## 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 the
rationality of decisions and actions? Since the past is already over,
isn't history simply "bunk"? A couple of everyday
locutions suggest otherwise. It is commonly held that
"history" (meaning historiography, the disciplined study
of what happened in history) is a debunker of myths. And politicians
are not the only people worried about "the judgment of
history". Both these ideas came into play in the new
historically-oriented philosophy of science that began to emerge at
the end of the 1950s. The "new historicists" (as we may
call them) included Thomas Kuhn, N.R. Hanson, Mary Hesse, Imre
Lakatos, Paul Feyerabend, Stephen Toulmin, Dudley Shapere, Larry
Laudan, Ernan McMullin, and Michael Ruse. They claimed that the
then-dominant positivist and Popperian accounts of science were
themselves bunk--myths about how science is done. Some new
historicists claimed to find larger units and a hitherto unnoticed
dynamic in the time-series of the historical record--long-term,
forward-looking research programs that included evolving series of
related theoretical moments. Above all, the historicists stressed the
depth of major historical changes and the resulting challenges to
cumulative scientific progress. They argued that there was nothing in
the traditional "logic of science" that could rationalize
such changes. The problem was to produce a new dynamical model of
science that would capture these patterns and rationally motivate
them.



Historicist philosophers did a convincing job of showing that
historical evidence called the received views into question. Most
philosophers today accept that verdict of history. Less successful was
the 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 false
predictions" or "Use double-blind experimental methods
when dealing with cognitive agents") and at the
metamethodological level, where they faced the problem of how to
rationally select among competing theories of scientific rationality,
without circularity. The disagreements here raised the question of
whether there *is* a general theory of scientific rationality
to 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 Zammito
2004. Space limitations have forced the omission of important
developments, including the Marxist dialectical tradition, e.g., Nowak
1980, and recent work on stance and rationality, e.g., van Fraassen
2002, Rowbottom & Bueno 2011.) 


### 1.2 The Historical Turn in Philosophy of Science



Kuhn's *Structure of Scientific Revolutions* (1962/1970a)
was the original manifesto of historicist philosophy of science and
remains the primary reference point. His work thus provides the most
useful platform for recounting early historicist efforts--and the
difficulties they faced. We shall then take a briefer look at other
major contributors. Kuhn had been anticipated in quite diverse ways by
Kant, Hegel, William Whewell, Emile Meyerson, Ernst Cassirer,
Alexandre Koyre, 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 on
 Thomas Kuhn;
 also Hoyningen-Huene [1989] 1993 and Rheinberger [2007] 2010b).



The famous opening sentence of *Structure* was:



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



Kuhn modeled the history of a science as a succession of dogmatic
periods of "normal science" under a
"paradigm", separated by "revolutionary"
transitions to the next paradigm. According to Kuhn such a break from
the past rejuvenates a field that had stagnated under the weight of
anomalies that it no longer seemed to have the resources to solve. A
new paradigm introduces changes at all levels, from established
databases and instrumentation to the conceptual framework, goals,
standards, institutional organization, and research culture--so
much so that some older practitioners can hardly recognize the new
paradigm as their field. This disconnect produces
"incommensurability" across paradigm change, ranging from
communication 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 the
community 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). Under
critical pressure, he subsequently softened his position. In fact, he sought
to clarify the notion of incommensurability to the end of his life
(Sankey 1997). Kuhn exemplifies the irony that, while historicists
used deep change as a weapon to beat up traditionalists, it presented
serious problems for the historicists themselves as well.



Kuhn's book was his attempt to answer the question posed by the
above quotation. This question immediately raised another: How can
appeal to history achieve that transformative change? In particular,
how can *descriptive* claims about the past (or present
science, for that matter) affect our *normative* judgments
about rational beliefs and behaviors? How can history inform a
*methodology* 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 to
agree that there was a disconnect between science as historically
practiced and the normative models of the received philosophers. The
historicists therefore presented the philosophical community with a
momentous dilemma: either reject most of science to date as irrational
or else accept that science is generally rational and use the
historical information to revise our deeply entrenched logical and
probabilistic conception of rationality. Some positivists and Popperians
attempted to finesse option one by arguing that the history of science
approximated the traditional view of rationality closely enough if we
treated their sanitized, abstract models of science as regulative
ideals. Kuhn and other historicists defended option two, taking the
rationality of science to be practically axiomatic. Wrote Kuhn,



> 
> 
> I do not for a moment believe that science is an intrinsically
> irrational enterprise .... I take this assertion not as a matter
> of fact, but rather of principle. Scientific behavior, taken as a
> whole, is the best example we have of rationality. (1971: 143f; quoted
> by Hoyningen-Huhne [1989] 1993: 251f.)
> 
> 
> 



What was Kuhn's revised conception of rationality and how was it
based on history (to the degree that it was)? While he provided no
explicit, general theory of rationality, Kuhn's challenge here
was greater than many appreciate. The positivists and Popperians had
practically invented modern, academic philosophy of science. For them,
scientific rationality was wholly a matter of making correct theory
acceptance decisions in context of justification, where the hypotheses
and test data are already on the table, the data are theory-neutral,
and the goals and standards are logically independent of theory. To
Kuhn this picture of science was more like a photographic negative in
which light and dark are reversed. Let us count the ways.



(1) Although his work deepened the problem of underdetermination by
insisting that logic plus data is insufficient to determine theory
choice, Kuhn reduced the magnitude of the problem of justifying
scientific claims by rejecting traditional realism and the
correspondence theory of truth. No longer must scientists justify a
theoretical claim as true. Instead, he adopted the Kantian critical
position that no enterprise, including science, has the ability to
establish the final, metaphysical truth about the world. Instead,
science is largely a problem-solving enterprise, and scientists
*are* in position to evaluate the goodness of proposed problem
solutions, relative to previous attempts. "[T]he unit of
scientific achievement is the solved problem" ([1962] 1970a:
169). What demarcates science from nonscience and pseudoscience is
sustained support (over historical time) of a puzzle-solving
tradition, not the application of a nonexistent "scientific
method" to determine whether the claims are true or false or
probable to some degree. With justified truth claims gone, new
accounts of scientific discovery, knowledge, explanation, and progress
will also be needed.



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



(3) Moreover, Kuhn extended the claim that observation is theory laden
to say that *all* major aspects of a science are laden by the
others. Substantive data and theoretical claims, methodological
standards, goals, and even the social institutions of science are all
bound up in mutual dependence. (The received view had kept them
separate and independent in order to avoid mutual contamination
allegedly leading to circularity; see Scheffler 1967.) It is this
internal feedback that introduces the interesting, nonlinear dynamics
into Kuhn's model, since the feedback produces coupled
interaction terms (Kuhn 1977: 336; Nickles 2013b; De Langhe
2014b).



(4) This tight coherence implies that normal science is conservative
and closed, in contrast to Popper's science as an "open
society" (Popper 1945). Contrary to tradition, said Kuhn,
scientific rationality does not consist in advancing hypotheses and
testing them severely. To challenge the constitutive pillars of a
scientific field, as Popper and the positivists advocated, would
destroy it, for all theories and conceptual frameworks face
potentially falsifying anomalies at all times (Kuhn [1962] 1970a and
1970b; Lakatos 1970 agreed). Popper's "critical
rationalism", the key to Popper's Enlightenment conception
of political democracy as well as scientific advance, is actually
*irrational*; for such criticism would undercut the
researchers' reason for being.



(5) Kuhn claimed that Popper and others had missed the existence of
key structures in the history of science--the longer-term
approaches that he called paradigms and hence both normal and truly
revolutionary science. There are different historical scales in play:
individual theories, paradigms, and the still longer-term perspective
of a succession of paradigms. So Kuhn adopted *a two-tiered or
double-process conception of science* in which there is, first, a
constitutive framework (the paradigm), held immune to revision during
periods of normal science, and, second, change from one framework to
another. For these frameworks are historically contingent and are
eventually displaced by others. Kuhn's two-process account
sharply clashed with the one-process account of Popper (1963) and many
others. Ironically, given that Kuhn was also attacking positivist
positions, and given his greater sympathy for Popper, the two-process
account was closer to the "positivists" Reichenbach and
Carnap than to Popper (see Reisch 1991; Carnap 1950; De Langhe
2014a,b; Nickles 2013a).



