Many scientists, philosophers, and laypersons have regarded science asthe one human enterprise that successfully escapes the contingenciesof history to establish eternal truths about the universe, via aspecial, rational method of inquiry. Historicists oppose this view. Inthe 1960s several historically informed philosophers of sciencechallenged the then-dominant accounts of scientific method advanced bythe Popperians and the positivists (the logical positivists andlogical empiricists) for failing to fit historical scientific practiceand failing particularly to account for deep scientific change. Whileseveral strands of historicism originated in nineteenth-centuryhistoriography, this article focuses, first, on the historicistconceptions of scientific rationality that became prominent in the1960s and 1970s, as the maturation of the field of historiography ofscience began to suggest competing models of scientific development,and, second, on recent approaches such as historical epistemology.

The “Battle of the Big Systems” of the 1960s and‘70s, involving historicists such as Thomas Kuhn, Imre Lakatos,Paul Feyerabend, and Larry Laudan, eventually gave way to a realistreaction, as many philosophers rejected the perceived skepticism andpotential relativism of the historicist movement, now reinforced bynew-wave sociology of science. The 1990s featured the so-calledScience Wars, as philosophers attempted to defend truth, rationality,objectivity, and scientific progress (and their own turf) from theperceived threats of rapidly developing, sociology-inspired scienceand technology studies and (other) postmodern influences. Since then,a group of interdisciplinary scholars have attempted to reimagine waysin which historical and philosophical work can be brought togetherfruitfully.

• 1. Historicist Conceptions of Rationality: The Battle of the Big Systems
  • 1.1 Overview
  • 1.2 The Historical Turn in Philosophy of Science
  • 1.3 The Methodology of Scientific Research Programs
  • 1.4 Methodological Anarchism
  • 1.5 The Pragmatic, Problem-Solving Approach
  • 1.6 Evolutionary Models of Scientific Development
  • 1.7 New-Wave Sociology of Science and the Realist Reaction
• 2. Rationality and History: Some Basic Questions
• 3. Historicism Then and Now
• 4. Related Developments and Further Challenges
• 5. Integrated HPS and Historical Epistemology: What Good Are They Regarding Scientific Rationality?
• Bibliography
• Academic Tools
• Other Internet Resources
• Related Entries

1. Historicist Conceptions of Rationality: The Battle of the Big Systems

1.1 Overview

What good is appeal to history when it comes to evaluating therationality of decisions and actions? Since the past is already over,isn’t history simply “bunk”? A couple of everydaylocutions suggest otherwise. It is commonly held that“history” (meaning historiography, the disciplined studyof what happened in history) is a debunker of myths. And politiciansare not the only people worried about “the judgment ofhistory”. Both these ideas came into play in the newhistorically-oriented philosophy of science that began to emerge atthe end of the 1950s. The “new historicists” (as we maycall them) included Thomas Kuhn, N.R. Hanson, Mary Hesse, ImreLakatos, Paul Feyerabend, Stephen Toulmin, Dudley Shapere, LarryLaudan, Ernan McMullin, and Michael Ruse. They claimed that thethen-dominant positivist and Popperian accounts of science werethemselves bunk—myths about how science is done. Some newhistoricists claimed to find larger units and a hitherto unnoticeddynamic in the time-series of the historical record—long-term,forward-looking research programs that included evolving series ofrelated theoretical moments. Above all, the historicists stressed thedepth of major historical changes and the resulting challenges tocumulative scientific progress. They argued that there was nothing inthe traditional “logic of science” that could rationalizesuch changes. The problem was to produce a new dynamical model ofscience that would capture these patterns and rationally motivatethem.

Historicist philosophers did a convincing job of showing thathistorical evidence called the received views into question. Mostphilosophers today accept that verdict of history. Less successful wasthe attempt to formulate an adequate positive theory of rationality,both at the first-order level of scientific methodological norms(e.g., “Reject a hypothesis that makes clearly falsepredictions” or “Use double-blind experimental methodswhen dealing with cognitive agents”) and at themetamethodological level, where they faced the problem of how torationally select among competing theories of scientific rationality,without circularity. The disagreements here raised the question ofwhether thereis a general theory of scientific rationalityto be found, or a need for one.

(For accessible, critical summaries of the “Big Systems”debate, see Suppe 1974, Newton-Smith 1981, McGuire 1992, and Zammito2004. Space limitations have forced the omission of importantdevelopments, including the Marxist dialectical tradition, e.g., Nowak1980, and recent work on stance and rationality, e.g., van Fraassen2002, Rowbottom & Bueno 2011.)

1.2 The Historical Turn in Philosophy of Science

Kuhn’sStructure of Scientific Revolutions (1962/1970a)was the original manifesto of historicist philosophy of science andremains the primary reference point. His work thus provides the mostuseful platform for recounting early historicist efforts—and thedifficulties they faced. We shall then take a briefer look at othermajor contributors. Kuhn had been anticipated in quite diverse ways byKant, Hegel, William Whewell, Émile Meyerson, Ernst Cassirer,Alexandre Koyré, Philipp Frank, Gaston Bachelard, Ludwik Fleck,Hans Reichenbach, Rudolf Carnap, W.V. Quine, Michael Polanyi, Hesse,Toulmin, and Hanson and was immediately followed by Lakatos,Feyerabend, Shapere, Laudan, and others (see the entry onThomas Kuhn; also Hoyningen-Huene [1989] 1993 and Rheinberger [2007] 2010b).

The famous opening sentence ofStructure was:

History, if viewed as a repository for more than anecdote orchronology, could produce a decisive transformation in the image ofscience by which we are now possessed. That image has previously beendrawn, even by scientists themselves, mainly from the study offinished scientific achievements as these are recorded in the classicsand, more recently, in the textbooks from which each new scientificgeneration learns to practice its trade. Inevitably, however, the aimof such books is persuasive and pedagogic; a concept of science drawnfrom them is no more likely to fit the enterprise that produced themthan an image of a national culture drawn from a tourist brochure or alanguage text. This essay attempts to show that we have been misled bythem in fundamental ways. Its aim is a sketch of the quite differentconcept of science that can emerge from the historical records of theresearch activity itself.

Kuhn modeled the history of a science as a succession of dogmaticperiods of “normal science” under a“paradigm”, separated by “revolutionary”transitions to the next paradigm. According to Kuhn such a break fromthe past rejuvenates a field that had stagnated under the weight ofanomalies that it no longer seemed to have the resources to solve. Anew paradigm introduces changes at all levels, from establisheddatabases and instrumentation to the conceptual framework, goals,standards, institutional organization, and research culture—somuch so that some older practitioners can hardly recognize the newparadigm as their field. This disconnect produces“incommensurability” across paradigm change, ranging fromcommunication failure to problems of rational choice between the two,since there exists no fixed measure of success. At his most radical,Kuhn modeled revolutionary decisions on political revolution at thecommunity level and on religious conversion at the individual level,adding that scientists on different sides of a paradigm debate“live in different worlds” ([1962] 1970a: ch. 10). Undercritical pressure, he subsequently softened his position. In fact, he soughtto clarify the notion of incommensurability to the end of his life(Sankey 1997). Kuhn exemplifies the irony that, while historicistsused deep change as a weapon to beat up traditionalists, it presentedserious problems for the historicists themselves as well.

Kuhn’s book was his attempt to answer the question posed by theabove quotation. This question immediately raised another: How canappeal to history achieve that transformative change? In particular,how candescriptive claims about the past (or presentscience, for that matter) affect ournormative judgmentsabout rational beliefs and behaviors? How can history inform amethodology of science? This is a version of the so-called“is-ought” problem. Can there really be a“judgment” of history?

Over the next decade or two, most philosophers of science came toagree that there was a disconnect between science as historicallypracticed and the normative models of the received philosophers. Thehistoricists therefore presented the philosophical community with amomentous dilemma: either reject most of science to date as irrationalor else accept that science is generally rational and use thehistorical information to revise our deeply entrenched logical andprobabilistic conception of rationality. Some positivists and Popperiansattempted to finesse option one by arguing that the history of scienceapproximated the traditional view of rationality closely enough if wetreated their sanitized, abstract models of science as regulativeideals. Kuhn and other historicists defended option two, taking therationality of science to be practically axiomatic. Wrote Kuhn,

I do not for a moment believe that science is an intrinsicallyirrational enterprise …. I take this assertion not as a matterof fact, but rather of principle. Scientific behavior, taken as awhole, is the best example we have of rationality. (1971: 143f; quotedby Hoyningen-Huhne [1989] 1993: 251f.)

What was Kuhn’s revised conception of rationality and how was itbased on history (to the degree that it was)? While he provided noexplicit, general theory of rationality, Kuhn’s challenge herewas greater than many appreciate. The positivists and Popperians hadpractically invented modern, academic philosophy of science. For them,scientific rationality was wholly a matter of making correct theoryacceptance decisions in context of justification, where the hypothesesand test data are already on the table, the data are theory-neutral,and the goals and standards are logically independent of theory. ToKuhn this picture of science was more like a photographic negative inwhich light and dark are reversed. Let us count the ways.

