CHAPTER 4

KUHN AND SCIENCE AS PUZZLE SOLVING





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Popper's rhetoric suggests that the path of scientific development would be a rocky one indeed, a series of bold conjectures most of which would immediately be eliminated by severe testing. As Agassi (and many others) have pointed out, Popper calls for "revolution in permanence" but actual, successful science is characterized by long periods of stability. Kuhn's paradigm theory of scientific change responds to this difficulty with Popper's account. What I will do in this chapter is first give an overview of Kuhn's theory and the common reactions to it. Then I will look in detail at what Kuhn tells us about the nature of scientific problem solving.
4.1 Kuhn's Paradigm Theory of Scientific Change
Contemporary American intellectuals are not noted for a consuming interest in philosophy of science, but Kuhn's The Structure of Scientific Revolutions, first published in 1962, has become an academic best seller. During one semester at my university, it was a required textbook in seven different departments. And the phrase 'Kuhnian paradigm' is heard on the lips of art historians, nursing educators, and theologians as well as scientists and philosophers. Popper claims to have killed logical positivism in 19?? and in a World-3 sense he may be correct, but it was Kuhn who presided over its public burial. A detailed summary of Kuhn's theory of scientific development is given in Figure 4.1. Even a cursory glance quickly reveals how different it is from the positivist account.
Philosophy of science need not be a reflexive activity - the methods and sources of evidence for good philosophizing could well be quite different from what is required for good science. Yet there are often striking parallels between the way a philosopher presents his or her philosophical account and the way they think good science should be pursued. For example, Popper stresses the importance of problem solving in science (as opposed to system building) and, sure enough, Popper does philosophy by working on discrete philosophical problems and does not go out of his way to provide a grand synthetic account.
Kuhn believes that fundamental shifts in science occur more as a result of learning to see phenomena from a whole new perspective instead of through detailed, point-by-point argumentation and likewise when he does philosophy he invites readers to share his philosophical conceptual scheme rather than pounding away at other philosophical views. Thus, in a famous confrontation with Popper in 1965, he begins by commenting on Popper's metaphors rather than by trying to analyze, sharpen, and argue about their points of disagreement.
Kuhn's mode of philosophizing makes it very difficult for critics to pin down exactly what his position is. In a later section we will review some of the major issues his work has raised, such as the problems of incommensurability and the rationality of normal science. But let me begin in a Kuhnian fashion by presenting a brief case study from the history of science in such a way that it may serve as an exemplar of Kuhnian scientific development, namely the Copernican Revolution. In doing so, I do not mean to imply that an interpretation of this episode from the perspective of Kuhn's philosophy is the correct or the best way to view it. Neither do I claim that Kuhn's own historical work on the Copernican Revolution is intended to buttress his later philosophical theory. He is much too good a historian to write history using any philosophical formula - even his own.



a. The Pre-paradigm Stage
According to Kuhn, science proper begins when there is agreement about basic explanatory principles, priorities for future research, and the general approach and methodology which should be followed -in short, when scientists share a paradigm.
Fields in a pre-paradigm stage, on the other hand, are characterized by fundamental and wide-spread disagreement between factions, which leads to constant debate and bickering. Thus in pre-Ptolemaic astronomy we find any number of rival cosmologies including a????'s cylindrical model of the universe in which there is a natural tendency for everything to fall down, Aristarchus' heliocentric model, the Pythagorean conception of a counter-earth, and Eudoxus' model of nested spheres centered on the earth. Each model had certain phenomena of which it gave a more or less plausible qualitative account, but it was not obvious how to develop these models in order to make them more precise or to cover new phenomena. Astronomy was unlike many pre-paradigm disciplines in that it had extensive data, dating back to the Babylonians, which was held in common to all and which could be extrapolated to construct almanacs, but there was no shared theoretical framework. All of this changed, however, thanks to the efforts of Claudius Ptolemy, who flourished around 140 A.D.

b. Normal Science
Kuhn's concept of paradigm is as rich (and vague!) as the related notions of ideology and Zeitgeist. However, the "Postscript" added to the 2nd edition of SSR suggests that it is useful to distinguish between a 'disciplinary matrix', i.e. the "constellation of beliefs, values, techniques, and so on shared by the members of a given community" (p. 175) and 'exemplars', those concrete achievements which not only persuade scientists of the value of the general paradigm, but also serve an important role in science education and as a guide to solving new puzzles. In the case of Ptolemaic astronomy, the most striking achievement was its solution to the problem of retrograde motion. Long before Ptolemy many elements of what would become the Ptolemaic paradigm were already at hand within Aristotle's cosmology and physics.
According to Aristotle, the universe is finite and is divided into two different regions: sub-lunar (or terrestrial) and celestial. Below the moon everything is composed of four elements - earth, air, fire, and water. Each element has associated with it a natural propensity for motion. Fire and air have levity and tend to go up (away from the center of the earth). Earth and water are heavy and tend to go down. Thus the upward motion of smoke (composed largely of the element air) and the downward motion of a cannon ball (largely earth) are natural motions requiring no further explanation. Cannon balls fall faster than cork balls because they are heavier (they have a larger percentage of the element earth in them). All objects move faster as they get closer to their natural place. Thus smoke goes faster and faster as it flees away from the earth and cannon balls go faster as they near the center of the earth.
In addition to these natural motions, there are also so-called "violent" motions. All horizontal motions, such as the flight of an arrow, are violent. Vertical motions are also violent if they are in an unnatural direction (e.g., when we throw a ball straight up). Whereas natural motions happen spontaneously, violent motions have to be forced to occur. They always require a source of motive power, such as the hand and arm of the person throwing the ball or the "animal soul" of a wiggling worm. The speed of violent motions increases with the strength of the motive force and decreases with resistance. For example, a sledge will go faster if it is pulled by two horses instead of one and slower if it is pulled through mud instead of on beaten ground.
According to Aristotle, things in the celestial domain behaved quite differently. Heavenly bodies were made out of a fifth element (called the "quintessence") and in this sphere there was no generation or corruption or change of any kind. The natural motion for bodies made of the fifth element was circular. The planets, stars, sun and moon were embedded in transparent crystalline spheres all of which were internested like a graduated series of embroidery hoops. The outermost sphere (called the primum mobile) provided the dominant 24 hour circular motion shared by all bodies in the celestial system, although each planet, etc., also had its own proper motion, too.
A popular analogical model which was used for pedagogical purposes in the Middle Ages was the following: Imagine a round solid wheel rotating on its axis. Suppose that there are also circular grooves on the wheel populated by marching ants. Here the wheel corresponds to the primum mobile which carries the stars around every 24 hours and the ants correspond to the sun, moon and planets. An ant's total motion is compounded of two parts - the basic motion of the wheel (shared by all ants) and its own proper motion as it walks along the wheel.
But although this simple concentric sphere model of the universe gave a rough, general description of the observed motions of the sun, moon and stars, it failed completed to give any account whatsoever of the retrograde motion of the planets - the fact that at certain regular intervals each planet appears to be almost standing still and then moves backwards across the sky making a little loop before taking up again its normal smooth path. Retrograde motion had been known since antiquity (the Greek work for planet originally meant "wandered") and Plato had articulated the problem of "saving the phenomena" of planetary motion, namely to model the observed trajectory of planets using only uniform circular motions.
Ptolemy's exemplary achievement was to solve this problem, using the geometrical device of epicycles. Intuitively, the general idea is rather as if we were to locate the little ants mentioned above on a Tilt-a-whirl! The basic motion of a planet moving on an epicycle can be diagrammed as follows:


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By a judicious adjustment of the sizes and velocities of the big circle (called the deferent) and the little circle (the epicycle) one could hope to reproduce both the velocity and duration of the retrograde motion. Note that on this model, the planet is closer to the earth when it is in retrograde motion and hence we should expect it to appear biggest and brightest at this time. This effect is in fact observed, and is especially dramatic in the case of Mars.
Ptolemy gave detailed theories of the motions of the sun, moon and planets, using the devices of epicycles and eccentrics in a monumental book which we call the Almagest, after its title in Arabic translation which means "the greatest." It thus provides another important component in a Kuhnian disciplinary matrix, namely, a textbook which contains problems worked out in detail ("How One is to Calculate...when...the Sun Comes to the Zenith"), descriptions of scientific instruments (such as the astrolabe), and clear statements of general theoretical principles ("...it is first necessary to assume in general that the motions of the planets in the direction contrary to the movement of the heavens are all regular and circular by nature...", p. 86).
The Almagest thus provides a framework for what Kuhn calls "normal science." It closes debate on foundational problems (in the very first chapter Ptolemy argues that all would "be thrown into utter confusion if the earth were not in the middle", p. 10) the exemplary achievements of the Ptolemaic approach build confidence that at last we're on the right track it leaves lots of detailed work to be done, but also furnishes the mathematical and experimental tools to carry out the research. In short, a "normal scientist" working in a strong paradigm is in an excellent position to impress funding agencies!
Ptolemaic astronomy is not typical of Kuhnian normal science in two respects: First of all, the political upheavals of what used to be called "The Dark Ages" interrupted and attenuated the teacher-student and colleague networks which usually play an important role in science. Therefore, not much Ptolemaic normal science was actually done until the late Middle Ages, by which time Ptolemy's constants were in obvious need of readjustment. Secondly, the dramatic improvements in observational techniques which should have been inspired by Ptolemy's books (Ptolemy had some very sophisticated things to say about the construction of instruments and experimental error) were not actually forthcoming until after Copernicus' work. On this latter point, however, Kuhn might remark that a paradigm in its wider sense of disciplinary matrix would also include methodological attitudes and ideas about the relative importance of more observations versus improved mathematical modelling, as well as more metaphysical goals such as whether the aim of science is merely to save appearances or whether we should also try to describe the reality which underlies appearances.

c. Science in Crisis
According to Kuhn, the routine puzzle-solving activity which is conducted by scientists who would never think of questioning the merits of the paradigm in which they are working (and much of this allegiance is unreflective because they've never really considered pursuing their discipline in any other way) eventually reveals the basic empirical deficiencies of the theoretical approach. What Kuhn calls "anomalies" keep on accumulating and eventually "normal" scientists in desperation start introducing conceptual devices or observational techniques which are more and more "abnormal" from the perspective of the old paradigm. At the same time people begin making explicit some of their most basic philosophical presuppositions and subjecting them to critical scrutiny.
So if the Ptolemaic paradigm were in a state of Kuhnian crisis we would expect to find astronomers vainly adding more and more epicycles in an attempt to match astronomical observations, and even abandoning the principles of uniform circular motion by introducing linear oscillations along an equant. And we might expect a growing skepticism about the reality of all those crystal spheres - how could the sphere of the epicycle mesh mechanically with the sphere of the deferent - accompanied by a reluctance to "cop out" by saying the science of astronomy was just a mathematical theory of appearances, not a physical description of how the heavens go. Once again there is not a complete match between Kuhn's general philosophical model and the detailed history of Ptolemaic astronomy, particularly with respect to the timing of the criticisms (for example, Ptolemy himself introduced the equant!), but our primary purpose here is to illustrate Kuhn's model, not to test it against history.