(6) Thus two different accounts of scientific rationality are
required, not one: one to cover the relatively smooth change within
normal science under a single paradigm and the other to handle radical
paradigm change. This immediately implies that there are two basic
types of scientific change, hence two problems of scientific change
and/or two problems of progress to be solved, hence two accounts of
scientific rationality needed to solve them. What were Kuhn's
constructive claims?



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



(8) Informal scientific judgment depends heavily upon rhetoric and
judgments of heuristic fertility in the context of discovery--the
very items that had been expressly excluded from the context of
rational justification by the dominant tradition. For Kuhn, normal
problem solving is a matter of modeling new puzzles solutions on
established precedents, the exemplars, where modeling crucially
involves judgments of similarity, analogy, or metaphor. (Whereas
Popper's methodology is a learning theory in which we learn only
from our mistakes, in Kuhn's we learn also (mainly) from our
successes--the exemplars, which, over time ratchet up our
knowledge within normal science.) In paradigm change, the rhetorical
tropes used in persuasion are typically more abstract and tenuous than
in normal science. Kuhn's account of the rational acceptance of
paradigm change had to remain thin because of incommensurability. Here
the justification problem was all the more difficult because new
paradigms 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 the
rationality of paradigm change was to bring in a prospective dimension
of 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 old
anomalies (retrospective confirmation) but, equally importantly, can
reinvent and thereby preserve the field by opening up new frontiers
with much interesting new work to be done. For them the field now had
a future. To be sure, heuristic guidance was also a feature of normal
science, 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 their
head. Ironically, once we take the research scientists' points
of view, the more interesting forms of scientific cognition, including
justification, occur in contexts of discovery. All of this according to Kuhn.



Critics countered that, while the historicist upstarts had scored some
damaging critical points, their positive accounts of scientific
rationality were underdeveloped, vague, and unconvincing. Political
revolution and religious conversion as models of *rational*
behavior?! Clark Glymour (1980: 7, 96ff) called the new approach
"the new fuzziness". Could intuitive judgment really
replace standard confirmation theory? And what would be the analogous
relation of evidence to theory at the metamethodological level, where
now "theory" was the set of methodological rules or theory
of rationality itself? (Historicists replied that it is not their fault
if real-life decision-making is a messy business that often outruns
available formal rules.) Shapere (1984: chs. 3-5) was a severe
early critic of Kuhn, and Lakatos (1970: 178) reported that Kuhn had
replaced rationality with "mob rule". Since Shapere and
Lakatos were historicists, we see that the historicists could disagree
sharply among themselves. Feyerabend will provide the most vivid
example.



Kuhn's insightful treatment of science from the working
scientists' point of view provided a microlevel conception of
rational decision-making. But did he have a metamethodological account
of how to decide among competing theories of scientific rationality?
Again, not an explicit and comprehensive account, only some
constructive suggestions. Like all historicists, he said that a
rationality theory must fit the history of science and that the
traditional accounts failed this history test. An adequate theory must
also be progressive and avoid epistemological relativism. Kuhn (and
many others) simply built in these norms from the outset. Such a move
works well among most friends of historicism but not well for critics,
who think these presuppositions simply beg the normativity of history
question. Given incommensurability, are not rationality,
progressiveness, and denial of relativism key items that must be
argued for? In other passages, Kuhn did argue for them, but few
critics were convinced.



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



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



It is clear that Kuhn considered science more
efficient on his own account than on Popper's, because the double process enables
extreme specialization (Wray 2011; De Langhe 2014c). Indeed,
traditional accounts fail Kuhn's demarcation
criterion--that a genuine science supports a puzzle-solving
tradition. Given Kuhn's conviction that science is progressive
in terms of problem-solving success, predictive accuracy, simplicity
(the reworking and streamlining of problem-solving efficiency over
time), and so on, it supposedly follows that his account makes science
both rational and non-relativistic. Critics disagreed.



There also seems to be a kind of transcendental argument strategy
behind Kuhn's approach, as a response to the quasi-Kantian
question: Given that science, as historically practiced, *is*
largely rational and progressive, but not in the standard way, how are
its rationality and progress possible? Supposedly, the study of the
historical patterns will show the way.



Kuhn often described his two-process view as "Kant with moveable
categories". Accordingly, there is also a dialectical,
quasi-Hegelian reading: from the myriad of micro-decisions by the
community of scientists in a given field over time, with lots of fits
and starts, a progressive enterprise emerges, although not one that is
teleologically converging on the metaphysical truth about the universe
or on any other "end". However, on this view we have
abandoned the idea that individual scientific decisions are typically
driven by an explicit concern for rationality. In several areas of
philosophy there are heated controversies about whether higher-order
emergents have genuine causal power and hence genuine explanatory
force. To that degree, it remains unclear what role the desire to be
rational plays, as opposed to more mundane motives. This problem
arises for other historicists as well, as David Hull will note. (See
the entries on
 mental causation
 and on
 internalist vs. externalist conceptions of epistemic justification.)



On rationality as socially emergent, we may jump ahead here to note that feminist
philosophers of science such as Helen Longino and Miriam Solomon have
defended scientific rationality as a socially emergent norm (Longino
1990, 2001; Solomon
2001). They thereby address the question of how a naturalistic,
science-as-practiced approach to scientific knowledge can nonetheless
have normative implications. However, they do not shy away from making
policy proposals for *changing* (improving) scientific
practices and their supporting institutions. On their accounts, some
other factors, such as political/ideological ones, also socially
emerge and can have top-down causal efficacy on individual
practitioners but without negating the agency and autonomy of those
individuals. Here familiar issues of "methodological
individualism" come into play. (See the entries on
 feminist epistemology and philosophy of science,
 feminist perspectives on science,
 feminist social epistemology,
 and
 feminist political philosophy.)



The vigorous attacks on Kuhn as a radical subjectivist and
irrationalist who was undermining not only philosophy but the Western
intellectual tradition now look exaggerated, but it is fair to say
that the five big problem-complexes of normativity, incommensurability
(including meaning change), relativism, social knowledge, and deep but
rational progressive change are extremely difficult and remain open to
debate today. For many philosophers of science, relativism is the big
bugaboo that must be defeated at all costs. For them, any view that
leads to even a moderate relativism is thereby reduced to absurdity.
Historicist philosophers have insisted on relativity to historical
context but, with few exceptions, have made a sharp distinction
between *relativity* and outright *relativism*. Some
critics have not found this distinction convincing (see the entry on
 relativism,
 Kindi & Arabatzis 2012 and Richards & Daston 2016).


### 1.3 The Methodology of Scientific Research Programs



*Criticism and the Growth of Knowledge* (1970), edited by
Lakatos and Alan Musgrave, was a second major contribution to the
historicism debate. This collection of articles, originating from a
1965 London conference, was in significant respects a reaction to
Kuhn; but it is especially important for Lakatos's own
contribution to the volume, "Falsification and the Methodology
of Scientific Research Programmes" (MSRP), an attempt to
accommodate a broadly Popperian perspective to some of Kuhn's
ideas and thereby to diverge from Popperian orthodoxy. Lakatos had
long favored an historical approach to the philosophy of mathematics
and science (see his 1976). One of his central concerns was to defend
the rational continuity and progressiveness of modern science from the
challenge of radical change. Another was to fend off charges of
historical relativism.



