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The Impact of Newton's Principia on the Philosophy of Science

Ernan McMullin
Department of Philosophy
University of Notre Dame,

This paper is a revised and enlarged version of a keynote address delivered at the Second International Conference on the History of the Philosophy of Science, held at the University of Notre Dame in 1998; also presented in the Pittsburgh Lecture Series in the Philosophy of Science, Fall 1999.

In the long history of the philosophy of science, the eighteenth century might well be regarded as Newton's century. The impact of his Philosophiae Naturalis Principia Mathematica on the imaginations of philosophers and physicists, now for the first time separating into two different professions, was so great that it was altogether natural that the work should rapidly become the paradigm of what natural science should look like. And his scattered remarks on method in the pages of the Principia and the Opticks took on a corresponding authority, even though it was not at all easy to weave from them a consistent philosophy of science. Hypothesis was clearly to be distrusted-and yet was not an appeal to ethers, subtle spirits, and active principles, a prominent feature of his own thinking? In the "experimental philosophy" that he advocated, propositions were to be inferred directly from the phenomena and then rendered general by induction-but had not his friend, John Locke, argued persuasively in his Essay Concerning Human Understanding that the invisibly small corpuscles, on whose properties and motions the properties of the bodies of our immediate experience were almost universally believed to depend, could not possibly be reached in this way? After a century in which hypothesis and forms of inference less direct than deduction and inductive generalization had been widely accepted among those who charted the course of the new sciences, Newton's admonitions seemed to strike a discordant note.

In order to evaluate the impact that Newton's example had upon the philosophy of science of the century that followed the publication of the Principia, it will be necessary first to outline some of the major developments in the philosophy of science of the decades preceding that work. (McMullin 1990) One of these is of particular relevance. The ancient ideal of demonstration that had been the defining characteristic of "science", that is, of knowledge in its fullest sense, from Aristotle's time onwards, had been effectively challenged by the new directions that natural philosophy had taken from the time of Kepler and Galileo. Two clearly non-deductive modes of validation now seemed to be making their way; the logical differences between the two were evidently of less import to their proponents than the fact that being non-deductive, they were in need of defence. A single loose label, 'induction', was commonly attached to both.

The appearance of Newton's Principia, however, led in a new direction. The mechanics laid out with such daunting brilliance in that work did not readily lend itself to logical categorization. Newton's own attempts to construe the warrant underlying the propositions of his new mechanics in terms of deduction and induction carried with them a hint of Aristotle's Posterior Analytics. But the procedures he was following were clearly remote from anything Aristotle had envisaged in his own Physics, different also from the hypothetical forms of inference his immediate predecessors had been led to believe natural science required. Section two of the essay traces Newton's negative response to the admission of hypothesis into science proper. His critics charged that the Principia itself fell short as physics, since it restricted itself to the mathematical principles of mechanics only, setting aside the issue of causal explanation. Section three asks whether explanation in terms of force might not still be construed as a form of explanation, though weaker than the agent-causal explanation his critics looked for. It was precisely because it was weaker that Newton could claim that his mechanics dispensed with the sort of hypothesis that agent-causal explanation of the traditional sort would have involved. He had contrived a new style of science, one that undoubtedly proved its worth for mechanics at least, in the century that followed.

The impact of the Principia on the philosophers of that century was not, in retrospect, quite so positive. A variety of morals for the philosophy of science were drawn from Newton's work. Three of these, and what philosophers made of them in fashioning their own philosophies of science, will be the topic of the remainder of the essay. These philosophers were at one in believing that the mechanics of the Principia could be held up as a model of the sort of knowledge to which the investigation of the natural world should aspire. We shall see, in necessarily sketchy outline, where this belief led for a time in the philosophy of science.

1. What went before

In the New Organon, Francis Bacon described a method he called "induction" that comprised two rather different logical procedures. The first of these would rise "by a gradual and continuous ascent" from the particulars of observation to broader and broader generalizations. (Bacon 1994, I, 19; 48) These generalizations would begin by being conjectural or hypothetical in character and would be tested in tables of presence, absence, and degree (which Mill in his later account of induction would appropriate and rename sameness, difference, and concomitant variation). These methods obviously can be applied only to observed features of the world, noting their co-occurrence, their non-co-occurrence, or their covariance. In this way, one can hit on the regularities that correspond, as he expresses it, to the laws that "govern and constitute any simple nature". (Bacon 1994, II, 17; 170) The goal of inquiry here is the discovery of observationally determinable lawlikeness amidst the welter and contingency of the world of nature.

As instances of lawlikeness, though in a broader sense than Bacon's, we might turn from Bacon's own extensive natural histories to two of the most celebrated discoveries of that day. Kepler's charting of the orbit of Mars yielded three regularities that, when extended to the orbits of the remaining planets, later became known as his three "laws". How were they validated? By pointing in the first instance to the way in which they synthesized Tycho's successive observations of the positions of a single planet, Mars. The continuous curve of the postulated ellipse constituted a generalization of the particulars of the Martian orbit as these had been laboriously reconstructed by Kepler by mathematically manipulating the observational data. The second element in the induction was the speculative extension of the conjecture to the sun's planets generally, based on a presumed commonality of nature.

The original generalizations that led to the three laws were in no sense simple ones. Kepler scholars delight in recounting the tribulations that the astronomer went through in his effort to impose mathematical order on data that for long months remained intractable. To make them leap together in happy consilience, complex mathematical techniques had to be employed, different orbital shapes had to be tried out in the effort to discover the one that would bring order to seeming confusion. But when finally all fell into place, the primary warrant of the claims being made about the orbit of Mars was one long familiar to mathematical astronomers: they saved the phenomena. The fact that they did so in a mathematically elegant way carried particular weight for Kepler, separating them in his mind from the awkward constructions of his Ptolemaic contemporaries.

On a different front, when some of Robert Boyle's correspondents noted a simple mathematical relationship between the values that Boyle had recorded of the volume and the "spring" of the air confined in a mercury column, they had, as it would soon turn out, hit on a relationship that would likewise be commemorated as a "law", a regularity one could count on, the first of many such regarding the behavior of gases. (Boyle 1965, I, 158-163) In this case, the data had been amassed in the pursuit of a quite different inquiry; the discovery was made almost by accident and not by the systematic testing of different hypotheses. But the evidential basis of the law was of the same kind: it was a plausible generalization from the sample of data available and it rested on observed covariance. It was also hypothetical in a number of respects. For instance, did the neat inverse mathematical relationship hold exactly? Could it be extended beyond the narrow range of the data available? And, then, could it be extended to gases other than air? At a deeper level, how was it to be shaped conceptually, how in particular was the notion of "spring" to be understood?

Here, then, are two familiar examples of the mode of evidence I am calling inductive, restricting this term to generalization from observed particulars to a regularity of which these particulars are instances. But another sort of inquiry was also opening up, as the works of both Bacon and Boyle illustrate. And it involved a significantly different logical procedure. After searching out empirical regularities and provisionally establishing their nomic or lawlike status, one might want to explain such regularities by seeking to discover their causes, to learn what brings them about. But, in practice, limiting possible explanations to a single one in such cases will rarely be possible, as the rapidly expanding observational practice of the seventeenth century made quite clear.

The newly developed telescope, for example, revealed all sorts of regularities in the skies that called out for explanation. What were the spots seen to traverse the sun's surface over the period of something less than a month? Galileo hypothesized that they were on or very near the sun's surface and that their motions indicated that the sun itself is rotating. Their changing shapes, appearances, and disappearances, suggested analogies with the clouds passing over the earth's surface. The aim of Galileo's inquiry was not just to establish new regularities as genuine evidences of nature but to identify the cause of regularities already observed. The sun's rotation was one possible cause provided that the spots were on or near the solar surface. What Galileo aimed to show was that the sun was in fact rotating, as well as to discover what the spots really were. It was not merely a matter of saving the phenomena, then, but of making solid existential claims about features that were not themselves directly observed and therefore not accessible to inductive inference. These claims depended on the quality of the explanation offered. Was his a better explanation than the rival one advanced by Scheiner? Galileo was quite sure that it was. He was, indeed, wont to overestimate the quality of his cosmological explanations. But in this case, he was right.

