Kuhn's STRUCTURE

[Boydstun]

I recently eliminated all of those essay-threads that I had created for the Boydstun Corner at OBJECTIVIST LIVING because the advertising at that site has made it no longer appropriate for sustained serious compositions and reading thereof. I've been making some of those old studies available at OBJECTIVISM ONLINE, and I think this one fits well in this sector.

~~~~~~~~~~~~~~~~

The Structure of Scientific Revolutions

Thomas S. Kuhn

I. Searching

In Thomas Kuhn's view, observation and experiment are essential to scientific understanding of the world (1990 [S], 42), but observation and experiment, in an established science, are guided and made sense of by one or another paradigm (S 109). Under the notion paradigm, Kuhn means to include theories, theoretical definitions, natural laws, particular models, and preeminently, concrete problem-solutions that exemplify theory and law, giving them empirical content (S 182–89). Scientific concepts, laws, and theories are presented and comprehended not in the abstract alone; but with applications to some concrete range of phenomena, purely natural, such as freely falling bodies, or natural-within-contrivance, such as pendulums (S 46–47, 187–91).

Normal science undertakes ever more exact and subtle experimental and observational investigation of "facts that the paradigm has shown to be particularly revealing of the nature of things" (S 25), determination of facts that "can be compared directly with predictions from the paradigm theory" (S 26), and articulation of the paradigm theory (S 27–29). These are roles of observation in science, I should say, even if we should reject Kuhn's distinction between normal and revolutionary periods of science as too sharply drawn.

One illustration of normal science would be the ongoing investigation of neutrinos. The existence of neutrinos is a fact established in 1956 (they were then detected) within the theoretical framework of quantum mechanics and detail conservation of energy. The characteristics of neutrinos are facts particularly revealing of the nature of elementary-particle interactions. The further, more refined determination of neutrino characteristics bears on the correctness and further refinement of a number of interconnected paradigms. Elaborate observations of solar neutrinos the past few decades provide quantitative constraints on models of nuclear reactions in the sun's core and on models of the sun's magnetic fields. And they provide constraints on the fundamental theory of neutrinos and of the electronuclear forces of nature (Bahcall 1990). Elaborate observations of cosmic neutrinos, these past few years [1], to ascertain whether they change flavors, hence whether they possess nonzero mass, inform efforts toward a Grand Unified Theory that may eventually supercede or subsume the Standard Model for elementary particles and their forces (Kearns, Kajita, and Totsuka 1999; Feldman and Steinberger 1991; Weinberg 1999). And they bear on current cosmology, under purview of general relativity.

Other normal-science investigations framed under the paradigm of general relativity are these: The finding of pulsar binary neutron stars has yielded, as hoped, empirical data for comparison with predictions from general relativity in the context of strong gravitational fields, predictions such as the rate of the orbital precession of the major axis of the stars' elliptical orbit and red-shifting of the pulse-clock (Piran 1995). Observation of quasi-periodic X-ray emissions from neutron stars pulling in matter from gaseous companion stars are yielding data indicating that, as predicted by general relativity (contrary the prediction from Newtonian gravitation), there is, just outside the neutron star, an innermost circular orbit for captured gas (Cowen 1998). Black holes are entities conceived and cultured solely by general relativity. Astronomical search for black holes and their distinctive features may yield an overwhelming vindication of general relativity (Lasota 1999).

There are three points made by Kuhn concerning the role of observation in science with which I should take some issue. One is his claim that "no part of the aim of normal science is to call forth new sorts of phenomena" (S 24). "Even the [normal-science] program whose goal is paradigm articulation does not aim at the unexpected novelty" (S 35). "Normal science does not aim at novelties of fact or theory and, when successful, finds none" (S 52). But scientists will be human, chronically so, hoping to catch something unexpected and momentous in their instruments, not only expected and readily comprehended phenomena. X-ray astronomer Bruno Rossi writes: "The initial motivation of the experiment which led to this discovery . . . was a subconscious trust of mine in the inexhaustible wealth of nature, a wealth that goes far beyond the imagination of man. This meant that, whenever technical progress opened up a new window into the surrounding world, I felt the urge to look through this window hoping to see something unexpected" (1977, 39).

Kuhn does say that "without the special apparatus that is constructed mainly for anticipated functions, the results that lead ultimately to novelty could not occur" (S 65, emphasis added). So I should productively construe the statements of his that I have quoted in the preceding paragraph as delineation of the strain that he calls normal science which in truth is found within a broader, richer actual practice of science.