Like Kuhn's paradigms and Laudan's research traditions
(see below), the unit of rational appraisal for Lakatos is not a
single theory at a point in time; instead, it is a series of theories
that are rationally-connected moments in the development of an
identifiable research program. In MSRP these theories share a
*negative heuristic* containing inviolable principles and a
*positive heuristic* that both provides a "protective
belt" around the negative heuristic and guides future research.
The forward-looking heuristic element was, as for Kuhn, an important
feature missing from traditional accounts of science. In MSRP,
research programs are evaluated as to their *progressiveness*
over historical time, i.e., which grows knowledge fastest.
Lakatos's measure of knowledge growth is novel prediction, the
advantage going to which program yields more novel
*theoretical* predictions and more *confirmed* novel
predictions than its competitors. This is a historicist position since
determining whether something is a novel prediction requires detailed
knowledge of the historical context of discovery in which the
predictive theory was produced (Lakatos & Zahar 1976).
Unfortunately, however, Lakatos's falsificationism had become so
sophisticated that he could provide no rule for when it was rational
to abandon a degenerating research program that was being outstripped
by a more progressive one; for scientists, he said, may legitimately
make risky choices. In any case, contrary to Kuhn, two or more
research programs may exist side-by-side. Lakatosian rationality does
not dictate that researchers all join the same program.



What is the relation between a theory of scientific rationality and a
general methodology of science? Like the Popperians from which he
diverged, Lakatos held that methodologies *are* theories of
scientific rationality (Curtis 1986). Similarly, a metamethodology
(tasked with determining which methodology outperforms others) is
identical with a metatheory of scientific rationality. Lakatos's
metatheory recapitulates MSRP at the metalevel. According to Lakatos,
his meta-MSRP shows that MSRP defeats competing methodologies, because
it provides the best fit with the history of science in the sense that
it renders the history of science maximally rational. That is, MSRP
makes rational sense of both the intuitively rational episodes and
some that its competitors have to exclude as externally caused
deviations from the rational ideal. Indeed, it *predicts* that
some counterintuitive cases will be seen to be rational when examined
closely.



Lakatos's paper, "The History of Science and Its Rational
Reconstructions" (1971: 91) opens with a promising paraphrase of
Kant (previously used by Hanson (1962: 575, 580) and by Herbert Feigl
(1970: 4): "Philosophy of science without history of science is
empty; history of science without philosophy of science is
blind". However, his use of rational reconstructions of
supporting historical episodes--the science as it allegedly could
have been done or *should* have been done--made the actual
science look more internally correct (according to MSRP) than it was.
Historians and philosophical critics replied sharply that this was not
genuine history and hence not a fair test (see Arabatzis forthcoming).



Lakatos and his followers (e.g., Worrall 1988, 1989) conceived MSRP as
a fixed and final methodology by contrast with Kuhn's,
Toulmin's, and (eventually) Laudan's changing
methodologies. The idea that all previous history of science was
working up to this final methodology that Lakatos was first to
divine--the end-of-history for methodology, so to speak--was
one of the broadly Hegelian themes in Lakatos's work. Another
was that there is no instant rationality as proposed by the formal
approaches of standard confirmation theory. Writes Daniel Little (in
the entry on
 philosophy of history)
 "Hegel finds reason in history; but it is a latent reason, and
one that can only be comprehended when the fullness of history's
work is finished... ". The owl of Minerva flies out at
dusk. For Lakatos rational judgments can only be made retrospectively.
For example, one cannot judge an experiment as crucial at the time it
occurs, only in historical retrospect (1970: 154ff). Appraisals are
made with hindsight. (See the entry on
 Lakatos.)


### 1.4 Methodological Anarchism



In his early work Feyerabend (1962) appealed to historical cases to
reject Hempel's account of explanation and Nagel's
parallel account of intertheoretic reduction (traditionally postulated
mechanisms of cumulative progress), on the ground that in actual
historical practice meaning change occurs from one major theory to its
successor. Deducibility thus fails. It also more obviously fails because
the two theories are typically mutually inconsistent. Accordingly, one
cannot reason by traditional logical argument from one to the other.
Feyerabend introduced his own conception of incommensurability into
this work. Anticipating his later broad pluralism, early Feyerabend
also extended the Popperian line on testing to a full-blown
proliferationist methodology. Competing theories should be multiplied
and tested against each other, because more empirical content is
thereby brought to light than in testing theories in isolation. In his
later work, Feyerabend (1975, 1987, 1989) moved vehemently away from
the positions of the Popper school. He vigorously rejected the idea of
a scientific method that makes science superior to other cultural
enterprises. According to his "methodological anarchism",
any so-called methodological rule, including logical consistency,
could be fruitfully violated in some contexts. That said, his
well-known slogan, "Anything goes", was widely read as
more radical than he intended, given his playful interactions with his
friend Lakatos.



This later Feyerabend declared that his primary aim was humanitarian,
not epistemological, so it was not his purpose to defend the rationality
of science. His attack on dogmatic, scientistic conservatism, both
within and without scientific communities, has methodological import,
albeit negative import. Feyerabend was one of the first to stress the
strong historical contingency of scientific work, in context of
justification as well as discovery, and he defended this contingency
at the methodological level as well. Thus there is no fixed
rationality of science. For example, Galileo (he argued in historical
detail) introduced a new sort of methodology, a new kind of
rationality, partly via rhetorical deception, partly with arresting
applications of mathematics to basic mechanical phenomena.
Galileo's new vision happened to win out, but there is no point
in calling it either rational or irrational in any absolute sense.



Philosophers, retreating from concrete detail to their abstract
formalisms, make science look far more rational than it is, stressed
Feyerabend. "*[H]istory, not argument, undermined the
gods*", and also undermined Aristotelian science and several
later scientific orthodoxies (1989: 397, his emphasis). Feyerabend
rejected "the separability thesis", according to which a
highly contingent historical processes can furnish scientific products
that are true and non-contingent, products that have achieved escape
velocity from history as it were (my expression). However, although
not as pronounced as in Lakatos, there remain traces of historicist
consequentialism in Feyerabend's view, as when he wrote that
"scientific achievements can be judged only after the
event" ([1975] 1993: 2). There is no "theory" of
scientific rationality in Feyerabend, only a historicist anti-theory,
as it were; but he was not quite the irrationalist that critics took
him to be. (See the entry on
 Feyerabend.
 For recent work on historical contingency, see Stanford 2006 and
Soler et al. 2015.)



Feyerabend embraced the relativism implied by the positions just
described. In a late work, *Science as Art*, influenced by the
prominent Viennese art historian Alois Riegl, he spoke of distinct,
self-contained scientific styles at different periods that are much
like the distinct styles in art (Ginzburg 1998). Such a view fit well
with his sometime assertion that there is no scientific progress, just
a succession or multiplicity of styles. Here there is a faint
connection to Kuhn's early views, although the two men
reportedly did not interact as much as one might expect while both
were at Berkeley.


### 1.5 The Pragmatic, Problem-Solving Approach



Laudan opened *Progress and Its Problems* (1977) with the claim
that providing an adequate model of rationality is the primary
business of the philosopher of science but that no extant
methodologies fit actual science. In this book his idea of good fit
was fit with a selection of intuitively strong historical instances
that any adequate theory must explain. (Laudan 1984 and 1996: ch. 7,
later rejected the intuitionistic elements that gave normative punch
to this model.) His response to the rationality question was to
propose a thoroughgoing, explicitly pragmatic, problem-solving account
of science. Problem-solving had been an important element in previous
accounts, notably those of Kuhn and Popper, but Laudan
*reversed* the usual account of scientific progress as a
temporal succession of atemporal rational decisions. Instead of
defining progress in terms of rationality, we should define
rationality in terms of progress. We cannot measure progress in terms
of approach to an unknowable, final, metaphysical truth, but we do
have reliable markers of progress in terms of numbers and relative
importance of both empirical and conceptual problems solved by
long-term "research traditions". Just as Lakatos's
research programs were a compromise between Popper and Kuhn, we can
read Laudan's "research traditions" as incorporating
elements of his major historicist predecessors, while departing
sharply from other tenets of their work.