Later, when he tried to settle the Copernican debate by advancing the dual motions of the earth as the explanation of the tides, he tended to assume that such motions were the only possible explanation. This would give him the quasi-demonstration he needed of the Copernican theses. There is no need to pursue that familiar story here. What needs emphasis, however, is that the form of reasoning Galileo presented in this case, as in his discussions of the nature of sunspots, comets, and the like, is not inductive in the sense defined above. It proceeds in hypothetical fashion from effect to cause, and it depends for its truth-value not on observed co-occurrence, as induction does, but on the much more problematic criterion of explanatory success.

It may be helpful to give one more example of this kind of reasoning from effect back to cause, rendered logically problematic by the possibility that other postulated causes might explain as well or better. Returning to Boyle for a moment, we have seen how the famous inductive law was discovered. But he was, as already noted, engaged in a different inquiry at the time. He wanted to reinforce Torricelli's explanation of the behavior of the mercury in a sealed-tube barometer in terms of a "sea of air" whose pressure on the open mercury surface sustained the mercury column in the tube. By exhausting the air above the open surface and noting the drop in the mercury column, Boyle was able to argue that this consequence could be explained easily by the Torricelli hypothesis but hardly at all by any of its rivals. In the case of the sunspots, what had to be established was not their existence, which was already known, but their identity. Explaining the barometer's observed behavior, however, required one to postulate an entity that was not in the ordinary sense observed, what would later be called the atmosphere. What Boyle aimed to do, as he himself says, was not merely to save the phenomena but to show that the sea of air really existed.

The effect of this sort of inference, conveniently described by the modern label due to Peirce, 'retroduction', is to enlarge the known world.(1) Retroductive inquiry takes the discovery of lawlikeness not as goal but as starting-point. Its terminus is the plausible affirmation of some entity or structure as agent cause of the observed behavior that serves as explanandum. Science of this sort can extend the range of human knowledge to realms distant from the immediate reaches of sense, to the very distant in space, the very small, and to happenings distant in past time. The causes it reaches for may not be themselves observed or perhaps even observable. The warrant it relies on is not just the observed co-occurrence that supports the induction from which it begins but also the quality of the explanation offered, a criterion far more difficult to assess. The threat is always the same: that among the possible causes one may have made the wrong choice. But the promise of retroduction is even greater: reasoning of this sort is the only way of breaking the hold of a narrow empiricism that would limit our knowledge to what lies within the immediate reach of our instruments or, even worse, of our senses.

All this may seem remote from the actual concerns of Newton's predecessors, a reading back of a later philosophical distinction into the reflections of a less distinction-prone time. It is true that the distinction between inductive and retroductive validation was not explicitly drawn at that time. Indeed, it was not clearly drawn until more than two centuries later, and even then was glossed over, notably by proponents of logical positivism in their effort to construct a unitary inductive logic. But the two different sorts of validation are easily found, as we have just seen, in the scientific practice of that early time. And there was a growing awareness, admittedly not shared by all, that argument from observed effect to hypothetical unobserved cause had somehow to be incorporated in the canon of approved scientific method.

Kepler and Boyle were among those who saw this most clearly. Kepler wanted to show, not so much that the Copernican system saved the phenomena better than its Ptolemaic rival did, as that what it claimed was true, that is, that the earth really moves around the sun. The inheritor of a long tradition in mathematical astronomy that recognized that saving the phenomena of itself warranted only a weak claim on truth, he argued that the Copernican system explained, made intelligible, many puzzling features of the planetary motions, like the retrograde motions of the planets and the yearly period associated with each planet as viewed from earth, features that had to be arbitrarily postulated in the Ptolemaic system. For the Copernican system to work so well as explanation, he claimed, it had to be true. To suppose that it merely saves the appearances would not be enough. In that event, it would not really explain, and hence would not establish the truth of the hypothesis. It would be as arbitrary as was the Ptolemaic system, as far as the true motions of the planets were concerned.

In his Astronomia Nova Kepler delved deeply into this issue. He had discovered the mathematical laws governing planetary motion. But these were merely descriptive. What was now needed was a physical explanation of why the planets moved in this way. In our terms, induction was not enough; it had to be complemented by retroduction in order for a true science of planetary motion to be achieved. And so he tried out some speculative analogies based on light and magnetism that might explain how the source of the planet's oddly-shaped orbital motion could lie in the sun. The details need not concern us and he continued to revise them in later works. (Stephenson 1994; McMullin 1989, 280-285) What was important was that he saw that an accurate kinematical description of planetary motions should serve as basis for a dynamical account of why these motions are what they are. I think that he might even have seen that such an account would, in turn, help to validate the kinematical descriptions themselves as true "laws" and not merely as a convenient inductive saving of the phenomena, "accidental generalizations" (our terms, not his).

Kepler's contemporaries in natural philosophy were slower than he to grasp the importance of hypothetical causal reasoning and the distinctiveness of the criteria needed to evaluate it. Galileo made free use of such reasoning in his investigations of astronomical topics but always retained the Aristotelian language of necessary demonstration that he had acquired during his youthful apprenticeship to natural philosophy. (Wallace 1984) He was further encouraged in this regard by the dramatic success of his new geometrically-expressed science of mechanics. His two laws of falling motion could be formulated without needing to invoke a causal hypothesis of any sort. It was not difficult, then, for him almost to convince himself that the resulting kinematics shared the demonstrative character of geometry.

Bacon on the other hand realized quite clearly the importance of effect-to-hidden-cause validation. What made it especially important for him was his conviction that the science he sought had to concern itself with "the investigation and discovery of the latent configuration in bodies". It had to trace latent processes "largely hidden from the sense", postulate "things too small to be perceived by the sense" on which the natural action of visible bodies depends. (Bacon 1994, II, pars. 6-7; 139-140) The only way to reach out to this hidden realm was by way of causal hypothesis. And such hypotheses were to be tested by a systematic review of observable consequences to be drawn from them. His "instances of the fingerpost" were intended to serve as guide in this matter. Suppose, he asks, one seeks to discover the cause of the gravitational behavior of bodies. Is it simply a natural tendency or is it the result of an attraction exercised by the earth? If it is the latter, then one might take two clocks, one powered by leaden weights, the other by a spring, and bring them to a high steeple or a deep mine. If attraction is the cause, the first clock should lose or gain time relative to the other. (Bacon 1994, II, par. 36; 216)

Bacon must have been aware that this mode of validation differs from that employed in his tables of presence, absence, and degree. Since attraction cannot be directly observed, it cannot appear as an item in one of his tables. It can be reached only indirectly, relying on the tables for evidence. If he seems to the modern reader to conclude too readily that the possible explanatory hypotheses in such cases can be reduced to two or three, thus allowing a sure affirmation of one of them when the others have been eliminated, what is more important for us is to note that he does lay out a form of hypothetico-deductive validation for causal hypotheses. He allows the single term 'induction' to cover both kinds of validation, perhaps intending his method of induction to cover two separate stages, the first a generalizing of a relationship over observed particulars, the second the testing of a causal conjecture arising from such generalizations. This elastic usage of the term 'induction' would long continue. Even Whewell, two centuries later, who saw clearly the difference between the two modes of validation, would still allow the ambiguity to pass, equivalently taking the term 'induction' to cover non-deductive validation generally.

As is well-known, Descartes took causal hypothesis very seriously; Laudan, indeed, regards him as the founder of the "method of hypothesis" in natural philosophy. (Laudan 1981, chap. 4) In a famous passage in the Discourse on Method where he is laying out a deductivist account of how the different kinds of natural things might have originally formed, Descartes concedes that at some point one has to work back from effects to causes and when one does this, one discovers that the power of nature is so vast that a multiplicity of different possible causes could account for the effects one is trying to explain. (Descartes 1985, I: 144) Like Bacon, he advises that in such a case one has to test the alternatives simply by the consequences drawn from them. He is obviously not comfortable with the notion of allowing hypothesis a permanent place in science, and in the Principles of Philosophy he makes an elaborate effort to show that in his natural philosophy the uncertainty of hypothetical reasoning from effect to cause can in practice be decreased until the reasoning becomes almost demonstrative. Speaking of the causal principles of his mechanics, he remarks optimistically: "it seems it would be an injustice to God to believe that the causes of the natural effects which we have thus discovered are false". (Descartes 1985, I: 255) Though Descartes sees that the natural philosopher must find a way to reduce the multiplicity of alternatives when arguing from effects back to their unobserved causes, it has to be said that he is not of much practical help in dealing with the challenge.