Kuhn errs secondly, though only slightly, in his contention that "the act of judgment that leads scientists to reject a previously accepted theory is always based upon more than a comparison of that theory with the world. The decision to reject one paradigm is always simultaneously the decision to accept another, and the judgment leading to that decision involves the comparison of both paradigms with nature and with each other" (S 77, further, 147). Not always so. We continue to test empirically whether any mass-energy can be transported faster than vacuum c (Alväger, Farley, Kjellman and Wallin 1964; Brecher 1977; Chiao, Kwait, and Steinberg 1993). Some of these experiments, in the last two decades, have helped to articulate more finely the light-speed postulate of relativistic kinematics. But it is perfectly possible that such tests in the future could dispositively contradict the postulate. That would be the demise of special relativity regardless of the existence of competitor theories. Without viable alternative kinematics already on the stage or in the wings, what should we do if the light-speed postulate were empirically refuted? We should take our cues from the particulars of the failure and from our old, very successful special-relativity kinematics, and then develop a new and better kinematics.

Again, we continue to test a principle of general relativity, the principle of the equivalence of inertial and gravitational mass. These tests are not simply tests that help us articulate the paradigm, as when we search the heavens for evidence bearing on whether Einstein's field equations should include a nonzero cosmological constant (Krauss 1999; Cowen 2000). No, tests of the equivalence of inertial and gravitational mass cut to the quick of general relativity (Wald 1984, 8, 66–67; Ciufolini and Wheeler 1995, 13–18, 90–116). As I understand it, if gravitational and inertial mass are not precisely equivalent, then gravity cannot rightly be made geometric. And we have no viable alternative (nongeometric) to general relativity waiting in the wings. Were gravitational and inertial mass shown inequivalent by experiment or observation, then theoretical physicists would scramble to construct a replacement theory. We need not already have a competing theory to prefer over general relativity in order to reject the latter on experimental or observational grounds [2].

II. Seeing

Kuhn errs thirdly, and most seriously, in his (inconstant) denial that in our scientific observations we can always separate and adequately express what we literally perceive and what we take those percepts to indicate. Having learned prevailing scientific concepts, theories, and natural laws under exemplifying concrete observational applications, one is not able to see the phenomena in those applications entirely freely of the prevailing conceptual apparatus (S 46–47, 111–12, 186–89). Scientific observational phenomena are to some extent inextricably structured by the scientific, theoretical paradigm under which one is operating (S 111–35, 147–50).

"Looking at a bubble-chamber photograph, the student sees confused and broken lines, the physicist a record of familiar subnuclear events" (S 111). To enter the physicist's scientific observational world, the student undergoes "transformations of vision," like coming "to see a new gestalt." Hardly. Throughout the student's entry into the observational world of physics, all participants easily, routinely, and expressly distinguish between what of the physicist's observational world is commonsense perception and what is scientific interpretation, however automatic the latter may become (cf. S 196–98).

A bubble-chamber photograph provides detailed records of particle events "in a form that experienced physicists can interpret at a glance" (Breuker et al. 1991, 61). The photographs from bubble, cloud, or spark-streamer chambers never do yield a strictly perceptual particle-interaction gestalt in the way, say, that an X-ray photograph of a hand yields a strictly perceptual hand-skeleton gestalt. In the hand X-ray, given our ontogeny and our ordinary visual experience with hands, we are required to see the hand-in-the-image. We can tell ourselves, truly, that what is before us when we see the hand-in-the-image is only the trace of a hand, shadows of hand preserved on film, but we cannot avoid seeing the hand-in-the-image all the same. That is our perceptual constitution. Gestalt shifts too, such as in the Necker cube, are mandated by our primate perceptual constitution. We can tell ourselves that before us are only lines on paper, but we are required to see one cube or the other, with alternations every few seconds (Logothetis 1999). Contemporary elementary-particle tracking is mediated by vast electronic and computer processing systems, embodying painstaking deliberate interpretations. What is perceptually obligatory in the resulting computer-image displays are things like colors, lines, and 3D perspectives; all of these, self-conscious visual aids to scientific, interpretive observation.