(1) Although his work deepened the problem of underdetermination byinsisting that logic plus data is insufficient to determine theorychoice, Kuhn reduced the magnitude of the problem of justifyingscientific claims by rejecting traditional realism and thecorrespondence theory of truth. No longer must scientists justify atheoretical claim as true. Instead, he adopted the Kantian criticalposition that no enterprise, including science, has the ability toestablish the final, metaphysical truth about the world. Instead,science is largely a problem-solving enterprise, and scientistsare in position to evaluate the goodness of proposed problemsolutions, relative to previous attempts. “[T]he unit ofscientific achievement is the solved problem” ([1962] 1970a:169). What demarcates science from nonscience and pseudoscience issustained support (over historical time) of a puzzle-solvingtradition, not the application of a nonexistent “scientificmethod” to determine whether the claims are true or false orprobable to some degree. With justified truth claims gone, newaccounts of scientific discovery, knowledge, explanation, and progresswill also be needed.

(2) Contrary to most empiricist views, the data are nottheory-neutral, hence not cumulative from one period of science toanother.

(3) Moreover, Kuhn extended the claim that observation is theory ladento say thatall major aspects of a science are laden by theothers. Substantive data and theoretical claims, methodologicalstandards, goals, and even the social institutions of science are allbound up in mutual dependence. (The received view had kept themseparate and independent in order to avoid mutual contaminationallegedly leading to circularity; see Scheffler 1967.) It is thisinternal feedback that introduces the interesting, nonlinear dynamicsinto Kuhn’s model, since the feedback produces coupledinteraction terms (Kuhn 1977: 336; Nickles 2013b; De Langhe2014b).

(4) This tight coherence implies that normal science is conservativeand closed, in contrast to Popper’s science as an “opensociety” (Popper 1945). Contrary to tradition, said Kuhn,scientific rationality does not consist in advancing hypotheses andtesting them severely. To challenge the constitutive pillars of ascientific field, as Popper and the positivists advocated, woulddestroy it, for all theories and conceptual frameworks facepotentially falsifying anomalies at all times (Kuhn [1962] 1970a and1970b; Lakatos 1970 agreed). Popper’s “criticalrationalism”, the key to Popper’s Enlightenment conceptionof political democracy as well as scientific advance, is actuallyirrational; for such criticism would undercut theresearchers’ reason for being.

(5) Kuhn claimed that Popper and others had missed the existence ofkey structures in the history of science—the longer-termapproaches that he called paradigms and hence both normal and trulyrevolutionary science. There are different historical scales in play:individual theories, paradigms, and the still longer-term perspectiveof a succession of paradigms. So Kuhn adopteda two-tiered ordouble-process conception of science in which there is, first, aconstitutive framework (the paradigm), held immune to revision duringperiods of normal science, and, second, change from one framework toanother. For these frameworks are historically contingent and areeventually displaced by others. Kuhn’s two-process accountsharply clashed with the one-process account of Popper (1963) and manyothers. Ironically, given that Kuhn was also attacking positivistpositions, and given his greater sympathy for Popper, the two-processaccount was closer to the “positivists” Reichenbach andCarnap than to Popper (see Reisch 1991; Carnap 1950; De Langhe2014a,b; Nickles 2013a).

(6) Thus two different accounts of scientific rationality arerequired, not one: one to cover the relatively smooth change withinnormal science under a single paradigm and the other to handle radicalparadigm change. This immediately implies that there are two basictypes of scientific change, hence two problems of scientific changeand/or two problems of progress to be solved, hence two accounts ofscientific rationality needed to solve them. What were Kuhn’sconstructive claims?

(7) We should seek neither a single, neutral method of all science atall times nor an account based on explicit methodological rules. Mostnormal scientific decisions are based on skilled judgments, not rules(Kuhn [1962] 1970a: chs. 5, 10). The appearance of rules in scientificpractice is a sign of crisis, of breakdown. Contrary to tradition,neither rationality within a paradigm nor rational choice betweenparadigms is a matter of following rules. It is not the application ofa formal, logic- or probability-based algorithm. In both cases it is amatter of skilled judgment (of different kinds).

(8) Informal scientific judgment depends heavily upon rhetoric andjudgments of heuristic fertility in the context of discovery—thevery items that had been expressly excluded from the context ofrational justification by the dominant tradition. For Kuhn, normalproblem solving is a matter of modeling new puzzles solutions onestablished precedents, the exemplars, where modeling cruciallyinvolves judgments of similarity, analogy, or metaphor. (WhereasPopper’s methodology is a learning theory in which we learn onlyfrom our mistakes, in Kuhn’s we learn also (mainly) from oursuccesses—the exemplars, which, over time ratchet up ourknowledge within normal science.) In paradigm change, the rhetoricaltropes used in persuasion are typically more abstract and tenuous thanin normal science. Kuhn’s account of the rational acceptance ofparadigm change had to remain thin because of incommensurability. Herethe justification problem was all the more difficult because newparadigms generally lose some of the successes of their predecessors(so called “Kuhn loss” of problem solutions but also data,theory, goals, and standards).

(9) Kuhn’s novel constructive move in dealing with therationality of paradigm change was to bring in a prospective dimensionof heuristic fertility judgments. From the point of view of key,creative scientists, the old paradigm has exhausted its resources,whereas radical new ideas and practices can not only resolve some oldanomalies (retrospective confirmation) but, equally importantly, canreinvent and thereby preserve the field by opening up new frontierswith much interesting new work to be done. For them the field now hada future. To be sure, heuristic guidance was also a feature of normalscience, but there it was built in implicitly.

In sum, Kuhn turned the traditional ideas of scientific justification,based on the discovery-justification-context distinction, on theirhead. Ironically, once we take the research scientists’ pointsof view, the more interesting forms of scientific cognition, includingjustification, occur in contexts of discovery. All of this according to Kuhn.

Critics countered that, while the historicist upstarts had scored somedamaging critical points, their positive accounts of scientificrationality were underdeveloped, vague, and unconvincing. Politicalrevolution and religious conversion as models ofrationalbehavior?! Clark Glymour (1980: 7, 96ff) called the new approach“the new fuzziness”. Could intuitive judgment reallyreplace standard confirmation theory? And what would be the analogousrelation of evidence to theory at the metamethodological level, wherenow “theory” was the set of methodological rules or theoryof rationality itself? (Historicists replied that it is not their faultif real-life decision-making is a messy business that often outrunsavailable formal rules.) Shapere (1984: chs. 3–5) was a severeearly critic of Kuhn, and Lakatos (1970: 178) reported that Kuhn hadreplaced rationality with “mob rule”. Since Shapere andLakatos were historicists, we see that the historicists could disagreesharply among themselves. Feyerabend will provide the most vividexample.

Kuhn’s insightful treatment of science from the workingscientists’ point of view provided a microlevel conception ofrational decision-making. But did he have a metamethodological accountof how to decide among competing theories of scientific rationality?Again, not an explicit and comprehensive account, only someconstructive suggestions. Like all historicists, he said that arationality theory must fit the history of science and that thetraditional accounts failed this history test. An adequate theory mustalso be progressive and avoid epistemological relativism. Kuhn (andmany others) simply built in these norms from the outset. Such a moveworks well among most friends of historicism but not well for critics,who think these presuppositions simply beg the normativity of historyquestion. Given incommensurability, are not rationality,progressiveness, and denial of relativism key items that must beargued for? In other passages, Kuhn did argue for them, but fewcritics were convinced.

On the positive side, Kuhn made an epistemological economy claim.

[I]n its normal state … a scientific community is an immenselyefficient instrument for solving the problems or puzzles that itsparadigms define. ([1962] 1970a: 166; cf. Wray 2011: ch. 7)

It is clear that Kuhn considered science moreefficient on his own account than on Popper’s, because the double process enablesextreme specialization (Wray 2011; De Langhe 2014c). Indeed,traditional accounts fail Kuhn’s demarcationcriterion—that a genuine science supports a puzzle-solvingtradition. Given Kuhn’s conviction that science is progressivein terms of problem-solving success, predictive accuracy, simplicity(the reworking and streamlining of problem-solving efficiency overtime), and so on, it supposedly follows that his account makes scienceboth rational and non-relativistic. Critics disagreed.

There also seems to be a kind of transcendental argument strategybehind Kuhn’s approach, as a response to the quasi-Kantianquestion: Given that science, as historically practiced,islargely rational and progressive, but not in the standard way, how areits rationality and progress possible? Supposedly, the study of thehistorical patterns will show the way.

Kuhn often described his two-process view as “Kant with moveablecategories”. Accordingly, there is also a dialectical,quasi-Hegelian reading: from the myriad of micro-decisions by thecommunity of scientists in a given field over time, with lots of fitsand starts, a progressive enterprise emerges, although not one that isteleologically converging on the metaphysical truth about the universeor on any other “end”. However, on this view we haveabandoned the idea that individual scientific decisions are typicallydriven by an explicit concern for rationality. In several areas ofphilosophy there are heated controversies about whether higher-orderemergents have genuine causal power and hence genuine explanatoryforce. To that degree, it remains unclear what role the desire to berational plays, as opposed to more mundane motives. This problemarises for other historicists as well, as David Hull will note. (Seethe entries onmental causation and oninternalist vs. externalist conceptions of epistemic justification.)

