In what follows this overall claim will
be referred to as the 'restricted role of logic claim'.
(4) A knowledge of the history of physical theory is important for
the physicist; for example, it can save the physicist from the "mad
ambitions of dogmatism as well as the despair of Pyrrhonian skepticism"
(Duhem 1954, p. 270). Duhem's fourth claim can be designated as the
'relevance of history claim'.
Let us now examine each of these four Duhemian claims about
physical theory, attempting in each instance to see whether analogues
applicable to mathematics can be formulated.
One of the most brilliant insights that Duhem drew from his experience teaching physics was that what he called the "Newtonian method"
of developing physical theory is a myth. He described this doctrine,
which he associated with Newton's ~'General Scholium" in his Principia,
as the requirement that the fundamental hypotheses of a physical theory
"'must be tested one by one: none would have to be accepted until it
presented all the certainty that experimental method can confer on an

abstract and general proposition; that is to say, each would necessarily
be either a law drawn from observation by the sole use of those two
intellectual operations called induction and generalization, or else a
corollary mathematically deduced from such laws" (Duhem 1954, p.
190). In his 'Physics of a Believer', Duhem recounted how, after having
been taught at the I~cole normale that this is the proper method for
physical theory, he found when he first began teaching physics at Lille
that this method is a myth (Duhem 1954, pp. 275-79), a "chimera" as
he called it (Duhem 1954, p. 200). In arguing against the Newtonian
method in his Aim and Structure, Duhem demonstrated that neither
Newton nor Amp6re, despite their claims to the contrary, followed this
method. Near the end of his analysis, Duhem asserted:
Experimental verifications are not the base of theory but its crown. Physics does not
make progress in the way geometry does: the latter grows by the continual contribution
of a new t h e o r e m demonstrated once and for all and added to theorems already demonstrated; the former is a symbolic painting in which continual retouching gives greater
comprehensiveness and unity, and the whole of which gives a picture resembling more
and more the whoi'e of the experimental facts . . . . ( D u h e m 1954, pp. 204-5)

Let us now ask: is there a myth about mathematical method analogous to that which Duhem detected for physical theory? I suggest that
this is in fact the case and that the myth can appropriately be called
the 'myth of tire Euclidean method'. The traditional interpretation of
Euclid, derived partly from Aristotle's writings, is that Euclid began
with a number of definitions, axioms, and postulates that were based
on experience and that from these fundamentals, by purely deductive
means, he derived the 465 theorems contained in his Elements. It is
further asserted that the truth of Euclid's later propositions, for example, the Pythagorean theorem (Bk. I, Prop. 47), is guaranteed by the
certainty of tile postulates and axioms as well as by the deductive
structure of the derivation. The idea is that the mathematician proceeds
from the better known postulates and axioms to the less well known
theorems. Moreover, it is frequently assumed that the logical structure
of Euclid's Elements more or less exactly duplicates the historical sequence in which the propositions were discovered. But this portrayal
of the Euclidean method is surely a myth. First of all, it may be
significant tha~ Euclid himself made no such explicit claims about the
certainty of his axioms and postulates. In fact, historical research has
shown that even before Euclid, a number of Greek mathematicians
favored a quasi-formalist approach, according to which the beginning

principles are taken simply as postulates, rather than as indubitable
generalizations from experience (Lasserre 1964, chap. 1). And there are
deeper difficulties. Recall that the Pythagorean theorem, rather than
being a creation of Euclid or even of Pythagoras, has been traced to
Babylonian clay tablets of the eighteenth century B.C. Such information
suggests that what Euclid knew best were not his somewhat artifically
formulated definitions, axioms, and postulates but such results as the
Pythagorean theorem, that Euclid, rather than composing this theorem
as the last stage of his preparation of Book One of his Elements, may
very well have formulated his definitions, axioms, and postulates late
in the process of composing Book One. Moreover, it seems plausible
to argue that what gave Euclid confidence in those beginning principles
was above all that he found he could derive from them such certain
results as the Pythagorean theorem. This is to suggest that in an important sense, mathematicians, including those who work in pure mathematics, employ the hypothetico-deductive method in which the fundamental principles are warranted by the conclusions that can be drawn
from them. 4
When examined from a broader perspective, this claim may appear
less extreme. Where and when did the fundamental postulates of modern Euclidean geometry have their origin? Their source is not lost in
the mists of Greek antiquity as is sometimes assumed; they derived
from late nineteenth-century Germany, in particular, from Hilbert's
Grundlagen der Geometrie. Possibly even this claim looks too far into
the past. The fundamental principles of the most recent geometry texts
are no doubt of more recent vintage, resulting from subsequent critiques
of Hilbert's formulation.
The Same point emerges from a knowledge of the history of other
areas of mathematics. When was the fundamental theorem of algebra
first proven? Early in the nineteenth century. The same period saw
the formulation of such other fundamental algebraic entities as the
associative, commutative, and distributive laws. Where in algebra texts
are these fundamental principles presented? At the very beginning,
whereas algebraic theorems developed in many cases centuries earlier
appear on subsequent pages. Similarly, examination of a calculus text
reveals that many of its most complicated theorems are of early vintage,
whereas the fundamental principles, the definitions of such crucial entities as function and limit, came forth a century or more later as a result

