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.