On rationality as socially emergent, we may jump ahead here to note that feministphilosophers of science such as Helen Longino and Miriam Solomon havedefended scientific rationality as a socially emergent norm (Longino1990, 2001; Solomon2001). They thereby address the question of how a naturalistic,science-as-practiced approach to scientific knowledge can nonethelesshave normative implications. However, they do not shy away from makingpolicy proposals forchanging (improving) scientificpractices and their supporting institutions. On their accounts, someother factors, such as political/ideological ones, also sociallyemerge and can have top-down causal efficacy on individualpractitioners but without negating the agency and autonomy of thoseindividuals. Here familiar issues of “methodologicalindividualism” come into play. (See the entries onfeminist epistemology and philosophy of science,feminist perspectives on science,feminist social epistemology, andfeminist political philosophy.)

The vigorous attacks on Kuhn as a radical subjectivist andirrationalist who was undermining not only philosophy but the Westernintellectual tradition now look exaggerated, but it is fair to saythat the five big problem-complexes of normativity, incommensurability(including meaning change), relativism, social knowledge, and deep butrational progressive change are extremely difficult and remain open todebate today. For many philosophers of science, relativism is the bigbugaboo that must be defeated at all costs. For them, any view thatleads to even a moderate relativism is thereby reduced to absurdity.Historicist philosophers have insisted on relativity to historicalcontext but, with few exceptions, have made a sharp distinctionbetweenrelativity and outrightrelativism. Somecritics have not found this distinction convincing (see the entry onrelativism, Kindi & Arabatzis 2012 and Richards & Daston 2016).

1.3 The Methodology of Scientific Research Programs

Criticism and the Growth of Knowledge (1970), edited byLakatos and Alan Musgrave, was a second major contribution to thehistoricism debate. This collection of articles, originating from a1965 London conference, was in significant respects a reaction toKuhn; but it is especially important for Lakatos’s owncontribution to the volume, “Falsification and the Methodologyof Scientific Research Programmes” (MSRP), an attempt toaccommodate a broadly Popperian perspective to some of Kuhn’sideas and thereby to diverge from Popperian orthodoxy. Lakatos hadlong favored an historical approach to the philosophy of mathematicsand science (see his 1976). One of his central concerns was to defendthe rational continuity and progressiveness of modern science from thechallenge of radical change. Another was to fend off charges ofhistorical relativism.

Like Kuhn’s paradigms and Laudan’s research traditions(see below), the unit of rational appraisal for Lakatos is not asingle theory at a point in time; instead, it is a series of theoriesthat are rationally-connected moments in the development of anidentifiable research program. In MSRP these theories share anegative heuristic containing inviolable principles and apositive heuristic that both provides a “protectivebelt” around the negative heuristic and guides future research.The forward-looking heuristic element was, as for Kuhn, an importantfeature missing from traditional accounts of science. In MSRP,research programs are evaluated as to theirprogressivenessover historical time, i.e., which grows knowledge fastest.Lakatos’s measure of knowledge growth is novel prediction, theadvantage going to which program yields more noveltheoretical predictions and moreconfirmed novelpredictions than its competitors. This is a historicist position sincedetermining whether something is a novel prediction requires detailedknowledge of the historical context of discovery in which thepredictive theory was produced (Lakatos & Zahar 1976).Unfortunately, however, Lakatos’s falsificationism had become sosophisticated that he could provide no rule for when it was rationalto abandon a degenerating research program that was being outstrippedby a more progressive one; for scientists, he said, may legitimatelymake risky choices. In any case, contrary to Kuhn, two or moreresearch programs may exist side-by-side. Lakatosian rationality doesnot dictate that researchers all join the same program.

What is the relation between a theory of scientific rationality and ageneral methodology of science? Like the Popperians from which hediverged, Lakatos held that methodologiesare theories ofscientific rationality (Curtis 1986). Similarly, a metamethodology(tasked with determining which methodology outperforms others) isidentical with a metatheory of scientific rationality. Lakatos’smetatheory recapitulates MSRP at the metalevel. According to Lakatos,his meta-MSRP shows that MSRP defeats competing methodologies, becauseit provides the best fit with the history of science in the sense thatit renders the history of science maximally rational. That is, MSRPmakes rational sense of both the intuitively rational episodes andsome that its competitors have to exclude as externally causeddeviations from the rational ideal. Indeed, itpredicts thatsome counterintuitive cases will be seen to be rational when examinedclosely.

Lakatos’s paper, “The History of Science and Its RationalReconstructions” (1971: 91) opens with a promising paraphrase ofKant (previously used by Hanson (1962: 575, 580) and by Herbert Feigl(1970: 4): “Philosophy of science without history of science isempty; history of science without philosophy of science isblind”. However, his use of rational reconstructions ofsupporting historical episodes—the science as it allegedly couldhave been done orshould have been done—made the actualscience look more internally correct (according to MSRP) than it was.Historians and philosophical critics replied sharply that this was notgenuine history and hence not a fair test (see Arabatzis forthcoming).

Lakatos and his followers (e.g., Worrall 1988, 1989) conceived MSRP asa fixed and final methodology by contrast with Kuhn’s,Toulmin’s, and (eventually) Laudan’s changingmethodologies. The idea that all previous history of science wasworking up to this final methodology that Lakatos was first todivine—the end-of-history for methodology, so to speak—wasone of the broadly Hegelian themes in Lakatos’s work. Anotherwas that there is no instant rationality as proposed by the formalapproaches of standard confirmation theory. Writes Daniel Little (inthe entry onphilosophy of history) “Hegel finds reason in history; but it is a latent reason, andone that can only be comprehended when the fullness of history’swork is finished… ”. The owl of Minerva flies out atdusk. For Lakatos rational judgments can only be made retrospectively.For example, one cannot judge an experiment as crucial at the time itoccurs, only in historical retrospect (1970: 154ff). Appraisals aremade with hindsight. (See the entry onLakatos.)

1.4 Methodological Anarchism

In his early work Feyerabend (1962) appealed to historical cases toreject Hempel’s account of explanation and Nagel’sparallel account of intertheoretic reduction (traditionally postulatedmechanisms of cumulative progress), on the ground that in actualhistorical practice meaning change occurs from one major theory to itssuccessor. Deducibility thus fails. It also more obviously fails becausethe two theories are typically mutually inconsistent. Accordingly, onecannot reason by traditional logical argument from one to the other.Feyerabend introduced his own conception of incommensurability intothis work. Anticipating his later broad pluralism, early Feyerabendalso extended the Popperian line on testing to a full-blownproliferationist methodology. Competing theories should be multipliedand tested against each other, because more empirical content isthereby brought to light than in testing theories in isolation. In hislater work, Feyerabend (1975, 1987, 1989) moved vehemently away fromthe positions of the Popper school. He vigorously rejected the idea ofa scientific method that makes science superior to other culturalenterprises. According to his “methodological anarchism”,any so-called methodological rule, including logical consistency,could be fruitfully violated in some contexts. That said, hiswell-known slogan, “Anything goes”, was widely read asmore radical than he intended, given his playful interactions with hisfriend Lakatos.

This later Feyerabend declared that his primary aim was humanitarian,not epistemological, so it was not his purpose to defend the rationalityof science. His attack on dogmatic, scientistic conservatism, bothwithin and without scientific communities, has methodological import,albeit negative import. Feyerabend was one of the first to stress thestrong historical contingency of scientific work, in context ofjustification as well as discovery, and he defended this contingencyat the methodological level as well. Thus there is no fixedrationality of science. For example, Galileo (he argued in historicaldetail) introduced a new sort of methodology, a new kind ofrationality, partly via rhetorical deception, partly with arrestingapplications of mathematics to basic mechanical phenomena.Galileo’s new vision happened to win out, but there is no pointin calling it either rational or irrational in any absolute sense.

Philosophers, retreating from concrete detail to their abstractformalisms, make science look far more rational than it is, stressedFeyerabend. “[H]istory, not argument, undermined thegods”, and also undermined Aristotelian science and severallater scientific orthodoxies (1989: 397, his emphasis). Feyerabendrejected “the separability thesis”, according to which ahighly contingent historical processes can furnish scientific productsthat are true and non-contingent, products that have achieved escapevelocity from history as it were (my expression). However, althoughnot as pronounced as in Lakatos, there remain traces of historicistconsequentialism in Feyerabend’s view, as when he wrote that“scientific achievements can be judged only after theevent” ([1975] 1993: 2). There is no “theory” ofscientific rationality in Feyerabend, only a historicist anti-theory,as it were; but he was not quite the irrationalist that critics tookhim to be. (See the entry onFeyerabend. For recent work on historical contingency, see Stanford 2006 andSoler et al. 2015.)

Feyerabend embraced the relativism implied by the positions justdescribed. In a late work,Science as Art, influenced by theprominent Viennese art historian Alois Riegl, he spoke of distinct,self-contained scientific styles at different periods that are muchlike the distinct styles in art (Ginzburg 1998). Such a view fit wellwith his sometime assertion that there is no scientific progress, justa succession or multiplicity of styles. Here there is a faintconnection to Kuhn’s early views, although the two menreportedly did not interact as much as one might expect while bothwere at Berkeley.