Kuhn writes: "Since remote antiquity most people have seen one or another heavy body swinging back and forth on a string or chain until it finally comes to rest. To the Aristotelians, who believed that a heavy body is moved by its own nature from a higher position to a state of natural rest at a lower one, the swinging body was simply falling with difficulty. Constrained by the chain, it could achieve rest at its low point only after a tortuous motion and a considerable time. Galileo, on the other hand, looking at the swinging body, saw a pendulum, a body that almost succeeded in repeating the same motion over and over again ad infinitum." (S 118–19)

To be sure, Kuhn was "acutely aware of the difficulties created by saying that when Aristotle and Galileo looked at swinging stones, the first saw constrained fall, the second a pendulum" (S 121). Yet Kuhn will not let go his continual equivocation on see and its cognates (S 196–97). He maintains that an embracer of the new paradigm of mechanics—such was Galileo—is not an interpreter of swinging stones as pendulums, but "is like a man wearing inverted lenses," like a man who's vision has adapted to those lenses (S 122). "Galileo interpreted observations on the pendulum, Aristotle observations on [constrained] falling stones" (ibid.). That is inaccurate, I should say. Rather, Galileo and we interpret swinging stones as pendulums, on which we then make further interpretative observations. Similarly, one may interpret the swinging stone as in Aristotelian mechanics, as a constrained body working its way to the lowest feasible point. We can deliberately, with training, switch our interpretative perspectives: Aristotelian, Galilean, Newtonian, Lagrangian.  Kuhn suggests that the contemporary scientist "who looks at a swinging stone can have no experience that is in principle more elementary than seeing a pendulum. The alternative is not some hypothetical 'fixed' vision, but vision through another paradigm, one which makes the swinging stone something else" (S 128). I suggest, to the contrary, that developmentally, epistemologically, and evidentially, it is a swinging stone that is most elementary for everyone. It is with respect to analysis that we "see" (take) the pendulum as most elementary.

I do not mean to contradict Kuhn's thesis that scientists do not come to reject scientific theories on account of uninterpreted observations (e.g. S 77). We can recognize that and assimilate that without conflating what we literally perceive and what we make of those percepts in thought.

III. Saying

According to Kuhn, "there can be no scientifically or empirically neutral system of language or concepts" (S 146). Moreover, since we have no rudimentary paradigm-neutral observation language, the pendulum and constrained fall must be simply different perceptions, rather than "different interpretations of the unequivocal data provided by observation of a swinging stone" (S 126). Kuhn has in mind "a generally applicable language of pure percepts," where, by the term percepts, he apparently thinks not of swinging stones, but of more primitive constituents that compose our perceptions of swinging stones. Attempts to construct such a language of pure percepts have not fully succeeded, and anyway, all such projects "presuppose a paradigm, taken either from current scientific theory or from some fraction of everyday discourse, . . . . [thereby yielding] a language that—like those employed in the sciences—embodies a host of expectations about nature and fails to function the moment these expectations are violated" (S 127).

I should say, with Willard Quine, that we do indeed have a trustworthy scientifically neutral system of observation language appropriate and necessary for the physical sciences. This is not a rarified, fully reductive language of "pure percepts," but a natural language of posited objects and events (1969 [EN], 74–79; 1995a [N], 252, 254; 1995b [SS], 10–21, 27–29, 35–42; cf. 1951, 293–98). Swinging body and pendulum are both legitimate expressions of things observed[3], the former providing a fallback in cases of dispute over the latter. "What counts as an observation sentence varies with the width of community considered. But we can always get an absolute standard by taking in all speakers of the language, or most" (EN 88; also N 255; SS 22, 42–45). Pendulum, damped harmonic oscillator, and electron-positron track may be rightly spoken of as observed in the narrower, scientific community. But when necessary, scientists can shift gears and recognize those items as interpretations of more widely accepted and developmentally prior observed items.

Our broadest and most rudimentary observation language is our language of everyday experience, in which we report "it is raining" or "the iron is on" and in which we generalize "swinging suspended bodies return to rest" or "if it is snowing, then it is cold" (N 252, 254–55; SS 22–26). That last ordinary observation sentence is an example of what Quine calls an observation categorical, which is an empirically testable hypothesis, standing (as Popper would have it) as not yet shown false. Quine supposes, reasonably I think, that an empirically testable scientific hypothesis can be cashed out as an elementary observation categorical (N 255; SS 43–47). The detection of cosmic background microwave radiation, for example, cashes to visible records of activities in an antenna (which antenna cashes to . . . ). Quine realizes, of course, that scientists do not trace all the links from their hypothesis to observational categorical. "Still, the deduction and checking of observation categoricals is the essence, surely, of the experimental method, . . . . [and it remains] that prediction of observable events is the ultimate test of scientific theory" (N 256).