Robert Boyle is another story. In his chemistry and his pneumatics, he found himself constantly referring to unobserved causes, in particular to the imperceptibly small corpuscles of which (he was convinced) all perceptible bodies are composed. He was not content simply to say, as Bacon had, that causal hypotheses should be tested against their observed consequences. This is an obvious first step. But it would be required of any hypothesis, for example an inductive generalization like the one regarding the spring of air. He believed that for causal hypotheses a more sophisticated answer could be given. In a short unpublished paper he laid down what he called the "requisites of a good hypothesis". (Westfall 1956) There were six such requisites, including internal consistency and consistency with established physical theory, for example. There were four further requisites for an "excellent" hypothesis; it should be simple; it should not be forced; it should lead to further testable results; it should afford the best explanation of the data available.

What is important about this list is not the individual requisites, but the philosophical realization that guided them, as it had Kepler's reflections earlier. Once argument from effect to unobserved cause be admitted into natural science, one has to ask what criteria should guide it. It is obviously more complex and more precarious than deduction or the simple induction that leads to a generalization like that about the pressure/volume relationship for gases. It is not simply a matter of saving the phenomena in hand, otherwise there would be no way of distinguishing between the constructions of a Ptolemy and the claim to a better explanation of a Kepler. It should not be ad hoc. Kepler remarks that a false hypothesis may "yield the truth once by chance" but will betray itself over the course of time by the ad hoc modifications its proponents are forced to introduce. (Kepler 1984, 140)

In the Preface to his Treatise on Light, Christian Huygens showed an admirable appreciation for the complexities of the form of argument his work on optics relied upon:

Here the principles are verified by the conclusions drawn from them, the nature of these things [that is, of light] not allowing of this being done otherwise. It is always possible to attain thereby to a degree of probability which very often is scarcely less than complete proof. Thus, when things which have been demonstrated by the principles that have been assumed correspond perfectly to the phenomena which experiment has brought under observation, especially when there are a great number of them, and further especially when one can imagine and foresee new phenomena which one employs and when one finds that therein the fact corresponds to our prediction. But if all these probable proofs are to be found [in my work], as it seems to me they are, this ought to be a very strong confirmation of the success of my inquiry. (Huygens 1912, vi-vii)

In this well-known passage, Huygens was defending the claims of his wave-theory of light, which employed hypothesis in arguing from the observed optical phenomena as effect to the unobserved periodic character of the mode of transmission as cause. What should be noted is his confidence in the method of causal hypothesis and his sophistication in philosophy of science. He realized that to understand the periodic character of certain optical effects he could appeal to a presumed periodic feature in the transmission of light, something akin to the wave phenomenon observable on water surfaces. He was confident that such an appeal was legitimate and that it could be epistemically justified, though what it would yield would normally be probability rather than demonstration. He may have been over-optimistic in estimating the degree of probability attainable, though one can see why the persuasive character of the argument for the wave analogy in light transmission would have encouraged this sort of confidence.

With Boyle and Huygens, then, it might be thought that inference to underlying hypothetical causal structure had, at last, become part of the accepted repertoire of natural philosophers as well as of those who reflected from a distance on the epistemic character of the new sciences of nature. But a challenge was in store. The source of this challenge and the profound impact it made on philosophers of the next generation will be the topics of the remainder of this essay. The challenge came from the new kind of science presented so masterfully in the Principia Mathematica (1687). Newton's innovative approach to the science of motion appeared to allow him to dispense with the troubling hypothetical element that the search for causal explanation had led his predecessors to admit into physics. Since mechanics was for Newton, as for his contemporaries generally, the paradigm of natural science, it was hardly surprising that this unexpected development should cast a shadow over the admission of causal hypothesis into natural science proper. If one could manage without hypothesis in mechanics, why not elsewhere in "experimental philosophy"? And that indeed was the moral that many would draw, first among them Newton himself. The great authority of the author of the Principia made an hypothesis-free science seem the ideal to philosophers who reflected on what a science of nature might aspire to.

Focusing on this aspect of the "Newtonian revolution", as I.B. Cohen terms it (Cohen 1980), ought not be taken to imply that distrust of retroductive inference was the only consequence of any moment for the philosophy of science of Newton's work. In particular, the present generation of Newton scholars has labored, with impressive success, to unravel the intricate logical structure of the Principia Mathematica itself, a structure to which Newton's own summary comments on method scarcely do justice. Philosophers of science have found it a challenge to decide just how exactly the work functions epistemically, what serves as evidence for what and how(2). But it was, of course, on the science of mechanics itself, not on philosophy of science, that the Principia had the most immediate impact in its own day. It initiated a remarkable century of achievement in rational mechanics on the part of some of the most illustrious figures in the history of science: Euler, d'Alembert, Lagrange, Laplace….

This essay is, however, restricted to the narrower question: What did the philosophers of that day take to be the lessons to be learnt from the success of the Principia for the philosophy of science, that is, for the reflective enterprise that stands back from the actual practice of science to discern forms of empirical practice, theoretical explanation, logical inference, and the rest? We shall see that a philosophy of science shaped by the mechanics of the Principia was rapidly accepted as appropriate for natural science generally. Newtonian mechanics was to become for a time the paradigm for what any science of nature ought to look like.

There were, of course, many other sorts of inquiry into nature being pursued by that time: heat, light, electricity, properties of gases, chemical combination, were being subjected to more and more systematic investigation. Where many of Newton's predecessors had allowed that forms of inquiry such as these could lead to a more relaxed notion of science, in which hypothesis and hence probability would play an ineliminable role, the strong inclination post-Principia was to suppose that phenomena other than the phenomena of motion that Newton had dealt with so successfully could be assumed either to reduce in one way or other to phenomena of motion lending themselves to "Newtonian" treatment, or else inquiry into their nature would inevitably fall short of science proper.

2. Newton on hypothesis

In the first edition of the Principia, Newton had nothing explicit to say on the topic of hypothesis or on the precise logical relationship between the "mathematical principles" that introduce the Principia and the observed phenomena of motion. In the twenty-six years intervening between the first and second editions of the work, however, he evidently became more and more irritated by the reproaches of his French and German critics, their allegation that despite its claim to have revealed the mathematical principles of natural philosophy, the Principia was basically hypothetical in character, appealing to an occult quality of universal attraction. And so he had his editor, Roger Cotes, insert a passage in the General Scholium added to the new edition, in words that would echo down the years:

But hitherto I have not been able to deduce the cause of these properties of gravity from phenomena and I feign no hypotheses; for whatever is not deduced from the phenomena is to be called an hypothesis; and hypotheses, whether metaphysical or physical, whether of occult qualities or mechanical, have no place in experimental philosophy. In this philosophy propositions are deduced from the phenomena and rendered general by induction. (Newton 1966, 547)

Historians have devoted much effort to decoding what Newton meant here by 'hypothesis'; I will return to some of those interpretations in a moment. But whatever he meant, there can be no doubt that this passage was taken by a later generation of philosophically-inclined readers to pronounce a ban on causal hypotheses in natural philosophy. The proper method is to deduce, or derive, principles directly from phenomena, without the intermediary of an hypothesis that would open the possibility that an alternative account might work equally well or better.