of the rigorization of calculus that was among the major achievements
of nineteenth-century mathematics. Mathematics is not a tree that
grows only at its upper extremities; rather the roots are involved in
continuous transformation. We can put this overall point in Duhemian
terms: the postulates and fundamental principles of mathematics are
not only the base of mathematics but also its crown. Mathematics
develops as a whole, with alterations occurring in every part, including
at its foundation. The growth of mathematics is not linear, but organic.
Before leaving this point, let us return twice to Duhem's text. In the
course of his refutation of the Newtonian method, Duhem made the
surprising remark:
It is as impracticable for the physicist to follow the inductive m e t h o d . . , as it is for the
mathematician to follow that perfect deductive method which would consist in defining
and demonstrating everything, a method of inquiry to which certain geometers seem
passionately attached, although Pascal properly and rigorously disposed of it a long time
ago. (Duhem 1954, p. 201) 5

It seems that Duhem, who as Niall Martin has shown drew so heavily
upon Pascal (Martin 1981, chaps. 6-7), failed to realize fully the implications of this assertion. Another conclusion that Duhem drew from
his analysis of the Newtonian method also merits consideration. Late
in that analysis in which he had vigorously contrasted the methodologies
of physics and mathematics, Duhem asserted that physical theory,
rather than beginning from experiments, is "grounded on postulates,
that is to say, on propositions that it is at leisure to state as it pleases,
provided that no contradiction exists among the terms of the same
postulate or between two distinct postulates" (Duhem 1954, p. 206). If
postulates play such a prominent role in physical theory, this surely
suggests that its methodology is not so dissimilar from that of mathematics.
Let us turn now to Duhem's claim concerning the ability of theories
to resist falsification. 6 In his exposition of this famous claim, Duhem,
again contrasting the methods of physics and mathematics, asserted:
Those who assimilate experimental contradiction to reduction to absurdity imagine that
in physics we may use a line of argument similar to the one Euclid employed so frequently
in geometry. Do you wish to obtain from a group of phenomena a theoretically certain
and indisputable explanation? Enumerate all the hypotheses that can be made to account
for this group of phenomena; then, by experimental contradiction eliminate all except
one: the latter will no longer be a hypothesis, but will become a certainty. (Duhem 1954.

p. 188)