Many analysts have played with possible relationships between the
sciences' assumed rationality and assumed progressiveness. The
central issue for them is analogous to the question in Rodgers and
Hammerstein's *Cinderella*: Is science progressive
because it's rational, or is it rational because it's
progressive? (Kuhn [1962] 1970a: 162, had asked: Does a field make
progress because it is a science, or is it a science because it makes
progress?") The underlying question is whether rationality is
basic and fundamental rather than derivative to something else. Those
like Laudan who make it derivative need to defend their position
against the objection that they are committing a verificationist
fallacy of confusing rationality itself (its constitutive nature) with
the criteria for applying the term 'rational'. Are
momentary success or longer-term progress *constitutive* of
rationality 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 on
Lakatos's. The temporality of his account led Laudan to
introduce an important distinction between *acceptance* of a
theory and *pursuit* that would explain how rational
transitions to a new research tradition are possible. Scientists
should accept the theory that, *pro tem*, has the greatest
overall problem-solving success, but pursue the tradition that now
enjoys a higher *rate* of success. Nearly everyone today
accepts a distinction of this sort, although not necessarily
Laudan's criteria of success.



Like *Structure* and MSRP, Laudan's model of science
received much discussion, both constructive and critical. It faced the
usual difficulties of how we are to count and weigh the importance of
problems in order to have a viable accounting scheme. Historicists can
reply that it is not their fault if this is a messy task, since that
is just historical reality, a reality that, if anything, favors expert
judgment over tidy decision algorithms.



Laudan (1984) agreed with Kuhn that the goals, standards, and methods
of science change historically as well as the theoretical and
observational claims, but his "reticulationist model"
rejected as historically inaccurate Kuhn's claim that sometimes they all
change together to constitute a (Kuhnian) revolution. Dramatic change in one
place need not seriously disturb fixity elsewhere and rarely or never does. Hence,
incommensurability is a pseudo-problem. Moreover, Laudan contended, his
reticulationist model overcomes the hierarchical problem that has led
thinkers such as Poincare and Popper to make the goals of
science arbitrary (the top of the hierarchy and hence the unjustified
justifier of what comes below), e.g., mere conventions. These authors have no
way to rationally appraise the goals themselves, leaving their positions stuck
with an account of merely instrumental reason: efficiency relative to
a given, arbitrary goal. By contrast, in Laudan's model, the
elements are mutually constraining, mutually adjusting, an idea
prominent in Dewey's attack on hierarchy in his 1939. None takes
absolute precedence over the others. Thus, some goals are irrational
because present and foreseeable knowledge and methods have no way to
achieve them or to measure progress toward them. (Laudan thereby
rejected strong realist goals as irrational.) An advance in substantive
or methodological expertise can make it rational to embrace new
standards and also new goals.



The debate between Laudan and Worrall over the value of a fixed
methodology of science wonderfully exemplifies the persistence of the
ancient problem of change (Laudan 1989; Worrall 1989). How is it
possible to explain, or even to measure, change except in terms of an
underlying fixity? Doesn't allowing change at all three of
Laudan's levels--matters of scientific fact and theory,
method and standards, and goals--leave us with a damaging
relativism? Worrall defends the fixity of Lakatos's MSRP but
agrees that it cannot be established *a priori*. Laudan's
reticulated model retains a more piecemeal and historically contingent fixity, as described
above.


 With all that said, the threat of relativism remains, for how can
a good, non-whiggish historicist have a trans-historical measure of
progress? Laudan's answer was that we can whiggishly measure
scientific progress by our own standards, regardless of what the goals
of the historical investigators were. This sounds right about what we
do. But if the reasons why the historical scientists in the trenches
made the decisions they did do not really matter to us (or to any
given generation), retrospectively, then how is rationality providing
a methodological guide or causal explanation why historical scientists
made the decisions they did? Their individual rationality would seem
to become irrelevant. And why, then, is rationality the central
problem of philosophy of science?



Departing sharply from traditional, non-naturalistic treatments of
norms, Laudan addressed the is-ought problem head-on by advancing an
important and influential, pragmatic "normative
naturalism" whereby the acceptable norms are those best
supported by successful historical practice--where, again,
success is as we judge it today. On this view, norms have empirical
content. They are winnowed from the history of successful practice,
again a broadly Deweyan idea (e.g., Dewey 1929). At Virginia Tech
Laudan and colleagues initiated a program to test the individual norms
present in various philosophical models of science against the history
of science (Laudan 1977: 7; Donovan et al. 1988). Like every major
philosophical proposal, this one came under critical fire, in this
case, e.g., for isolating individual methodological rules from their
historical contexts and for reverting to a traditional, positivistic,
hypothetico-deductive model of testing. In short, critics complained
that Laudan's metatheory of rationality did not match his
first-order, problem-solving-progress theory of rationality. And
professional historians did not welcome this invitation to
cooperation, since the project implied a division of labor that
regarded philosophers as the theoreticians proposing rules to test,
while the historians were relegated to fact-grubbing handmaidens doing
the testing. To be fair, as a historicist philosopher, Laudan himself
had done a good deal of historical work.



On another front, Laudan's (1981) attempt to
"confute" scientific realism on the basis of historical
examples of major scientific change stimulated much discussion, since
the status of realism had become a central issue in philosophy of
science. Indeed, Laudan's article helped to make it so.


### 1.6 Evolutionary Models of Scientific Development



Toulmin (1972) produced an evolutionary model of scientific
development in terms of populations of concepts, a gradualist account
of scientific change that he considered more historically accurate and
philosophically defensible than Kuhn's discontinuous model.
Toulmin's "concepts" are historically malleable, yet they are
characterized by historicity. He quotes Kierkegaard: "Concepts,
like individuals, have their histories, and are just as incapable of
withstanding the ravages of time as are individuals" (1972:
frontispiece). Toulmin held that biological, social, and conceptual
evolution, including scientific development, are all instances of the
same generalized variation-selection-transmission schema, albeit with
quite different concrete implementations. For Toulmin, disciplines
(specialties) are analogous to biological species. He touted his model
as naturalistic, indeed ecological, but not in a way that excludes
rationality. 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 or
Kuhnian framework through thick and thin. Rather, it is a matter of
adapting appropriately to changing circumstances. Like Newtonian
force, rationality has to do with change, not maintenance of the same
state. Thus no Kuhnian revolution is needed in order to break out of
an old conceptual framework.



As for the descriptive-normative problem, thinkers from Kuhn to Robert
Brandom (e.g., 2002: 13, 230ff) have appealed to the common law
tradition as an instructive analogy, and Toulmin was no exception.
Published legal cases provide legal precedents that later legal
argumentation can cite for support. Over time, normative traditions
emerge. Explicit rules may be formulated by reflecting on the history
of precedents, but the practices typically remain implicit. There is a
whiff of Hegelian, retrospective reconstruction in this idea of
extracting norms from patterned historical practices that embody them
implicitly and contingently. The main trouble with Toulmin's
account, said critics, is that it is so vague and abstract that it
tells us little about how science works. It would seem to apply to
just about everything.



Donald Campbell (1960, 1974) had previously defended the generalized
variation plus selective retention schema, which he traced back to
William James. Popper regarded his own evolutionary account of
scientific development as similar to Campbell's (1974). Ditto
for David Hull (1988) with his more detailed evolutionary model.
However, Hull rejected evolutionary *epistemology*, as such,
and denied that he was doing epistemology at all. (Evolutionary
epistemologies face the problem of why we should expect a contingent
selectionist process to be truth-conducive: see the entry on
 evolutionary epistemology.
 Assuming that it is can also tempt one to fall into whiggism
regarding the past in a social Darwinist sort of way.) Hull rejected
Toulmin's biological species analogy, as based only on
feature-similarity rather than on the historical-causal continuity of
genuine biological species. Hull's book reflected his own deep
involvement in the controversy between cladists, evolutionary
systematicists, and pheneticists over biological classification. (He
served terms as president of both the Society for Systematic Biology
and the Philosophy of Science Association.) Hull generalized his
important biological concepts of replicator (gene) and interactor
(organism) to scientists and communities. His central unit of and for
analysis was the deme, or research group, in its competition with
others.



Hull (1988) argued that the success of science can be explained by an
invisible hand mechanism rather than in terms of rational
decision-making. He did not deny that most scientists regard
themselves as rational truth seekers, but on his account the primary
motivation is the drive for professional recognition and credit via
positive citation by others, and avoidance of violations of
institutionalized standards. The term 'rationality' does
not even appear in the book's index. Nonetheless, the
institutional incentive structure of science works to produce
generally reliable results and scientific progress, so that, to
rationality-minded philosophers, science looks *as if* it is
driven by the intentional rationality of its practitioners. We might
say that, for Hull, rationality explains nothing without causal
backing, but once we bring the causal mechanisms into play, there is
no longer a need to foreground rationality, at least not intentional
rationality.