In a Query added to the second edition of the Opticks in 1706, which became the famous Query 31 of the third edition of 1717, Newton had already made his aversion to hypotheses public and clear: they are not, he says, "to be regarded in experimental philosophy". (Newton 1952, 404) Instead, his "method of analysis" prescribes that one should draw general conclusions from experiments and observations by means of induction. In this way, he claims, one can proceed "from effects to their causes and from particular causes to more general ones till the argument ends in the most general". He makes much the same point in Query 28. Criticizing the mechanical philosophers for their habit of "feigning" hypotheses, he asserts that: "the main business of natural philosophy is to argue from phenomena without feigning hypotheses and to deduce causes from effects till we come to the very first cause which certainly is not mechanical". (Newton 1952, 369)

Here, then, was a weighty part of Newton's legacy to philosophers of the century that followed. It was not just his published remarks on method that influenced his successors, of course. There was also the example of the Principia itself. It seemed to have dispensed quite successfully with retroductive hypothesis to underlying agent causes, just as Newton claimed it did. If the Principia were to be taken as the paradigm of what a natural science should look like, then Newton's assault on hypothesis might well be justified, even though it ran contrary to the consensus that had been growing among the natural philosophers of his own generation.

But did it really run contrary? Historians have been divided on this issue, many arguing that the famous ban on hypothesis did not extend to the sorts of hypothesis that had attained respectability among the likes of Boyle and Huygens. The problem lies, they claim, in the ambiguity of the term 'hypothesis' in Newton's usage. What he was rejecting, they suggest, was not hypothesis in general but only the speculative hypotheses characteristic of the Cartesian tradition. These were no better than conjectures, enjoying a modest degree of explanatory plausibility, like the Cartesian ether vortices, but lacking any testable observational consequences.

There can be no doubt that Newton was especially critical of speculative hypotheses of this sort. When he sent the copy for the General Scholium containing the famous "hypotheses non fingo" line to Cotes, he was at pains to explain in the covering letter that by 'hypothesis' he meant a proposition that "is not a phenomenon nor deduced from any phenomena but assumed or supposed without any experimental proof". In an earlier draft of the same letter he had made clear that the "hypothetical philosophy" he opposed "consists in imaginary explications of things and imaginary arguments for or against such explications" especially against the well-founded inductive arguments of "experimental philosophers" like himself. (Turnbull 1959, V, 397-399)

Does this mean that he thought causal hypotheses, having some limited degree of empirical warrant, were an acceptable part of natural philosophy? I do not think so, although his views on this were less dogmatic earlier in his career, prior to the publication of the Principia. In his first publication, "A new theory about light and colours" (1672), he had argued that the colors produced by a prism are not created by the prism but are intrinsic properties of the light itself. In a letter to Oldenburg (6 February 1671-2), he emphasized that this:

is not an hypothesis but most rigid consequence, not conjectured by barely inferring 'tis thus because not otherwise or because it satisfies all phenomena (the philosophers' universal topic) but evinced by the mediation of experiments concluding directly and without any suspicion of doubt. (Turnbull 1959, I, 96-97)

This is a striking passage because it indicates that even if an hypothesis "satisfies all phenomena", that was not enough in his eyes at this point to warrant its admission into natural philosophy. He never did concede to critics like Hooke and Pardies that his theory could properly be described as hypothetical. Hypotheses, he insists to Pardies, are "foreign to the purpose" of natural science. (Cohen 1958, 106)

A few years later, however, he did relent somewhat and publish "A hypothesis explaining the properties of light". He excuses this venture into hypothesis by conceding that it might help to make his original claim about colors more intelligible, though he admits that it may involve him in "troublesome and insignificant disputes", the outcome that by temperament he most wanted to avoid. And so he launched into a freely speculative discussion involving an aethereal medium, akin to spirit, that may by coagulating into a "humid active matter" within the "pores" of earth give the earth the power to draw bodies downward. And he goes on to discuss an "animal spirit" that might in similar ways explain muscular action. These "spirits" would have to possess "some secret principle of unsociableness" to achieve this end; he speculates on how such a principle might operate. (Cohen 1958, 179, 181, 183)

This venture into causal hypothesis is radically at odds with his later strictures against speculative conjecture of precisely this sort. Whatever persuasive force these explanations possess could come only from a very loose sort of explanatory coherence but with no suggestion of testable consequences that might serve as partial warrant. Newton nowhere addresses here the sort of issue that earlier defenders of the method of hypothesis had thought to be important, namely the epistemic criteria that would be appropriate for the evaluation of explanatory hypotheses generally. He seems to say to his readers in this early paper on the hypothetical explanation of the properties of light: "well, if this is the kind of thing you want, here goes!"

Thirty years later, when he decided to rework the results of these early researches on light and colors into a proper science of optics, he found himself faced with this same issue: ought he include speculative causal explanations of this sort or not? The famous opening sentence of the Opticks of 1704 runs: "My design in this book is not to explain the properties of light by hypotheses but to propose and prove them by reason and experiments". There follows a set of definitions and axioms reminiscent of the Principia Mathematica. But what comes next is not the cascade of theorems of that earlier work but a series of independent arguments from experimental results to numerous laws more or less inductively arrived at, notably to his most cherished result, namely that sunlight consists of rays differently refrangible(3). The proof in all cases is by experiment and induction, not by deductive derivation from an axiomatic starting-point. On the whole, in this first part of the Opticks, he avoids causal hypotheses that appeal to the nature of light itself to explain why these experimentally discovered laws are what they are.

Finally, however, he breaks off, unable to achieve the consilience that the concept of attraction had afforded him in the Principia, and begins the series of Queries already alluded to. These give free rein to his powerful speculative imagination, introducing hypotheses about how bodies may act at a distance to bend light-rays, about how vibrations caused by light rays in the optic nerves may produce the sensations of different colors, about the source of the "fits of easy reflection and easy transmission" of light he had already noted in his experiments on refraction, about differences in density in the aethereal medium as a possible cause of the gravitational behavior of the planets, about the exhalations from electric bodies, and much else.

Hypotheses are freely introduced here as "queries", as questions for later experimental resolution. This is the second line of defense for those who argue that Newton is really not opposed to admitting hypothesis into natural philosophy, despite appearances to the contrary. So long as hypothesis is understood as no more than a question, so long as it is taken to be a heuristic strategy only, Newton evidently has no objection to it, they say, since he employs it himself so extensively in his optical investigations. But, of course, this is no way implies that he accepts the proper presence in natural philosophy of hypothetically-justified claims of the sort Boyle and Huygens had sought to domesticate. Newton seems to assume that his queries can ultimately be answered by means of the sort of inductive generalization across the experimental data that he prescribes in the concluding pages of the Opticks. Though he allows causal hypotheses from effect to unobserved cause to be introduced on heuristic grounds, they must ultimately, it seems, be replaced by conclusions drawn directly from the experimental data by inductive generalization proper.

That this is what he means is clear from the qualifications he admits at the end of the Opticks, somewhat reluctantly one guesses, on the certainty of the inductive conclusions arrived at in response to the queries he has listed. This method, he says, falls something short of demonstration, but:

it is the best way of arguing which the nature of things admits of, and may be looked on as so much the stronger, by how much the induction is more general. And if no exception occur from phenomena, the conclusion may be pronounced generally. But if at any time afterwards any exception shall occur from experiments, it may then begin to be pronounced with such exceptions as occur. (Newton 1952, 404)

This passage brings out admirably the fundamental difference between the inductive generalization Newton here favors and retroduction. When inductive generalizations are extended (think of Boyle's Law, for example), exceptions may be found and the generalization may have to be modified, though it still holds good at the original level of generality. Inductive generalizations thus can command a high degree of assent; there is little danger that they will be entirely refuted. At worst, they will simply be sharpened, reformulated, made more accurate. Natural philosophy will thus progress through steadily improving approximation. But causal hypotheses, even those with a measure of explanatory success, may turn out to be simply wrong. The alternative here is not a mere exception that leaves the original claim more or less intact, within its level of generality. It may be a different hypothesis entirely, that light transmission is basically wavelike instead of particle-like, for example. Here the consequences can be much more epistemically drastic, and it was almost surely this feature of causal hypothesis that prevented Newton from ever allowing it to be part of natural philosophy proper. His program was, from the beginning and always remained, as Shapiro puts it, to "construct a hypothesis-free science". (Shapiro 1993, 181)

Why was he so devoted to this ideal, at a time when natural philosophers generally were more and more inclined to settle for probability? There was, of course, the matter of temperament. William Whiston, his successor in the Lucasian Chair at Cambridge judged him, not altogether sympathetically, to be "of the most fearful, cautious, and suspicious temper I ever knew" (Westfall 1980, 652). That he was imperious and thin-skinned in regard to his own achievements, we have ample evidence. That Hooke should describe his work on colors as an "hypothesis" was not in Newton's eyes just a mistake, it was a mortal insult.