1.5 The Pragmatic, Problem-Solving Approach

Laudan openedProgress and Its Problems (1977) with the claimthat providing an adequate model of rationality is the primarybusiness of the philosopher of science but that no extantmethodologies fit actual science. In this book his idea of good fitwas fit with a selection of intuitively strong historical instancesthat any adequate theory must explain. (Laudan 1984 and 1996: ch. 7,later rejected the intuitionistic elements that gave normative punchto this model.) His response to the rationality question was topropose a thoroughgoing, explicitly pragmatic, problem-solving accountof science. Problem-solving had been an important element in previousaccounts, notably those of Kuhn and Popper, but Laudanreversed the usual account of scientific progress as atemporal succession of atemporal rational decisions. Instead ofdefining progress in terms of rationality, we should definerationality in terms of progress. We cannot measure progress in termsof approach to an unknowable, final, metaphysical truth, but we dohave reliable markers of progress in terms of numbers and relativeimportance of both empirical and conceptual problems solved bylong-term “research traditions”. Just as Lakatos’sresearch programs were a compromise between Popper and Kuhn, we canread Laudan’s “research traditions” as incorporatingelements of his major historicist predecessors, while departingsharply from other tenets of their work.

Many analysts have played with possible relationships between thesciences’ assumed rationality and assumed progressiveness. Thecentral issue for them is analogous to the question in Rodgers andHammerstein’sCinderella: Is science progressivebecause it’s rational, or is it rational because it’sprogressive? (Kuhn [1962] 1970a: 162, had asked: Does a field makeprogress because it is a science, or is it a science because it makesprogress?”) The underlying question is whether rationality isbasic and fundamental rather than derivative to something else. Thoselike Laudan who make it derivative need to defend their positionagainst the objection that they are committing a verificationistfallacy of confusing rationality itself (its constitutive nature) withthe criteria for applying the term ‘rational’. Aremomentary success or longer-term progressconstitutive ofrationality or merely consequential indicators of it (or neither)?

Be that as it may, since progress is a historical (history-laden)concept, so is rationality on Laudan’s conception, as it was onLakatos’s. The temporality of his account led Laudan tointroduce an important distinction betweenacceptance of atheory andpursuit that would explain how rationaltransitions to a new research tradition are possible. Scientistsshould accept the theory that,pro tem, has the greatestoverall problem-solving success, but pursue the tradition that nowenjoys a higherrate of success. Nearly everyone todayaccepts a distinction of this sort, although not necessarilyLaudan’s criteria of success.

LikeStructure and MSRP, Laudan’s model of sciencereceived much discussion, both constructive and critical. It faced theusual difficulties of how we are to count and weigh the importance ofproblems in order to have a viable accounting scheme. Historicists canreply that it is not their fault if this is a messy task, since thatis just historical reality, a reality that, if anything, favors expertjudgment over tidy decision algorithms.

Laudan (1984) agreed with Kuhn that the goals, standards, and methodsof science change historically as well as the theoretical andobservational claims, but his “reticulationist model”rejected as historically inaccurate Kuhn’s claim that sometimes they allchange together to constitute a (Kuhnian) revolution. Dramatic change in oneplace need not seriously disturb fixity elsewhere and rarely or never does. Hence,incommensurability is a pseudo-problem. Moreover, Laudan contended, hisreticulationist model overcomes the hierarchical problem that has ledthinkers such as Poincaré and Popper to make the goals ofscience arbitrary (the top of the hierarchy and hence the unjustifiedjustifier of what comes below), e.g., mere conventions. These authors have noway to rationally appraise the goals themselves, leaving their positions stuckwith an account of merely instrumental reason: efficiency relative toa given, arbitrary goal. By contrast, in Laudan’s model, theelements are mutually constraining, mutually adjusting, an ideaprominent in Dewey’s attack on hierarchy in his 1939. None takesabsolute precedence over the others. Thus, some goals are irrationalbecause present and foreseeable knowledge and methods have no way toachieve them or to measure progress toward them. (Laudan therebyrejected strong realist goals as irrational.) An advance in substantiveor methodological expertise can make it rational to embrace newstandards and also new goals.

The debate between Laudan and Worrall over the value of a fixedmethodology of science wonderfully exemplifies the persistence of theancient problem of change (Laudan 1989; Worrall 1989). How is itpossible to explain, or even to measure, change except in terms of anunderlying fixity? Doesn’t allowing change at all three ofLaudan’s levels—matters of scientific fact and theory,method and standards, and goals—leave us with a damagingrelativism? Worrall defends the fixity of Lakatos’s MSRP butagrees that it cannot be establisheda priori. Laudan’sreticulated model retains a more piecemeal and historically contingent fixity, as describedabove.

With all that said, the threat of relativism remains, for how cana good, non-whiggish historicist have a trans-historical measure ofprogress? Laudan’s answer was that we can whiggishly measurescientific progress by our own standards, regardless of what the goalsof the historical investigators were. This sounds right about what wedo. But if the reasons why the historical scientists in the trenchesmade the decisions they did do not really matter to us (or to anygiven generation), retrospectively, then how is rationality providinga methodological guide or causal explanation why historical scientistsmade the decisions they did? Their individual rationality would seemto become irrelevant. And why, then, is rationality the centralproblem of philosophy of science?

Departing sharply from traditional, non-naturalistic treatments ofnorms, Laudan addressed the is-ought problem head-on by advancing animportant and influential, pragmatic “normativenaturalism” whereby the acceptable norms are those bestsupported by successful historical practice—where, again,success is as we judge it today. On this view, norms have empiricalcontent. They are winnowed from the history of successful practice,again a broadly Deweyan idea (e.g., Dewey 1929). At Virginia TechLaudan and colleagues initiated a program to test the individual normspresent in various philosophical models of science against the historyof science (Laudan 1977: 7; Donovan et al. 1988). Like every majorphilosophical proposal, this one came under critical fire, in thiscase, e.g., for isolating individual methodological rules from theirhistorical contexts and for reverting to a traditional, positivistic,hypothetico-deductive model of testing. In short, critics complainedthat Laudan’s metatheory of rationality did not match hisfirst-order, problem-solving-progress theory of rationality. Andprofessional historians did not welcome this invitation tocooperation, since the project implied a division of labor thatregarded philosophers as the theoreticians proposing rules to test,while the historians were relegated to fact-grubbing handmaidens doingthe testing. To be fair, as a historicist philosopher, Laudan himselfhad done a good deal of historical work.

On another front, Laudan’s (1981) attempt to“confute” scientific realism on the basis of historicalexamples of major scientific change stimulated much discussion, sincethe status of realism had become a central issue in philosophy ofscience. Indeed, Laudan’s article helped to make it so.

1.6 Evolutionary Models of Scientific Development

Toulmin (1972) produced an evolutionary model of scientificdevelopment in terms of populations of concepts, a gradualist accountof scientific change that he considered more historically accurate andphilosophically defensible than Kuhn’s discontinuous model.Toulmin’s “concepts” are historically malleable, yet they arecharacterized by historicity. He quotes Kierkegaard: “Concepts,like individuals, have their histories, and are just as incapable ofwithstanding the ravages of time as are individuals” (1972:frontispiece). Toulmin held that biological, social, and conceptualevolution, including scientific development, are all instances of thesame generalized variation-selection-transmission schema, albeit withquite different concrete implementations. For Toulmin, disciplines(specialties) are analogous to biological species. He touted his modelas naturalistic, indeed ecological, but not in a way that excludesrationality. Rationality enters primarily at the selection level,determining which families of concepts (including methodological ones)get selected and reproduced. Rationality is not a matter of“logicality”, i.e., of sticking to a given logical orKuhnian framework through thick and thin. Rather, it is a matter ofadapting appropriately to changing circumstances. Like Newtonianforce, rationality has to do with change, not maintenance of the samestate. Thus no Kuhnian revolution is needed in order to break out ofan old conceptual framework.

As for the descriptive-normative problem, thinkers from Kuhn to RobertBrandom (e.g., 2002: 13, 230ff) have appealed to the common lawtradition as an instructive analogy, and Toulmin was no exception.Published legal cases provide legal precedents that later legalargumentation can cite for support. Over time, normative traditionsemerge. Explicit rules may be formulated by reflecting on the historyof precedents, but the practices typically remain implicit. There is awhiff of Hegelian, retrospective reconstruction in this idea ofextracting norms from patterned historical practices that embody themimplicitly and contingently. The main trouble with Toulmin’saccount, said critics, is that it is so vague and abstract that ittells us little about how science works. It would seem to apply tojust about everything.

Donald Campbell (1960, 1974) had previously defended the generalizedvariation plus selective retention schema, which he traced back toWilliam James. Popper regarded his own evolutionary account ofscientific development as similar to Campbell’s (1974). Dittofor David Hull (1988) with his more detailed evolutionary model.However, Hull rejected evolutionaryepistemology, as such,and denied that he was doing epistemology at all. (Evolutionaryepistemologies face the problem of why we should expect a contingentselectionist process to be truth-conducive: see the entry onevolutionary epistemology. Assuming that it is can also tempt one to fall into whiggismregarding the past in a social Darwinist sort of way.) Hull rejectedToulmin’s biological species analogy, as based only onfeature-similarity rather than on the historical-causal continuity ofgenuine biological species. Hull’s book reflected his own deepinvolvement in the controversy between cladists, evolutionarysystematicists, and pheneticists over biological classification. (Heserved terms as president of both the Society for Systematic Biologyand the Philosophy of Science Association.) Hull generalized hisimportant biological concepts of replicator (gene) and interactor(organism) to scientists and communities. His central unit of and foranalysis was the deme, or research group, in its competition withothers.