d. Switch to a New Paradigm
Science in crisis, like pre-paradigm science, is not very productive. In a state of cognitive anomie, no one knows what to do, or even if individuals think they know what direction inquiry should take, there is no consensus which will guarantee that their efforts will be recognized or appreciated by the scientific community. If science is not to stagnate, Kuhn believes that it is essential that a new paradigm emerge, a new way of viewing the world that promises to be more coherent and more productive than the old. When the new paradigm is successful, there will be new textbooks, which incorporate new exemplary achievements, new methods, new instruments, and new metaphysical conceptions of the world. Kuhn also believes that the switch-over in both individuals and the community is accomplished fairly rapidly. Because the diverse aspects of a paradigm form a coherent whole and are so mutually reinforcing, they cannot easily be either discarded or adopted in a piecemeal fashion. Hence, Kuhn's controversial comparison of scientific revolutions to religious conversions and perceptual Gestalt switches.
It is true that after the Copernican Revolution astronomers adopted a heliocentric cosmology planetary orbits became elliptical not circular, terrestrial and celestial phenomena were assumed to obey the same physical and chemical laws, the new telescopic instruments such as the telescope were used to collect information about new phenomena, such as sunspots, the mountains on our moon, the orbits of comets, the satellites of Jupiter, and the phases of Venus. And typical research projects of Ptolemaic astronomy, such as finding better values for the constants which defined epicyclic motion, were considered to have no value whatsoever.
Nevertheless, there is a marked discrepancy between the actual history of astronomy and the Kuhnian account, for the world view which we associate with the post-Copernican epoch was assembled in a piecemeal fashion and each step was debated in a more or less rational fashion. There follows a very brief sketch of some of the important intermediate steps on the way to a new paradigm (apologies to historians for this over-simplified account).
Let us begin with Copernicus' contributions. In De revolutionibus orbium caelestium, published just after his death in 1543, Copernicus put forward a detailed heliocentric system of the universe. Like Ptolemy's system it was constructed out of circles (Kepler introduced elliptical orbits in 1609-1619). It was superior to Ptolemy's account in two major respects. First, it gave more accurate predictions as to exactly where the heavenly bodies would be seen at any given time. This improved accuracy was not due to any intrinsic superiority of the Copernican system, but arose simply because he had used more up-to-date observations in fixing the various orbital parameters. The second advantage of the new system was the fact that it was supposedly simpler. Although Copernicus used at least as many circles as Ptolemy did (hence the parametric simplicity of the new system was hardly greater), his theory did have one impressive feature: It was not necessary to introduce epicycles to explain the existence of retrograde motion. The qualitative aspects of the retrograde motions of both the superior and inferior planets were a natural result of the basic geometry of the situation. Since the earth was moving around the sun with all the other planets, it was relatively easy to see that sometimes they might appear to be moving backwards - for example, when the earth passed the outer planets which were moving more slowly.
There were some other technical qualitative advantages to Copernicus' system which appealed to astronomers. However, it presented real problems for the physicists. In his introductory chapter, Copernicus tried to suggest a modification of the Aristotelian doctrine of natural motions. But his system required that the earth have two "natural" motions. One, the yearly revolution around the sun, wasn't so bad - at least the other planets also moved this way. But the daily rotation around its axis caused all sorts of problems. None of the other heavenly bodies were observed to spin. And if the earth was whirling around like a great top, why didn't things fly off like mud from the rim of a spinning wheel? Why weren't there terrible winds?
Copernicus hinted at a couple of possible answers, but he didn't work out the details. Neither did he offer any arguments for either of them: "Perhaps the contiguous air contains an admixture of earthy or watery matter and so follows the same natural law as the Earth, or perhaps the air acquires motion from the perpetually rotating Earth by propinquity and absence of resistance..." [De revolutionibus, Section 8]
Even though the Copernican system desperately needed the foundations which only a new physics could provide, it might still have been taken as a serious new cosmological conjecture had it not been for its cautious preface. The story of the publication of De revolutionibus is a very complicated one, full of unknowns and ironies. A few of the facts are these. It is almost certain that Copernicus would never have gotten around to publishing anything had not Rheticus, a young enthusiastic Lutheran astronomer and mathematician, heard about his heliocentric ideas and literally seduced Copernicus into writing them up. Rheticus took the finished manuscript from Copernicus' house in Frauenburg up on the Baltic Sea down to Nuremberg and was intending to see it through publication but had to leave town unexpectedly. (It seems that he got into trouble because of his liking for what the Germans call "the Italian perversion.")
In any case, another Lutheran, this one a theologian called Osiander, took over responsibility for the printing. Although Osiander was sympathetic to the Copernican system, he knew that Luther opposed it and so he added a preface to the reader in which he proposed that the heliocentric system not be construed as a realistic description of the universe but merely as a useful device for making astronomical calculations: "For these hypotheses need not be true or even probable...as far as hypotheses are concerned, but no one expect anything certain from astronomy, which cannot furnish it, lest he accept as the truth ideas conceived for another purpose [i.e., as mere calculating aids], and depart from this study a greater fool than when he entered it. Farewell." Osiander's Preface accomplished what he intended it to. Copernicus' system became popular as a basis for making calendars and star charts. But it had little impact on pure science.
A second major step towards the new world view comes over fifty years later with Galileo. In 1609 Galileo heard about the newly invented telescope and designed one which was good enough for astronomical observations. By March, 1610, he had already made a series of discoveries which refuted or at least seriously undermined several features of Aristotle's cosmology. First of all, he "observed" (we will return later to the question of the reliability of Galileo's interpretations of what he saw) that the moon had mountains. This was inconsistent with Aristotle's claim that the heavenly bodies were perfect and suggested that some of them might be made of stuff similar to the earth. Secondly, he "observed" (again there are some problems about interpretation) that Jupiter had four moons (he called them "Medicean stars" in order to gain points with the Venetian Duke). This discovery argued against the claim that Jupiter was carried along by an invisible crystalline sphere. (Tycho Brahe had reached a similar conclusion in 1577 when he observed a comet move freely through several places where spheres were supposed to be.)
The moons revolving around Jupiter also showed conclusively that there was more than one center of motion in the universe. This was important because Copernicus had the moon moving around the earth as the earth in turn moved around the sun. The Jupiter-four moon system showed that such a motion was possible. It did not of course prove that the earth-moon system actually worked in a similar manner. Galileo also determined the composition of the Milky Way. This discovery had no direct relevance to the debate over the Copernican system. However, it did indicate that Aristotle didn't get everything right and also that the Universe was bigger than had been previously suspected.
In 1543 Copernicus had pointed out two important areas in which his system and Ptolemy's made different predictions. One concerned the phases of Venus. On Copernicus' account, if Venus shone by reflected light, it should appear to wax and wane. According to the Ptolemaic system it should always appear crescent shaped. Since Venus always appears round, some Ptolemains concluded that it must generate its own light as do the stars and the sun. In 1610 (but not in time to be reported in The Starry Messenger), Galileo observed that Venus did indeed have phases, the timing and apparent magnitudes of which were just as predicted by the Copernican system.
This discovery provided a decisive refutation of the Ptolemaic system. Unfortunately, the other major new prediction of the Copernican system, stellar parallax, told against it and for a geocentric system. If the earth is in motion, a line between an observer on earth and a fixed star does not quite stay parallel the year around. Therefore, each star should seem to shift its position slightly with respect to the pole of the stellar sphere. However, stellar parallax could not be detected - even with the new telescope. (It was eventually observed in 1838.) Defenders of Copernicus could explain this away by postulating that the stars were much farther away than had been thought, but this seemed like a rather ad hoc move since there was no reason to believe it except that it would save the Copernican theory from refutation.
The observations of the sunspots around 1612 by Galileo and others showed that Aristotle was wrong in claiming that the heavenly bodies were immutable. It was not clear exactly what or where the sunspots were, but they surely came and went in a most imperfect fashion! Less spectacular perhaps than Galileo's more or less qualitative, telescopic findings, but even more directly relevant to the adoption of the new world view were Tycho's careful quantitative observations. First, his measurement of the angles of parallax on the comet of 1577 which demonstrated conclusively that its orbit was beyond the moon. Not only was there change in the supra-lunar region, there was also a celestial object whose path was far from circular and whose trajectory intersected the deferents (and hence the crystal spheres) of planets. Brahe also collected the body of accurate data on the orbits of Mars and other planets which in a sense guided Kepler to his elliptical orbits.
An absolutely crucial series of steps in the formation of what we today tend to think of as the Copernican system were taken by Johannes Kepler, again at the turn of the 17th century. He first improved on the details of Copernicus' mathematical theories but eventually decided that no system of compounded circles could account for Brahe's data, and in 1609 in his Astronomia Nova he presented his theory of elliptical orbits. And in his 1619 Harmonice Mundi, his third law which showed the mathematical harmonies among the periods and distances from the sun for all the planets gave another compelling argument for the uniqueness of the heliocentric aspect of Copernicus' approach while further underscoring the importance of switching from circular to elliptical orbits.
Yet without a new physics the Copernican-Keplerian paradigm was not complete. In 1632 Galileo published his Dialogo sopra i due Massimi Sistemi del Mondo; Tolemaico, e Copernico. His strategy had two parts. First, he wished to show that it was possible that the earth moved. To do so he had to answer all the physical arguments against Copernicus, e.g., that birds would get left behind, etc. Essentially what was required was a new physics of inertial motion. Secondly, he wanted to show that the earth actually moved. His major argument here was his theory of the tides (which, as we will see, many historians of science find embarrassingly mistaken).
Before looking at these arguments in detail, the significance of the title must be pointed out. Galileo speaks of two world systems, but in so doing he omits a third possibility, the very one which was most popular in the early 17th century. Tycho Brahe, a very good Danish astronomer, who invented many new instruments and had by far the most accurate astronomical data available at that time, had proposed a third alternative which seemed to many to be the ideal compromise. It was geocentric - so there were no problems about birds getting blown away and furthermore it explained the absence of stellar parallax. But all the planets revolved around the sun - so, unlike the Ptolemaic system, it made the right predictions about the phases of Venus. Galileo, unlike his contemporaries, never took Tycho's system seriously. For one thing, he considered it to be very inelegant - it seems rather clumsy to have all the planets carried around the earth by the sun. But more importantly, he recognized that if his theory of the tides was correct, it would refute all geostatic systems, Ptolemaic, Tychonic, or what have you. It all hinged on his theory of the tides.
Galileo's Dialogo is a masterpiece of both polemics and popular scientific writing. There are three protagonists: Simplicio is a very likable but fundamentally stupid Aristotelian. Salviati is the slick expert who often refers in reverential tones to a learned Academician (obviously Galileo). The moderator is Sagredo, a kind of Dick Cavett character - personable, alert and determined to keep both sides honest. (Unfortunately, Sagredo does not know about the Tychonic system.) Almost all of the discussion is non-technical. Galileo's quantitative theory of motion came later in the Discorsi.
From the beginning Galileo attacks a naive reliance on observation and common sense reasoning. He points out that as we walk along the street at night the moon appears to run along behind us like a cat on the rooftops. Likewise as a ship floats along the canal, the shore sometimes appears to be moving instead. A tower in the distance appears to be a continuous translucent streak. But all of these appearances are deceiving. The observations suitable for science have to be based on correct theories and good instruments. For example, observations of size (such as in the case of the tower) have to be corrected by the laws of perspective. Many observations with the naked-eye can be improved by using the telescope. And observations of relative motion alone can never tell us which object is actually at rest.
Galileo also extols the use of what are sometimes misleadingly called "thought experiments." For example, in criticizing the Aristotelian claim that heavier bodies fall faster, he not only reports on experiments done by dropping balls from towers, but also argues as follows: Suppose Aristotle were right. Now imagine two identical cannon balls with strings attached falling side by side. Now suppose the strings become knotted. We now have a composite body which weighs twice as much as the separate parts. It follows on Aristotle's account that they should immediately start falling faster. But that is absurd. Therefore, Aristotle is wrong.
Because Galileo criticized naive observation and relied on thought experiments, some historical commentators have concluded that he was not an empiricist. However, this may only show that he was a sophisticated empiricist. It hinges in part on what is meant by "absurd" in the above argument. Do we conclude that the cannon balls would not speed up when tied together because of some a priori metaphysical principle such as "no effect without a cause"? Or is it because we have lots of experience which indicates that a change in velocity requires some force to be applied?
Galileo argues in a variety of ways that the birds would not get left behind if the earth were moving. He points out that flies in the cabin of a ship share the ship's motion and do not have to fly all the way from Venice to Constantinople. Likewise, if a ball is dropped from the mast of a moving ship it lands at the foot of the mast, not behind it.
In the fourth and final section of the book Galileo switches from merely arguing that it is possible that the Copernican system is true and tries to prove that it is true. Here the claims that the ebbing and flowing of the tides is caused by a combination of the daily rotation and yearly revolution of the earth. Roughly, the theory goes like this: Consider a given point on the earth's surface. During the night the two motions add up so that water accelerates. During the day the daily and yearly motions partly cancel out, so the water slows down.
This theory, which Santillana calls "Galileo's folly" and Koestler labels as an idee fix, is unsatisfactory for two reasons. First of all it violates Galileo's own ideas about motion. Relative to the earth, the water does not speed up or get left behind. It travels along with the earth just as the air does. Galileo's theory of the tides is inconsistent with his own physics. Secondly, it predicts that there should be a high tide once a day. However, tides are generally observed to occur about every twelve hours. Galileo explained this discrepancy away by vague talk about the major tide bounding back and forth in the sea bed. It was not a good concluding section for an otherwise brilliant book.
In the Dialogue Galileo was able to answer many of the objections to the idea that the earth moved - for example, he argued that birds might "share" the motion of the earth just as a fly in the cabin shared the motion of the moving ship. But his systematic theory of motion only came after his condemnation and house imprisonment. His manuscript, Discourse on Two New Sciences, was smuggled out to Holland and published at Leyden in 1638. In it he made an important beginning contribution to our modern theory of mechanics. He gave the correct law for falling bodies - namely, that the acceleration is constant (assuming no air resistance of course). And he gave a correct mathematical description of both projectile motion and bodies moving down inclined planes. To do so, he analyzed these motions into two components, vertical and horizontal. (Compare Aristotle's distinction between natural and violent motions.) The vertical motion was due to the acceleration experienced by any falling body. The horizontal motion was not caused by anything. Unlike Aristotle who believed that a steady input was necessary to keep an object moving horizontally, Galileo realized that in the absence of friction, a moving body would continue to move indefinitely. Although Galileo may have had a concept of inertia somewhat similar to the one we learn in physics class today, he certainly did not state it as a law. (Descartes was the first to do so.) Neither did he have a concept of gravitational attraction. (That was one of Newton's contributions.)
Let us interrupt the story here. I hope that even this brief excursion into history reveals the following: In this case, at least, the adoption of a new paradigm takes place in a protracted piecemeal fashion and each step of the process seems to occur after considerable debate which certainly include (although they are not limited to) rational appeals to the relationship between theory and experiment. This case also illustrates the practical problem of individuating a paradigm. Is Kepler's introduction of ellipses so revolutionary that we should speak of a Keplerian paradigm which replaces the Copernican one? And how much physics should be included within an astronomical paradigm? Kepler and Galileo felt their two fields were mutually relevant, yet the concrete puzzle-solving techniques which are used to compute the trajectory of a cannon ball and the orbit of Mars are quite different, so were Galileo and Kepler working in two different paradigms although they were both Copernicans? Clearly, there are many puzzles to be solved if we seriously try to apply Kuhn's stage theory to the actual development of science.
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4.2 Reactions to Kuhn
Although Kuhn explicitly says that a philosophical theory of science should be elucidated by applying it to the history of science (S.S.R., p. 9) and although his writings are chock full of short allusions to historical episodes, there have been few explicit attempts either to write history of science from a Kuhnian perspective or to systematically test Kuhn's theory against detailed historical case studies. Nevertheless, there have emerged several general reservations about the adequacy of Kuhn/s model as an accurate description of either the past or present workings of science.
The most common criticism is that Kuhn exaggerates both the breadth and depth of consensus within science. For example, David Hull has argued that there were no theoretical principles that leading Darwinians agreed on (Hull, ). When one looks closely at any period of what one might expect to be normal, monoparadigmatic science, there always seems to emerge an amazing diversity of views and on a variety of levels: some phlogistonists believed in three earths, others in four; some post-Lavoisier chemists thought muriatic acid contained oxygen, others didn't; there were repeated debates about atomism from the middle of the 19th century until the energetics movement with Ostwald and Mach; there is a continuing history of debated amongst scientists over the interpretation of quantum mechanics; on a more mundane level quantum chemists have disagreed about the relative advantages of the "valance bond" versus "molecular orbital" computational approaches. And in the Postscript to the 2nd edition of his book, Kuhn admits that the size of the scientific community which share a paradigm may be fewer than twenty-five people and that the various restructurings of group commitments which takes place may not seem at all revolutionary to folks outside the small research group (p 181). Of course, once the existence of micro-paradigms and mini-revolutions is granted, the distinctions between pre-paradigm science, normal science, and crisis science become somewhat blurred and Kuhn's model seems less attractive as a framework for characterizing distinct developmental stages in various disciplines.
By far the most critical commentary on Kuhn's theory, however, has dealt not with its descriptive adequacy, but with the normative issues which it raises. In short, the question is not whether most scientific communities do in fact
operate according to Kuhn's model, but whether they should. This normative critique asks whether on Kuhn's account there is any objective sense in which a later paradigm is better than an earlier account. On his account does science really progress or does it just change? And if it does progress, are the mechanisms by which paradigm shifts occur rational ones? Can one give cogent arguments for the way scientists operate with paradigms or is their scientific behavior the result of blind social dynamics? I cannot begin to summarize in detail this multi-faceted debate here - in fact much of recent philosophy of science can be thought of as reactions to Kuhn - but we will look briefly at the key issues.