And then there was also his intellectual background in the tradition of "mixed mathematics" stretching all the way back to Aristotle. In that tradition, the principles of the mixed sciences, the sciences that lay between physics and mathematics, were mathematical; these sciences were, in Aristotle's words, to be treated as "the most physical parts of mathematics", not, as one might have expected, the other way round. Thus, geometrical optics could be treated as applied geometry, its theorems possessing the same kind of certitude as that of geometry itself. Newton was probably introduced to this tradition by attending the lectures of Isaac Barrow, his predecessor in the Lucasian Chair, who carried the mathematization of such mixed sciences as optics and mechanics to an extreme. According to Barrow, they are all simply branches of geometry: "they scarce require anything which is not granted and proved in that science, nor use any other principles or reasonings than what are strictly geometrical". (Shapiro 1993, 34) These principles are not a matter of conjecture or probability; though they derive from observation and experiment, they are known with certainty. No, wonder then, to find Newton writing in his early unpublished Optical Lectures that geometry and natural philosophy must finally be blended, so that:

with the help of philosophical geometers and geometrical philosophers, instead of the conjectures and probabilities that are being blazoned about everywhere, we shall finally achieve a science of nature supported by the highest evidence. (Shapiro 1993, 25)

At this point, we surely have part of the story of Newton's almost obsessive attachment to the ideal of certainty, an attachment which grew stronger, rather than lessening, as he grew older. But there is a further reason, I am convinced, and it is this reason that I want finally to underline, because it contributed so directly to the shaping of the Newtonian legacy in the philosophy of science. This reason hinges on a discovery Newton made in the writing of the Principia; nothing corresponding had happened during his earlier researches in optics. It had to do with a peculiarity of the cluster of concepts, force, attraction, gravity, that lay at the heart of his new mechanics.

3. Dynamic explanation

These concepts were oddly ambiguous as they emerged from the long shaping that went to the axiomatic section with which the Principia opens. The eight Definitions and three Laws or Axioms went through draft after draft as Newton tried to put together a coherent physico-conceptual structure that would support the mathematical work already done. (Cohen 1971, 59-66; 92-96) His aim was to construct a mechanics that would account for the various known regularities of motion, most particularly for the regularities Kepler had discovered in the planetary motions. And on the face of it, he had succeeded.

But had he explained them? Critics like Leibniz and Berkeley thought not. Had he identified the agent-cause of motion under an attractive force, the "cause of gravity", as he called it? He had to admit that he had not. Among the possible causes, he had eliminated ethers possessing mechanical properties. And even though he would sometimes speak of the sun as "drawing" the planets as though it were the immediate agent-cause of their motions, it was not clear how it could be; he had himself strongly discounted the possibility of the sort of action at a distance such an explanation would require. A further reason not to admit the sun as cause of the planetary motions was his conviction, one not shared by most of his contemporaries, that matter must be regarded as a passive principle. But in this case, what is left? No agent-causal explanation of the planetary motions seemed to be possible, unless one invoked God as direct mover, as Berkeley would later do. Though Newton toyed with this idea, he evidently found it unsatisfactory. (McMullin 1978, chap. 4)

His failure to fill this gap seemed altogether decisive to his critics. Though the Principia might well serve the practical purposes of prediction, as Ptolemy's epicycles had done long before, it could not in their view be regarded as natural philosophy proper. Aware of their reservations, Newton continued from time to time to search for agent-causal explanations of gravitational behavior, a search in which he never succeeded. But he remained convinced that the scientific status of the Principia did not depend on filling out the causal story in the conventional way: he had discovered the "mathematical principles" of natural philosophy. Was this not enough to set mechanics on its way?

And, of course, as we know, it was. In the Principia, Newton postponed pursuit of the "physical principles". But he had already provided a conceptual structure whose further development would occupy the best mathematical minds for decades to come. Above all, he had unified the disparate phenomena of motion by the concept of attraction, and more generally by that of force. Nor was this a mere saving of the phenomena, an achievement serving practical ends only. The conceptual basis of the new mechanics was impressively (even if not yet perfectly) coherent. The notion of attraction was, of course, undeniably problematic when understood "physically".

Newton had, however, hit on a way to lessen, if not to neutralize, its problematic character. The term, 'attraction', could be understood in two very different ways. In one, it is an agent-causal term: to say that the sun "attracts" the earth is to attribute active causal agency to the sun. In the other, it is a dispositional term: to say that the earth is "attracted" by the sun is to say no more than that the earth has a disposition to move in a certain way when in a particular configuration with the sun. The actual agent-cause (the "cause of gravity") is left unspecified. This disposition is not like the disposition to natural motion in Aristotle's physics; it is not a simple consequence of a particular nature. This attraction depends on both the distance and the mass of the distant sun, so that the sun must in some way be causally involved. But the manner of this involvement is left unstated. Newton's reiterated limiting of the scope of his mechanics to the "mathematical" was equivalently, to restrict it to "attraction" in the second sense only.

In this way the issue of agent-cause was finessed. And, in consequence, there was no need to resort to specific causal hypothesis. The disposition to move in the ways that Kepler described could be linked to the inverse-square law, so that the confident language that Newton used to describe this move ("deduced from the phenomena") was, in fact, justified(4). But, of course, such an inference will be possible only when one is arguing from the "phenomena of motions" to the "forces of nature", as Newton describes it in the Preface to the Principia. In such a case, one can speak the language of disposition and thus dispense with causal hypothesis. Outside of mechanics, however, how often will this be possible? Elsewhere in the inquiry into Nature, as we have seen, the quest for agent-cause cannot so readily be set aside. Dispositions (like Galileo's "repugnance to the void") are not of much help when arguing from the phenomena of the air-pump to the existence of the atmosphere. Newton suggested that the behavior of gases might be understood by supposing that different laws of force might operate between the minute corpuscles of which he believed gases to consist. But, of course, the catch (as Locke saw) was how to arrive at a sufficient specification of the (unobserved) corpuscles and their motions to enable either the derivation or application of force laws.

In mechanics itself, however, Newton established the credentials of a new and unfamiliar way of proceeding. The language of force and attraction carried with it the suggestion of agency, of the sun drawing the planets, of an agent-causal explanation being given, even though this was expressly excluded by Newton himself. But the suggestion here was not entirely deceptive: the Principia is pointing to an agency of some unspecified sort being at work and being responsible for the multiple sorts of observed regularity of motion, linking them together in a common explanatory network. The form of explanation given is weaker than agent-causal, where the agency itself is identified and the mechanisms of its action described. It might be called "dynamic" since it is dependent on the peculiarity of the notion of force as Newton elaborates it.

Dynamic explanation lies somewhere between two forms of explanation over which philosophers of science have long disagreed. First of these is the strong agent-causal form of explanation offered by retroductive inference to underlying structure, with the multiple epistemic criteria that hypothesis of this sort calls for. (McMullin 1992, 1996) Second is the weak form of explanation given by subsuming a puzzling instance under a particular law. The law itself in this case will be the product of induction, and if cause is involved, it will ordinarily be described in terms of event-causation. The D-N model of explanation, as Hempel originally defined it, is of this sort.

Dynamic explanation in one respect resembles the latter because of their common emphasis on lawlikeness as explanatory. But in another respect, it carries more genuine explanatory force than does the latter, because of the suggestion of a single sort of underlying active agency at work and because of the strong unification of mechanics that this form of explanation brings about. Whewell would later present this feature of the Principia as a primary example of the epistemic virtue he called consilience. And some contemporary philosophers of science, Michael Friedman and Philip Kitcher among them, would go so far as to take such unification to be at the heart of scientific explanation generally.