Quine recognizes that some hypotheses thus far not testable are accepted, rationally, even in the hard sciences. They may be accepted because "they fit in smoothly by analogy, or they symmetrize and simplify the overall design. . . . Moreover, such acceptations are not idle fancy; their proliferation generates, every here and there, a hypothesis that can indeed be tested. Surely this is the major source of testable hypotheses and the growth of science" (N 256; also SS 49). Can we test whether spacetime is curved? Well, yes, indirectly, more and more, we can.

Kuhn overrated the difficulties of vocabulary translations between alternative paradigms (S 149, 201). He did seem to allow that eventually translation can be effected (S 201–3). Such has been effected between Newtonian gravitational theory and general relativity, and gradually physics has attained more and more tests between those deep and grand theories, tests such as that for an innermost circular orbit about a neutron star.

 

Notes

1.  This study was composed in 2000.

2.   Hilary Putnam points out that Kuhn exaggerates in asserting that a paradigm can never be overthrown in the absence of a competitor paradigm. But Putnam then deflates the demerit of the exaggeration by posing as a hypothetical counterexample to Kuhn's universal claim only a Goodmanesque scenario: the world simply starts to behave radically differently. Barring such an implausible scenario, Putnam then expressly affirms the Kuhnian generalization at issue (Putnam 1974, 69–70). My counterexample scenarios (failure of light-speed postulate or failure of principle of equivalence) are intended to be entirely, mundanely realistic.

3.  Rudolf Carnap (1966) likewise recognized that what in one context of inquiry should be taken as inferred from what was observed could in another context be rightly taken as simply observed (Suppe 1977, 47).

 

References

Alväger, T., Farley, F.J.M., Kjellman, J., and I. Wallin 1964. Test of the Second Postulate of Special Relativity in the Gev Region. Physics Letters 12:260.

Bahcall, J.N. 1990. The Solar-Neutrino Problem. Sci. Amer. (May):54–61.

Brecher, K. 1977. Is the Speed of Light Independent of the Velocity of the Source? Phy. Rev. Ltrs. 39(17):1051–54.

Breuker, H., Drevermann, H., Grab, C., Rademakers, A.A., and H. Stone 1991. Tracking and Imaging Elementary Particles. Sci. Amer. (Aug):58–63.

Chiao, R.Y., Kwait, P.G., and A.M. Steinberg 1993. Faster than Light? Sci. Amer. (Aug):52–60.

Ciufolini, I., and J.A. Wheeler 1995. Gravitation and Inertia. Princeton: University Press.

Cowan, R. 1998. All in the Timing. Sci. News 154:318–19.

——. 2000. Revved-Up Universe. Sci. News 157:106–8.

Feldman, G.J., and J. Steinberger 1991. The Number of Families of Matter [= Three]. Sci. Amer. (Feb):70–75.

Kearns, E., Kajita, T., and V. Totsuka 1999. Detecting Massive Neutrinos. Sci. Amer. (Aug):64–71.

Krauss, L.M. 1999. Cosmological Antigravity. Sci. Amer. (Jan):52–59.

Kuhn, T.S. 1990 [1970, 1962]. The Structure of Scientific Revolutions. 2nd ed. Chicago: Univerity Press.

Lasota, J-P. 1999. Unmasking Black Holes. Sci. Amer. (May):40–47.

Logothetis, N.K. 1999. Vision: A Window on Consciousness. Sci. Amer. (Nov):69–75.

Piran, T. 1995. Binary Neutron Stars. Sci. Amer. (May):53–61.

Putnam, H. 1974. The "Corroboration" of Theories. In Scientific Revolutions. I. Hacking, editor. 1981. New York: Oxford University Press.

Quine, W.V.O. 1951. Two Dogmas of Empiricism. In Philosophy of Science: The Central Issues. M. Curd and J.A. Cover, editors. 1998. New York: W.W. Norton.

——. 1969. Epistemology Naturalized. In Ontological Relativity and Other Essays. New York: Columbia University Press.

——. 1995a. Naturalism, or, Living within One's Means. Dialectica 49(2–4):251–61.

——. 1995b. From Stimulus to Science. Cambridge, MA: Harvard University Press.

Rossi, B. 1977. X-Ray Astronomy. Daedalus 106(4):37–58.