a. Scientific Progress
Outside the circle of Anglo-American philosophers of science, the claim that science has obviously progressed is viewed as tendentious or at best naive. For, the argument would go, it is not at all obvious that the negative effects of twentieth century science, such as the threat of nuclear weapons and the various chemicals which endanger our environment are outweighed by the positive contributions science has made in controlling disease and relieving drudgery. From this perspective the claim that there has been scientific progress is quite problematic and the idea that we want to encourage the growth of science conjures up pictures of an ever expanding army of white-coated Dr. Frankensteins in quest of the "technically sweet."
However, when philosophers wonder if, on Kuhn's account, science progresses, what they have in mind is cognitive progress and here the assumption is that science clearly makes a dramatic kind of cognitive progress which any respectable philosophical account should describe. Even if we limit our appraisal to the cognitive aspects of science, it could still be disputed whether later cognitive schema are clearly superior, especially if we consider lost technical skills, such as making Stradavarius violins and the rapidly disappearing expertise of various native peoples. However, all that is assumed here is that there is overall progress. It is not assumed that every single step is progressive nor that there are never cognitive losses.
I have deliberately left the phrase 'cognitive progress' quite vague, for each philosophy of science analyzes it somewhat differently. Let us review a couple of definitions of progress and then see why there are concerns about whether Kuhn's account attributes progress to science. In almost all contexts, progress has the connotation of moving towards a desirable goal or in a favorable direction. So if science makes cognitive progress, later scientific systems should be cognitively superior to earlier ones, but philosophers differ about the dimension(s) along which improvement is made.
According to the positivists, science, if properly conducted, would yield more and more true, justified beliefs. The scientific process would produce a more or less continuous accumulation of information about the world which hopefully could be codified in a more and more unified structure. In short, the layer cake should expand in both the horizontal and vertical dimensions.
For the early Popper, the attribution of progress to science was a little more problematic. If the history of science is viewed simply as a string of falsified conjectures with only the very latest one as yet unrefuted, it is difficult to see how we have progressed, at least on the theoretical level. Of course, our stock of 'basic' statements will have expanded, so there are an increasing number of constraints on any new conjectures - so in a sense our problems are getting progressively more difficult. The need to have a notion of progress was one of Popper's main motivations for the introduction his theory of verisimilitude. If we look at the Aristotelian, Galilean, and Newtonian account of falling bodies from a post-Einsteinian perspective, we see that all are strictly speaking false, yet intuitively there is clearly an increase in verisimilitude because Newton's account (which takes account of the varying strength of the gravitational field) is a better approximation than Galileo's than Aristotle's (which is only semi-quantitative). Philosophers have discovered technical problems in making the notion of verisimilitude more precise and in measuring it (see Boones), but Popper's informal notion certainly captures a lot of what we have in mind when we talk about scientific progress - scientists seem to be trying to weed out the false parts of our conceptual scheme while increasing the number of true components.
When we turn to Kuhn's theory of the development of science it is easy to see how one could describe the periods of normal science as progressive. Scientists are successful in extending the primary theories of the paradigm to cover new phenomena, more accurate instruments are designed, and some of the puzzles set by the paradigm are solved. Normal science seems to generate theoretical, empirical and technological progress. But it is less clear whether we would be justified in claiming there is progress during scientific revolutions. It would seem from his informal commentary that Kuhn himself believes that the switch to the Newtonian paradigm, say, was a progressive one, but on his philosophical account of the nature of revolutions it is difficult to see exactly how the paradigms could be compared because they are, as Kuhn says, incommensurable. We will discuss exactly what he might mean by this in the next section. But the general problem is this: To speak of progress implies that there are one or more scales or dimensions on which we can rank order items. But in the case of paradigm change it's difficult to think what candidates for the scale might be. Progress can't be an increase of observation statements because these will be quite different in successive paradigms. Even when the words remain invariant, as in "The sun rises in the East", there will typically be a dramatic change of meaning, for example, in the way "rise" is interpreted or in the important properties ascribed to the sun.
It is not even possible to speak unambiguously about improvements in measuring instruments as we move from one paradigm to another. Strictly speaking, on Kuhn's account the barometer was developed to measure the "force of the vacuum", not atmospheric pressure, and the original calorimeter measured the amount of the element caloric which was released, not a quantity related to the average motion of molecules. So even when a bit of pre-revolutionary apparatus remains in the post-revolutionary laboratory, Kuhn would say that it is used to measure different things! Of course, some devices may get thrown out completely, such as craniometers and leeches. Others, such as Rohrschach tests and alchemical retorts, fall out of favor and are relegated to the attic, not because there is a new, better device which serves exactly the same function, but because in the light of the new paradigm the task is no longer considered to be important.
Kuhn says that scientists prefer the new paradigm because they believe it has more problem-solving power than the old one which was known to be besieged with anomalies. But he also emphasizes that, strictly speaking, new paradigms never solve the problems set by their predecessors because the problems themselves, as well as the proffered solutions, are paradigm dependent. Textbooks may say that the problem of projectile motion was always an anomaly for Aristotelians whereas Galileo solved it. But if we look carefully, Galileo didn't actually solve Aristotle's problem - he reformulated it. For Aristotle, the major puzzle was how a projectile could keep moving without a mover once it was launched. In Galileo's inertial theory, this problem is obviated.
Kuhn also emphasizes the explanatory losses which accompany paradigm shifts. For example, the Aristotelian paradigm tried to give a unified account of the growth of plants, the motions of falling bodies, and the goal-directed activities of human beings. Later paradigms repudiated teleological explanations, but it could be argued that there is nevertheless a kind of loss; as the current interest in the so-called Anthropic Principle illustrates, people still find such modes of explanation very attractive. Loss on a less grand scale is illustrated by Kuhn's example of the switch from phlogiston theory to oxygen theory which involved a loss of attempts to relate the color changes which occurred during chemical reactions to a change in the state of phlogistication.
My conclusion so far is this: If Kuhn's account of scientific revolutions were correct, then it seems very difficult to specify any objective sense in which the new paradigm is better than the old one. (Of course, scientists feel it is better or they wouldn't switch.) Thus if one judges later paradigms, such as Keplerian astronomy, to constitute genuine progress over earlier ones, such as Ptolemaic astronomy, then one must reject Kuhn's detailed account of the nature of paradigms and/or scientific revolutions. In the next section we will report some of the aspects of Kuhn's account which philosophers think are wrong and which prevent him from accounting for objective progress in science.