Duhem proceeded to argue that the reduction to absurdity method,
although of such great power in mathematics, is not comparably applicable in physics. As he stated: "Unlike the reduction to absurdity
employed by geometers, experimental contradiction does not have the
power to transform a physical hypothesis into an indisputable t r u t h . . . "
(Duhem 1954, p. 190). Implicit in his analysis was the doctrine that
whenever a contradiction is encountered in mathematics, the mathematical claim from which the contradiction was derived must be abandoned.
Although this may seem sensible, good evidence indicates that this is
not a mandate that mathematicians have always felt constrained to
follow. I know of no better demonstration of this point than Imre
Lakatos's Proofs and Refutations. In that work, Lakatos examined the
history of Euler's claim that the number of faces, edges, and vertices
of polyhedra always obey the equation V - E + F = 2. What Lakatos
found was that throughout its history, this claim, as well as proofs
presented for it, repeatedly encountered contradictions, none of which
was deemed decisive; in fact, Euler's conjecture was in every instance
rescued from falsification. In tracing this history, Lakatos revealed the
rich repertoire of techniques available to mathematicians wishing to
rescue mathematical entities beset by counterexamples. Moreover,
numerous other cases of apparent contradictions can be cited from the
history of mathematics in which the favored concept, law, or theorem
was salvaged. Consider the celebrated theorem with which Euclid
brought his Elements to a close and for the sake of which, according
to some commentators, he composed the entire work: "No other figure,
besides [the five regular solids] can be constructed which is contained
by equilateral and equiangular figures equal to one another". Suppose
Euclid were shown the six-sided figure (see figure) formed by placing
together two regular tetraheda. This new solid, although fully conforming to Euclid's definition of 'regular solid', refutes his theorem. One
can scarcely imagine that Euclid would have been led thereby to abandon his theorem. Rather what he would have done is to salvage his
theorem by modifying his definition of regular solid, as was later done,
so as to exclude this counterexample. To provide another example:
think of complex numbers, which faced constant contradictions.
Throughout most of their history they stood in contradiction to the
such laws as that every number must be greater than, equal to, or less
than zero, that the square of any number must be positive, and that
any algebraic entity must be geometrically representable. They survived

tations, although other elements in mathematics, for example, the definition of number itself required modification, It can of course occur
that the mathematical community will decide to declare a contradiction
to be conclusive, but this is a matter of choice and may involve extensive
controversy
This analysis of Duhem's second claim sets the stage for a consideration of his third claim, what I have called the "restricted role of logic
claim". In one of the most controversial, and possibly least understood
sections of Duhem's Aim and Structure, he stressed that at times physicists find themselves convinced that a theoretical system must be modified, even though experiment has not provided sufficient evidence as
to what elements are to be altered. In those instances, D u h e m asserted,
"No absolute principle directs this inquiry, which different physicists
may conduct in very different ways without having the right to accuse
one another of illogicality" (Duhem 1954, p. 216). What is to be done
in such cases? Duhem's answer, which some see as implying the abandonment of logic and as entailing surrendering to relativism, was to
remind his readers that
Pure logic is not the only rule for our judgments; certain opinions [in theoretical physics]
which do not fall under the hammer of the principle of contradiction are in any case
perfectly unreasonable. These motives which do not proceed from logic and yet direct
our choices, these "reasons which reason does not know" and which speak to the ample
"mind of finesse" but not to the ~'geometrical mind", constitute what is appropriately
called good sense. (Duhem 1954, p. 217)

Duhem further underlined the inevitably human character of theoretical
work in physics by adding:
The sound experimental criticism of a hypothesis is subordinate to certain moral conditions; in order to estimate correctly the agreement of a physical theory with the facts,

it is not enough to be a good mathematician and a skilled experimenter; one must also
be an impartial and faithful judge. (Duhem 1954, p. 218)
In short, D u h e m espoused the position, too rarely explicitly admitted
in treatises on scientific method and sometimes implicitly denied in
them, that important as logic is in physical inquiry, human factors
influence the inquirer. Among such factors are impartiality and the
'reasons of the heart', which cannot, ultimately be reduced to quasimechanical processes of reasoning.
Certainly a comparably human element is to be found among mathematicians, who repeatedly face decisions that are not governed solely
by logic. Many areas of mathematics, analysis most famously, have
been beset by inconsistencies, anomalies, contradictions (real and apparent), and counter-intuitive deductions, concerning which mathematicians have been forced to adopt a position. Mathematicians must also
select the postulates from which a mathematical system begins. In this
regard, it is relevant to recall Duhem's statement, cited previously, that
it is impractical for the mathematician to rely on that "perfect deductive
method which would consist in defining and demonstrating everything,
a method of inquiry [that] Pascal properly and rigorously disposed
o f . . . a long time ago" (Duhem 1954, p. 201). Moreover, mathematicians must regularly choose among various mathematical methods of
attacking problems; a relevant example, where Duhem was himself
involved, was the decision as to whether or which vectorial methods
should be employed.
In this overall context, it is interesting to note that Duhem, following
Pascal, stressed the variety of styles exhibited by working mathematicians. In particular, he pointed out that important contributions have
been made to mathematics by persons possessing the ample mind of
finesse rather than the geometrical mind. D u h e m asserted:
It i s . . . ampleness of mind which constitutes the peculiar genius of many a geometer and
algebraist. More than one reader of Pascal, perhaps, will not fail to be astonished on
seeing him sometimesplace mathematicians among the number of ample but weak minds.
This cross-classificationis not one of the lesser proofs of [Pascal's] penetration. (Duhem
1954, p. 62).