Much more could be said about the later elaboration of this form of explanation, about the emergence from it of the concept of a field(5), about Einstein's postulation of space-time structure that would end the search for the "cause of gravity", about force as "explained" by elementary particle exchange in quantum field theory. . . . With these developments, mechanics went well beyond the safe language of disposition and entered the riskier realm of retroduction. Suffice it to say here that dynamic explanation proved a bridge to kinds of causal structure that Newton could never have anticipated but for which he laid the groundwork.

But the theme for which this essay has been preparing is the impact that the Principia and Newton's comments on method made not on the science but on the philosophy of science of the age that followed. And here the assessment from the vantage-point of a later day has to be less favorable. Many of the most influential philosophers of the eighteenth century tended to view the Principia not just as a giant step forward for mechanics but as the paradigm of what a natural science should look like. The consequences of this assumption were far-reaching and to a significant extent negative. In the remainder of the essay, the influence of this assumption on four major philosophers will be briefly recalled.

4. Causal inference

A notable feature of the Principia, as we have seen, is the way that it sets aside hypothetical inference to underlying agent-causes. Newton's own way of thinking about this feature of the work, so far as one can tell, was that it amounted to a deferral, not an abandoment, of that quest. But others drew a different implication. Might not Newton be underrating his work by regarding it as incomplete in this way? What if the admittedly limited form of explanation of motion afforded by the Principia were all the explanation possible in the natural order?

George Berkeley was the one who followed up this lead most energetically and who made it, in fact, a cornerstone of his own account of natural action. Where the Principia was concerned, he was both critic and admirer. In The Principles of Human Knowledge (1710) and at more length in De Motu (1721), he commented acidly on the convenient ambiguity of such terms as 'atttraction' and 'force': they convey, he notes, the illusion that a causal explanation is being offered but in fact all they do is describe "mutual tendencies to motion". He characterized gravity itself as an occult quality, as other philosophers had already done. It should be dismissed from natural philosophy where, he argues, "it is vain to adduce things which are neither evident to the senses nor intelligible to reason". (Berkeley 1992, pars. 21, 82) He rejected Newton's absolutes of space, time, and motion. Since they do not affect the senses, and cannot even be conceived, they are "necessarily quite useless" for the natural philosopher. Mathematical hypotheses like these, or like the forces of attraction attributed by some to sun and planets, "have no stable essence in the nature of things". (Berkeley 1992, pars. 67, 104) As far as Berkeley was concerned, the "forces" that played so large a part in Newton's exposition simply did not exist. The Principia could have got along perfectly well without them.

These were obviously not minor reservations. Nevertheless, where others like Leibniz saw it as a critical failing of that "justly admired treatise" (Berkeley's description) that it left entirely blank how forces operate, Berkeley on the contrary looked to this for significant support of his own critique of the materialism that he found implicit in the work of "corpuscularians" like Boyle and Locke. Attributing causal agency to bodies, Berkeley insisted, led to irreligion by diverting such agency from its true source in God. His own analysis of causality led him to restrict genuine causal agency to mind alone; bodies of themselves (in Berkeley's system, ideas of bodies) are inert, incapable of acting on one another. From Berkeley's perspective, Newton had shown that one could construct a highly successful mechanics of bodily motions without ever needing to go beyond a description of these motions to an explanation of them that would explicitly commit one to attributing agency to material bodies.

Newton's critics took this to be a crucial failing of the Principia. Berkeley thought otherwise. In his eyes, Newton had shown, in effect, that this was the best that could be done in the domain of body and that it warranted weaker notions of cause and of explanation in that domain than the traditional ones. One could then draw the sharp distinction he needed between the "true efficient causes" to be found only in the action of mind and the weaker "second corporeal causes", as he calls them, that attribute no agency to body, only regularity of observed behavior. Such regularity does not derive from the nature of the bodies concerned but from the benevolent choice of the Creator acting on human behalf. There is thus no intrinsic necessity about the causal relationship in this secondary sense of 'cause'.

Berkeley interpreted the achievement of the Principia as showing that the most a physicist should aspire to is to study "the series or successions of sensible things, noting by what laws they are connected and in what order, what precedes as cause, and what follows as effect". (Berkeley 1992, pars. 71, 106) Causality in this secondary sense, the only sense appropriate to a science of bodies, reduces to regular and observable succession, no more. What allows one to call this "explanation" is that Newton had, after all, succeeded in unifying disparate sorts of observed regularities of motion in an ingenious mathematical scheme, of obviously great practical utility. It did not explain in the deeper, proper, agent sense of cause, Berkeley insisted. But then, in his view, no one should ever have expected that it would, or even could. Newton had to all intents and purposes demonstrated the limits of explanation in natural philosophy; explanation at the level of real cause ought be left to metaphysics.

Berkeley's proposal in the De Motu to limit explanation in natural philosophy to subsumption under laws of nature, understood merely as systematically observed and mathematically organized regularities, found an immediate echo, of course, in Hume's Enquiry a few decades later (as well as a more distant echo in the DN model of explanation favored by the logical empiricists of our own century). Hume denied, however, what Berkeley would have regarded as the key element in his own account of causality, the appeal to what Berkeley called real causality, namely, the causality of mind, ultimately the Divine Mind. For Hume there were no real causes in that sense. The only sort of "causal" explanation he would allow derived from the constant conjunction between succeeding and contiguous events, the sort that Berkeley had regarded as causal only in an extended sense. By limiting himself to this form of explanation and then by setting aside the causal agency of God that Berkeley (like the nominalists of a much earlier century) had seen as the guarantor of the stability of the contingent regularities of our experience, Hume created for himself the problem of induction that has preoccupied those philosophers of recent generations who share his empiricist principles.

To what extent was Hume's philosophy of science influenced by Newton's writings? Far less obviously than Berkeley's. He derives his account of causality as constant conjunction from his empiricist starting point, with no reference to the Principia nor indeed to natural science more generally. In the eleven explicit references to Newton that James Force has managed to find in Hume's voluminous writings, only three refer to issues of method in natural philosophy and of these, only one, from his History of England, not from the Treatise or the Enquiry, is at all specific. There he acknowledges the greatness of Newton: "In Newton this island may boast of having produced the greatest and rarest genius that ever arose for the ornament and instruction of the species". (Hume 1756, VIII, 334; quoted in force 1987, 176) And he goes on to indicate the moral he draws from the great man's work: the importance of caution "in admitting no principles but such as were founded upon experiment". He sums up Newton's legacy in these words:

While Newton seemed to draw off the veil from some of the mysteries of nature, he showed at the same time the imperfections of the mechanical philosophy, and thereby restored her ultimate secrets to that obscurity in which they ever did and ever will remain.

He is less enthusiastic about Boyle's contribution, much though he appreciates Boyle's experimental talent. On the previous page of the History, he describes Boyle's mechanical philosophy as "a theory, which, by discovering some of the secrets of nature and allowing us to imagine the rest, is so agreeable to the natural vanity and curiosity of man".

In his campaign against a too-tolerant mechanical philosophy that appealed to underlying and often unobservable causal mechanisms, Hume evidently regarded Newton as an ally. Newton too saw the goal of natural philosophy as the discovery of the laws of nature; he too cast the mechanics of the Principia in minimalist terms as subsumption under such laws; he too regarded inductive generalization as the means of discovering and extending such laws; he too distrusted hypothesis and would not allow ethers and the like a respectable place in his philosophy unless and until they could be derived properly from the only admissible sort of evidence, sense-observation. Hume does not make these affinities explicit; he nowhere appeals, for example, to Newton's strictures against hypotheses. But he was undoubtedly aware of them and would have been encouraged by them along the skeptical path he was charting. Newton himself would have drawn back from this path, had it been offered him. Hume's challenge to the logical cogency of inductive inference, his attacks on the design arguments in natural theology so dear to Newton's heart, would have been fiercely opposed by Newton had he been faced with them.