b. Incommensurability
Kuhn's most famous and controversial claim is that the process of paradigm change is like a Gestalt switch or religious conversion. Although dissatisfactions with the old paradigm may accumulate over a long period of time and one may articulate them in a fairly rational manner, the change itself occurs rapidly, irreversibly, and arationally. One cannot be argued into switching paradigms any more than one can be argued into seeing the rabbit as a duck. Of course, once the transition has occurred, scientists in the new paradigm loudly proclaim its 'objective' virtues and denounce their former colleagues as irrational old fogies.
Kuhn's account of paradigm transition fits in very well with his characterization of normal science. Because the different aspects of a good paradigm are so well-integrated (instruments and observations are interpreted via the paradigm's theory and regulated by its methodology; the preferred methodology depends on ontology, which in turns interacts with theory), it becomes almost impossible to make piecemeal evaluations of the paradigm -it stands or falls as a whole. Critical analysis is made even more difficult by the fact that much of the cognitive content of the paradigm is tacit. For example, the problem-solving and interpretive skills which scientists have learned by working with exemplary cannot be articulated. The positivist Neurath wrote of how difficult it is to rebuild a ship while at sea. On Kuhn's account the planks of the ship are so invisible and so welded together that it is impossible to repair it - one simply jumps on to some quite different boat.
Probably all of us have experienced something like the clash between incommensurable systems which Kuhn describes - cases where rational argument seems ineffective and the only ways which seem open to a resolution of the conflict is to either banish our bloody-minded opponents or else try to convert them through threats, bribes, or rhetorical persuasion. (The examples which spring to my mind include not only big international ideological conflicts but also academic debates over the merits of Women's Studies Programs, inter-disciplinary discussions on any topic, and conversations between teenagers and their parents about music, clothes and etiquette!) So let us grant for the moment that phenomena reminiscent of Kuhnian incommensurability are widespread. But does this sort of conflict play a major role in scientific revolutions? I will proceed by looking at various aspects of the incommensurability claim. How exactly is it that communications between holders of two rival scientific paradigms is supposed to be impeded?
First, let us dispose of one rather crude mistake which I will call pseudo-conceptual incommensurability. It is sometimes claimed that Aristotle had no concept of inertia or of motion in a vacuum, while Newtonians did, the implication being that since the systems employ different concepts they cannot be compared. It is true that Aristotle didn't believe that there could be motion without a mover nor motion except in a plenum because he said so! So in some crude ordinary language sense he didn't "have" the modern concepts, but since he explicitly brought up these possibilities only to refute them, he could have understood immediately what the moderns were claiming about these topics, although he might not have immediately grasped why they were making these claims. Conversely, the moderns knew full well that they were directly contradicting Aristotle on these points - they were not just inviting Aristotelians to forget about ducks and change to rabbits. There is a big difference between lacking the linguistic capabilities to discuss an idea and failing to believe that the world instantiates the idea.
Having described this basic mistake as a crude one, let me now admit there can be confusing cases! First of all, although Aristotle had a single word for void (since the atomists had discussed it), there was at his time no simple expression for inertia. So although Aristotle explicitly denied the possibility of what we call inertial motion, it is true that he would have had to learn a new term in order to discuss this idea using Newtonians terminology. In this case it seems obvious that Aristotle had the linguistic resources to easily do so. However, whenever one is dealing with non-formalized natural languages we could imagine cases arising where it is unclear exactly what the capacity of the pre-revolutionary language is. And there could in principle be cases where a new concept, though technically expressible in the old language, could only become psychological accessible through prolonged training. (Imagine trying to plunge into a late chapter in the Principia Mathematica equipped only with the axioms and a string of definitions.)
Let us now turn to a case of genuine conceptual incommensurability, a situation in which it is impossible to define a concept from one scientific theory (S) using the terminology of a second scientific theory (T). To illustrate, consider a mathematical example. According to Euclidean geometry it is logically impossible to have a triangle whose angles don't add up to 180_. Hence, it is not possible even to ask from within Euclidean geometry about the properties of Riemannian triangles. Unlike the Aristotle examples above, the claim is not that Riemannian triangles don't exist; rather the situation is that they are unspeakable! A scientific example arose in connection with the word element. If by element we mean the last product of analysis, then strictly speaking someone who claims to have separated the element hydrogen into deuterium and light hydrogen is uttering contradictions. And after the discovery of isotopes, chemists struggled over how to re-define the concept of chemical element.
So there indeed appear to be cases of genuine conceptual incommensurability, cases where concepts within competing theories S and T are not intertranslatable. Does this mean, however, that it is impossible for scientists to make a reasoned comparison between S and T? Not at all. Let us see why.
Thanks to the logical positivists when philosophers speak of the language of a science, say the language of Newtonian mechanics, we tend to think primarily of the language used to express axioms of the core theory plus perhaps descriptions of measuring instruments. However, there is no way Newtonian scientists can develop Newtonian science without a rich philosophical meta-language. Scientists (not just philosophers) need to talk about whether Newton's first law is a tautology, to clarify what is meant by action at a distance, to discuss the status of the infinitesimals used in Newton's formulation of the calculus, the domains in which the law of universal gravitation has been tested, etc. The same sort of meta-language needed for the conduct of normal science can also be used for the comparison of two theories which are not intertranslatable. In the meta-language one can then discuss which geometry is most useful for surveying or which theory of elements better represents chemical phenomena. So conceptual incommensurability does not preclude the rational comparison of theories. Of course, this debate conducted within the meta-language can only take place in a sensible fashion if both parties understand both of the conceptually incommensurable theories, and there could be cases where this task of dual comprehension is psychologically difficult.
But what if the holders of the two rival paradigms hold different cognitive values? If their standards and methods of appraising scientific systems do not agree, then we are indeed left with a conflict which is irresolvable at this level a situation we might call value incommensurability. We will discuss the extent to which scientists really have deep disagreements about what constitutes good science later in our discussion of Laudan. But suffice it so say for now that there seems to be much less dispute about the desiderata for a good scientific theory than there is about what constitutes good art, good literature, good history, or good theology. More often, I think, scientists are disagreeing about their guesses as to which direction of research is more likely to produce the kind of theory which all agree would be desirable. In our chapter on Lakatos, we will look in more detail at the problem of giving an objective appraisal of the heuristic power of a research program.
So far we have looked at various sources of scientific incommensurability and concluded that at least until we get to questions of values, they need not lead to a breakdown of rational debate. (Laudan argues that even value conflicts can be resolved.) But we have also admitted that it may not be easy to get clear about exactly what the rival theories are saying and what the relative strengths and weaknesses of their claims are. Let us now look at some of the sources of what we might call psychological incommensurability. If the task of rational theory comparison, though logically possible, turned out to be too psychologically demanding, then we would have to concede Kuhn some aspects of his account of non-rational paradigm change.
Kuhn places a lot of emphasis on the tacit (inarticulated) content of a paradigm, stressing the role of concrete exemplars which serve both as an embodiment of theory and as a heuristic guide for the application of rather abstract theoretical claims to new situations. If crucial aspects of a theoretical approach cannot be written down but reside only in the "know-how" of a practitioner, then paradigm comparison becomes rather like trying on shoes or choosing a violin - one may talk a lot about width of the last or sweetness of sound (and indeed there are clear cases of bad fitting shoes and inferior violins) - but in the last resort it seems to be a matter of what "feels" right. The subtle, yet crucial differences are indescribable. Furthermore, once we get accustomed to our Birkenstocks or Stradivarius, it becomes increasingly difficult to even imagine that anything could be better and so we have a tremendous psychological resistance even to trying on any alternative.
Current work in cognitive science is now giving us some insight into how Kuhn's concrete exemplars might work. For example, according to prototype theory, the structure of a concept, say bird, contains not only universal characteristics, such as is an animal, but also prototypical instances, such as robin. From the prototypes we extract default rules, such as "if it's a bird, [assume] it eats bugs and flies [unless you have explicit information to the contrary]." Thus we can imagine a situation where two parties agree on the defining characteristics of birds and on all the universal generalizations regarding birds, but yet have very different bird prototypes and hence different default rules. (If my prototypical bird is a penguin, my hunches, identification errors, the analogies to birds which I generate, etc. will be quite different from the person whose Ur-bird is a flamingo!)
Now with effort, we can probably learn to articulate these prototypes (my guess is that good real estate agents have the knack of figuring out what each client's prototypical house is like). But unless we do so, we are apt to end up in strange-sounding conversations about whether an Irish Wolfhound is "really" a dog, or the earth "really" a planet. What is being disputed in such cases is not what technically falls under the concept of dog or planet, but the choice of prototypes. Undoubtedly similar conflicts occur in science. For Galileo, prototypical free fall took place in a vacuum; for Aristotle bodies typically fell through a medium. For Plato, the prototypical motion of a celestial body was a circle; for Newton, it was a conic section with some other mass at the focus. For Mendel, the prototypical inheritance pattern let to assortment; others posited blending.
Disagreements over prototypes are difficult to articulate and very hard to arbitrate, partly because we need not be committed to saying that our prototype is in fact statistically most common! But by the same token, if all the dispute amounts to is a disagreement about prototypes, then little hinges on it. Even Kuhn admits that the tacit components of a paradigm tend to be made more explicit during times of crisis. And of course that is just when we need to have them articulated for purposes of rational choice between paradigms.
4.3 Kuhn and Puzzles
When Kuhn writes history of science, he structures it around grand explanatory problems in Popper's sense. The Copernican Revolution carefully describes the problem of the planets and then presents the old and new solutions to it. His book on black-body radiation begins with the black-body problem and analyzes the development of two solutions to it, one classical and one involving quanta. Furthermore, Kuhn is explicit about the problems which motivate his own work as an historian. The Preface of Black-Body Theory and The Quantum Discontinuity begins: "This book is the outcome of a project I had not intended to undertake" (p. vii). He goes on to describe his search for the origins of quantum conditions in Planck and how he arrived at the "extraordinary result" that Planck's first quantum papers "did not posit or imply the quantum discontinuity" (p. viii). This discovery led to the problem of how then discontinuity had entered physics. (p. ix). His philosophical writings, especially the essays in The Essential Tension, also deal with interesting problems: What is the role of thought experiments within science? What is the proper relationship of the disciplines of history of science and philosophy of science? And most important to his entire philosophical enterprise: How are the elements of tradition and innovation combined within mature scientific research?
It is only in his answer to the latter question, i.e., in his theory of the importance of "normal" science that Kuhn stops talking about genuine problems, in Popper's sense, and begins to speak instead of puzzles. (Kuhn's account of science education stresses the role of "problems" in textbooks, but he obviously views these textbook exercises as puzzles.)
Neither ordinary language nor philosophical usage make clear and consistent demarcations between question, problem, and puzzle. For example, by problem we might well mean either a puzzling question, a difficulty in achieving a goal, or a cognitive task to be carried out (cf. the Problemata in Greek mathematics). Eventually, we shall propose some standard terminology, but for now we will have to work with each author's way of using these words. When Kuhn speaks of puzzle-solving within normal science, he means "that special category of problems that can serve to test ingenuity or skill in solution" (SR, p. 36). He stresses that whereas "intrinsic value is no criterion for a puzzle, the assumed existence of a solution is." (p. 37) Already we see two major differences between Popperian problems and Kuhnian puzzles: For Popper, scientific problems are (or should be) of either practical or cognitive importance and there is no guarantee that a solution to any of them exists or that we will be able to find it. As Kuhn himself says, "... the really pressing problems, e.g., a cure for cancer or the design of a lasting peace, are often not puzzles at all, largely because they may not have any solution." (SR, pp. 36-37).
What then are these puzzles which are characteristic of Kuhnian normal science? Kuhn groups them into three classes: "determination of significant facts, matching of facts with theory, and articulation of theory" (SR, p. 34). I will discuss these in turn, using in some cases my own examples. (My account depends in part on a paper by Giunti.)
First, let us recall that these puzzles all arise within an agreed upon paradigm, or what Kuhn later called a "disciplinary matrix". Thus scientists already have a fairly clear idea both about the kind of phenomena they hope to explain or codify (e.g., planetary positions, or the melting points of solids) and the kinds of properties which are supposed to account for or be correlated with the above (e.g., gravitational attractions, or atomic weights). One obvious job for the experimental scientist is to determine the values of more and more instances of these "significant facts," and to measure them more and more accurately. Thus T. A. Richards won a Nobel prize for his exten-sive, accurate measurements of atomic weights. This activity is different from wholesale so-called "Baconian" fact-collecting, because the paradigm assigns importance to only certain facts. As the paradigm changes, so do the assignments of significance. In the 19th Century, atomic weights were thought to be fundamental properties of atoms. We now know that the atomic weights of naturally occurring elements which Richards was measuring are in fact weighted averages of the various long lived isotopes found on the earth's surface. Atomic number (the charge on the nucleus) is now recognized as the fundamental property of chemical elements.
The second type of activity, matching facts with theory, can involve both experimenters and theoreticians. There is always a gap between our somewhat idealized theoretical descriptions and the messy complexity of real-life situations. (For example, Galileo's law of free fall neglects air resistance.) How then can we hope to check the truth of our theories against the world? (See my Galileo paper.) There are two obvious strategies -- one is to complicate the theory, the other is to simplify a part of the world. So in the case of free-fall, we can either try to compute the effects of the medium (cf., Stokes' Law) or we can invent a vacuum pump (or fly to the moon) and see how well the law applies when there is no air. I have chosen a very simple example. Clearly the tasks of developing both theory and experiment in such a way that it is fruitful to compare them is a very difficult task. However, as Kuhn emphasizes, the paradigm assures us that it can be done.
Under his category of theory articulation, Kuhn seems mainly to have in mind the work of conceptually clarifying theories or reformulating them, especially with the aid of new mathematical techniques (such as perhaps LaGrange's introduction of _________ into Newtonian mechanics). I am tempted to add here the activity of drawing out dramatic unexpected consequences from the formalism (such as Dirac's prediction of the positron), but I hesitate to do so because of Kuhn's insistence that people working within normal science do not anticipate any major surprises, so perhaps Dirac's problem was what Kuhn would call an "extraordinary" one. It all depends on how revoluntionary one considers the idea of a positron to be!
Although Kuhn repeatedly emphasizes that the puzzles of normal science are seen as a test of the skill and ingenuity of the scientist, not as a test of the truth of the theory, he also reiterates that the unintended consequence of this tradition-bound activity is the discovery of novelty and the revolution of our most fundamental beliefs about the world:
"[The normal science] mode of problem selection, however, though it makes short-term successes particularly likely, also guarantees long-run failures that prove even more consequential to scientific advance." (ET, p. 262).
"There are also extraordinary problems, and it may well be their resolution that makes the scientific enterprise as a whole so particularly worthwhile. But extraordinary problems are not to be had for the asking," (SR, p. 34).
"...revolutionary shifts of a scientific tradition are relatively rare, and extended periods of convergent research are the necessary preliminary to them. ...Almost none of the research undertaken by even the greatest scientists is designed to be revolutionary..." (ET, p. 227).
There might be a temptation to consider Popper's theory of scientific problems and Kuhn's account of normal science puzzles as complementary. After all, Popper, in his discussion of what I have called the Duhemian problem, stresses the role of auxiliary hypotheses and theories of instrumentation. He fully realizes that it may take time and effort before a theory can actually be subjected to a test decisive enough to be a possible refutation. And Kuhn, as we have just seen, admits that our big leaps of understanding are the result of the confronting of extraordinary problems and the subsequent discovery of a revolutionary solution to them.
But neither party would accept such a synthesis. In "Against `Normal Science'" and "Normal Science and its Dangers," Watkins and Popper argue that the sort of paradigm-bound, uncritical puzzle-solving activity described by Kuhn either does not occur frequently, or to the extent to which it does occur, scientific progress is thereby jeopardized. Kuhn, himself no longer a normal scientist but a historian and philosopher who traffics in open-ended problems, argues that the most distinctive and important aspect of the successful sciences is their far-ranging consensus on ontology, theories, experimental techniques, experimental and methodology. In a conference on the Identification of Scientific Talent, Kuhn reacted against the popular stereotype of the scientist as a mentally flexible innovator as follows: "We are, I think, more likely fully to exploit our potential scientific talent if we recognize the extent to which the basic scientist must also be a firm traditionalist, or, if I am using your vocabulary at all correctly, a convergent thinker." (ET, p. 237). Some readers of Kuhn seem to think that one can enable a science to progress by actively trying to impose a consensus. (See, for example, Von Eckhart's .) Kuhn's own view seems to be that paradigms must themselves earn the consensus through some exemplary achievements, not just through heuristic promise. However, it is true that once a disciplinary matrix is in place, the practice of professional science education efficiently indoctrinates future practitioners into the prevailing paradigm. (At one point Kuhn says only theological training is as doctrinaire as science education.) By solving lots of textbook problems (especially "story" problems) and replicating simple experiments that "work" in the classroom laboratory, the student not only learns the achievements of the paradigm but also gets practice in applying it to concrete situations. Thus the paradigm becomes part of the student's tacit knowledge. And since the science student is given no familiarity with older theories or contemporary alternatives, any other way of looking at the world becomes unthinkable.
Small wonder that Kuhn argues that many scientific revolutions are instigated by "outsiders," people who were never thoroughly indoctrinated into the old paradigm. One might then expect Kuhn to advocate a liberalization of science education. After all, if most progress comes through revolutions, and if scientists with non-normal training are best at dreaming up new paradigms.... But Kuhn does not draw this conclusion, perhaps because he thinks revolutions can only occur during periods of crisis. And crises can only arise after a long period of articulation and consolidation of the old view. (It's more efficient to pick one raspberry bush clean before moving on, instead of flitting around from bush to bush looking for the biggest, juiciest berries!)
While the science student is learning how to trim, color and stretch the world until it fits into the boxes provided by the one and only paradigm, s/he is simultaneously being taught that science is a heroic, fair-minded, open search for the truth and given a naive version of scientific method. In a provocative article entitled, "Should the History of Science Be X-Rated?" Stephen Brush suggests that the absence of history and philosophy of science from the science curriculum is no accident and may in fact be a good thing as far as the progress of science is concerned. Popper, on the other hand, calls for "revolution in permanence," advocating that scientists declare in advance what would make them give up their theories, and then sincerely try to refute them through severe testing. In his "Science in Flux" Agassi calls for less indoctrination in science education and
more emphasis on free wheeling problem solving. Only then will science make better progress.
In order to arbitrate between these extreme views, it might be helpful to distinguish between proximate and ultimate problems or sub-tasks and goals. As sociologists of science remind us,
on the most mundane level, the working scientist is obviously preoccupied with problems such as finding leaks in the vacuum line, solving a second-order differential equation, getting grants, or hiring research assistants. Likewise, we could point out an artist's concern with high quality pigments and quick-drying lacquers. On the other hand, on the most exalted and abstract level we could say the scientists were looking for Truth and the artist for Beauty. But there is an intermediate level -- one which gives an analysis of the project at hand which doesn't bog us down in a minute-by-minute account of daily activities but which does provide us with a raison d'etre for them.
As far as science education is concerned, one is immediately struck by the fact that although Kuhn refers to various times and places, his description rings most true for fairly recent educational practice in America. Although physics is the most "mature" science and the one that should have the most monolithic paradigm and the most rigid educational system, nevertheless European physicists, perhaps due to their gymnasium training, have displayed lots of interest in philosophy and metaphysics, not just as an avocation, but when they are discussing theoretical physics.
Perhaps Kuhn would say that these great 20th Century physicists are all really extraordinary revolutionaries working at the theoretical fringe -- that he's talking about the vast hoard of "civil servants". Maybe so, but yet Kuhn also admits that applied scientists and inventors also need to engage in rule-breaking behavior. He points out that "Edison's electric light was produced in the face of unanimous scientific opinion that the arc light could not be `subdivided'" ET, p. 228. Kuhn even speculates that the applied scientist "may profit by a far broader and less rigid education than that to which the pure scientist has characteristically been exposed." (ET, p. 238). So even on Kuhn's account, practitioners of pre-paradigm science, revolutionary scientists, and applied scientists all need to be able to challenge orthodoxy. Puzzle-solving is by no means the whole story.
Let us now turn to Kuhn's account of the problems characteristic of non-normal science. Most important perhaps are the problems posed by anomalies. Anomaly is a technical term in Kuhn's philosophy of science referring to "discrepancies between theory and experiment" (ET, p. 202). Kuhn emphasizes that most anomalies a scientist encounters are ignored and rightly so, but in certain circumstances they will not be dismissed:
"If the effect is particularly large when compared with well-established measures of "reasonable agreement" applicable to similar problems, or if it seems to resemble other difficulties encountered repeatedly before, or if, for personal reasons it intrigues the experimenter, then a special research project is likely to be dedicated to it." (E.T., pp. 202-203.)
If an anomaly resists repeated attempts to solve it, it may signal the beginning of a crisis and may even lead to a revolution. But even if a wholesale revision is not required, generally the discovery of something unexpected will be the result. As Kuhn puts it, serious anomalies "tell scientists when and where to look for a new qualitative phenomenon." (p. 205) Among Kuhn's examples of anomalies which turned out to be important are Mercury's motion (p. 191), the discrepancy in gas densities which led to the discovery of argon (p. 205), Kepler's 8" of arc (p. 209), and the energy-momentum gap which led to the discovery of the neutrino (p. 205). So it is through a non-paradigm bound form of inquiry that the most exciting scientific discoveries are made. Since on Kuhn's own account of science there is an "essential tension" between dogmatism and iconoclasm, we might conclude, though Kuhn does not, that students need to be trained in and taught about both aspects of scientific activity.