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



Like Adam Smith's view of the invisible hand regarding altruism
and the public good, rationalists can interpret Hull's account
as broadly Hegelian in the sense that the rationality of science
emerges (insofar as it does) from the complex social interactions of scientists
and groups of scientists going about their normal business in ordinary
ways that satisfy community norms and incentive structures, not from
their explicit intentions to make rational decisions. While Hull gave
close attention to these social interactions and to the institutions
that enable them, he claimed that his appeal to social factors was
internal to science rather than external.


### 1.7 New-Wave Sociology of Science and the Realist Reaction



Left relatively untouched by historicist philosophers during the
Battle of the Big Systems was the internal/external distinction. The
philosophers, consonant with traditional sociology of science (e.g.,
Merton 1973) and sociology of knowledge more generally, defended a
kind of "inertial principle" (Fuller 1989: xiii *et
passim*): social and psychological factors such as economic and
political interests and psychological dispositions should be brought
into play only to explain deviation from the rational path. This
distinction began to erode already in Kuhn, who stressed the social
factors *internal* to the organization of science itself:
science education, the strong role of scientific communities with
their distinctive cultures, etc. (See also Lakatos on comprehensive
theories of rationality that can turn apparent external considerations
into internal ones, and Hull 1988 on career advancement.)



In the 1970s, new-wave sociologists of science quickly rejected the
division of labor implied by the inertial principle and took sociology
far beyond where Kuhn had left it (much to his chagrin). These
sociologists insisted that sociology, via social interests and other
social motivational causes, had much to say about the internal,
technical content of science--so much, in fact, that it was not
clear that there was any room left for the rational explanations of
the philosophers. The Edinburgh Strong Programme founded by David
Bloor and Barry Barnes (see Bloor 1976), the Bath relativist school of
Harry Collins and Trevor Pinch (Collins 1981), and later
constructivist work of Bruno Latour and Steve Woolgar (1979), Karin
Knorr-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 on
historical case studies, we find more radical historicisms challenging
less radical ones. Although the sociologists often disagreed among
themselves, as the philosophers did, the general thrust of their work
was that the philosophical historicists had failed to take
socio-political context into account and thus were still too much
wedded to the old, abstract, acausal ideals of rationality,
objectivity, and progress toward truth. Much sociological work was
explicitly anti-realist and relativist, at least as a methodology.



Most philosophers of science strongly rejected the new sociology as
relativist and irrationalist, the non-historicists among them adopting
versions of strong realism, according to which mature science can
knowingly, on internalist grounds, arrive at theoretical truth and
genuine reference to theoretical entities, or closely enough. The
eventual upshot was "the Science Wars" of the 1990s. By
now (2017), the sides in this dispute have mellowed, fruitful
conversations are taking place, and some degree of reconciliation has
occurred (see Labinger & Collins 2001). Work by feminists in
science studies such as Donna Haraway (2004) and feminist philosophers
of 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, and
less hierarchical options. Distinct prominent approaches to social
epistemology by philosophers include Fuller 1988, Goldman 1999, and
Rouse 2002. (See the entries on
 social epistemology,
 scientific method,
 scientific realism,
 and the
 social dimensions of science
 as well as the feminist entries referenced above.)



Some of the sociological work had a postmodern cast, and so did
contributions by some philosophers. For example, Richard Rorty's
version of historicist pragmatism rejected correspondence theories of
truth and the related idea that we humans have some
naturalized-theological obligation faithfully to represent
metaphysical nature with our science. He spoke suggestively but
vaguely of major transformations in the sciences (or anywhere else in
culture), such as that achieved by Galileo, as the invention of a new
"vocabulary" that worked well enough for certain purposes
to catch on, but not as new truths established by logical reasoning. As
for rationality itself, it is a matter of maintaining an honest, civil
"conversation":



> 
> 
> On a pragmatist view, rationality is not the exercise of a faculty
> called "reason"--a faculty which stands in some
> determinate relation to reality. Nor is [it] the use of a method. It
> is *simply* a matter of being open and curious, and of relying
> on persuasion rather than force. (1991: 62).
> 
> 
> 



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



A view sometimes ascribed to Rorty's hero Dewey is that
rationality is not an *a priori*, universal method of thinking
and acting properly; rather, it is like a box of intellectual tools,
each of which, as humans have learned from craft experience, work better than
others 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 of
rationality remain unresolved, but the approach has the merit of
bringing back into discussion several interrelated questions.


1. What is it to be rational, anyway, once we situate agents in
real-life socio-cultural situations?
2. Is an account of rationality something discovered rather than
humanly constructed?
3. Is a theory of rationality something that can be fixed *a
priori*, 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 of
rationality, of universal applicability?
5. Can (should) our concept of rationality be relativized to
specifically human capabilities and to specific kinds of
decision-action situations, or could it turn out, by some universal
standard, perhaps realized by future artificial intelligence or by
(other) aliens, that we are all terribly non-rational, scientists
included?
6. Is scientific rationality special in some way, as distinct from
rationality in general?
7. Is a theory of specifically scientific rationality the same as an
account of scientific method? (If so and there is no unique scientific
method, then there is no single, general account of scientific
rationality either.)
8. Is second-order rationality possible, i.e., rational changes in
scientific goals and standards of rationality themselves?
9. Should a metatheory of scientific rationality match the theory of
first-order methodological rules?
10. Do we even need a theory of scientific rationality, either to
explain research at the microlevel or scientific development at the
macrolevel? 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 the
rationality of the working group and to the community of specialists
as a whole? In other words, how does (or should) the distribution of
cognitive labor affect the discussion of rationality?
12. Are rationality assessments instantaneous (given the logical or
mathematical relations of the available information) or do they (at
least sometimes) require historical retrospect or prospect?
13. What good is the historical study of how basic categories of
description such as 'fact', 'experiment',
'objective', 'replication', and 'novel
prediction' change over time? What does such history tell us, if
anything, about human inquiry or epistemology?
14. What does 'historicism' mean in this context, and
what could a constitutively historicist theory of rationality be?


## 3. Historicism Then and Now



Nineteenth-century philosophers and (especially) historians are
commonly credited with the modern "discovery" of history,
especially political history, via developing the discipline of
evidence-based, interpretive and explanatory historiography. Hegel
historicized Kant at the beginning of that century, but it was
primarily German historians such as Ranke, Droysen, Windelband,
Dilthey, Rickert, and Weber who developed competing conceptions of
what is required for rigorous historical research. (For an in-depth
survey, see Beiser 2011.) These historians were concerned to develop
historiography as *wissenschaftlich* but autonomous from the
natural sciences, where positivism reigned. They also rejected the
grand, Hegel-type philosophies of history. Toward the end of the
century, this opposition produced the *Methodenstreit*, the
vehement debate over differences between the natural sciences
(*Naturwissenschaften*) and the socio-historical sciences
(*Geisteswissenschaften*). Historicists saw naturalism and
materialistic mechanism as threats.



The connection of the historicization of philosophy of science in the
1960s to the German historicist tradition is indirect, given the
time-gap of decades. However, the historicists of scientific
rationality discussed in this article did (or do) agree to several of
the following (overlapping) tenets, most of them traceable to
nineteenth-century antecedents. There exist tensions among the
following claims, so internal disagreement among historicists is to be
expected.



1. *The historicity of all things.* Virtually all things come
into existence and pass away in historical time. Nothing is guaranteed
to be fixed and permanent, written in the stone of the universe.



2. *History vs. a priori reason or logic alone*. Human beings
do not possess a faculty of *a priori* reason capable of
surveying the space of all logical possibilities. The emergence of
non-Euclidean geometry illustrates this point. Human inconceivability
is not an adequate criterion of either logical or historical
possibility.