Hull (1988) argued that the success of science can be explained by aninvisible hand mechanism rather than in terms of rationaldecision-making. He did not deny that most scientists regardthemselves as rational truth seekers, but on his account the primarymotivation is the drive for professional recognition and credit viapositive citation by others, and avoidance of violations ofinstitutionalized standards. The term ‘rationality’ doesnot even appear in the book’s index. Nonetheless, theinstitutional incentive structure of science works to producegenerally reliable results and scientific progress, so that, torationality-minded philosophers, science looksas if it isdriven by the intentional rationality of its practitioners. We mightsay that, for Hull, rationality explains nothing without causalbacking, but once we bring the causal mechanisms into play, there isno longer a need to foreground rationality, at least not intentionalrationality.

The better [scientists] are at evaluating the work of others when itis relevant to their own research, the more successful they will be.The mechanism that has evolved in science that is responsible for itsunbelievable success may not be all that “rational”, butit is effective, and it has the same effect that advocates of scienceas a totally rational enterprise prefer. (1988: 4)

Like Adam Smith’s view of the invisible hand regarding altruismand the public good, rationalists can interpret Hull’s accountas broadly Hegelian in the sense that the rationality of scienceemerges (insofar as it does) from the complex social interactions of scientistsand groups of scientists going about their normal business in ordinaryways that satisfy community norms and incentive structures, not fromtheir explicit intentions to make rational decisions. While Hull gaveclose attention to these social interactions and to the institutionsthat enable them, he claimed that his appeal to social factors wasinternal to science rather than external.

1.7 New-Wave Sociology of Science and the Realist Reaction

Left relatively untouched by historicist philosophers during theBattle of the Big Systems was the internal/external distinction. Thephilosophers, consonant with traditional sociology of science (e.g.,Merton 1973) and sociology of knowledge more generally, defended akind of “inertial principle” (Fuller 1989: xiiietpassim): social and psychological factors such as economic andpolitical interests and psychological dispositions should be broughtinto play only to explain deviation from the rational path. Thisdistinction began to erode already in Kuhn, who stressed the socialfactorsinternal to the organization of science itself:science education, the strong role of scientific communities withtheir distinctive cultures, etc. (See also Lakatos on comprehensivetheories of rationality that can turn apparent external considerationsinto internal ones, and Hull 1988 on career advancement.)

In the 1970s, new-wave sociologists of science quickly rejected thedivision of labor implied by the inertial principle and took sociologyfar beyond where Kuhn had left it (much to his chagrin). Thesesociologists insisted that sociology, via social interests and othersocial motivational causes, had much to say about the internal,technical content of science—so much, in fact, that it was notclear that there was any room left for the rational explanations ofthe philosophers. The Edinburgh Strong Programme founded by DavidBloor and Barry Barnes (see Bloor 1976), the Bath relativist school ofHarry Collins and Trevor Pinch (Collins 1981), and laterconstructivist work of Bruno Latour and Steve Woolgar (1979), KarinKnorr-Cetina (1981), Steve Shapin (1982), Shapin and Simon Schaffer(1985), and Andy Pickering (1984) were important early developments.(See Shapin 1982 for a helpful discussion.)

Since the new sociology of science was also heavily based onhistorical case studies, we find more radical historicisms challengingless radical ones. Although the sociologists often disagreed amongthemselves, as the philosophers did, the general thrust of their workwas that the philosophical historicists had failed to takesocio-political context into account and thus were still too muchwedded to the old, abstract, acausal ideals of rationality,objectivity, and progress toward truth. Much sociological work wasexplicitly anti-realist and relativist, at least as a methodology.

Most philosophers of science strongly rejected the new sociology asrelativist and irrationalist, the non-historicists among them adoptingversions of strong realism, according to which mature science canknowingly, on internalist grounds, arrive at theoretical truth andgenuine reference to theoretical entities, or closely enough. Theeventual upshot was “the Science Wars” of the 1990s. Bynow (2017), the sides in this dispute have mellowed, fruitfulconversations are taking place, and some degree of reconciliation hasoccurred (see Labinger & Collins 2001). Work by feminists inscience studies such as Donna Haraway (2004) and feminist philosophersof science such as Helen Longino (1990, 2001) and Miriam Solomon(2001) have rejected assumptions common to both sides in the debate,thereby opening the way to their more pluralistic, interactive, andless hierarchical options. Distinct prominent approaches to socialepistemology by philosophers include Fuller 1988, Goldman 1999, andRouse 2002. (See the entries onsocial epistemology,scientific method,scientific realism, and thesocial dimensions of science as well as the feminist entries referenced above.)

Some of the sociological work had a postmodern cast, and so didcontributions by some philosophers. For example, Richard Rorty’sversion of historicist pragmatism rejected correspondence theories oftruth and the related idea that we humans have somenaturalized-theological obligation faithfully to representmetaphysical nature with our science. He spoke suggestively butvaguely of major transformations in the sciences (or anywhere else inculture), such as that achieved by Galileo, as the invention of a new“vocabulary” that worked well enough for certain purposesto catch on, but not as new truths established by logical reasoning. Asfor rationality itself, it is a matter of maintaining an honest, civil“conversation”:

On a pragmatist view, rationality is not the exercise of a facultycalled “reason”—a faculty which stands in somedeterminate relation to reality. Nor is [it] the use of a method. Itissimply a matter of being open and curious, and of relyingon persuasion rather than force. (1991: 62).

So rationality is not the key to scientific success, and it has asmuch to do with rhetoric as with logic. Pragmatists, he said, preferto speak of the success or failure of problem-solving efforts, ratherthan rationality or irrationality (1991: 66).

A view sometimes ascribed to Rorty’s hero Dewey is thatrationality is not ana priori, universal method of thinkingand acting properly; rather, it is like a box of intellectual tools,each of which, as humans have learned from craft experience, work better thanothers in various situations, the result being what might be called a“teleonormative” conception of rationality.

2. Rationality and History: Some Basic Questions

Many of the issues raised by and about historicist conceptions ofrationality remain unresolved, but the approach has the merit ofbringing back into discussion several interrelated questions.

1. What is it to be rational, anyway, once we situate agents inreal-life socio-cultural situations?
2. Is an account of rationality something discovered rather thanhumanly constructed?
3. Is a theory of rationality something that can be fixedapriori, or can it (must it?) be naturalized, in whole or in part,i.e., shaped by a broadly empirical mode of inquiry?
4. Is there just one, unique, correct conception or theory ofrationality, of universal applicability?
5. Can (should) our concept of rationality be relativized tospecifically human capabilities and to specific kinds ofdecision-action situations, or could it turn out, by some universalstandard, perhaps realized by future artificial intelligence or by(other) aliens, that we are all terribly non-rational, scientistsincluded?
6. Is scientific rationality special in some way, as distinct fromrationality in general?
7. Is a theory of specifically scientific rationality the same as anaccount of scientific method? (If so and there is no unique scientificmethod, then there is no single, general account of scientificrationality either.)
8. Is second-order rationality possible, i.e., rational changes inscientific goals and standards of rationality themselves?
9. Should a metatheory of scientific rationality match the theory offirst-order methodological rules?
10. Do we even need a theory of scientific rationality, either toexplain research at the microlevel or scientific development at themacrolevel? If so, precisely how does appeal to rationality explain?Does it provide a causal mechanism?
11. How is the individual rationality of a researcher related to therationality of the working group and to the community of specialistsas a whole? In other words, how does (or should) the distribution ofcognitive labor affect the discussion of rationality?
12. Are rationality assessments instantaneous (given the logical ormathematical relations of the available information) or do they (atleast sometimes) require historical retrospect or prospect?
13. What good is the historical study of how basic categories ofdescription such as ‘fact’, ‘experiment’,‘objective’, ‘replication’, and ‘novelprediction’ change over time? What does such history tell us, ifanything, about human inquiry or epistemology?
14. What does ‘historicism’ mean in this context, andwhat could a constitutively historicist theory of rationality be?

3. Historicism Then and Now

Nineteenth-century philosophers and (especially) historians arecommonly credited with the modern “discovery” of history,especially political history, via developing the discipline ofevidence-based, interpretive and explanatory historiography. Hegelhistoricized Kant at the beginning of that century, but it wasprimarily German historians such as Ranke, Droysen, Windelband,Dilthey, Rickert, and Weber who developed competing conceptions ofwhat is required for rigorous historical research. (For an in-depthsurvey, see Beiser 2011.) These historians were concerned to develophistoriography aswissenschaftlich but autonomous from thenatural sciences, where positivism reigned. They also rejected thegrand, Hegel-type philosophies of history. Toward the end of thecentury, this opposition produced theMethodenstreit, thevehement debate over differences between the natural sciences(Naturwissenschaften) and the socio-historical sciences(Geisteswissenschaften). Historicists saw naturalism andmaterialistic mechanism as threats.

The connection of the historicization of philosophy of science in the1960s to the German historicist tradition is indirect, given thetime-gap of decades. However, the historicists of scientificrationality discussed in this article did (or do) agree to several ofthe following (overlapping) tenets, most of them traceable tonineteenth-century antecedents. There exist tensions among thefollowing claims, so internal disagreement among historicists is to beexpected.

1.The historicity of all things. Virtually all things comeinto existence and pass away in historical time. Nothing is guaranteedto be fixed and permanent, written in the stone of the universe.