And D u h e m illustrated this point by a rich array of examples. 7
Duhem's use of Pascal's famous classification of minds suggests another point, which is of general relevance. It should come as no surprise
that Duhem's ideas about physical theory have applications to mathematics if it is recalled that Duhem, when formulating his views on

methodology, relied heavily on the writing of Pascal, who had originally
formulated many of his methodological ideas with reference primarily
to mathematics.
Finally, let us turn to Duhem's claim that a knowledge of the history
of physical theory is of direct value to physicists. One Of the chief
arguments Duhem provided for this claim was that, as he stated, "To
give the history of a physical principle is at the same time to make a
logical analysis of it" (Duhem 1954, p. 269). This statement, however,
needs commentary, because its deeper meaning is somewhat different
from what one might infer from a first reading. In particular, it seems
probable that what Duhem was suggesting was not that historical analysis does precisely what ordinary logic can also accomplish, but rather
that a historical investigation of a physical theory can create an awareness of the deeper logic of the theory, of those "reasons that reason
does not know", those reasons that transcend ordinary logic but that
are the province of 'bon sens'. A number of the arguments made in
this paper, and not least its central theses, suggest that a comparable
benefit should result from approaching mathematics in a historical
manner. Moreover, a knowledge of the historical development of mathematics may save not only the mathematician, but also the philosopher
of physical theory, from distorted claims about the aim and structure
and development of mathematics.
Before concluding this paper, I should add a final note that is both
historically significant and a further support for its central claim. After
drafting the paper, I read an essay published in 1907 by Pierre Boutroux
(1880-1922), the son of the philosopher Emile Boutroux. The younger
Boutroux was a mathematician who also made important contributions
to the history and philosophy of mathematics. In his essay, which he
entitled 'La Thgorie physique de M. Duhem et les math6matiques',
Boutroux, using a different set of arguments from those I have presented, urged that a number of Duhem's doctrines concerning physical
theory are also applicable to mathematics. For example, Boutroux
stated:
For some years I have sought to s h o w . . , that Mathematical Analysis is not a perfect
and exceptional science, that its evolution recalls to mind, in many cases, the evolution
of the physical sciences . . . . I have the impression that one can apply to mathematics
what D u h e m says of physics. (Boutroux 1907, p. 368)

Boutroux illustrated this claim by noting, for example, the importance
of experimentation in mathematics as well as of 'bon sens' and intuition.

I s h a l l n o t a t t e m p t t o r e c a p i t u l a t e his v a l u a b l e a n a l y s i s , b u t s h a l l o n l y
n o t e t h a t I s h a r e n o t o n l y B o u t r o u x ' s v i e w b u t a l s o his h o p e t h a t D u h e m
would find such an analysis of interest and value.