3. *Our historical boundedness: anti-whiggism and the principle of
no privilege.* We inquirers are also historically situated. While
we are not slaves to our cultural context, we can escape it only
partially and with difficulty. Our horizons sometimes prevent us from
recognizing our own presuppositions, not to mention future
possibilities. Wrote Mary Hesse: "our own scientific theories
are held to be as much subject to radical change as past theories are
seen to be" (1976: 264). Although we have good reason to hold
that our science is superior to that of the past, this does not confer
an absolute, ahistorical privilege on our science. Rather than succumb
to this perspectival illusion, we must imagine that our successors may
look at us as we see our predecessors. We, too, are just a
transitional stage into a future that is likely to include much that
is beyond our present horizon of imagination. We must avoid the flat
future illusion that sees the future a tame continuation of the
present (Nickles forthcoming).



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



5. *Historical content of theory of justification: The complexity
of history.* History is too complex and too subtle to be captured
by a fixed, formal system or in terms of the dynamical relationships
of a set of "state variables". Logical and probabilistic
systems alone are crude tools for capturing the reasoning of real
people, scientists included. Besides the subtle, contextual reasons,
innovative scientists work at moving research frontiers
("context of discovery") and, so, must make many decisions
under uncertainty (not only under mere risk). Rationality has more to do with
appropriate response to change than with sticking rigidly to
one's initial standpoint. This challenge strikes at the heart of
traditional accounts of context of justification, hence at the heart
of traditional philosophy of science. Thinkers from Kuhn to van
Fraassen (2002: 125) have taken a dim view of confirmation theory,
although Bayesians have made valiant attempts to capture historicist
insights. (For examples, see Salmon 1990 and Howson & Urbach
1993).



6. *Consequentialism and history as a judge.* Frontier
epistemology teaches that we can often only learn which modes of
action are successful via historical experience of the consequences.
(Non-historicists can reply that the eventual judgment is not itself
historical but only delayed, because based on evidence gathered over
time.) In its strongest form, historical judgment replaces "the
Last Judgment", the judgment of God, as reflected in the common
expression "the judgment of history". (Of course, this
view is itself anti-historicist in its conception of finality.)



7. *Genetic, genealogical understanding.* Since nearly
everything is the product of historical development or disintegration,
studying its historical genesis and dissolution is key to
understanding it. Genetic fallacies are avoidable by including
development and maintenance as part of the narrative, since
development can be transformative. Today many writers are exploring
the biological and socio-cultural evolutionary origins of human
rationality, going far deeper, historically, than to recent historical
developments 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 be
liberating, as when we see that institutions and conceptual frameworks
are, to a large degree, human constructions with a historical origin,
not things irremediably fixed in the foundation of the universe. For that
very reason it produces a degree of skepticism toward all human
things. Although the natural world shapes human cultures, including
scientific ones, it far from dictates a single, fixed culture.
Historiography discloses that human enterprises, including the
sciences, are imbedded in deep cultures with their distinctive norms.
There is no "God's-eye", history-neutral set of
meta-norms, no "Archimedean point" from which these
cultures can be objectively compared. Thus it is difficult or
impossible to evaluate all science with a single standard. Here lurks
the problems of cultural incommensurability and relativism.



9. *Pluralism.* Methodological pluralism is a natural
consequence of historicist approaches. Historical study discloses that
the various sciences employ quite different methods and often harbor
competing research programs. The emergence of philosophy of biology as
a specialty area in the wake of the 1959 Darwin centennial added
substance to this claim. (For entries into the pluralism literature,
see Dupre 1993; Galison & Stump 1996; Mitchell 2003; and
Kellert et al. 2006.)



10. *Science as a model of rationality.* On this theme,
historicists are divided. Some strong historicists, especially
Feyerabend, Hull, and thoroughgoing social constructivists, deny that
science is rationally or methodologically special among human
enterprises.



11. *Science as a model of progress.* This, too, is practically
axiomatic among philosophers of science. The idea of history
"itself" as progressive came in with the Enlightenment and
was severely challenged by the world wars.



12. *Historicism as half-naturalistic.* Historicist accounts do
not appeal to supernatural factors or to factors beyond the
possibility of human cognition such as clairvoyance or the
metaphysical truth about reality. Historicists usually take a second
step toward naturalism in considering humans as biologically limited
beings, but they resist reduction to the natural science brand of
naturalism. Philosophical historicists also reject the reduction of
norms to facts. (But, late in life, R.G. Collingwood may have come to hold a
strong version of historicism according to which philosophy reduces to
history: see the entry on
 Collingwood.
 Some new-wave sociologists may have held a parallel reductionist view
about philosophy and sociology, insofar as philosophy was worth
saving.)



13. *Major historical change as emergent--against intelligent
design and the conscious model.* Many historical developments are
not deliberately chosen or designed but emerge from numbers of people
carrying out their individual and collective activities. The rise of the nation-state
and of the international capitalist economic system were not the
products of centralized, rational planning, nor were modern science
and technology, although there were, of course, many micro-instances
of such planning. This point applies to the idea of scientific method,
which tradition often depicted as clairvoyantly, intelligently guiding
scientific innovation. But as Hume already anticipated, no method is
guaranteed in advance to work in a novel domain. Methodological
innovation typically follows rather than precedes innovative work
(Hull 1988; Dennett 1995; Nickles 2009, forthcoming). This is a
broadly Hegelian idea.



14. *Strong historical determinism is mistaken.* A controversy
among historicists of various stripes is whether there are "iron
laws of historical development". Hegel and Marx, in quite
different but related ways, believed in a teleological conception of
history, that "it" was working its way inevitably through
known stages toward a final goal that would amount to "the end
of history" in the sense that deep historical change would now
cease. This is the view that Popper termed "historicism"
in *The Poverty of Historicism* (1957; see also his 1945).
Popper vehemently rejected this version of historicism, as do
virtually all historicist philosophers of science today. For them,
history is non-teleological and highly contingent. This includes
Kuhn's ([1962] 1970a) model, although the latter does posit an
almost inevitable, unending alternation of normal and revolutionary
periods--a final pattern without end, as it were.



15. *Hermeneutic interpretation*. The received, covering-law
model of explanation is inadequate to explain historical action,
including that of scientists and communities of scientists. Kuhn
described his method as hermeneutic, but few historicist philosophers
of science are full-blown hermeneuticists or as fully committed to
empathic understanding as were some of the classic German
historicists. Most or all historicists are somewhat partial to
narrative forms of explanation. (See the entry on
 scientific explanation.)


## 4. Related Developments and Further Challenges



The battle of the big systems seems to be over, and likewise for the
heyday of interdisciplinary departments and programs of history and
philosophy of science (but see below). So are historicist conceptions
of rationality dead? Despite claims that historicist philosophy of
science has been "withering on the vine" (Fuller 1991), it
is fair to say that historicist influences remain important, but in a
subtler way. Most philosophers of science are more historically
sensitive than before, whether or not they identify as historicists.
Historicist interests have expanded into "the naturalistic
turn", "the models turn", and "the practice
turn", which includes interest in contemporary practices, and,
to a lesser degree, in future history (Nickles forthcoming).



Moreover, in parallel developments, the classical conception of
rationality is under attack on many fronts. Herbert Simon (1947)
introduced the ideas of bounded rationality and satisficing. Simon
later championed the need for a heuristic approach to problem solving
by humans and computers (Newell & Simon 1972). Various flavors of
artificial intelligence then led the way in the methodology of problem
solving, with heuristics as a central topic and no longer the temporary
scaffolding of positivism and Popper. Simon's program in
adaptive, "ecological rationality" is now being expanded
by Gerd Gigerenzer and the Adaptive Behavior and Cognition group in
Berlin (Gigerenzer et al. 1999). Simon's approach and the
"heuristics and biases" program of Daniel
Kahneman and Amos Tversky (Kahneman et al. 1982), plus work by the
latter on prospect theory, triggered the emergence of behavioral
economics, which rejects the neo-classical *homo economicus*
rationality model. Philosopher Christopher Cherniak's
*Minimal Rationality* (1986) also brought out sharply how
idealized were traditional philosophical assumptions about
rationality. In other directions, some computer scientists are
challenging the anthropocentrism of received conceptions of rational
inference by asking why artificial intelligence, including deep
learning, 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 should
withhold attributions of rationality to animals from chimps and
elephants to octopuses, simply because they seem to lack a human sort
of conceptual language.