2.History vs. a priori reason or logic alone. Human beingsdo not possess a faculty ofa priori reason capable ofsurveying the space of all logical possibilities. The emergence ofnon-Euclidean geometry illustrates this point. Human inconceivabilityis not an adequate criterion of either logical or historicalpossibility.

3.Our historical boundedness: anti-whiggism and the principle ofno privilege. We inquirers are also historically situated. Whilewe are not slaves to our cultural context, we can escape it onlypartially and with difficulty. Our horizons sometimes prevent us fromrecognizing our own presuppositions, not to mention futurepossibilities. Wrote Mary Hesse: “our own scientific theoriesare held to be as much subject to radical change as past theories areseen to be” (1976: 264). Although we have good reason to holdthat our science is superior to that of the past, this does not conferan absolute, ahistorical privilege on our science. Rather than succumbto this perspectival illusion, we must imagine that our successors maylook at us as we see our predecessors. We, too, are just atransitional stage into a future that is likely to include much thatis beyond our present horizon of imagination. We must avoid the flatfuture illusion that sees the future a tame continuation of thepresent (Nickles forthcoming).

4.History as endlessly creative, thus an endless frontier.Strong historicists think an endless frontier is likely, history asopen, and productive of perpetual novelty (no agency intended).

5.Historical content of theory of justification: The complexityof history. History is too complex and too subtle to be capturedby a fixed, formal system or in terms of the dynamical relationshipsof a set of “state variables”. Logical and probabilisticsystems alone are crude tools for capturing the reasoning of realpeople, scientists included. Besides the subtle, contextual reasons,innovative scientists work at moving research frontiers(“context of discovery”) and, so, must make many decisionsunder uncertainty (not only under mere risk). Rationality has more to do withappropriate response to change than with sticking rigidly toone’s initial standpoint. This challenge strikes at the heart oftraditional accounts of context of justification, hence at the heartof traditional philosophy of science. Thinkers from Kuhn to vanFraassen (2002: 125) have taken a dim view of confirmation theory,although Bayesians have made valiant attempts to capture historicistinsights. (For examples, see Salmon 1990 and Howson & Urbach1993).

6.Consequentialism and history as a judge. Frontierepistemology teaches that we can often only learn which modes ofaction are successful via historical experience of the consequences.(Non-historicists can reply that the eventual judgment is not itselfhistorical but only delayed, because based on evidence gathered overtime.) In its strongest form, historical judgment replaces “theLast Judgment”, the judgment of God, as reflected in the commonexpression “the judgment of history”. (Of course, thisview is itself anti-historicist in its conception of finality.)

7.Genetic, genealogical understanding. Since nearlyeverything is the product of historical development or disintegration,studying its historical genesis and dissolution is key tounderstanding it. Genetic fallacies are avoidable by includingdevelopment and maintenance as part of the narrative, sincedevelopment can be transformative. Today many writers are exploringthe biological and socio-cultural evolutionary origins of humanrationality, going far deeper, historically, than to recent historicaldevelopments such as the so-called Scientific Revolution.

8.Historical skepticism, incommensurability, and relativism.One role of historiography is to debunk myths. As such, it can beliberating, as when we see that institutions and conceptual frameworksare, to a large degree, human constructions with a historical origin,not things irremediably fixed in the foundation of the universe. For thatvery reason it produces a degree of skepticism toward all humanthings. Although the natural world shapes human cultures, includingscientific ones, it far from dictates a single, fixed culture.Historiography discloses that human enterprises, including thesciences, are imbedded in deep cultures with their distinctive norms.There is no “God’s-eye”, history-neutral set ofmeta-norms, no “Archimedean point” from which thesecultures can be objectively compared. Thus it is difficult orimpossible to evaluate all science with a single standard. Here lurksthe problems of cultural incommensurability and relativism.

9.Pluralism. Methodological pluralism is a naturalconsequence of historicist approaches. Historical study discloses thatthe various sciences employ quite different methods and often harborcompeting research programs. The emergence of philosophy of biology asa specialty area in the wake of the 1959 Darwin centennial addedsubstance to this claim. (For entries into the pluralism literature,see Dupré 1993; Galison & Stump 1996; Mitchell 2003; andKellert et al. 2006.)

10.Science as a model of rationality. On this theme,historicists are divided. Some strong historicists, especiallyFeyerabend, Hull, and thoroughgoing social constructivists, deny thatscience is rationally or methodologically special among humanenterprises.

11.Science as a model of progress. This, too, is practicallyaxiomatic among philosophers of science. The idea of history“itself” as progressive came in with the Enlightenment andwas severely challenged by the world wars.

12.Historicism as half-naturalistic. Historicist accounts donot appeal to supernatural factors or to factors beyond thepossibility of human cognition such as clairvoyance or themetaphysical truth about reality. Historicists usually take a secondstep toward naturalism in considering humans as biologically limitedbeings, but they resist reduction to the natural science brand ofnaturalism. Philosophical historicists also reject the reduction ofnorms to facts. (But, late in life, R.G. Collingwood may have come to hold astrong version of historicism according to which philosophy reduces tohistory: see the entry onCollingwood. Some new-wave sociologists may have held a parallel reductionist viewabout philosophy and sociology, insofar as philosophy was worthsaving.)

13.Major historical change as emergent—against intelligentdesign and the conscious model. Many historical developments arenot deliberately chosen or designed but emerge from numbers of peoplecarrying out their individual and collective activities. The rise of the nation-stateand of the international capitalist economic system were not theproducts of centralized, rational planning, nor were modern scienceand technology, although there were, of course, many micro-instancesof such planning. This point applies to the idea of scientific method,which tradition often depicted as clairvoyantly, intelligently guidingscientific innovation. But as Hume already anticipated, no method isguaranteed in advance to work in a novel domain. Methodologicalinnovation typically follows rather than precedes innovative work(Hull 1988; Dennett 1995; Nickles 2009, forthcoming). This is abroadly Hegelian idea.

14.Strong historical determinism is mistaken. A controversyamong historicists of various stripes is whether there are “ironlaws of historical development”. Hegel and Marx, in quitedifferent but related ways, believed in a teleological conception ofhistory, that “it” was working its way inevitably throughknown stages toward a final goal that would amount to “the endof history” in the sense that deep historical change would nowcease. This is the view that Popper termed “historicism”inThe Poverty of Historicism (1957; see also his 1945).Popper vehemently rejected this version of historicism, as dovirtually all historicist philosophers of science today. For them,history is non-teleological and highly contingent. This includesKuhn’s ([1962] 1970a) model, although the latter does posit analmost inevitable, unending alternation of normal and revolutionaryperiods—a final pattern without end, as it were.

15.Hermeneutic interpretation. The received, covering-lawmodel of explanation is inadequate to explain historical action,including that of scientists and communities of scientists. Kuhndescribed his method as hermeneutic, but few historicist philosophersof science are full-blown hermeneuticists or as fully committed toempathic understanding as were some of the classic Germanhistoricists. Most or all historicists are somewhat partial tonarrative forms of explanation. (See the entry onscientific explanation.)

4. Related Developments and Further Challenges

The battle of the big systems seems to be over, and likewise for theheyday of interdisciplinary departments and programs of history andphilosophy of science (but see below). So are historicist conceptionsof rationality dead? Despite claims that historicist philosophy ofscience has been “withering on the vine” (Fuller 1991), itis fair to say that historicist influences remain important, but in asubtler way. Most philosophers of science are more historicallysensitive than before, whether or not they identify as historicists.Historicist interests have expanded into “the naturalisticturn”, “the models turn”, and “the practiceturn”, which includes interest in contemporary practices, and,to a lesser degree, in future history (Nickles forthcoming).

Moreover, in parallel developments, the classical conception ofrationality is under attack on many fronts. Herbert Simon (1947)introduced the ideas of bounded rationality and satisficing. Simonlater championed the need for a heuristic approach to problem solvingby humans and computers (Newell & Simon 1972). Various flavors ofartificial intelligence then led the way in the methodology of problemsolving, with heuristics as a central topic and no longer the temporaryscaffolding of positivism and Popper. Simon’s program inadaptive, “ecological rationality” is now being expandedby Gerd Gigerenzer and the Adaptive Behavior and Cognition group inBerlin (Gigerenzer et al. 1999). Simon’s approach and the“heuristics and biases” program of DanielKahneman and Amos Tversky (Kahneman et al. 1982), plus work by thelatter on prospect theory, triggered the emergence of behavioraleconomics, which rejects the neo-classicalhomo economicusrationality model. Philosopher Christopher Cherniak’sMinimal Rationality (1986) also brought out sharply howidealized were traditional philosophical assumptions aboutrationality. In other directions, some computer scientists arechallenging the anthropocentrism of received conceptions of rationalinference by asking why artificial intelligence, including deeplearning, should be restricted to human forms of reasoning. Meanwhile,biologists and philosophers are studying the evolution of rationality(Okasha & Binmore 2012), and ethologists ask why we shouldwithhold attributions of rationality to animals from chimps andelephants to octopuses, simply because they seem to lack a human sortof conceptual language.