Suppe, F. 1977 [1973]. The Search for Philosophic Understanding of Scientific Theories. In The Structure of Scientific Theories. 2nd. ed. Urbana: University of Illinois Press.

Wald, R.M. 1984. General Relativity. Chicago: University Press.

Weinberg, S. 1999. A Unified Physics by 2050? Sci. Amer. (Dec):68–75.

[Boydstun]

 

SEP – Thomas Kuhn

[Boydstun]

 

Kuhn's Intellectual Path <– a review by Howard Sankley of this book by K. Brad Wray

(My copy of that book of Wray's arrives tomorrow.)

Of related interest (which I have already):

The Essential Tension by Thomas Kuhn

The Road Since Structure edited by Conant and Haugeland

Reconsidering Logical Positivism by Michael Friedman

The Cambridge Companion to Carnap edited by Friedman and Creath

Scientific Revolutions edited by Ian Hacking

Interpreting Kuhn edited by Brad Wray

The Cognitive Structure of Scientific Revolutions by Anderson, Barker, and Chen

 

 

[Jim Henderson]

As an example of the popularity of this book, when I was in college in the late 1960s it was already part of the required reading for not only my History of Science course, but also the History of Economics and Sociology. 

[Boydstun]

A transcript of a lecture David Harriman delivered with the title “Do Scientists Need Philosophy” has recently been put online and is under discussion on Facebook.* 

I read the lecture, and my responses have led to some further information on Kuhn in the course of exchanges with Mr. Harriman. 

My initial response to the lecture:

No. Science (or mathematics) is not waiting for philosophers and their philosophic recommendations about science. But it is illuminating for some of us, for the betterment of philosophy, to learn the long and winding interplay of what we would today distinguish as science and philosophy. 1, 2, 3

David asked: "Do [Did] you read my lecture? Do you have a response to my argument?"

Was "you" the person named Stephen Boydstun? If so, Yes, I did. I'll read it again.

. . .

You [David] said "So, let’s see how strong a case can be made for the widespread view that philosophy is at best irrelevant to science and at worst it is actually harmful." Well, I don't think those are points of view weighty enough for the bulk of attention. I never heard any of my physics professors (or chemistry ones) talk about any debts to philosophy or badmouth philosophy either. They were teaching me methods, for sure, but if these were handed down from philosophers, it was not from individuals in their clearly philosophical hat as distinct from their physics and mathematical hats. I'm thinking just now of the estimation of tolerances for accuracy in measurements in the lab and how to propagate those error margins in equations.

It's not that philosophy (general metaphysics and general epistemology) was irrelevant, but to be of any traction, it has seemed to me it needs to be generated by and kept close by those who are engaged in the physics. Laws of nature as stated in mathematical relations of quantities of physical qualities was not an advice from philosophers. Nor the importance later on of group theory, symmetries and symmetry breaking. To be sure, we hear of influences on their physics developments reported by Helmholtz or Mach or Bohr or Einstein, but at least those latter two are pretty embarrassing when looking closely at what they actually did in making their contribution in physics rolling back the darkness. What philosophy was needed by Bohr to construct operators for QM constraining them to lead to corresponding algebraic variables of physics in the classical regime? What philosophy was needed by Einstein to seek invariance of mathematical form in the laws of electrodynamics across inertial frames? Nothing from the philosophies they drew attention to. Nor any from the discipline Philosophy at all, I’d say. I don’t mean to imply that philosophy SHOULD guide physics, in any sense in which the physicists don’t already possess the philosophy anyway. 

My geology professor did speak of Whewell's consilience of inductions and did illustrate it in some geologist's argument for why we can know that a river makes the bed and not vice versa. I do not recall who was that geologist and whether he was influenced by Whewell, but that was a lovely harmony on display between philosophy and science.

Step-backs for wide views on issues in physics from physics-informed philosophers such as Sklar or Healey or Frisch or Harriman are desirable for MY mind. But I don't see they are NEEDED for conduct of the science they reflect upon.

I am still developing my settled view on the proper relationships between the enterprise of philosophy and the enterprise of physics. One way I am approaching this is by study of the overlaps and differences between axiomatizations in mathematics, physics, and philosophy in the contemporary context. Another of my approaches is by study of the history of analysis and synthesis in mathematics and its relations to history of the analytic-synthetic distinction in philosophy. Then too, I'm absorbing the modern literature on the rational relationship of philosophy (especially metaphysics) to physics in the contemporary context, as addressed in the books by Chakravartty, Maudlin, Mumford and Tugby, and Morganti.