Hume's minimalist option extolled induction but by equivalently rejecting retroduction deprived induction of that further indispensable theoretical warrant that might make it possible to distinguish between genuine laws and accidental generalizations. This option would reduce all explanation in science to nomological explanation, making theoretical explanation and the theoretical terms on which it depends problematic. It implicitly favored anti-realism and set the realm of the unobservable forever out of epistemic bounds. This last, of course, did not reflect Newton's own thinking. And it is important to emphasize once more that Hume built his case, not on the Principia, but primarily on his own radical empiricist epistemology. True, the Principia could serve as implicit model for the sort of natural science that Hume was envisaging, with some amendments, of course, like the elimination of the absolutes of space and time. But others could take that same model, as Kant would do, and find in it the materials for an account of science about as different from Hume's as one could well imagine.

5. Hypothesis-free science

Before coming to Kant, there is one other philosopher who, more explicitly perhaps than any other, promoted the Principia and Newton's methodological comments thereon as the unchallengeable authority in philosophy of science. Thomas Reid's early formation was in mathematics and physics; it was as a lecturer on the Principia that he first made his name. Reacting against Hume's account of mind, especially against the theory of ideas that was its basis, he turned to developing his own science of mind, and not surprisingly took Newton as his guide in deciding what a science should look like. In his principal work, Essays on the Intellectual Powers (1785), he writes:

Sir Isaac Newton, the greatest of natural philosophers, has given an example well worthy of imitation, by laying down the common principles or axioms on which the reasonings in natural philosophy are built. . . . [In this way,] a solid foundation is laid in that science, and a noble superstructure is laid upon it, about which there is now no more dispute or controversy among men of knowledge than there is about the conclusions of mathematics. (Reid 1967, I:231).

And again:

Since Sir Isaac Newton laid down the rules of philosophizing in our inquiries into the works of nature, many philosophers have deviated from them in practice. . . . But [they rules] have met with very general approbation as being founded in reason, and pointing out the only path to the knowledge of nature's works. (251)

"The only path"-and not just in mechanics but in the investigation of nature generally. The four Rules of Reasoning in Philosophy that serve as preface to Book 3 of the Principia furnished him with general guidance. Rule I set the standard: "We are to admit no more causes of natural things than such as are both true and sufficient to explain their appearances". Newton's restriction of inquiry to "true causes" (verae causae) has puzzled generations of commentators. Where exactly are such causes to be found in the account of planetary motion that immediately follows the Rules? Is Newton thinking here of 'cause' in a weaker sense, as Berkeley thought he should? How is one to know in advance that a proposed cause is the true cause? Reid tells the reader what it means for him: True causes must "have a real existence". That is: they must not be conjectured; there must be "proof" that they exist. And, second, they must be sufficient to explain the effect (250). This latter condition is obvious. But what of the other?

What Reid made of it was an absolute ban on "conjecture", hypothesis", "theory" (he tends to equate the three), in science proper. Following Newton, he allowed that hypothesis could serve as query, as a means to direct inquiry. But in science itself, "let just induction alone govern our belief". (251) Hypothesis can of itself never "beget knowledge"; knowledge can come only through "patient observation", "accurate experiment", or "strict reasoning" from these two sources alone. (235) The reasoning has to be strict, just like the deduction from the phenomena that Newton held up as model in his mechanics. Newton, he remarks, could have invented an hypothesis to try to provide a cause of gravity. But he expressly forbade such a move with his emphatic: "Hypotheses non fingo!" (236).

Reid took this enjoinder as his own in the polemic he launched against David Hartley's neurophysiological account of mind in terms of a doctrine of "vibrations". Hartley had to lean heavily in his account on what Reid calls "the exploded method of hypothesis". (251) But attaching a probability to an hypothesis just because it happens to explain "many appearances of nature" still, Reid argues, leaves it as no better than a conjecture, a guess: "every conjecture we can form with regard to the works of God [i.e. the natural world] has as little probability as the conjectures of a child with regard to the works of a man". (235)

In his later Essays on the Active Powers of Man (1788), Reid goes further, taking the "Newtonian philosopher" as authority for denying that natural philosophy can discover a single efficient (agent) cause in nature. (1967, II: 526) In the spirit of Berkeley, he holds that all that the science of nature can do is to discover the laws by which observable effect follows observable cause. He cites the law of gravitation as the paradigm of what science can achieve but asserts that Newton well knew he "discovered no real cause". The unobservable mechanisms offered as real causes in the mechanical philosophy are "fictions, hypotheses", and these "ought to have no place in the philosophy of nature". (526) Unlike Berkeley, he is not willing to allow that explanation in terms of law can be called causal. There must be a real cause, he concedes, that is, an agent cause, responsible for the lawlike behavior of bodies. But what that agent "behind the scene" is in each case, we can never know. (527) And to speculate is pointless.

Reid is thus setting aside the method that had allowed Newton's predecessors to claim, for example, the atmosphere as the cause of the barometer's behavior. In their view, as we have seen, the product of this method is admissible into science since it is, in the nature of things, the best that can be achieved, allowing in favorable cases a high degree of probability. Where Reid was concerned, however, the hypothesis-free mechanics of the Principia beckoned. And in his defence it must be said that Hartley's hypotheses about the operations of "vibratiuncles" and other mechanisms of a like sort in the brain would never have passed muster were the criteria advocated by a Boyle or a Huygens to be applied to them. Might Reid's polemic against hypotheses be understood to be directed against unfounded, overly speculative, hypotheses only?

This is a sympathetic reading, defended by some. But the fact remains that Reid nowhere suggests that he is restricting his ban to hypothesis of this sort. More important, his readers evidently took the ban to be absolute. The method of hypothesis was simply not to be trusted; argument to underlying agent-cause was a chimera. Reid's works went on to attain a very wide readership and exerted an enormous influence first in Britain and then, in the early nineteenth century, in the U.S. It may not be too much to say, indeed, that the distrust of "mere theory", the tendency to restrict "real science" to the "facts", that manifests itself in all sorts of ways in contemporary English-speaking popular culture owes something to Reid's Essays in the long ago.

6. Transcendental method

And now finally to the greatest Newtonian philosopher of them all, Immanuel Kant. It is impossible in short space to do justice to the intricacies and the sometimes stubborn obscurities of Kant's transcendental method. It was forged in response to Hume's challenge to metaphysics. In his Prolegomena to Any Future Metaphysics (1783), Kant set out to show how the enterprise of metaphysics could be radically reconstructed to qualify as what he calls "real science". Achieving certainty is for him the key to this task. And in the Preface to the Metaphysical Foundations of Natural Science (1786), where he shows how such a task could be accomplished, he is explicit about the quality of certainty that is required: "Only that whose certainty is apodeictic can be called science proper; cognition that can contain merely empirical certainty is only improperly called science". (Kant 1985, 4) What assures him in advance that knowledge of this sort, enjoying not just certainty but necessity, is possible is that, in fact, it already exists in the form of "pure natural science". The science he has in mind here is, of course, the science defined by the axiomatic opening section of the Principia. More exactly, it is the science arrived at by transforming the empirical certainty of the Principia into apodeictic certainty by means of the transcendental method, by arguments ("transcendental deductions") bearing on the real possibility of experience. In this way, the transcendental method itself could be both illustrated and validated as part of the larger task of grounding metaphysics.

From Kant's standpoint, a crucial weakness in Newton's presentation of mechanics is his rejection of action at a distance. Kant argues that there is no compelling reason why bodies cannot act on one another at a distance. There is, therefore, no need for any hypothetical intermediary, an ether or the like; the search for a cause of gravity that Newton expressly left open could thus be set aside as pointless, and the certainty of the inference from motion to force could thus be assured. But this is still empirical certainty. What is needed is a transcendental deduction of the concepts involved and of the principles derivative from them. The possibility of matter, for example, must be shown to require both forces of repulsion and of attraction. The conceptual structure underlying the "mathematical principles" of the Principia's title can be clarified in such a way as to confer synthetic a priori status upon the science it defines.

The Principia evidently played a fundamental role in the shaping not only of Kant's philosophy of science but of his entire philosophical system. Without it to serve as paradigm for what natural science, and more broadly the human powers of understanding, could achieve, it seems doubtful whether Kant's transcendental turn would ever have taken place, or at the very least, could have claimed the credibility that it did. The impression of inevitability suggested by the conceptual structure outlined in the Definitions and Laws of Motion of the Principia could readily translate into the claims of necessity to which the transcendental method could then give metaphysical substance.