Nonetheless, there is wide agreement that historicist accounts ofscientific rationality cannot fully supplant traditional views. Forexample, there surely does exist some “instantrationality” even at research frontiers. One finds a widevariety of decision contexts there, and some of these decisions willbe uncontroversially warranted at that time and in that context, whileothers will not be. Hesse (1980) and many others (see Radnitzky &Andersson 1978) raised the issue of how to generalize from historicalcase studies, for citing case studies can be like citing theBible. One can cherry-pick one’s case studies tosupport most any position. In any case it is fallacious to generalizefrom a few, highly contextualized case studies to conclusions aboutall science at all times. Early historical work in social studies ofscience faced the same problem. Ironically, such generalizationabstracts away from the historicity of the case studies themselves.The attempt to replace inductive generalization by testing via an H-Dmodel also runs into trouble, as we noted in connection to theVirginia Tech project. And why should case studies from two or threehundred years ago be taken seriously when science itself has changedsignificantly in the meantime? Partly for this reason Ronald Giere(1973) contended that it was necessary to study only today’sscientific practices, that philosophers had no special need ofconsulting historians.

Late in life, Kuhn himself, surprisingly, rejected the case-study method as toowedded to the traditional view of science as a direct search for thetruth about the universe. The first generations of historical inquiryby philosophers and sociologists so shockingly revealed the presenceof many non-epistemic factors and the general failure of any methodfully to justify scientific beliefs, he said, that skepticism was theresult. The more people learned about how science is actually done,the more skeptical they became. Declared Kuhn, we can more securelyderive historical patterning “from first principles” and“with scarcely a glance at the historical record itself”(1991: 111ff). This is not a complete departure from history, however,for it begins from what he termed “the historicalperspective”, a non-whiggish understanding of the decisionsactually available to the historical actors in their own context.Kuhn’s main point is that such decisions should be consideredcomparative (“Is this item better than that one, given thecontextual knowledge and standards?”), not as judgments of truthor probability. This move reduces the problem of understandingbehavior in rational terms to something manageable, he explained.Developing this point, Kuhn said, will bring the only defensible sortof rationality back into scientific practice in a way that largelyavoids the old problems of incommensurability. It will also provide adefensible concept of scientific progress and of scientificknowledge (almost by definition)—knowledge as what thescientific process produces. This historical perspective was part ofKuhn’s project of developing a biological analogy for thedevelopment of science, wherein disciplinary speciation eventscorrespond to revolutions. Kuhn held that his approach applied to allhuman enterprises, not just science (Kuhn 2000).

Recently, Rogier De Langhe (2014a,b,c, 2017) has been developing abroadly Kuhnian, two-process account of science from an economicsstandpoint. Instead of doing a series of historical cases, De Langheand colleagues are developing algorithms to detect subtle patterns inthe large citation databases now available. In sum, both late Kuhn andearly De Langhe are now appealing to the history of science in a moreabstract, or perhaps comprehensive, manner, a manner complementary to the two-process approach ofMichael Friedman (below).

Another general challenge for historicists and others concerned withthe rationality of science is how to factor the division of labor inscience into a model of scientific rationality. How does individualrationality (the traditional focus of economists as well asphilosophers) relate to the collective rationality of working groupsor entire specialist communities? (See Sarkar 1983; Kitcher 1993;Mirowski 1996; Downes 2001; De Langhe 2014b; Latour 1987 and later for hisactor-network theory; and the entry onsocial epistemology.) Feminist philosophers such as Longino (1990, 2001) and Solomon (2001)have proposed more thoroughgoing social epistemologies of science thatgo beyond the problem of division of labor, which, in their view, isstill often treated individualistically.

5. Integrated HPS and Historical Epistemology: What Good Are They Regarding Scientific Rationality?

The attempt to integrate historiography and philosophy of science hasa troubled history. Several joint departments and programs were formedin the heady 1960s, just as much historiography of science was turningaway from internalist approaches. As professional historians andphilosophers came to realize that their interests differed, many ofthese programs did wither.

In the meantime, several philosophers have engaged in seriousinternalist studies for philosophical purposes, usually focusing on“big names” such as Galileo, Newton, Lavoisier, Darwin,and Einstein, or big developments such as the route to the doublehelix. More recently, scholars such as Nancy Nersessian with her“cognitive history” project (1995) have employed newresources from the cognitive sciences in this regard, a move neglectedby Kuhn himself and resisted by sociologists concerned by thephilosophers’ neglect of the social basis of the knowledgeenterprise. (See also Giere 1988; Bechtel & Richardson 1993;Darden 2006; Andersen et al. 2006; Thagard, e.g., 2012.) Historians,meanwhile, have focused on social history and, more recently, onsocial microhistory and lesser-known figures, including women, ratherthan on the internalist moves of big-name scientists. Consequently,historicists today still feel the need to respond to Giere’s(1973) question of whether history and philosophy of science can be anintimate marriage.

Since 1990 promising new movements have emerged that bring togetherphilosophy of science and historiography of science. First,philosophers of science became interested in the historical emergenceand professionalization of their own field. Early work quicklydestroyed some myths about the Vienna Circle, for example. The primaryorganization here is the International Society for the History ofPhilosophy of Science (HOPOS), with its own journal and regularmeetings. More recently, the Integrated History and Philosophy ofScience (&HPS) organization has sponsored several conferences withthe goal of maintaining the standards of both fields rather thancompromising one for the supposed advantage of the other. (Forbackground, see Schickore 2011, 2017. Consult the &HPS website forother contributors.)

Theodore Arabatzis (forthcoming) distinguishes two ways of integratinghistory and philosophy of science: the familiar “historicalphilosophy of science” (HPS), usually based on“historical” case studies; and the less familiar“philosophical history of science” (PHS). It is well knownthat historians have found most philosophical work of little use, andArabatzis aims to help correct the asymmetric relationship betweenhistory and philosophy.

[P]hilosophical reflection on these concepts can behistoriographically fruitful: it can elucidate historiographicalcategories, justify historiographical choices and, thereby, enrich andimprove the stories that historians tell about past science as aknowledge-producing enterprise.

Labels for movements can be arbitrary and misleading, but several ofthe authors cited by Arabatzis have been identified with a movementusually called “historical epistemology”, the goal ofwhich is to combine excellent history of science with philosophicalsophistication or excellent philosophy with more historicalsophistication than is usually found in case-studies approaches. Giventhe epistemological focus, here is where we might expect to find thegreater concentration of work relevant to questions of scientificrationality. The epicenter of the movement is the Max Planck Institutefor the History of Science in Berlin, whose directors over the years,Lorenz Krüger (who died before he could assume the post),Lorraine Daston, Hans-Jörg Rheinberger, and Jürgen Renn,have promoted historical epistemology. A recent, special issue ofErkenntnis (Sturm & Feest (eds.) 2011) on historicalepistemology derives from a conference at the Institute. In theirintroductory essay to the special issue, the co-editors, Uljana Feestand Thomas Sturm, ask “What (Good) is HistoricalEpistemology?” (Feest & Sturm 2011). The special issueincludes a baker’s dozen authors who develop and/or critiquevarious approaches to historical epistemology. The participants rangefrom older hands such as Philip Kitcher, Michael Friedman, and MaryTiles to more recent contributors such as Jutta Schickore andFeest. (See Tiles & Tiles 1993 for an early philosophicalintroduction to the field.)

Feest & Sturm (2011) divide the movement into three streams. One streamstudies historical changes in epistemology-ladenconceptssuch as objectivity, observation, evidence, experimentation,explanation, and probability. How do new concepts emerge? How are theystabilized? At what point do they become conscious rather thanremaining implicit in practice? How do they shift over time and howwell do they travel to different scientific contexts (cf. Howlett& Morgan 2011)? Insofar as they are initially metaphorical, how dothey become dead metaphors? How do they fade out of use? LorraineDaston’s work is a good example of this approach (e.g., 1988,1991; Daston & Galison 2007; Daston & Lunbeck 2011). Thismeans looking at the evolution of concepts or organizing“categories” of action and thought within a historicallyconfined project, however interdisciplinary it mightbe—something between the eternal, global, and maximal oftenfavored by philosophers and the evanescent, local, and contingentfavored by many historians. Gone is the old-fashioned“conceptual history” of the sort exemplified by MaxJammer’s (1957),which traces “the concept” of force from ancient Egypt tothe twentieth century. Wrote Daston in an early paper:

To my mind, the most able practitioners of historical epistemologythese days are philosophers rather than historians—I think ofthe remarkable recent work of Ian Hacking and ArnoldDavidson—although I think they, intellectual historians, andhistorians of science might well make common cause in such a venture.(1991: 283, footnote omitted; see also Davidson 2002)

Daston then asks, “What good is historical epistemology?”Her opening (but later qualified) suggestion is that it goes part waytoward “releasing us from our bondage to the past by haulingthat past into conscious view”, although we must recognize thatcalling attention to the contingent origins of something is notsufficient to debunk it, upon pain of committing a genetic fallacy.Nor can we simply reject something without having an alternative toput in its place. “That is, historicizing is not identical torelativizing, much less to debunking”.

The second strand of historical epistemology identified by Feest andSturm in their introduction to the special issue focuses on the trajectories of theobjects ofresearch—“epistemic things”—rather than onconcepts, and here the well-known work of Rheinberger (1997, [2006]2010a, [2007] 2010b) is emblematic. Renn (1995, 2004) represents thethird approach, an attempt to understandthe longer-term dynamics ofscience. For example, Renn attempts to solve several mysteries abouthow Einstein was able to accomplish the relativity revolution. Hisanswer takes into account the long history of developments in distinctfields that Einstein was able to bring together, partly because of hiswide philosophical and other cultural interests. Renn looks atlong-term developments by analogy with biological development. NortonWise (2011) also brings biological metaphor into play. He observesthat historical narrative as a form of explanation is now makingserious incursions into physics, in the physics of complex or highlynonlinear systems. “Covering law” explanations are notavailable there, he says, and sometimes we must resort to simulationsin order to understand how systems evolve. “We know what we cangrow”.