NOTES
* I am indebted to Professors Douglas Jesseph and Philip Quinn for helpful comments
on this paper.
1 On Duhem's views concerning the nature of mathematics, see Boutroux (1907), his
nearly identical Boutroux (1920), and Jaki (1984), 349-51,361.
2 1 have discussed the views of a number of authors, including Duhem, on the historiography of mathematics in Crowe (1988).
3 Duhem did discuss non-Euclidean geometries to some extent in his La Science allemande; see, for example, pp. 113-22, where he expressed major reservations about such
geometries.
4 This point is developed in more detail in Crowe (1988), where it is shown that Hilary
Putnam and others have maintained that mathematicians employ the hypothetico-deductire method.
5 Although Duhem did not specify where Pascal had formulated this claim, he was no
doubt thinking of Pascal's fragmentary 'De l'esprit g6om6trique'.
6For an important analysis of Duhem's ideas in this regard, see Ariew (1984).
7 Duhem extensively discussed the relation to mathematics of the two types of minds in
his La Science allemande
REFERENCES
Ariew, R.: 1984, 'The Duhem Thesis". British Journal for the Philosophy of Science 35,
313-25.
Bonola, R.: 1955, Non-Euclidean Geometry: A Critical and Historical Study of Its Development, trans, by H. S. Carslaw, Dover Publications, Inc., New York.
Boutroux, P.: 1907, 'La Thdorie physique de M. Duhem et les math~matiques', Revue de
mgtaphysique et de morale 15, 363-76.
Boutroux, P.: 1920, L'Iddal scientifique des mathdmatiens: darts l'antiquitd et dans les
temps modernes, Paris, pp. 230-48.
Boyer, C, B.: 1968: A History of Mathematics. Wiley. New York.
Crowe. M. J.: 1985. A History of Vector Analysis: The Evolution of the Idea of a Vectorial
System, Dover Publications. Inc.. New York.
Crowe, M. J.: 1988. "Ten Misconceptions about Mathematics and Its History'. in William
Aspray and Philip Kitcher (eds.), History and Philosophy of Modern Mathematics,
University of Minnesota Press. Minneapolis. pp. 260-77.
Duhem, P.: 1912, "La Nature du raisonnement math6matique'. Revue de philosophie 21,
531-43.
Duhem, P.: 1915, La Science allemande. A. Hermann & Fils, Paris.
Duhem. P.: 1954. The Aim and Structure of Physical Theory, trans, by Philip P. Wiener
from the 1914, 2nd ed.. Princeton University Press, Princeton. New Jersey.

Gray, J.: 1979, Ideas of Space: Euclidean, Non-Euclidean, and Relativistic, Clarendon
Press, Oxford.
Hahn, H.: 1956, 'The Crisis in Intuition', in James Newman (ed.), The World of Mathematics, vol.3, Simon and Schuster, New York, pp. 1956-76.
Jaki, S. L.: 1984, Uneasy Genius: The Life and Work of Pierre Duhem, Martinus Nijhoff,
Dordrecht.
Kline, M.: 1980, Mathematics: The Loss of Certainty, Oxford University Press, New
York.
Lakatos, I.: 1976, Proofs and Refutations: The Logic of Mathematical Discovery, J.
Worrall and E. Zahar (eds.), Cambridge University Press, Cambridge.
Lasserre, F.: 1964, The Birth of Mathematics in the Age of Plato, Hutchinson, London.
Martin, N.: 1981, The Philosophy of Physics According to Pierre Duhem: An Historical
and Critical Essay on the Philosophy and Historiography of a Catholic Physicist, a
London School of Economics doctoral dissertation.
Pierce, C. S.: 1892, 'The Non-Euclidean Geometry', in Charles S. Peirce: Contributions
to The Nation. Part One: 1869-1893, compiled and annotated by K. L. Ketner and
J. E. Cook, Texas Tech University, Lubbock, 1975, pp. 135-8.
Poincar6, H.: 1952, Science and Hypothesis, Dover Publications, Inc., New York.
Richards, J.: 1988, Mathematical Visions: The Pursuit of Geometry in Victorian England,
Academic Press, Inc., Boston.
Trudeau, R.J.: 198'7, The Non-Euclidean Revolution, Birkh~iuser, Boston.

History and Philosophy of Science Program
University of Notre Dame
Notre Dame, IN 46556
U.S.A.

RIGOROUS

PROOF

MATHEMATICS:

AND THE HISTORY

COMMENTS

OF

ON CROWE

ABSTRACT. Duhem's portrayal of the history of mathematics as manifestingcalm and
regular development is traced to his conception of mathematical rigor as an essentially
static concept. This account is undermined by citing controversiesover rigorous demonstration from the eighteenth and twentieth centuries.