Chapter IV: Bibliography
Giunti,. .

Koertge, Noretta. .

Kuhn, Thomas S. (1978). Black-Body Theory and the Quantum Discontinuity, 1884-1912. Oxford: Oxford University Press.

Kuhn, Thomas S. (1957). The Copnerican Revolution. Cambridge: Harvard University Press.

Kuhn, Thomas S. (1977). The Essential Tension. Chicago: The University of Chicago Press.

Kuhn, Thomas S. (1962). The Structure of Scientific Revolutions. Chicago: The University of Chicago Press.

Lakatos, Imre and Alan Musgrave. (1970). Criticism and the Growth of Knowledge. London: Cambridge University Press.

Von Eckhardt. .

4.4 The Objective Aspects of Kuhnian Puzzles
The popularity of Kuhn's book demonstrates the extent to which it rings true to many people's experience with and conception of science. Our job as philosophers is to extract what is right about Kuhn's account and formulate it in more precise terms. One major strategy for improving Kuhn's account is to try to de-psychologize it. Instead of just taking his claims at face value we should ask to what extent is his account of science grounded in scientific psychology and to what extent is he using terms like gestalt switch in a metaphorical sense. (See O'Donohue.)
When Dewey spoke of puzzles he was definitely referring to the psychological state of perplexity, of mental bewilderment of the problem solver. But when Kuhn describes puzzles as testing the ingenuity of the experimenter not the truth of the paradigm or of the paradigm giving scientists confidence that certain problems can be solved. I think that it is helpful to sort out the objective vs. subjective aspects of his claims and evaluate them separately.
If I were to translate (or transform) Kuhn into an objective mode, I would extract the following insights:
1) The problems scientists work on frequently have a lot of internal structure and there are typically lots of constraints on the set of acceptable candidate solutions. (Later we will see how Nickles develops this point.) The complex structure of scientific problems is best learned by internalizing commonly used sub-routines and production rules, but all of this material can be subjected to critical scrutiny if the situation makes it appropriate to do so.
2) When scientists select research problems it is rational for them to consider not just the cognitive benefits which would accrue were the problem to be solved, but also the probability that it can be solved. Kuhnian puzzles are problems which we either have good reasons to believe can be solved or which have a structure which makes them accessible to investigation using familiar techniques. We might even go so far as to say that Kuhnian puzzles are just those problems which do not instill in us the kinds of feelings of doubt or puzzlement which Dewey took as so important! Perhaps this is why scientists so often appear cocky, over-confident -- they are working on problems whose objective structure is indicative of their susceptibility to solution!
What now needs to be done is to spell out in more detail the objective structure of problems, and the objective features of heuristic methods for solving them. Lakatos' methodology of scientific research programmes, which we will discuss in the next chapter, is a beginning effort in this direction.
Almagest thus provides a framework for what Kuhn calls "normal science." It closes debate on foundational problems (in the very first chapter Ptolemy argues that all would "be thrown into utter confusion if the earth were not in the middle", p. 10) the exemplary achievements of the Ptolemaic approach build confidence that at last we're on the right track it leaves lots of detailed work to be done, but also furnishes the mathematical and experimental tools to carry out the research. In short, a "normal scientist" working in a strong paradigm is in an excellent position to impress funding agencies!
Ptolemaic astronomy is not typical of Kuhnian normal science in two respects: First of all, the political upheavals of what used to be called "The Dark Ages" interrupted and attenuated the teacher-student and colleague networks which usually play an important role in science. Therefore, not much Ptolemaic normal science was actually done until the late Middle Ages, by which time Ptolemy's constants were in obvious need of readjustment. Secondly, the dramatic improvements in observational techniques which should have been inspired by Ptolemy's books (Ptolemy had some very sophisticated things to say about the construction of instruments and experimental error) were not actually forthcoming until after Copernicus' work. On this latter point, however, Kuhn might remark that a paradigm in its wider sense of disciplinary matrix would also include methodological attitudes and ideas about the relative importance of more observations versus improved mathematical modelling, as well as more metaphysical goals such as whether the aim of science is merely to save appearances or whether we should also try to describe the reality which underlies appearances.

c. Science in Crisis
According to Kuhn, the routine puzzle-solving activity which is conducted by scientists who would never think of questioning the merits of the paradigm in which they are working (and much of this allegiance is unreflective because they've never really considered pursuing their discipline in any other way) eventually reveals the basic empirical deficiencies of the theoretical approach. What Kuhn calls "anomalies" keep on accumulating and eventually "normal" scientists in desperation start introducing conceptual devices or observational techniques which are more and more "abnormal" from the perspective of the old paradigm. At the same time people begin making explicit some of their most basic philosophical presuppositions and subjecting them to critical scrutiny.
So if the Ptolemaic paradigm were in a state of Kuhnian crisis we would expect to find astronomers vainly adding more and more epicycles in an attempt to match astronomical observations, and even abandoning the principles of uniform circular motion by introducing linear oscillations along an equant. And we might expect a growing skepticism about the reality of all those crystal spheres - how could the sphere of the epicycle mesh mechanically with the sphere of the deferent - accompanied by a reluctance to "cop out" by saying the science of astronomy was just a mathematical theory of appearances, not a physical description of how the heavens go. Once again there is not a complete match between Kuhn's general philosophical model and the detailed history of Ptolemaic astronomy, particularly with respect to the timing of the criticisms (for example, Ptolemy himself introduced the equant!), but our primary purpose here is to illustrate Kuhn's model, not to test it against history.