Nonetheless, there is wide agreement that historicist accounts of
scientific rationality cannot fully supplant traditional views. For
example, there surely does exist some "instant
rationality" even at research frontiers. One finds a wide
variety of decision contexts there, and some of these decisions will
be uncontroversially warranted at that time and in that context, while
others will not be. Hesse (1980) and many others (see Radnitzky &
Andersson 1978) raised the issue of how to generalize from historical
case studies, for citing case studies can be like citing the
*Bible*. One can cherry-pick one's case studies to
support most any position. In any case it is fallacious to generalize
from a few, highly contextualized case studies to conclusions about
all science at all times. Early historical work in social studies of
science faced the same problem. Ironically, such generalization
abstracts away from the historicity of the case studies themselves.
The attempt to replace inductive generalization by testing via an H-D
model also runs into trouble, as we noted in connection to the
Virginia Tech project. And why should case studies from two or three
hundred years ago be taken seriously when science itself has changed
significantly in the meantime? Partly for this reason Ronald Giere
(1973) contended that it was necessary to study only today's
scientific practices, that philosophers had no special need of
consulting historians.



Late in life, Kuhn himself, surprisingly, rejected the case-study method as too
wedded to the traditional view of science as a direct search for the
truth about the universe. The first generations of historical inquiry
by philosophers and sociologists so shockingly revealed the presence
of many non-epistemic factors and the general failure of any method
fully to justify scientific beliefs, he said, that skepticism was the
result. The more people learned about how science is actually done,
the more skeptical they became. Declared Kuhn, we can more securely
derive 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 historical
perspective", a non-whiggish understanding of the decisions
actually available to the historical actors in their own context.
Kuhn's main point is that such decisions should be considered
comparative ("Is this item better than that one, given the
contextual knowledge and standards?"), not as judgments of truth
or probability. This move reduces the problem of understanding
behavior in rational terms to something manageable, he explained.
Developing this point, Kuhn said, will bring the only defensible sort
of rationality back into scientific practice in a way that largely
avoids the old problems of incommensurability. It will also provide a
defensible concept of scientific progress and of scientific
*knowledge* (almost by definition)--knowledge as what the
scientific process produces. This historical perspective was part of
Kuhn's project of developing a biological analogy for the
development of science, wherein disciplinary speciation events
correspond to revolutions. Kuhn held that his approach applied to all
human enterprises, not just science (Kuhn 2000).



Recently, Rogier De Langhe (2014a,b,c, 2017) has been developing a
broadly Kuhnian, two-process account of science from an economics
standpoint. Instead of doing a series of historical cases, De Langhe
and colleagues are developing algorithms to detect subtle patterns in
the large citation databases now available. In sum, both late Kuhn and
early De Langhe are now appealing to the history of science in a more
abstract, or perhaps comprehensive, manner, a manner complementary to the two-process approach of
Michael Friedman (below).



Another general challenge for historicists and others concerned with
the rationality of science is how to factor the division of labor in
science into a model of scientific rationality. How does individual
rationality (the traditional focus of economists as well as
philosophers) relate to the collective rationality of working groups
or entire specialist communities? (See Sarkar 1983; Kitcher 1993;
Mirowski 1996; Downes 2001; De Langhe 2014b; Latour 1987 and later for his
actor-network theory; and the entry on
 social epistemology.)
 Feminist philosophers such as Longino (1990, 2001) and Solomon (2001)
have proposed more thoroughgoing social epistemologies of science that
go beyond the problem of division of labor, which, in their view, is
still 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 has
a troubled history. Several joint departments and programs were formed
in the heady 1960s, just as much historiography of science was turning
away from internalist approaches. As professional historians and
philosophers came to realize that their interests differed, many of
these programs did wither.



In the meantime, several philosophers have engaged in serious
internalist 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 double
helix. More recently, scholars such as Nancy Nersessian with her
"cognitive history" project (1995) have employed new
resources from the cognitive sciences in this regard, a move neglected
by Kuhn himself and resisted by sociologists concerned by the
philosophers' neglect of the social basis of the knowledge
enterprise. (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, on
social microhistory and lesser-known figures, including women, rather
than 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 an
intimate marriage.



Since 1990 promising new movements have emerged that bring together
philosophy of science and historiography of science. First,
philosophers of science became interested in the historical emergence
and professionalization of their own field. Early work quickly
destroyed some myths about the Vienna Circle, for example. The primary
organization here is the International Society for the History of
Philosophy of Science (HOPOS), with its own journal and regular
meetings. More recently, the Integrated History and Philosophy of
Science (&HPS) organization has sponsored several conferences with
the goal of maintaining the standards of both fields rather than
compromising one for the supposed advantage of the other. (For
background, see Schickore 2011, 2017. Consult the &HPS website for
other contributors.)



Theodore Arabatzis (forthcoming) distinguishes two ways of integrating
history and philosophy of science: the familiar "historical
philosophy of science" (HPS), usually based on
"historical" case studies; and the less familiar
"philosophical history of science" (PHS). It is well known
that historians have found most philosophical work of little use, and
Arabatzis aims to help correct the asymmetric relationship between
history and philosophy.



> 
> 
> [P]hilosophical reflection on these concepts can be
> historiographically fruitful: it can elucidate historiographical
> categories, justify historiographical choices and, thereby, enrich and
> improve the stories that historians tell about past science as a
> knowledge-producing enterprise. 
> 
> 
> 



Labels for movements can be arbitrary and misleading, but several of
the authors cited by Arabatzis have been identified with a movement
usually called "historical epistemology", the goal of
which is to combine excellent history of science with philosophical
sophistication or excellent philosophy with more historical
sophistication than is usually found in case-studies approaches. Given
the epistemological focus, here is where we might expect to find the
greater concentration of work relevant to questions of scientific
rationality. The epicenter of the movement is the Max Planck Institute
for the History of Science in Berlin, whose directors over the years,
Lorenz Kruger (who died before he could assume the post),
Lorraine Daston, Hans-Jorg Rheinberger, and Jurgen Renn,
have promoted historical epistemology. A recent, special issue of
*Erkenntnis* (Sturm & Feest (eds.) 2011) on historical
epistemology derives from a conference at the Institute. In their
introductory essay to the special issue, the co-editors, Uljana Feest
and Thomas Sturm, ask "What (Good) is Historical
Epistemology?" (Feest & Sturm 2011). The special issue
includes a baker's dozen authors who develop and/or critique
various approaches to historical epistemology. The participants range
from older hands such as Philip Kitcher, Michael Friedman, and Mary
Tiles to more recent contributors such as Jutta Schickore and
Feest. (See Tiles & Tiles 1993 for an early philosophical
introduction to the field.)



Feest & Sturm (2011) divide the movement into three streams. One stream
studies historical changes in epistemology-laden *concepts*
such as objectivity, observation, evidence, experimentation,
explanation, and probability. How do new concepts emerge? How are they
stabilized? At what point do they become conscious rather than
remaining implicit in practice? How do they shift over time and how
well do they travel to different scientific contexts (cf. Howlett
& Morgan 2011)? Insofar as they are initially metaphorical, how do
they become dead metaphors? How do they fade out of use? Lorraine
Daston's work is a good example of this approach (e.g., 1988,
1991; Daston & Galison 2007; Daston & Lunbeck 2011). This
means looking at the evolution of concepts or organizing
"categories" of action and thought within a historically
confined project, however interdisciplinary it might
be--something between the eternal, global, and maximal often
favored by philosophers and the evanescent, local, and contingent
favored by many historians. Gone is the old-fashioned
"conceptual history" of the sort exemplified by Max
Jammer's (1957),
which traces "the concept" of force from ancient Egypt to
the twentieth century. Wrote Daston in an early paper:



> 
> 
> To my mind, the most able practitioners of historical epistemology
> these days are philosophers rather than historians--I think of
> the remarkable recent work of Ian Hacking and Arnold
> Davidson--although I think they, intellectual historians, and
> historians 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 way
toward "releasing us from our bondage to the past by hauling
that past into conscious view", although we must recognize that
calling attention to the contingent origins of something is not
sufficient to debunk it, upon pain of committing a genetic fallacy.
Nor can we simply reject something without having an alternative to
put in its place. "That is, historicizing is not identical to
relativizing, much less to debunking".