I suggest that philosophy can protect physics from the wider culture, and physics can inform philosophy (e.g. from chaos theory of late last century: determinacy does not imply predictability even in principle in a finite universe; also, control does not always require predictability), but I expect the unexpected in the vistas yet to learn.

(Continued)

 

[Boydstun]

(Continued)

Mr. Harriman, you said “the dominant viewpoint in philosophy of science during the past fifty years is called the ‘sociology of knowledge’ school. According to these philosophers, scientific truth is determined by authority and consensus within a social context.” You do not offer a single name of a philosopher holding that viewpoint. Let me check who exactly these philosophers are and what proportion they are in the profession. I’ve been a member of the Philosophy of Science Association since 2000. So I have all issues of its journal Philosophy of Science since then. In my most recent issue, April 2024, I find 16 papers, and not one of them is taking a sociology-of-knowledge angle on their topic or taking such a thing for their topic. One paper in this issue would be of interest to the both of us: “Mathematizing Metaphysics: The Case of the Principle of Least Action” by Michael Veldman. His subsections include: “The Maupertuis-Euler teleological metaphysics” “Varieties of teleology in physics” “Mathematization and the metaphysics-physics relation” 

Conclusion: “In the 1740’s, a metaphysical thesis asserting the economy of Nature came to underwrite a new, general principle of physics, but as I have argued, the process of working out these ideas soon led to contradictions between the metaphysics of ‘least action in Nature’ and the mathematical theory that was supposed to provide a rigorous foundation for it. As a result, this teleological metaphysics could no longer find footing in its mathematical representation. Formal, mathematical considerations—not a priori philosophical reasoning or empirical test—resulted in the rejection of a metaphysical thesis. Mathematization was supposed to finally place physical teleology on a rigorous foundation. Ironically, it provided novel, scientific reasons to decisively reject it.”

The variety of physical teleology shredded in this history was “an immanent physical teleology, not formal teleology,  divine teleology, or teleological explanation” (355–56). I should note that in no way does the process and outcome in this history rattle teleological causes in biology at the vegetative level which today is sensibly seen as overarching cause by its constraint of the efficient causes of natural selection and cellular, biochemical activities holding up that teleological structure.

The Maupertius-Euler teleology likely had some ancestry in the theological thinking of Leibniz. I’d part from the reasoning David held up in saying that such thinking is arbitrary. Basis of such a metaphysical pattern in wisdom of God or Descartes’s rationalizing of his laws of mechanics on wisdom of God is a flimsy basis (and cheap) because God and Its character are only in those thinkers' heads. I’d not say that what’s wrong with such a basis is that it is arbitrary. Those gentlemen of yore devised rational arguments, faulty as they were, for the existence of such a God. When Leibniz said the cosmos might be merely a watch in the pocket of some giant, were Leibniz serious, THAT would be an arbitrary start. (He was only joking.)

I did not understand, David, why you said that Descartes’s principle of inertia was not useful to Newton and that Galileo’s principle of inertia was useful to Newton. Galileo had things moving in a circle around the earth on their own without a continuing mover, if I recall correctly, and Descartes had them moving, rather, in a straight line. In connection with Newton’s particular concept of force, it is the straight-line principle of inertia that was useful to Newton (not the circle principle), however Descartes arrived (I could look it up, but I have to rush) at the straight-line version. 

But back to domination in recent times of philosophy of science by a sociology-of-knowledge quarter among philosophers. I could step back through all my issues of Philosophy of Science to see if I can find a paper taking a sociology-of-knowledge viewpoint such as you described. But I’m too pessimistic on that and rushed by now that I’ll not do that inventory for now. I have on hand some text-book collections of papers in the philosophy of science, and it seems none of them include words from a sociology-of-knowledge quarter. These are the book of Boyd, Casper, and Trout (1991); Curd and Cover (1998); Nola and Sankey (2007); and Earman and Norton (1997). That last one does have a paper by Frederick Suppe titled “Science without Induction.” We better look into that.

I do recall a sociology-of-scientific-knowledge guy speaking some years ago at a Meeting of either APA or PSA. He wore red tennis shoes with his suit, and as I recall, he was a bit of a red himself. His name is Steve Fuller. His paper was shredded by a philosopher in the audience whose name was John Post.