d. Switch to a New Paradigm
Science in crisis, like pre-paradigm science, is not very productive. In a state of cognitive anomie, no one knows what to do, or even if individuals think they know what direction inquiry should take, there is no consensus which will guarantee that their efforts will be recognized or appreciated by the scientific community. If science is not to stagnate, Kuhn believes that it is essential that a new paradigm emerge, a new way of viewing the world that promises to be more coherent and more productive than the old. When the new paradigm is successful, there will be new textbooks, which incorporate new exemplary achievements, new methods, new instruments, and new metaphysical conceptions of the world. Kuhn also believes that the switch-over in both individuals and the community is accomplished fairly rapidly. Because the diverse aspects of a paradigm form a coherent whole and are so mutually reinforcing, they cannot easily be either discarded or adopted in a piecemeal fashion. Hence, Kuhn's controversial comparison of scientific revolutions to religious conversions and perceptual Gestalt switches.
It is true that after the Copernican Revolution astronomers adopted a heliocentric cosmology planetary orbits became elliptical not circular, terrestrial and celestial phenomena were assumed to obey the same physical and chemical laws, the new telescopic instruments such as the telescope were used to collect information about new phenomena, such as sunspots, the mountains on our moon, the orbits of comets, the satellites of Jupiter, and the phases of Venus. And typical research projects of Ptolemaic astronomy, such as finding better values for the constants which defined epicyclic motion, were considered to have no value whatsoever.
Nevertheless, there is a marked discrepancy between the actual history of astronomy and the Kuhnian account, for the world view which we associate with the post-Copernican epoch was assembled in a piecemeal fashion and each step was debated in a more or less rational fashion. There follows a very brief sketch of some of the important intermediate steps on the way to a new paradigm (apologies to historians for this over-simplified account).
Let us begin with Copernicus' contributions. In De revolutionibus orbium caelestium, published just after his death in 1543, Copernicus put forward a detailed heliocentric system of the universe. Like Ptolemy's system it was constructed out of circles (Kepler introduced elliptical orbits in 1609-1619). It was superior to Ptolemy's account in two major respects. First, it gave more accurate predictions as to exactly where the heavenly bodies would be seen at any given time. This improved accuracy was not due to any intrinsic superiority of the Copernican system, but arose simply because he had used more up-to-date observations in fixing the various orbital parameters. The second advantage of the new system was the fact that it was supposedly simpler. Although Copernicus used at least as many circles as Ptolemy did (hence the parametric simplicity of the new system was hardly greater), his theory did have one impressive feature: It was not necessary to introduce epicycles to explain the existence of retrograde motion. The qualitative aspects of the retrograde motions of both the superior and inferior planets were a natural result of the basic geometry of the situation. Since the earth was moving around the sun with all the other planets, it was relatively easy to see that sometimes they might appear to be moving backwards - for example, when the earth passed the outer planets which were moving more slowly.
There were some other technical qualitative advantages to Copernicus' system which appealed to astronomers. However, it presented real problems for the physicists. In his introductory chapter, Copernicus tried to suggest a modification of the Aristotelian doctrine of natural motions. But his system required that the earth have two "natural" motions. One, the yearly revolution around the sun, wasn't so bad - at least the other planets also moved this way. But the daily rotation around its axis caused all sorts of problems. None of the other heavenly bodies were observed to spin. And if the earth was whirling around like a great top, why didn't things fly off like mud from the rim of a spinning wheel? Why weren't there terrible winds?
Copernicus hinted at a couple of possible answers, but he didn't work out the details. Neither did he offer any arguments for either of them: "Perhaps the contiguous air contains an admixture of earthy or watery matter and so follows the same natural law as the Earth, or perhaps the air acquires motion from the perpetually rotating Earth by propinquity and absence of resistance..." [De revolutionibus, Section 8]
Even though the Copernican system desperately needed the foundations which only a new physics could provide, it might still have been taken as a serious new cosmological conjecture had it not been for its cautious preface. The story of the publication of De revolutionibus is a very complicated one, full of unknowns and ironies. A few of the facts are these. It is almost certain that Copernicus would never have gotten around to publishing anything had not Rheticus, a young enthusiastic Lutheran astronomer and mathematician, heard about his heliocentric ideas and literally seduced Copernicus into writing them up. Rheticus took the finished manuscript from Copernicus' house in Frauenburg up on the Baltic Sea down to Nuremberg and was intending to see it through publication but had to leave town unexpectedly. (It seems that he got into trouble because of his liking for what the Germans call "the Italian perversion.")
In any case, another Lutheran, this one a theologian called Osiander, took over responsibility for the printing. Although Osiander was sympathetic to the Copernican system, he knew that Luther opposed it and so he added a preface to the reader in which he proposed that the heliocentric system not be construed as a realistic description of the universe but merely as a useful device for making astronomical calculations: "For these hypotheses need not be true or even probable...as far as hypotheses are concerned, but no one expect anything certain from astronomy, which cannot furnish it, lest he accept as the truth ideas conceived for another purpose [i.e., as mere calculating aids], and depart from this study a greater fool than when he entered it. Farewell." Osiander's Preface accomplished what he intended it to. Copernicus' system became popular as a basis for making calendars and star charts. But it had little impact on pure science.
A second major step towards the new world view comes over fifty years later with Galileo. In 1609 Galileo heard about the newly invented telescope and designed one which was good enough for astronomical observations. By March, 1610, he had already made a series of discoveries which refuted or at least seriously undermined several features of Aristotle's cosmology. First of all, he "observed" (we will return later to the question of the reliability of Galileo's interpretations of what he saw) that the moon had mountains. This was inconsistent with Aristotle's claim that the heavenly bodies were perfect and suggested that some of them might be made of stuff similar to the earth. Secondly, he "observed" (again there are some problems about interpretation) that Jupiter had four moons (he called them "Medicean stars" in order to gain points with the Venetian Duke). This discovery argued against the claim that Jupiter was carried along by an invisible crystalline sphere. (Tycho Brahe had reached a similar conclusion in 1577 when he observed a comet move freely through several places where spheres were supposed to be.)
The moons revolving around Jupiter also showed conclusively that there was more than one center of motion in the universe. This was important because Copernicus had the moon moving around the earth as the earth in turn moved around the sun. The Jupiter-four moon system showed that such a motion was possible. It did not of course prove that the earth-moon system actually worked in a similar manner. Galileo also determined the composition of the Milky Way. This discovery had no direct relevance to the debate over the Copernican system. However, it did indicate that Aristotle didn't get everything right and also that the Universe was bigger than had been previously suspected.
In 1543 Copernicus had pointed out two important areas in which his system and Ptolemy's made different predictions. One concerned the phases of Venus. On Copernicus' account, if Venus shone by reflected light, it should appear to wax and wane. According to the Ptolemaic system it should always appear crescent shaped. Since Venus always appears round, some Ptolemains concluded that it must generate its own light as do the stars and the sun. In 1610 (but not in time to be reported in The Starry Messenger), Galileo observed that Venus did indeed have phases, the timing and apparent magnitudes of which were just as predicted by the Copernican system.
This discovery provided a decisive refutation of the Ptolemaic system. Unfortunately, the other major new prediction of the Copernican system, stellar parallax, told against it and for a geocentric system. If the earth is in motion, a line between an observer on earth and a fixed star does not quite stay parallel the year around. Therefore, each star should seem to shift its position slightly with respect to the pole of the stellar sphere. However, stellar parallax could not be detected - even with the new telescope. (It was eventually observed in 1838.) Defenders of Copernicus could explain this away by postulating that the stars were much farther away than had been thought, but this seemed like a rather ad hoc move since there was no reason to believe it except that it would save the Copernican theory from refutation.
The observations of the sunspots around 1612 by Galileo and others showed that Aristotle was wrong in claiming that the heavenly bodies were immutable. It was not clear exactly what or where the sunspots were, but they surely came and went in a most imperfect fashion! Less spectacular perhaps than Galileo's more or less qualitative, telescopic findings, but even more directly relevant to the adoption of the new world view were Tycho's careful quantitative observations. First, his measurement of the angles of parallax on the comet of 1577 which demonstrated conclusively that its orbit was beyond the moon. Not only was there change in the supra-lunar region, there was also a celestial object whose path was far from circular and whose trajectory intersected the deferents (and hence the crystal spheres) of planets. Brahe also collected the body of accurate data on the orbits of Mars and other planets which in a sense guided Kepler to his elliptical orbits.
An absolutely crucial series of steps in the formation of what we today tend to think of as the Copernican system were taken by Johannes Kepler, again at the turn of the 17th century. He first improved on the details of Copernicus' mathematical theories but eventually decided that no system of compounded circles could account for Brahe's data, and in 1609 in his Astronomia Nova he presented his theory of elliptical orbits. And in his 1619 Harmonice Mundi, his third law which showed the mathematical harmonies among the periods and distances from the sun for all the planets gave another compelling argument for the uniqueness of the heliocentric aspect of Copernicus' approach while further underscoring the importance of switching from circular to elliptical orbits.
Yet without a new physics the Copernican-Keplerian paradigm was not complete. In 1632 Galileo published his Dialogo sopra i due Massimi Sistemi del Mondo; Tolemaico, e Copernico. His strategy had two parts. First, he wished to show that it was possible that the earth moved. To do so he had to answer all the physical arguments against Copernicus, e.g., that birds would get left behind, etc. Essentially what was required was a new physics of inertial motion. Secondly, he wanted to show that the earth actually moved. His major argument here was his theory of the tides (which, as we will see, many historians of science find embarrassingly mistaken).
Before looking at these arguments in detail, the significance of the title must be pointed out. Galileo speaks of two world systems, but in so doing he omits a third possibility, the very one which was most popular in the early 17th century. Tycho Brahe, a very good Danish astronomer, who invented many new instruments and had by far the most accurate astronomical data available at that time, had proposed a third alternative which seemed to many to be the ideal compromise. It was geocentric - so there were no problems about birds getting blown away and furthermore it explained the absence of stellar parallax. But all the planets revolved around the sun - so, unlike the Ptolemaic system, it made the right predictions about the phases of Venus. Galileo, unlike his contemporaries, never took Tycho's system seriously. For one thing, he considered it to be very inelegant - it seems rather clumsy to have all the planets carried around the earth by the sun. But more importantly, he recognized that if his theory of the tides was correct, it would refute all geostatic systems, Ptolemaic, Tychonic, or what have you. It all hinged on his theory of the tides.
Galileo's Dialogo is a masterpiece of both polemics and popular scientific writing. There are three protagonists: Simplicio is a very likable but fundamentally stupid Aristotelian. Salviati is the slick expert who often refers in reverential tones to a learned Academician (obviously Galileo). The moderator is Sagredo, a kind of Dick Cavett character - personable, alert and determined to keep both sides honest. (Unfortunately, Sagredo does not know about the Tychonic system.) Almost all of the discussion is non-technical. Galileo's quantitative theory of motion came later in the Discorsi.
From the beginning Galileo attacks a naive reliance on observation and common sense reasoning. He points out that as we walk along the street at night the moon appears to run along behind us like a cat on the rooftops. Likewise as a ship floats along the canal, the shore sometimes appears to be moving instead. A tower in the distance appears to be a continuous translucent streak. But all of these appearances are deceiving. The observations suitable for science have to be based on correct theories and good instruments. For example, observations of size (such as in the case of the tower) have to be corrected by the laws of perspective. Many observations with the naked-eye can be improved by using the telescope. And observations of relative motion alone can never tell us which object is actually at rest.
Galileo also extols the use of what are sometimes misleadingly called "thought experiments." For example, in criticizing the Aristotelian claim that heavier bodies fall faster, he not only reports on experiments done by dropping balls from towers, but also argues as follows: Suppose Aristotle were right. Now imagine two identical cannon balls with strings attached falling side by side. Now suppose the strings become knotted. We now have a composite body which weighs twice as much as the separate parts. It follows on Aristotle's account that they should immediately start falling faster. But that is absurd. Therefore, Aristotle is wrong.
Because Galileo criticized naive observation and relied on thought experiments, some historical commentators have concluded that he was not an empiricist. However, this may only show that he was a sophisticated empiricist. It hinges in part on what is meant by "absurd" in the above argument. Do we conclude that the cannon balls would not speed up when tied together because of some a priori metaphysical principle such as "no effect without a cause"? Or is it because we have lots of experience which indicates that a change in velocity requires some force to be applied?
Galileo argues in a variety of ways that the birds would not get left behind if the earth were moving. He points out that flies in the cabin of a ship share the ship's motion and do not have to fly all the way from Venice to Constantinople. Likewise, if a ball is dropped from the mast of a moving ship it lands at the foot of the mast, not behind it.
In the fourth and final section of the book Galileo switches from merely arguing that it is possible that the Copernican system is true and tries to prove that it is true. Here the claims that the ebbing and flowing of the tides is caused by a combination of the daily rotation and yearly revolution of the earth. Roughly, the theory goes like this: Consider a given point on the earth's surface. During the night the two motions add up so that water accelerates. During the day the daily and yearly motions partly cancel out, so the water slows down.
This theory, which Santillana calls "Galileo's folly" and Koestler labels as an idee fix, is unsatisfactory for two reasons. First of all it violates Galileo's own ideas about motion. Relative to the earth, the water does not speed up or get left behind. It travels along with the earth just as the air does. Galileo's theory of the tides is inconsistent with his own physics. Secondly, it predicts that there should be a high tide once a day. However, tides are generally observed to occur about every twelve hours. Galileo explained this discrepancy away by vague talk about the major tide bounding back and forth in the sea bed. It was not a good concluding section for an otherwise brilliant book.
In the Dialogue Galileo was able to answer many of the objections to the idea that the earth moved - for example, he argued that birds might "share" the motion of the earth just as a fly in the cabin shared the motion of the moving ship. But his systematic theory of motion only came after his condemnation and house imprisonment. His manuscript, Discourse on Two New Sciences, was smuggled out to Holland and published at Leyden in 1638. In it he made an important beginning contribution to our modern theory of mechanics. He gave the correct law for falling bodies - namely, that the acceleration is constant (assuming no air resistance of course). And he gave a correct mathematical description of both projectile motion and bodies moving down inclined planes. To do so, he analyzed these motions into two components, vertical and horizontal. (Compare Aristotle's distinction between natural and violent motions.) The vertical motion was due to the acceleration experienced by any falling body. The horizontal motion was not caused by anything. Unlike Aristotle who believed that a steady input was necessary to keep an object moving horizontally, Galileo realized that in the absence of friction, a moving body would continue to move indefinitely. Although Galileo may have had a concept of inertia somewhat similar to the one we learn in physics class today, he certainly did not state it as a law. (Descartes was the first to do so.) Neither did he have a concept of gravitational attraction. (That was one of Newton's contributions.)
Let us interrupt the story here. I hope that even this brief excursion into history reveals the following: In this case, at least, the adoption of a new paradigm takes place in a protracted piecemeal fashion and each step of the process seems to occur after considerable debate which certainly include (although they are not limited to) rational appeals to the relationship between theory and experiment. This case also illustrates the practical problem of individuating a paradigm. Is Kepler's introduction of ellipses so revolutionary that we should speak of a Keplerian paradigm which replaces the Copernican one? And how much physics should be included within an astronomical paradigm? Kepler and Galileo felt their two fields were mutually relevant, yet the concrete puzzle-solving techniques which are used to compute the trajectory of a cannon ball and the orbit of Mars are quite different, so were Galileo and Kepler working in two different paradigms although they were both Copernicans? Clearly, there are many puzzles to be solved if we seriously try to apply Kuhn's stage theory to the actual development of science.
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Insert Fig. 4.3 about here
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4.2 Reactions to Kuhn
Although Kuhn explicitly says that a philosophical theory of science should be elucidated by applying it to the history of science (S.S.R., p. 9) and although his writings are chock full of short allusions to historical episodes, there have been few explicit attempts either to write history of science from a Kuhnian perspective or to systematically test Kuhn's theory against detailed historical case studies. Nevertheless, there have emerged several general reservations about the adequacy of Kuhn/s model as an accurate description of either the past or present workings of science.
The most common criticism is that Kuhn exaggerates both the breadth and depth of consensus within science. For example, David Hull has argued that there were no theoretical principles that leading Darwinians agreed on (Hull, ). When one looks closely at any period of what one might expect to be normal, monoparadigmatic science, there always seems to emerge an amazing diversity of views and on a variety of levels: some phlogistonists believed in three earths, others in four; some post-Lavoisier chemists thought muriatic acid contained oxygen, others didn't; there were repeated debates about atomism from the middle of the 19th century until the energetics movement with Ostwald and Mach; there is a continuing history of debated amongst scientists over the interpretation of quantum mechanics; on a more mundane level quantum chemists have disagreed about the relative advantages of the "valance bond" versus "molecular orbital" computational approaches. And in the Postscript to the 2nd edition of his book, Kuhn admits that the size of the scientific community which share a paradigm may be fewer than twenty-five people and that the various restructurings of group commitments which takes place may not seem at all revolutionary to folks outside the small research group (p 181). Of course, once the existence of micro-paradigms and mini-revolutions is granted, the distinctions between pre-paradigm science, normal science, and crisis science become somewhat blurred and Kuhn's model seems less attractive as a framework for characterizing distinct developmental stages in various disciplines.
By far the most critical commentary on Kuhn's theory, however, has dealt not with its descriptive adequacy, but with the normative issues which it raises. In short, the question is not whether most scientific communities do in fact
operate according to Kuhn's model, but whether they should. This normative critique asks whether on Kuhn's account there is any objective sense in which a later paradigm is better than an earlier account. On his account does science really progress or does it just change? And if it does progress, are the mechanisms by which paradigm shifts occur rational ones? Can one give cogent arguments for the way scientists operate with paradigms or is their scientific behavior the result of blind social dynamics? I cannot begin to summarize in detail this multi-faceted debate here - in fact much of recent philosophy of science can be thought of as reactions to Kuhn - but we will look briefly at the key issues.