Running through much historical epistemology is a century-long line ofneo-Kantian thinking, from Ernst Cassirer and the Marburg school toReichenbach and Carnap and then to Kuhn, Ian Hacking, MichaelFriedman, Daston, Renn, and others. Theirs are diverse versions of thetwo-process view introduced inSection 1.2above. On this view, there are long-term socio-cognitive stabilities(not necessarily the paradigms or research programs discussed above)that have a beginning, middle, and end in historical time. They arehistoricized Archimedean points or platforms that organizehuman experience, rather than fixed Kantian categories. But, likeKant’s categories, they are presuppositions that define howcoherent perception and the formation of true or false propositionsare possible.

Friedman speaks of these as “historically contingent but constitutivea prioris”. His 2011 takes first steps beyond the two-processdynamic of his 2001 to address the problem of changing conceptions ofrationality (i.e., intersubjective objectivity) and to bring in awider social dimension. Like Renn, Friedman makes philosophicalreflection a key to understanding changes so rapid that they amount todiscontinuities. Up to a point he defends Kuhn on the existence ofscientific revolutions and incommensurability. Kuhn ran into troublewith incommensurability and relativism, he says, for failing toinclude the history of scientificphilosophical reflectionthat parallels the first-order, technical scientific work itself.Friedman’s leading example is also the relativityrevolution.

Why do philosophers need to appeal to serious history of science? Fromthe beginning, Friedman has answered this question by insisting on theimportance of the history of science to locate the emergence ofphilosophical ideas in their historical scientific context and viceversa—thus to understand theinteraction between whatis commonly called scientific work and philosophical work (Domski& Dickson 2010: 4). For example, Newton’s mechanical systemof the world was shaped by philosophical and theological intereststhat Newton and his contemporaries considered directly relevant(internal not external), as well as socio-political interests. Andlikewise for Kant and Poincaré and Einstein and many otherthinkers, great and small. To the degree that we retain aninternal/external distinction, it is historically relative. Unlikemost other historical philosophers, Friedman furnishes the intricatetechnical and contextual detail to support such claims.

Inspired by Friedman’s approach is the rich collection,Discourse on a New Method: Reinvigorating the Marriage of Historyand Philosophy of Science (2010), edited by Mary Domski andMichael Dickson, and containing a book-length response (Friedman2010). Their introduction to the volume is a “manifesto”for “synthetic history” (2010: 11ff, 572ff). This sense of‘synthetic’ is not opposed to ‘analytic’, theyinsist. For example, rather than separating out the mathematical,physical, philosophical, theological and other social-contextualconstituents of Newton’s work for separate disciplinarytreatment, synthetic history follows Friedman in exploring the waysthese relate to one another to achieve an outcome with a satisfyingconvergence (2010: 15ff). Although inspired by Friedman’s work,the manifesto denies that Friedman’s two-process view isessential to synthetic history. (See also the extensive discussion ofFriedman by Menachem Fisch (forthcoming), a work centered on GeorgePeacock’s struggle with rational consistency that helped producea transformation in nineteenth-century mathematics.)

A somewhat different sort of two-levels position is the“historical ontology” of Ian Hacking. Hacking (2002, 2012)cites Foucault’s “discursive formations”(epistèmes) and Alistair Crombie’s “stylesof scientific thinking” (Crombie 1994) as inspirations. Examplesof such styles are the Greek discovery or invention of axiomaticgeometry, the laboratory science that emerged in the ScientificRevolution (Shapin & Schaffer 1985), and modern probability theoryand statistical inference (Hacking 1975). Hacking returns toKant’s “how possible?” question, the answer to whichestablishes the necessary conditions for a logical space of reasons inwhich practitioners can make true or false claims about objects andpose research questions about them. And Hacking also historicizes theKantian conception.

The historicala priori points at conditions whose dominionis as inexorable, there and then, as Kant’s syntheticapriori. Yet they are at the same time conditioned and formed inhistory, and can be uprooted by later, radical, historicaltransformations. T.S. Kuhn’s paradigms have some of thecharacter of a historicala priori. (Hacking 2002: 5)

…

[S]cientific styles of thinking & doing are not goodbecause they find out the truth. They have become part of ourstandards for what it is, to find out the truth. They establishcriteria of truthfulness. … Scientific reason, as manifested inCrombie’s six genres of inquiry, has no foundation. The stylesare how we reason in the sciences. To say that these stylesof thinking & doing are self-authenticating is to say that theyare autonomous: they do not answer to some other, higher, or deeper,standard of truth and reason than their own. To repeat: No foundation.The style does not answer to some external canon of truth independentof itself. (2012: 605; Hacking’s emphasis)

As in early Kuhn, there is a kind of circularity here that is perhaps notvicious but, quite the contrary, bootstraps the whole enterprise.Hacking describes changes in historicala prioris as“significant singularities during which the coordinates of‘scientific objectivity’ are rearranged” (2002:6).

Unlike Kuhnian paradigms, several of Hacking’s styles ofthinking and doing can exist side by side, e.g., the laboratory andhypothetical modeling traditions. Yet people living before and afterthe historical crystallization of a style would find each othermutually unintelligible. Hacking recognizes that Kuhnian problems ofrelativism lurk in such positions. “Just as statistical reasonshad no force for the Greeks, so one imagines a people for whom none ofour reasons for belief have force” (2002: 163). This sort ofincommensurability is closer to Feyerabend’s extreme cases (asin the ancient Greek astronomers versus their Homeric predecessors)than to Kuhn’s “no common measure” (2002: chap. 11).Writes Hacking,

Many of the recent but already “classical” philosophicaldiscussions of such topics as incommensurability, indeterminacy oftranslation, and conceptual schemes seem to discuss truth where theyought to be considering truth-or-falsehood. (2002: 160)

For an illuminating exposition and critique of Hacking’sposition, see Kusch (2010, 2011).

A still more integrative role for historical epistemology isarticulated by Hasok Chang (2004, 2012). Chang is a nonrealist whoboldly goes beyond the case-study genres of both philosophers andprofessional historians to propose what he terms “complementaryscience”, a fully integrated historical and philosophicalapproach that does not stop with pointing out historical contingenciesbut also investigates them scientifically, e.g., by repeating andextending historical experimental practices. Chang’s idea isthat complementary science can preserve previously gained knowledgeand unanswered questions now in danger of becoming lost, and can evenbuild upon them as a complement to today’s highly specializedscientific disciplines. The results can be published as genuine, ifnon-mainstream, scientific contributions. For example, in his own workhe tries to bring the debate over phlogiston to life as well as thatover the nature of water and the question of its boiling point. Forhis work, Chang leaves both his armchair and the library, for he needsscientific equipment and laboratory space in addition to the usualscholarly materials.

Historical epistemology faces a variety of criticisms, including someinherited from the Battle of the Big Systems, e.g., whetherrationality and objectivity can be locally preserved during majortransformations and how to have thoroughgoing historicity, includinghistorical relativity, without full-blown relativism. Generalizationproblems still lurk at the meso-scale of historical epistemology. Somecritics question whether historical epistemology is anything new,sometimes complaining that it just revives traditional history ofideas. Some would question its neo-Kantian underpinnings. For example,how can we really identify and individuate the“categories” employed by scholars such as Hacking andDaston? (See Kusch 2010, 2011 and Sciortino 2017.) Skeptics ask whatdifference historical epistemology makes to science, history, orphilosophy of science. Is it more than a faddish relabeling of workalready well underway? Are new historical and/or philosophical methodsrequired to conduct such a study? Given its different strands, is itcoherent as a movement? Various adherents disagree on what it includesand even what to call it. Although Daston declares thatHacking’s work provided much of her original inspiration,Hacking denies that he is doing historical epistemology, preferring“meta-epistemology”. He also says that he is doingwhiggish “history of the present”. Scholars such asNersessian, ABC (Andersen, Barker, & Chen 2006), and Renn relyheavily on recent work in cognitive science, whereas sociologistsstill tend to shun cognitive psychology.

How significant can we expect historical epistemology to be in thelonger run? History will be the judge!

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Other Internet Resources

• Matheson, Carl and Justin Dallmann, “Historicist Theories ofScientific Rationality,”Stanford Encyclopedia ofPhilosophy (Spring 2017 Edition), Edward N. Zalta (ed.), URL =<https://plato.stanford.edu/archives/spr2017/entries/rationality-historicist/>.[This was the previous entry on historicist theories of rationality in theStanford Encyclopedia of Philosophy — see theversion history.]
• The Integrated History and Philosophy of Science (&HPS) website
• Hasok Chang 2015 Royal Society Wilkins-Bernal-Medawar Lecture, “Who cares about the history of science?”, (YouTube video, 65 minutes)

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Acknowledgments

I am indebted to Carl Matheson and Justin Dallmann, for their work inthe previous SEP entry on this topic. Thanks also to the SEP editorsand to Miriam Solomon, Theodore Arabatzis, and Ken Westphal forhelpful advice.