I’m getting the definite impression that history and philosophy of science are doing very well—if once sociology-of-knowledge was a dominating quarter, it seems to have dried up—and, as ever since the scientific revolution, physics is doing mighty fine.

~~~~~~~~~~~~~~~~

David Harriman: “Stephen Boydstun, I’m surprised that you have never heard of Thomas Kuhn.”

~~~~~~~~~~~~~~~~

David, I’ll have to review what I've written about him tomorrow. And think about the "consensus" approach you mentioned. And the opponents to his way with things. On down from my paper linked here in this post, I think I've kept adding the more recent works about Structure after that paper, scrollling on down. In the 1960's his book was one of the readings we had for my course in History of science; it was recent then, and he did come to our school for some conference in which he reported on work he was then doing on Ostwald v. someone (Planck or perhaps your Mach), which I imagine he later wrote about. I've always wanted to study his earlier work on Copernicus. As far as my Philosophy of Science course at that first-degree university, they were still using the Cohen and Nagel text. I'll indeed try to look back through my Philosophy of Science journals tomorrow to see if Kuhn or relatives have continued to be current. He does come up in some positive ways in some current scientific realist work (probably a book) I was reading recently, but I'll have to look for what that was. I'll look up what you say also in your book. This linked (next Comment-post) little paper of mine was written for a graduate course (Daniel Garber) in philosophy of science at University of Chicago 25 years ago. I'll dig out my notes and see what was said of Kuhn there. I kept also all the vast amount of xeroxing he had staff do for us.

~~~~~~~~~~~~~~~~

I just did a quick read of my paper* , and I see that for all the characteristic views of Kuhn in STRUCTURE which I undertook to assess, "scientific truth is determined by authority and consensus within a social context" was not a doctrine I had noticed in studying his book. Most likely that is because it's a doctrine not literally his, but of people coming after him and putting about the doctrine (they favor, either because it's easier to knock a tall man down or because they favor the doctrine and like to read it out as from the distinguished man).

(I have detailed that sort of pattern in connection with an ascription to Kant before. There were philosophers immediately after him who favored the idea that objectivity be replaced by inter-subjective agreement, so they drew that idea as a view of Kant, as expressed in some statement(s) he had made in KrV. But in fact Kant had flatly repudiated such a view in Critique of Practical Reason later in the ’80’s (and again in the ethical theory book in the 90’s if I recall my citations well enough). I have detailed the exact source of Kant’s initial statement in KrV which the immediately following creeping-subjectivists circled, and that source was in a sensible informal fallacy called out in the logic text from which Kant lectured. Then, come to today, if one is too lazy to topple Kant by grasping what he actually wrote and arguing what is wrong with that real mccoy, one again might sing the old refrain that Kant replaced objectivity with inter-subjective agreement, because that view [not really Kant’s] is easily sensed to be haywire.) 

I’ll look through the professional commentary and critiques of Kuhn concerning this particular ascription to him tomorrow. Hopefully some names standing squarely on, favoring, the consensus view of scientific knowledge will surface.

~~~~~~~~~~~~~~~~

From David’s lecture: “The dominant viewpoint in philosophy of science during the past fifty years is called the “sociology of knowledge” school. . . . You can establish whether an idea is true or false simply by getting together and voting.” I see now that the regular name of this school is the “strong program in the sociology of science”. Kuhn attacks this program vigorously in, for instance, his 1992 paper “The Trouble with the Historical Philosophy of Science”. This program, I gather, had its interval of fashion, but whether it was ever the dominant school in the philosophy of science remains for me to confirm. Who are the proponents of that program? Not Kuhn, but who? I’ll find out. 

Kuhn took their account to be “a grave loss in our understanding of the nature of scientific knowledge” (1992,110). The strong program “fails to account for essential aspects of scientific development” (114).” “Of course power and interest play a role in scientific development, but there’s room for a great deal else besides” (116). Kuhn seems to have approached the nature of scientific knowledge with a view of knowledge in general, which did not depend from examinations of particular scientific episodes. The criticisms I made of him in my paper still hold fast through his life. He figured that all knowledge has to be developmental—fair point—but he went on to fumble in thinking that entails there is no truth independent of our investigations to which science is tending. That is a poor look at human evolution, human ontogeny, and developmental cognitive psychology, and someone more informed in the pertinent parts of those, such as Tomasello these decades of research later, could lift their view to the survival advantages of the ability (a significantly social ability really, together with individual thought) to conform to mind-independent reality and make inventions upon it, rather than remain mired in the dilemmas of classical American Pragmatism as it assimilated biological evolution. But the fall off the horse by Kuhn, as by Peirce, is nothing so sorry and flaky as the strong program in sociology of science.