a. Scientific Progress
Outside the circle of Anglo-American philosophers of science, the claim that science has obviously progressed is viewed as tendentious or at best naive. For, the argument would go, it is not at all obvious that the negative effects of twentieth century science, such as the threat of nuclear weapons and the various chemicals which endanger our environment are outweighed by the positive contributions science has made in controlling disease and relieving drudgery. From this perspective the claim that there has been scientific progress is quite problematic and the idea that we want to encourage the growth of science conjures up pictures of an ever expanding army of white-coated Dr. Frankensteins in quest of the "technically sweet."
However, when philosophers wonder if, on Kuhn's account, science progresses, what they have in mind is cognitive progress and here the assumption is that science clearly makes a dramatic kind of cognitive progress which any respectable philosophical account should describe. Even if we limit our appraisal to the cognitive aspects of science, it could still be disputed whether later cognitive schema are clearly superior, especially if we consider lost technical skills, such as making Stradavarius violins and the rapidly disappearing expertise of various native peoples. However, all that is assumed here is that there is overall progress. It is not assumed that every single step is progressive nor that there are never cognitive losses.
I have deliberately left the phrase 'cognitive progress' quite vague, for each philosophy of science analyzes it somewhat differently. Let us review a couple of definitions of progress and then see why there are concerns about whether Kuhn's account attributes progress to science. In almost all contexts, progress has the connotation of moving towards a desirable goal or in a favorable direction. So if science makes cognitive progress, later scientific systems should be cognitively superior to earlier ones, but philosophers differ about the dimension(s) along which improvement is made.
According to the positivists, science, if properly conducted, would yield more and more true, justified beliefs. The scientific process would produce a more or less continuous accumulation of information about the world which hopefully could be codified in a more and more unified structure. In short, the layer cake should expand in both the horizontal and vertical dimensions.
For the early Popper, the attribution of progress to science was a little more problematic. If the history of science is viewed simply as a string of falsified conjectures with only the very latest one as yet unrefuted, it is difficult to see how we have progressed, at least on the theoretical level. Of course, our stock of 'basic' statements will have expanded, so there are an increasing number of constraints on any new conjectures - so in a sense our problems are getting progressively more difficult. The need to have a notion of progress was one of Popper's main motivations for the introduction his theory of verisimilitude. If we look at the Aristotelian, Galilean, and Newtonian account of falling bodies from a post-Einsteinian perspective, we see that all are strictly speaking false, yet intuitively there is clearly an increase in verisimilitude because Newton's account (which takes account of the varying strength of the gravitational field) is a better approximation than Galileo's than Aristotle's (which is only semi-quantitative). Philosophers have discovered technical problems in making the notion of verisimilitude more precise and in measuring it (see Boones), but Popper's informal notion certainly captures a lot of what we have in mind when we talk about scientific progress - scientists seem to be trying to weed out the false parts of our conceptual scheme while increasing the number of true components.
When we turn to Kuhn's theory of the development of science it is easy to see how one could describe the periods of normal science as progressive. Scientists are successful in extending the primary theories of the paradigm to cover new phenomena, more accurate instruments are designed, and some of the puzzles set by the paradigm are solved. Normal science seems to generate theoretical, empirical and technological progress. But it is less clear whether we would be justified in claiming there is progress during scientific revolutions. It would seem from his informal commentary that Kuhn himself believes that the switch to the Newtonian paradigm, say, was a progressive one, but on his philosophical account of the nature of revolutions it is difficult to see exactly how the paradigms could be compared because they are, as Kuhn says, incommensurable. We will discuss exactly what he might mean by this in the next section. But the general problem is this: To speak of progress implies that there are one or more scales or dimensions on which we can rank order items. But in the case of paradigm change it's difficult to think what candidates for the scale might be. Progress can't be an increase of observation statements because these will be quite different in successive paradigms. Even when the words remain invariant, as in "The sun rises in the East", there will typically be a dramatic change of meaning, for example, in the way "rise" is interpreted or in the important properties ascribed to the sun.
It is not even possible to speak unambiguously about improvements in measuring instruments as we move from one paradigm to another. Strictly speaking, on Kuhn's account the barometer was developed to measure the "force of the vacuum", not atmospheric pressure, and the original calorimeter measured the amount of the element caloric which was released, not a quantity related to the average motion of molecules. So even when a bit of pre-revolutionary apparatus remains in the post-revolutionary laboratory, Kuhn would say that it is used to measure different things! Of course, some devices may get thrown out completely, such as craniometers and leeches. Others, such as Rohrschach tests and alchemical retorts, fall out of favor and are relegated to the attic, not because there is a new, better device which serves exactly the same function, but because in the light of the new paradigm the task is no longer considered to be important.
Kuhn says that scientists prefer the new paradigm because they believe it has more problem-solving power than the old one which was known to be besieged with anomalies. But he also emphasizes that, strictly speaking, new paradigms never solve the problems set by their predecessors because the problems themselves, as well as the proffered solutions, are paradigm dependent. Textbooks may say that the problem of projectile motion was always an anomaly for Aristotelians whereas Galileo solved it. But if we look carefully, Galileo didn't actually solve Aristotle's problem - he reformulated it. For Aristotle, the major puzzle was how a projectile could keep moving without a mover once it was launched. In Galileo's inertial theory, this problem is obviated.
Kuhn also emphasizes the explanatory losses which accompany paradigm shifts. For example, the Aristotelian paradigm tried to give a unified account of the growth of plants, the motions of falling bodies, and the goal-directed activities of human beings. Later paradigms repudiated teleological explanations, but it could be argued that there is nevertheless a kind of loss; as the current interest in the so-called Anthropic Principle illustrates, people still find such modes of explanation very attractive. Loss on a less grand scale is illustrated by Kuhn's example of the switch from phlogiston theory to oxygen theory which involved a loss of attempts to relate the color changes which occurred during chemical reactions to a change in the state of phlogistication.
My conclusion so far is this: If Kuhn's account of scientific revolutions were correct, then it seems very difficult to specify any objective sense in which the new paradigm is better than the old one. (Of course, scientists feel it is better or they wouldn't switch.) Thus if one judges later paradigms, such as Keplerian astronomy, to constitute genuine progress over earlier ones, such as Ptolemaic astronomy, then one must reject Kuhn's detailed account of the nature of paradigms and/or scientific revolutions. In the next section we will report some of the aspects of Kuhn's account which philosophers think are wrong and which prevent him from accounting for objective progress in science.