Newton himself made no such claim for his mechanics. On the other hand, it would hardly have occurred to that enemy of hypothesis to entertain the possibility that his entire mechanics, regarded as a single complex conceptual system, could itself be regarded as an hypothesis. The eight Definitions over which he labored so long and that went through so many modifications are presented by him as though they need no justification other than their intuitive appeal and their internal coherence. When Cotes was preparing the second edition of the Principia, he queried Newton regarding the epistemic status of the three Laws of Motion. Newton's response was the oft-quoted assertion that the laws "are deduced from the phenomena and made general by induction which is the highest evidence that a proposition can have in this philosophy". (Turnbull 1959-1977, 5: 397)

But in what sense can the Laws be regarded as derived directly, without hypothesis, from the phenomena? In the comments he appends to the First Law, Newton mentions projectiles, tops, planets, and the effects of resistance on their motions, implicitly suggesting an inductive generalization of some sort. But the Law itself refers to a counterfactual state, never actually found in experience, where a body is not acted on by forces of any sort. The Second Law offers a precision of the notion of force that no one before Newton had thought of. In his comment on the Third Law, he reminds the reader that "if a horse draws a stone tied to a rope, the horse will be equally drawn back to the stone", once again suggesting an inductive basis for the Law. But how is one to know empirically that the reaction on the part of the horse would be exactly equal to the action of the stone? Prior to the Principia, no one seems to have thought this a feature of our experience.

What warranted the axiomatics on which the Principia was built is not, from a later perspective, the self-evidence of its Definitions taken separately nor the inductive evidence supporting its Laws, each regarded as a separate empirical claim. Rather, it is that, as a single extraordinarily complex hypothesis, it works so well to organize the inductive evidence already at hand, to unify in an elegant way the entire domain of mechanics, and to allow further fruitful extension and clarification. (McMullin 1985a) A successful hypothesis, then, but nonetheless an hypothesis, not a series of separate empirical, let alone necessary, truths.

In the last years of Kant's life, the assurance conveyed in the title of the Metaphysical Foundations of Science began to waver. (Friedman 1992; McMullin 2001) A variety of new areas of research: chemistry, optics, calorics, were beginning to show results. It had been possible in the Metaphysical Foundations to dismiss chemistry as "systematic art rather than science". (Kant 1985, 4) But by the 1790's, this judgment seemed increasingly vulnerable. Faced with a growing gap between the metaphysical foundations laid so carefully in his earlier work and the diverse new bodies of knowledge insistently laying claim to the title of "science", Kant began work on a "Transition" that would, he hoped, bridge that gap. The work was never finished, but over seven years (1796-1803) he wrote hundreds of pages, only recently organized as his Opus Postumum. (Kant 1993)

As organizing concept in this later work Kant introduced an aether pervading all of space, in strong contrast with the unmediated action at a distance he still attributed to gravitation, a contrast that he himself emphasized. He hoped that this aether could serve as carrier for light, heat, and the forces responsible for chemical interactions. His aim was to achieve the desired transition from the transcendentally-validated conceptual structure of the Metaphysical Foundations to the empirical articulations then in progress in the active new areas of research.

As Kant himself may very well have come to realise, it could not work (Förster 1987). The methods of the transcendental deduction had been tailored to the action at a distance of gravitation where the operation of forces could be deduced more or less directly from the phenomena of motion and there was no intermediary explanatory concept like aether or chemical element requiring justification of a retroductive sort. The warrant for this latter sort of inference, as Newton's predecessors had long ago seen, would necessarily be of a less direct sort, in no way amenable to the dramatic sort of validation Kant could offer the mechanics of the Principia. The century-long hold that the Principia had exercised on the philosophy of science was finally being challenged by the onward progress of "real science" under a new and more relaxed definition.


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1. I apply the term 'retroduction' primarily to the process of theory-validation. Peirce more often relates it to the prior process of theory-creation. Despite this ambiguity, the term is an obvious choice on etymological grounds for the second of the two modes of validation described above: proceeding from effect back to postulated agent-cause. The conflation of the two senses of the term (or of its more common synonym, 'abduction') has been the cause of continuing confusion in the philosophy of science. See McMullin 1990 and 1994.

2. See, for example, Palter 1967; Westfall 1971; Cohen 1971, 1980; Cushing 1982; Stein 1990; Brackenridge 1995. Smith in his 2001 a and 2001b takes Newton at his word in the Preface to the Principia when he says that he is about to unveil a new way of doing empirical science ("finding the forces of nature from the phenomena of notions"). Smith argues that this way was not only much more complicated, but also far more epistemically secure, than Newton's laconic reference to "induction" might suggest. Focussed scholarship of this sort brings home to the modern reader just what philosophy of science can learn from the Principia-but took a long while to do so.

3. Whether or not it could be considered an inductive finding depended on how literally the notion of a "light-ray" was to be understood, Hooke thought it involved an implicit commitment to a corpuscular theory of light-transmission, making the analysis hypothetical. Newton, naturally, saw it otherwise. In his view, light-rays as they had long been employed in geometrical optics could be regarded as analytic devices, making no ontological commitment. Still, 'consists of rays differently refrangible' did undoubtedly have an ontological ring to it, just as 'attraction' would later have in his mechanics.

4. The precise manner of this linkage is more complicated, however, than the term 'deduce' would suggest to the modern reader. (Smith 2001a, 2001b) One feature of the "deduction" of the inverse-square law of force from Kepler's laws that has attracted much comment from philosophers of science is that the postulate of universal gravitation as well as the Third Law imply that the orbits of the planets around the sun cannot be true ellipses because of the perturbations brought about by the planets' gravitational relations to one another, as well as the slight movements of the sun itself in consequence of its relations to its attendant planets. Smith shows that Newton was acutely aware of this issue and dealt effectively with it. He shows, in fact, how much additional strength is brought to the argument by the way in which, when approximations made along the way are more carefully treated, the consequent corrections turn out to be observationally verified.

5. Historians of science disagree as to whether Newtonian attraction ought properly be said to constitute a field. As the notion of a field finds expression finally in Faraday's work, it requires something more than dispositions towards motion associated with points in empty space. See McMullin 2001.

6. Berkeley's later work, Siris (1744), seems to depart rather dramatically from this view of cause and explanation, leaving Berkeley scholars with several puzzling questions: Did he change his mind or not? And if he did, can his larger system be saved? (Moked 1986; Wilson 1994; Downing 1995). In Siris, Berkeley discusses the nature of plants in some detail and attributes a variety of microstructures and active virtues to them. How can he attribute active agency to the ethers and spirits he supposes to be at work within plants and maintain his earlier denial of active agency to body? More important for our theme, is he not resorting here to retroduction, inferring hypothetically from observed regularities to underlying unobserved entities and structures postulated to be causally responsible? But this is precisely the mode of inference that the empiricism of his earlier works had appeared to prohibit. Physics was to confine itself to the observed regularities of nature, "proved by experiments, refined by reason, and rendered universal." (Berkeley 1992, pars. 36, 89) Siris, on the face of it, seems to abandon the Principia as a guide to the forms of inference appropriate to natural science.

7. Reid claims that Newton did not believe that a knowledge of the "real" (i.e. agent) cause of lawlike observed behavior, e.g. the cause of gravity, is attainable. (527) Newton's persistent attempts throughout his later years to assign a cause for gravitational behavior is, however, sufficient evidence that this was not, in fact, the case. (McMullin 1978, chap. 4) Even in the Principia itself Newton took care to point out that he is pursuing only the "mathematical" principles of natural philosophy, leaving the "physical" principles for later inquirers. But he never really expanded on this, and his ruling out of hypothesis as epistemic intermediary encouraged Reid and others who followed him to doubt whether Newton was really serious about a pursuit so clearly hypothetical in nature.

8. Kant scholars are divided on how precisely to spell this out, how far, for example, one can go in identifying the axiomatics of the Principia as a "pure natural science". Or again, to what extent, if any, is the empirical success of Newton's mechanics a factor in Kant's overall argument? I have to leave these and related issues aside. Fortunately, the general point I want to make is not dependent on them.

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