Before turning to strong-program folks, I should underscore that it is one thing to say that philosophy of science has taken some sorry turns and was under some wrong general conceptions even with the philosophers who first established this specialty within philosophy. It is another, in need of specific demonstration, to maintain that any philosophy of science has influenced the course of physics, specifically, that the strong program in the sociology of science has had a bad influence on physics and that physics stands in need of corrected direction from better philosophy. 

(Continued)

References

Conant, J., and J. Haugeland 2000. The Road Since STRUCTURE – Thomas S. Kuhn. Chicago: University of Chicago Press.

Kuhn, T. 1992. The Trouble with the Historical Philosophy of Science. In Conant and Haugeland 2000.

[Boydstun]

So, finally, Who are the proponents of the Strong Program in the sociology of science? 

I’d suspect among that cadre are the authors of this introductory textbook (I’ve not read): Scientific Knowledge – A Sociological Analysis (1996).

We have a help from David Friedman from his 1998 paper “On the Sociology of Scientific Knowledge and Its Philosophical Agenda.”

Quote

 

For a philosopher seriously interested in the history and historiography of science, perhaps the most interesting—if also the most troubling—theoretical development of the last twenty years has been the sociology of scientific knowledge (SSK) articulated at Edinburgh by Barry Barnes and David Bloor and at Bath by H. M. Collins.[1]”

“[1] Barry Barnes – Scientific Knowledge and Sociological Theory (1974); T. S. Kuhn and Social Science (1982).

David Bloor – Knowledge and Social Imagery (1976, 1991); Wittgenstein: A Social Theory of Knowledge (1983).

Barnes and Bloor – “Relativism, Rationalism and the Sociology of Knowledge” in Rationality and Relativism (Hollis and Lukes, eds. 1982). 

H. M. Collins – Changing Order (1985, 1992).

 

The philosophical agenda Friedman mentions in the title of this paper is down from Wittgenstein’s Philosophical Investigations (1953; Philosophische Untersuchungen, 1945) with its concepts of “language-game” and “form of life” interpreted in SSK as

Quote

particular socio-linguistic activities and practices associated with particular socio-cultural groups—where the practices in question are regulated by socio-cultural norms conventionally adopted by the relevant groups. Wittgenstein’s insistence on the need for renouncing traditional philosophy in favor of the careful description of particular “language-games” expressing particular “forms of life” is then read as the call for an empirical sociological investigation of the way in which the traditional categories of knowledge, objectivity, and truth are socially constituted and determined by the norms, needs, and interests of particular socio-cultural groups. This idea is of course most explicit in the work of Bloor, who devotes an entire book to just such a sociological (and relativistic)reading of Wittgenstein. And Bloor’s conclusion is nothing less than that the sociology of knowledge should be the replacement for traditional philosophy. For Bloor, the traditional problems of philosophy—which concern, in  particular, “the nature of rationality, objectivity, logical necessity and truth”—can after all be solved, and solved by empirical sociological means. (240–41)

One might expect there to be a conflict with SSK’s replacement for objectivity with an empirical approach to showing the fine quality of that replacement.

Today, among philosophers, scientific realism is alive and thriving, and I’d like to recommend two books to that point: Realism and Anti-Realism by Stuart Brock and Edwin Mares (2007) and Scientific Realism – How Science Tracks Truth by Stathis Psillos (1999).

I have to get back to work on my own philosophical projects now. My conclusions are (and are at odds with the picture put forth by Mr. Harriman): Though Kuhn’s STRUCTURE is anti-realist, he was not a proponent of the Strong Program in the sociology of scientific knowledge (notwithstanding the wish of Strong Program advocates to claim him as showing their view correct). That program had its interval of interest among philosophers of science. It was never the dominant view among philosophers of science, and interest in Kuhn’s STRUCTURE is not a right measure of such interest. Philosophy of science of any stripe has no significant influence on the conduct of physics, and if one aspires to become a physicist, I recommend leaving aside your philosophy of science books and indeed all other books but ones in physics and its required mathematics.