b. Incommensurability
Kuhn's most famous and controversial claim is that the process of paradigm change is like a Gestalt switch or religious conversion. Although dissatisfactions with the old paradigm may accumulate over a long period of time and one may articulate them in a fairly rational manner, the change itself occurs rapidly, irreversibly, and arationally. One cannot be argued into switching paradigms any more than one can be argued into seeing the rabbit as a duck. Of course, once the transition has occurred, scientists in the new paradigm loudly proclaim its 'objective' virtues and denounce their former colleagues as irrational old fogies.
Kuhn's account of paradigm transition fits in very well with his characterization of normal science. Because the different aspects of a good paradigm are so well-integrated (instruments and observations are interpreted via the paradigm's theory and regulated by its methodology; the preferred methodology depends on ontology, which in turns interacts with theory), it becomes almost impossible to make piecemeal evaluations of the paradigm -it stands or falls as a whole. Critical analysis is made even more difficult by the fact that much of the cognitive content of the paradigm is tacit. For example, the problem-solving and interpretive skills which scientists have learned by working with exemplary cannot be articulated. The positivist Neurath wrote of how difficult it is to rebuild a ship while at sea. On Kuhn's account the planks of the ship are so invisible and so welded together that it is impossible to repair it - one simply jumps on to some quite different boat.
Probably all of us have experienced something like the clash between incommensurable systems which Kuhn describes - cases where rational argument seems ineffective and the only ways which seem open to a resolution of the conflict is to either banish our bloody-minded opponents or else try to convert them through threats, bribes, or rhetorical persuasion. (The examples which spring to my mind include not only big international ideological conflicts but also academic debates over the merits of Women's Studies Programs, inter-disciplinary discussions on any topic, and conversations between teenagers and their parents about music, clothes and etiquette!) So let us grant for the moment that phenomena reminiscent of Kuhnian incommensurability are widespread. But does this sort of conflict play a major role in scientific revolutions? I will proceed by looking at various aspects of the incommensurability claim. How exactly is it that communications between holders of two rival scientific paradigms is supposed to be impeded?
First, let us dispose of one rather crude mistake which I will call pseudo-conceptual incommensurability. It is sometimes claimed that Aristotle had no concept of inertia or of motion in a vacuum, while Newtonians did, the implication being that since the systems employ different concepts they cannot be compared. It is true that Aristotle didn't believe that there could be motion without a mover nor motion except in a plenum because he said so! So in some crude ordinary language sense he didn't "have" the modern concepts, but since he explicitly brought up these possibilities only to refute them, he could have understood immediately what the moderns were claiming about these topics, although he might not have immediately grasped why they were making these claims. Conversely, the moderns knew full well that they were directly contradicting Aristotle on these points - they were not just inviting Aristotelians to forget about ducks and change to rabbits. There is a big difference between lacking the linguistic capabilities to discuss an idea and failing to believe that the world instantiates the idea.
Having described this basic mistake as a crude one, let me now admit there can be confusing cases! First of all, although Aristotle had a single word for void (since the atomists had discussed it), there was at his time no simple expression for inertia. So although Aristotle explicitly denied the possibility of what we call inertial motion, it is true that he would have had to learn a new term in order to discuss this idea using Newtonians terminology. In this case it seems obvious that Aristotle had the linguistic resources to easily do so. However, whenever one is dealing with non-formalized natural languages we could imagine cases arising where it is unclear exactly what the capacity of the pre-revolutionary language is. And there could in principle be cases where a new concept, though technically expressible in the old language, could only become psychological accessible through prolonged training. (Imagine trying to plunge into a late chapter in the Principia Mathematica equipped only with the axioms and a string of definitions.)
Let us now turn to a case of genuine conceptual incommensurability, a situation in which it is impossible to define a concept from one scientific theory (S) using the terminology of a second scientific theory (T). To illustrate, consider a mathematical example. According to Euclidean geometry it is logically impossible to have a triangle whose angles don't add up to 180_. Hence, it is not possible even to ask from within Euclidean geometry about the properties of Riemannian triangles. Unlike the Aristotle examples above, the claim is not that Riemannian triangles don't exist; rather the situation is that they are unspeakable! A scientific example arose in connection with the word element. If by element we mean the last product of analysis, then strictly speaking someone who claims to have separated the element hydrogen into deuterium and light hydrogen is uttering contradictions. And after the discovery of isotopes, chemists struggled over how to re-define the concept of chemical element.
So there indeed appear to be cases of genuine conceptual incommensurability, cases where concepts within competing theories S and T are not intertranslatable. Does this mean, however, that it is impossible for scientists to make a reasoned comparison between S and T? Not at all. Let us see why.
Thanks to the logical positivists when philosophers speak of the language of a science, say the language of Newtonian mechanics, we tend to think primarily of the language used to express axioms of the core theory plus perhaps descriptions of measuring instruments. However, there is no way Newtonian scientists can develop Newtonian science without a rich philosophical meta-language. Scientists (not just philosophers) need to talk about whether Newton's first law is a tautology, to clarify what is meant by action at a distance, to discuss the status of the infinitesimals used in Newton's formulation of the calculus, the domains in which the law of universal gravitation has been tested, etc. The same sort of meta-language needed for the conduct of normal science can also be used for the comparison of two theories which are not intertranslatable. In the meta-language one can then discuss which geometry is most useful for surveying or which theory of elements better represents chemical phenomena. So conceptual incommensurability does not preclude the rational comparison of theories. Of course, this debate conducted within the meta-language can only take place in a sensible fashion if both parties understand both of the conceptually incommensurable theories, and there could be cases where this task of dual comprehension is psychologically difficult.
But what if the holders of the two rival paradigms hold different cognitive values? If their standards and methods of appraising scientific systems do not agree, then we are indeed left with a conflict which is irresolvable at this level a situation we might call value incommensurability. We will discuss the extent to which scientists really have deep disagreements about what constitutes good science later in our discussion of Laudan. But suffice it so say for now that there seems to be much less dispute about the desiderata for a good scientific theory than there is about what constitutes good art, good literature, good history, or good theology. More often, I think, scientists are disagreeing about their guesses as to which direction of research is more likely to produce the kind of theory which all agree would be desirable. In our chapter on Lakatos, we will look in more detail at the problem of giving an objective appraisal of the heuristic power of a research program.
So far we have looked at various sources of scientific incommensurability and concluded that at least until we get to questions of values, they need not lead to a breakdown of rational debate. (Laudan argues that even value conflicts can be resolved.) But we have also admitted that it may not be easy to get clear about exactly what the rival theories are saying and what the relative strengths and weaknesses of their claims are. Let us now look at some of the sources of what we might call psychological incommensurability. If the task of rational theory comparison, though logically possible, turned out to be too psychologically demanding, then we would have to concede Kuhn some aspects of his account of non-rational paradigm change.
Kuhn places a lot of emphasis on the tacit (inarticulated) content of a paradigm, stressing the role of concrete exemplars which serve both as an embodiment of theory and as a heuristic guide for the application of rather abstract theoretical claims to new situations. If crucial aspects of a theoretical approach cannot be written down but reside only in the "know-how" of a practitioner, then paradigm comparison becomes rather like trying on shoes or choosing a violin - one may talk a lot about width of the last or sweetness of sound (and indeed there are clear cases of bad fitting shoes and inferior violins) - but in the last resort it seems to be a matter of what "feels" right. The subtle, yet crucial differences are indescribable. Furthermore, once we get accustomed to our Birkenstocks or Stradivarius, it becomes increasingly difficult to even imagine that anything could be better and so we have a tremendous psychological resistance even to trying on any alternative.
Current work in cognitive science is now giving us some insight into how Kuhn's concrete exemplars might work. For example, according to prototype theory, the structure of a concept, say bird, contains not only universal characteristics, such as is an animal, but also prototypical instances, such as robin. From the prototypes we extract default rules, such as "if it's a bird, [assume] it eats bugs and flies [unless you have explicit information to the contrary]." Thus we can imagine a situation where two parties agree on the defining characteristics of birds and on all the universal generalizations regarding birds, but yet have very different bird prototypes and hence different default rules. (If my prototypical bird is a penguin, my hunches, identification errors, the analogies to birds which I generate, etc. will be quite different from the person whose Ur-bird is a flamingo!)
Now with effort, we can probably learn to articulate these prototypes (my guess is that good real estate agents have the knack of figuring out what each client's prototypical house is like). But unless we do so, we are apt to end up in strange-sounding conversations about whether an Irish Wolfhound is "really" a dog, or the earth "really" a planet. What is being disputed in such cases is not what technically falls under the concept of dog or planet, but the choice of prototypes. Undoubtedly similar conflicts occur in science. For Galileo, prototypical free fall took place in a vacuum; for Aristotle bodies typically fell through a medium. For Plato, the prototypical motion of a celestial body was a circle; for Newton, it was a conic section with some other mass at the focus. For Mendel, the prototypical inheritance pattern let to assortment; others posited blending.
Disagreements over prototypes are difficult to articulate and very hard to arbitrate, partly because we need not be committed to saying that our prototype is in fact statistically most common! But by the same token, if all the dispute amounts to is a disagreement about prototypes, then little hinges on it. Even Kuhn admits that the tacit components of a paradigm tend to be made more explicit during times of crisis. And of course that is just when we need to have them articulated for purposes of rational choice between paradigms.
4.3 Kuhn and Puzzles
When Kuhn writes history of science, he structures it around grand explanatory problems in Popper's sense. The Copernican Revolution carefully describes the problem of the planets and then presents the old and new solutions to it. His book on black-body radiation begins with the black-body problem and analyzes the development of two solutions to it, one classical and one involving quanta. Furthermore, Kuhn is explicit about the problems which motivate his own work as an historian. The Preface of Black-Body Theory and The Quantum Discontinuity begins: "This book is the outcome of a project I had not intended to undertake" (p. vii). He goes on to describe his search for the origins of quantum conditions in Planck and how he arrived at the "extraordinary result" that Planck's first quantum papers "did not posit or imply the quantum discontinuity" (p. viii). This discovery led to the problem of how then discontinuity had entered physics. (p. ix). His philosophical writings, especially the essays in The Essential Tension, also deal with interesting problems: What is the role of thought experiments within science? What is the proper relationship of the disciplines of history of science and philosophy of science? And most important to his entire philosophical enterprise: How are the elements of tradition and innovation combined within mature scientific research?
It is only in his answer to the latter question, i.e., in his theory of the importance of "normal" science that Kuhn stops talking about genuine problems, in Popper's sense, and begins to speak instead of puzzles. (Kuhn's account of science education stresses the role of "problems" in textbooks, but he obviously views these textbook exercises as puzzles.)
Neither ordinary language nor philosophical usage make clear and consistent demarcations between question, problem, and puzzle. For example, by problem we might well mean either a puzzling question, a difficulty in achieving a goal, or a cognitive task to be carried out (cf. the Problemata in Greek mathematics). Eventually, we shall propose some standard terminology, but for now we will have to work with each author's way of using these words. When Kuhn speaks of puzzle-solving within normal science, he means "that special category of problems that can serve to test ingenuity or skill in solution" (SR, p. 36). He stresses that whereas "intrinsic value is no criterion for a puzzle, the assumed existence of a solution is." (p. 37) Already we see two major differences between Popperian problems and Kuhnian puzzles: For Popper, scientific problems are (or should be) of either practical or cognitive importance and there is no guarantee that a solution to any of them exists or that we will be able to find it. As Kuhn himself says, "... the really pressing problems, e.g., a cure for cancer or the design of a lasting peace, are often not puzzles at all, largely because they may not have any solution." (SR, pp. 36-37).
What then are these puzzles which are characteristic of Kuhnian normal science? Kuhn groups them into three classes: "determination of significant facts, matching of facts with theory, and articulation of theory" (SR, p. 34). I will discuss these in turn, using in some cases my own examples. (My account depends in part on a paper by Giunti.)
First, let us recall that these puzzles all arise within an agreed upon paradigm, or what Kuhn later called a "disciplinary matrix". Thus scientists already have a fairly clear idea both about the kind of phenomena they hope to explain or codify (e.g., planetary positions, or the melting points of solids) and the kinds of properties which are supposed to account for or be correlated with the above (e.g., gravitational attractions, or atomic weights). One obvious job for the experimental scientist is to determine the values of more and more instances of these "significant facts," and to measure them more and more accurately. Thus T. A. Richards won a Nobel prize for his exten-sive, accurate measurements of atomic weights. This activity is different from wholesale so-called "Baconian" fact-collecting, because the paradigm assigns importance to only certain facts. As the paradigm changes, so do the assignments of significance. In the 19th Century, atomic weights were thought to be fundamental properties of atoms. We now know that the atomic weights of naturally occurring elements which Richards was measuring are in fact weighted averages of the various long lived isotopes found on the earth's surface. Atomic number (the charge on the nucleus) is now recognized as the fundamental property of chemical elements.
The second type of activity, matching facts with theory, can involve both experimenters and theoreticians. There is always a gap between our somewhat idealized theoretical descriptions and the messy complexity of real-life situations. (For example, Galileo's law of free fall neglects air resistance.) How then can we hope to check the truth of our theories against the world? (See my Galileo paper.) There are two obvious strategies -- one is to complicate the theory, the other is to simplify a part of the world. So in the case of free-fall, we can either try to compute the effects of the medium (cf., Stokes' Law) or we can invent a vacuum pump (or fly to the moon) and see how well the law applies when there is no air. I have chosen a very simple example. Clearly the tasks of developing both theory and experiment in such a way that it is fruitful to compare them is a very difficult task. However, as Kuhn emphasizes, the paradigm assures us that it can be done.
Under his category of theory articulation, Kuhn seems mainly to have in mind the work of conceptually clarifying theories or reformulating them, especially with the aid of new mathematical techniques (such as perhaps LaGrange's introduction of _________ into Newtonian mechanics). I am tempted to add here the activity of drawing out dramatic unexpected consequences from the formalism (such as Dirac's prediction of the positron), but I hesitate to do so because of Kuhn's insistence that people working within normal science do not anticipate any major surprises, so perhaps Dirac's problem was what Kuhn would call an "extraordinary" one. It all depends on how revoluntionary one considers the idea of a positron to be!
Although Kuhn repeatedly emphasizes that the puzzles of normal science are seen as a test of the skill and ingenuity of the scientist, not as a test of the truth of the theory, he also reiterates that the unintended consequence of this tradition-bound activity is the discovery of novelty and the revolution of our most fundamental beliefs about the world:
"[The normal science] mode of problem selection, however, though it makes short-term successes particularly likely, also guarantees long-run failures that prove even more consequential to scientific advance." (ET, p. 262).
"There are also extraordinary problems, and it may well be their resolution that makes the scientific enterprise as a whole so particularly worthwhile. But extraordinary problems are not to be had for the asking," (SR, p. 34).
"...revolutionary shifts of a scientific tradition are relatively rare, and extended periods of convergent research are the necessary preliminary to them. ...Almost none of the research undertaken by even the greatest scientists is designed to be revolutionary..." (ET, p. 227).
There might be a temptation to consider Popper's theory of scientific problems and Kuhn's account of normal science puzzles as complementary. After all, Popper, in his discussion of what I have called the Duhemian problem, stresses the role of auxiliary hypotheses and theories of instrumentation. He fully realizes that it may take time and effort before a theory can actually be subjected to a test decisive enough to be a possible refutation. And Kuhn, as we have just seen, admits that our big leaps of understanding are the result of the confronting of extraordinary problems and the subsequent discovery of a revolutionary solution to them.
But neither party would accept such a synthesis. In "Against `Normal Science'" and "Normal Science and its Dangers," Watkins and Popper argue that the sort of paradigm-bound, uncritical puzzle-solving activity described by Kuhn either does not occur frequently, or to the extent to which it does occur, scientific progress is thereby jeopardized. Kuhn, himself no longer a normal scientist but a historian and philosopher who traffics in open-ended problems, argues that the most distinctive and important aspect of the successful sciences is their far-ranging consensus on ontology, theories, experimental techniques, experimental and methodology. In a conference on the Identification of Scientific Talent, Kuhn reacted against the popular stereotype of the scientist as a mentally flexible innovator as follows: "We are, I think, more likely fully to exploit our potential scientific talent if we recognize the extent to which the basic scientist must also be a firm traditionalist, or, if I am using your vocabulary at all correctly, a convergent thinker." (ET, p. 237). Some readers of Kuhn seem to think that one can enable a science to progress by actively trying to impose a consensus. (See, for example, Von Eckhart's .) Kuhn's own view seems to be that paradigms must themselves earn the consensus through some exemplary achievements, not just through heuristic promise. However, it is true that once a disciplinary matrix is in place, the practice of professional science education efficiently indoctrinates future practitioners into the prevailing paradigm. (At one point Kuhn says only theological training is as doctrinaire as science education.) By solving lots of textbook problems (especially "story" problems) and replicating simple experiments that "work" in the classroom laboratory, the student not only learns the achievements of the paradigm but also gets practice in applying it to concrete situations. Thus the paradigm becomes part of the student's tacit knowledge. And since the science student is given no familiarity with older theories or contemporary alternatives, any other way of looking at the world becomes unthinkable.
Small wonder that Kuhn argues that many scientific revolutions are instigated by "outsiders," people who were never thoroughly indoctrinated into the old paradigm. One might then expect Kuhn to advocate a liberalization of science education. After all, if most progress comes through revolutions, and if scientists with non-normal training are best at dreaming up new paradigms.... But Kuhn does not draw this conclusion, perhaps because he thinks revolutions can only occur during periods of crisis. And crises can only arise after a long period of articulation and consolidation of the old view. (It's more efficient to pick one raspberry bush clean before moving on, instead of flitting around from bush to bush looking for the biggest, juiciest berries!)
While the science student is learning how to trim, color and stretch the world until it fits into the boxes provided by the one and only paradigm, s/he is simultaneously being taught that science is a heroic, fair-minded, open search for the truth and given a naive version of scientific method. In a provocative article entitled, "Should the History of Science Be X-Rated?" Stephen Brush suggests that the absence of history and philosophy of science from the science curriculum is no accident and may in fact be a good thing as far as the progress of science is concerned. Popper, on the other hand, calls for "revolution in permanence," advocating that scientists declare in advance what would make them give up their theories, and then sincerely try to refute them through severe testing. In his "Science in Flux" Agassi calls for less indoctrination in science education and
more emphasis on free wheeling problem solving. Only then will science make better progress.
In order to arbitrate between these extreme views, it might be helpful to distinguish between proximate and ultimate problems or sub-tasks and goals. As sociologists of science remind us,
on the most mundane level, the working scientist is obviously preoccupied with problems such as finding leaks in the vacuum line, solving a second-order differential equation, getting grants, or hiring research assistants. Likewise, we could point out an artist's concern with high quality pigments and quick-drying lacquers. On the other hand, on the most exalted and abstract level we could say the scientists were looking for Truth and the artist for Beauty. But there is an intermediate level -- one which gives an analysis of the project at hand which doesn't bog us down in a minute-by-minute account of daily activities but which does provide us with a raison d'etre for them.
As far as science education is concerned, one is immediately struck by the fact that although Kuhn refers to various times and places, his description rings most true for fairly recent educational practice in America. Although physics is the most "mature" science and the one that should have the most monolithic paradigm and the most rigid educational system, nevertheless European physicists, perhaps due to their gymnasium training, have displayed lots of interest in philosophy and metaphysics, not just as an avocation, but when they are discussing theoretical physics.
Perhaps Kuhn would say that these great 20th Century physicists are all really extraordinary revolutionaries working at the theoretical fringe -- that he's talking about the vast hoard of "civil servants". Maybe so, but yet Kuhn also admits that applied scientists and inventors also need to engage in rule-breaking behavior. He points out that "Edison's electric light was produced in the face of unanimous scientific opinion that the arc light could not be `subdivided'" ET, p. 228. Kuhn even speculates that the applied scientist "may profit by a far broader and less rigid education than that to which the pure scientist has characteristically been exposed." (ET, p. 238). So even on Kuhn's account, practitioners of pre-paradigm science, revolutionary scientists, and applied scientists all need to be able to challenge orthodoxy. Puzzle-solving is by no means the whole story.
Let us now turn to Kuhn's account of the problems characteristic of non-normal science. Most important perhaps are the problems posed by anomalies. Anomaly is a technical term in Kuhn's philosophy of science referring to "discrepancies between theory and experiment" (ET, p. 202). Kuhn emphasizes that most anomalies a scientist encounters are ignored and rightly so, but in certain circumstances they will not be dismissed:
"If the effect is particularly large when compared with well-established measures of "reasonable agreement" applicable to similar problems, or if it seems to resemble other difficulties encountered repeatedly before, or if, for personal reasons it intrigues the experimenter, then a special research project is likely to be dedicated to it." (E.T., pp. 202-203.)
If an anomaly resists repeated attempts to solve it, it may signal the beginning of a crisis and may even lead to a revolution. But even if a wholesale revision is not required, generally the discovery of something unexpected will be the result. As Kuhn puts it, serious anomalies "tell scientists when and where to look for a new qualitative phenomenon." (p. 205) Among Kuhn's examples of anomalies which turned out to be important are Mercury's motion (p. 191), the discrepancy in gas densities which led to the discovery of argon (p. 205), Kepler's 8" of arc (p. 209), and the energy-momentum gap which led to the discovery of the neutrino (p. 205). So it is through a non-paradigm bound form of inquiry that the most exciting scientific discoveries are made. Since on Kuhn's own account of science there is an "essential tension" between dogmatism and iconoclasm, we might conclude, though Kuhn does not, that students need to be trained in and taught about both aspects of scientific activity.

Chapter IV: Bibliography
Giunti,. .

Koertge, Noretta. .

Kuhn, Thomas S. (1978). Black-Body Theory and the Quantum Discontinuity, 1884-1912. Oxford: Oxford University Press.

Kuhn, Thomas S. (1957). The Copnerican Revolution. Cambridge: Harvard University Press.

Kuhn, Thomas S. (1977). The Essential Tension. Chicago: The University of Chicago Press.

Kuhn, Thomas S. (1962). The Structure of Scientific Revolutions. Chicago: The University of Chicago Press.

Lakatos, Imre and Alan Musgrave. (1970). Criticism and the Growth of Knowledge. London: Cambridge University Press.

Von Eckhardt. .

4.4 The Objective Aspects of Kuhnian Puzzles
The popularity of Kuhn's book demonstrates the extent to which it rings true to many people's experience with and conception of science. Our job as philosophers is to extract what is right about Kuhn's account and formulate it in more precise terms. One major strategy for improving Kuhn's account is to try to de-psychologize it. Instead of just taking his claims at face value we should ask to what extent is his account of science grounded in scientific psychology and to what extent is he using terms like gestalt switch in a metaphorical sense. (See O'Donohue.)
When Dewey spoke of puzzles he was definitely referring to the psychological state of perplexity, of mental bewilderment of the problem solver. But when Kuhn describes puzzles as testing the ingenuity of the experimenter not the truth of the paradigm or of the paradigm giving scientists confidence that certain problems can be solved. I think that it is helpful to sort out the objective vs. subjective aspects of his claims and evaluate them separately.
If I were to translate (or transform) Kuhn into an objective mode, I would extract the following insights:
1) The problems scientists work on frequently have a lot of internal structure and there are typically lots of constraints on the set of acceptable candidate solutions. (Later we will see how Nickles develops this point.) The complex structure of scientific problems is best learned by internalizing commonly used sub-routines and production rules, but all of this material can be subjected to critical scrutiny if the situation makes it appropriate to do so.
2) When scientists select research problems it is rational for them to consider not just the cognitive benefits which would accrue were the problem to be solved, but also the probability that it can be solved. Kuhnian puzzles are problems which we either have good reasons to believe can be solved or which have a structure which makes them accessible to investigation using familiar techniques. We might even go so far as to say that Kuhnian puzzles are just those problems which do not instill in us the kinds of feelings of doubt or puzzlement which Dewey took as so important! Perhaps this is why scientists so often appear cocky, over-confident -- they are working on problems whose objective structure is indicative of their susceptibility to solution!
What now needs to be done is to spell out in more detail the objective structure of problems, and the objective features of heuristic methods for solving them. Lakatos' methodology of scientific research programmes, which we will discuss in the next chapter, is a beginning effort in this direction.