In contrast to the history and philosophy of the physical sciences,
relatively little scholarly attention has been devoted to the history
and philosophy of mathematics. As Professor Crowe's paper suggests,
however, the field is by no means sterile and we can be glad that the
history and philosophy of mathematics is becoming the focus of more
sustained and widespread scholarly activity. The main lesson to be
drawn from Professor Crowe's investigation is that Duhem's views on
the history and philosophy of mathematics, although not elaborated in
great detail, stand in sharp contrast with his widely known account of
the history and philosophy of physical science. I accept this fundamental
claim as well as the suggestion that our understanding of the history
and philosophy of mathematics would be improved if we applied
Duhem's more celebrated account of the development of physical theory to episodes of conceptual change in the history of mathematics. In
what follows, I would like to offer my own account of why we find
D u h e m treating physical and mathematical theories so differently and
to show how his mistaken conception of the history and philosophy of
mathematics is rooted in a misunderstanding of mathematical rigor.
Thus, my purpose is to extend Professor Crowe's analysis in some
respects and to link his treatment of D u h e m with some of my own
concerns about the history of the ideal of rigorous proof.
The best way to characterize Duhem's approach to the history and
philosophy of mathematics is to see him as embracing an extreme
continuity thesis - a thesis which holds in effect that the mathematical
work of all eras has been the elaboration of the very same set of
fundamental concepts, with innovation kept to an absolute minimum.
Synthese 83: 449-453, 1990.
© 1990 Kluwer Academic Publishers. Printed in the Netherlands.

Duhem is noted for claiming continuity between the physical theories
of the Middle Ages and the seventeenth century, so it might not be too
surprising to find him treating mathematical theories from Ancient
Greece to the early twentieth century as continuous. Although I find
the famous Duhem continuity thesis appealing as an account of the
development of physical theory, I think his extreme conservatism about
the history of mathematics goes too far. Let me first explain why I
think it appropriate to characterize Duhem's approach to the history
and philosophy of mathematics as a continuity thesis, and then go on
to show what is wrong with it.
As Professor Crowe has noted, Duhem claimed that there are various
respects in which the history of physics and the history of mathematics
are different. It is worth observing, however, that these differences
suggest that mathematical theories should be relatively unchanging
when compared with physical theories. For example, Duhem's characterization of the growth of mathematics as 'calm and regular' suggests
that mathematicians of the past have broken new ground by plodding
along down the same path as their predecessors, only making an original
contribution when they reached the limits of what had been previously
established. In a similar vein, Duhem insists that the development of
mathematics has been cumulative; on this account, geometry "only adds
new final and indisputable propositions to the final and indisputable
propositions it already possessed". Moreover, Duhem claims that the
development of mathematics has not been marred by the sterile metaphysical disputes which have hindered the progress of physical theory.
These alleged differences between the history of mathematics and
the history of physics all suggest an extreme continuity in the development of mathematics. In such a history of mathematics, all of the main
players appear to be working on essentially the same project, results
are added but never challenged, theories change (if at all) only by being
generalized to include more cases, and there are no 'metaphysical'
disputes which require that mathematicians return to the proverbial
square one and wrangle over fundamental concepts.
Given that Duhem accepts such a view of the history and philosophy
of mathematics, I think we can say that he was led to it by a conception
of mathematical rigor which is essentially static. Such a static conception
of rigor holds that the criteria for rigorous demonstration have been
essentially the same over time, that they have been well understood
and well articulated by mathematicians in all eras, and that new results

have been added in the calm, regular development of mathematics
when (and only when) they have been demonstrated according to this
universally accepted standard of rigor.
Indeed, it is difficult to comprehend how Duhem's approach to the
history of mathematics could get started without such an account of
rigor. His repeated contrast of the 'method' of mathematics with the
'methods' of physics suggests that he believes that there is a unique
mathematical method which has been followed for centuries, while the
physical sciences have enjoyed no such unity of method. This unique
mathematical method presumably requires an adherence to an unchanging conception of rigor and has (at least on Duhem's understanding of
the matter) been followed at least since the time of Euclid.
Unfortunately for Duhem, this understanding of the history of mathematics is rather simplistic. Professor Crowe has drawn attention to
nineteenth-century episodes in the history of mathematics which show
the inadequacy of Duhem's approach, but I think that the case can
be strengthened in important ways by directing our attention toward
important controversies in the eighteenth and twentieth centuries. The
controversies I have in mind are two: Berkeley's critique of the
infinitesimal calculus in his 1734 work The Analyst and Brouwer's attack
on nonconstructive analysis in the early decades of this century. These
episodes are important not merely because they amplify the case made
by Professor Crowe, but also because they suggest that the very notion
of mathematical rigor has not been nearly as fixed and settled as Duhem
apparently beliLeved. A brief account of both of these controversies
should serve te, make my point.
In 1734, George Berkeley published a curious work entitled The
Analyst which argued in part that the accepted methods of the calculus
did not satisfy the proper criterion of rigor? He observed that continental analysts in the Leibnizian tradition were quite happy to admit that
there were quantities greater than nothing but less than any positive
real number, but complained that the admission of such infinitesimal
quantities did violence to the accepted canons of mathematical rigor.
No such infinitesimal quantity can be observed, and it seems quite
impossible to imagine a magnitude that satisfies these conditions. Moreover, he noted that the supposedly more rigorous Newtonian formulation of the calculus was equally unacceptable. Although Newton professed to be able to derive the fundamental results of the calculus
without recourse to infinitesimal magnitudes, Berkeley noted that the

Newtonian demonstrations required a subtle but apparently fallacious
maneuver in which a finite increment was supposed to be both greater
than and equal to zero.
The responses to Berkeley's challenge are intriguing because they
took exactly the form that Duhem suggests has never occurred in the
history of mathematics. The dispute was unabashedly metaphysical,
with emphasis being placed upon such topics as what laws of logic are
correct, what kinds of entities may be introduced in a mathematical
demonstration, and the subtle distinction between absolute nothing and
the mere privation of something. 2
The details are of no immediate interest here, but the point should be
clear: in the mid-eighteenth century there was no universally accepted
account of mathematical rigor, and the dispute between Berkeley and
his opponents was largely a dispute over what constitutes rigorous
demonstration. Berkeley advocated an essentially classical conception
of rigor which denied the legitimacy of infinitesimal mathematics, while
his opponents charged him with failing to understand the nature of
mathematical demonstration. Curiously, Berkeley's opponents did not
stop short of asserting that the calculus had to be legitimate simply
because it worked, even though they admitted that its foundations were
obscure.
But such disputes are not isolated episodes confined to the 1730s.
Anyone who is familiar with mathematical intuitionism will admit that
the issue of mathematical rigor has not always been the object of
universal agreement. Brouwer and his followers claimed that much
of what is accepted in 'classical' analysis is either false, improperly
demonstrated, or downright meaningless. 3 Moreover, the Brouwerian
insistence upon constructive proofs is quite obviously founded upon
'metaphysical' arguments concerning the capacity of human minds to
comprehend infinitary quantifications. Thus, the dispute between intuitionists and classical mathematicians reduces to a dispute over the
proper criteria for rigorous demonstration. Intuitionists are prepared
even to reject classical logic in their campaign for a new standard
of rigor, while their opponents insist that the accepted methods are
unobjectionable and deserve to be retained because they are easier
and more useful than the austere procedures of intuitionistic analysis.
Whatever else one may chose to make of it, the development of analysis
in the twentieth century suggests that Duhem's picture of the history

of mathematics as a steady and unchallenged accumulation of new and
universally accepted results is in need of drastic revision.
What, then, is the proper course to take in analyzing the history of
mathematics? My proposal is that we abandon the idea that there is a
fixed, immutable conception of mathematical rigor. This does not mean
that 'anything goes' in mathematics, but rather that our understanding
of the history of mathematics will be enhanced if we accept that the
standards of rigor are not as unchanging as Duhem would have us
believe. In this respect, Professor Crowe's suggestions for a reorientation of the history and philosophy of mathematics seem imminently
reasonable, and we can expect to have a better understanding of the
history and philosophy of mathematics if we discard the myth that
mathematicians have always been guided by the same conception of
rigor.
NOTES
1 See Berkeley (1734) for the details of Berkeley's case against the calculus.
2 See Cajori (1919) for a summary of this dispute.

3 The-case for intuitionism can be found in several papers by Brouwer, Heyting, and
Dummett in Benacerraf and Putnam (1983).

REFERENCES

Benacerraf, P. and H. Putnam: 1983, Philosophy of Mathematics: Selected Readings,
Cambridge University Press, Cambridge.
Berkeley, G.: 172.4, The Analyst, in A. A. Luce and T. E. Jessop (eds.): 1957, The
Works of George Berkeley Bishop of Cloyne, 9 vols, T h o m a s Nelson and Sons, London,
vol. 4, pp. 53-102.
Cajori, F.: 1919, A History of the Conceptions of Limits and Fluxions in Great Britain

from Newton to Woodhouse, Open Court, Chicago and London.
Department of Humanities
Illinois Institute of Technology
Chicago, IL 60616
U.S.A.