The second strand of historical epistemology identified by Feest and
Sturm in their introduction to the special issue focuses on the trajectories of the *objects* of
research--"epistemic things"--rather than on
concepts, and here the well-known work of Rheinberger (1997, [2006]
2010a, [2007] 2010b) is emblematic. Renn (1995, 2004) represents the
third approach, an attempt to understand *the longer-term dynamics* of
science. For example, Renn attempts to solve several mysteries about
how Einstein was able to accomplish the relativity revolution. His
answer takes into account the long history of developments in distinct
fields that Einstein was able to bring together, partly because of his
wide philosophical and other cultural interests. Renn looks at
long-term developments by analogy with biological development. Norton
Wise (2011) also brings biological metaphor into play. He observes
that historical narrative as a form of explanation is now making
serious incursions into physics, in the physics of complex or highly
nonlinear systems. "Covering law" explanations are not
available there, he says, and sometimes we must resort to simulations
in order to understand how systems evolve. "We know what we can
grow".



Running through much historical epistemology is a century-long line of
neo-Kantian thinking, from Ernst Cassirer and the Marburg school to
Reichenbach and Carnap and then to Kuhn, Ian Hacking, Michael
Friedman, Daston, Renn, and others. Theirs are diverse versions of the
two-process view introduced in
 Section 1.2
above. 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 are
*historicized* Archimedean points or platforms that organize
human experience, rather than fixed Kantian categories. But, like
Kant's categories, they are presuppositions that define how
coherent perception and the formation of true or false propositions
are possible.



Friedman speaks of these as "historically contingent but constitutive
*a prioris*". His 2011 takes first steps beyond the two-process
dynamic of his 2001 to address the problem of changing conceptions of
rationality (i.e., intersubjective objectivity) and to bring in a
wider social dimension. Like Renn, Friedman makes philosophical
reflection a key to understanding changes so rapid that they amount to
discontinuities. Up to a point he defends Kuhn on the existence of
scientific revolutions and incommensurability. Kuhn ran into trouble
with incommensurability and relativism, he says, for failing to
include the history of scientific *philosophical* reflection
that parallels the first-order, technical scientific work itself.
Friedman's leading example is also the relativity
revolution.



Why do philosophers need to appeal to serious history of science? From
the beginning, Friedman has answered this question by insisting on the
importance of the history of science to locate the emergence of
philosophical ideas in their historical scientific context and vice
versa--thus to understand the *interaction* between what
is commonly called scientific work and philosophical work (Domski
& Dickson 2010: 4). For example, Newton's mechanical system
of the world was shaped by philosophical and theological interests
that Newton and his contemporaries considered directly relevant
(internal not external), as well as socio-political interests. And
likewise for Kant and Poincare and Einstein and many other
thinkers, great and small. To the degree that we retain an
internal/external distinction, it is historically relative. Unlike
most other historical philosophers, Friedman furnishes the intricate
technical 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 History
and Philosophy of Science* (2010), edited by Mary Domski and
Michael Dickson, and containing a book-length response (Friedman
2010). Their introduction to the volume is a "manifesto"
for "synthetic history" (2010: 11ff, 572ff). This sense of
'synthetic' is not opposed to 'analytic', they
insist. For example, rather than separating out the mathematical,
physical, philosophical, theological and other social-contextual
constituents of Newton's work for separate disciplinary
treatment, synthetic history follows Friedman in exploring the ways
these relate to one another to achieve an outcome with a satisfying
convergence (2010: 15ff). Although inspired by Friedman's work,
the manifesto denies that Friedman's two-process view is
essential to synthetic history. (See also the extensive discussion of
Friedman by Menachem Fisch (forthcoming), a work centered on George
Peacock's struggle with rational consistency that helped produce
a 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"
(*epistemes*) and Alistair Crombie's "styles
of scientific thinking" (Crombie 1994) as inspirations. Examples
of such styles are the Greek discovery or invention of axiomatic
geometry, the laboratory science that emerged in the Scientific
Revolution (Shapin & Schaffer 1985), and modern probability theory
and statistical inference (Hacking 1975). Hacking returns to
Kant's "how possible?" question, the answer to which
establishes the necessary conditions for a logical space of reasons in
which practitioners can make true or false claims about objects and
pose research questions about them. And Hacking also historicizes the
Kantian conception.



> 
> 
> The historical *a priori* points at conditions whose dominion
> is as inexorable, there and then, as Kant's synthetic *a
> priori*. Yet they are at the same time conditioned and formed in
> history, and can be uprooted by later, radical, historical
> transformations. T.S. Kuhn's paradigms have some of the
> character of a historical *a priori*. (Hacking 2002: 5)
> 
> 
> 
> ...
> 
> 
> 
> [S]cientific styles of thinking & doing are not good
> *because* they find out the truth. They have become part of our
> standards for what it is, to find out the truth. They establish
> criteria of truthfulness. ... Scientific reason, as manifested in
> Crombie's six genres of inquiry, has no foundation. The styles
> *are* how we reason in the sciences. To say that these styles
> of thinking & doing are self-authenticating is to say that they
> are 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 independent
> of itself. (2012: 605; Hacking's emphasis)
> 
> 
> 



As in early Kuhn, there is a kind of circularity here that is perhaps not
vicious but, quite the contrary, bootstraps the whole enterprise.
Hacking describes changes in historical *a prioris* as
"significant singularities during which the coordinates of
'scientific objectivity' are rearranged" (2002:
6).



Unlike Kuhnian paradigms, several of Hacking's styles of
thinking and doing can exist side by side, e.g., the laboratory and
hypothetical modeling traditions. Yet people living before and after
the historical crystallization of a style would find each other
mutually unintelligible. Hacking recognizes that Kuhnian problems of
relativism lurk in such positions. "Just as statistical reasons
had no force for the Greeks, so one imagines a people for whom none of
our reasons for belief have force" (2002: 163). This sort of
incommensurability is closer to Feyerabend's extreme cases (as
in 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" philosophical
> discussions of such topics as incommensurability, indeterminacy of
> translation, and conceptual schemes seem to discuss truth where they
> ought to be considering truth-or-falsehood. (2002: 160)
> 
> 
> 



For an illuminating exposition and critique of Hacking's
position, see Kusch (2010, 2011).


 A still more integrative role for historical epistemology is
articulated by Hasok Chang (2004, 2012). Chang is a nonrealist who
boldly goes beyond the case-study genres of both philosophers and
professional historians to propose what he terms "complementary
science", a fully integrated historical and philosophical
approach that does not stop with pointing out historical contingencies
but also investigates them scientifically, e.g., by repeating and
extending historical experimental practices. Chang's idea is
that complementary science can preserve previously gained knowledge
and unanswered questions now in danger of becoming lost, and can even
build upon them as a complement to today's highly specialized
scientific disciplines. The results can be published as genuine, if
non-mainstream, scientific contributions. For example, in his own work
he tries to bring the debate over phlogiston to life as well as that
over the nature of water and the question of its boiling point. For
his work, Chang leaves both his armchair and the library, for he needs
scientific equipment and laboratory space in addition to the usual
scholarly materials.



Historical epistemology faces a variety of criticisms, including some
inherited from the Battle of the Big Systems, e.g., whether
rationality and objectivity can be locally preserved during major
transformations and how to have thoroughgoing historicity, including
historical relativity, without full-blown relativism. Generalization
problems still lurk at the meso-scale of historical epistemology. Some
critics question whether historical epistemology is anything new,
sometimes complaining that it just revives traditional history of
ideas. Some would question its neo-Kantian underpinnings. For example,
how can we really identify and individuate the
"categories" employed by scholars such as Hacking and
Daston? (See Kusch 2010, 2011 and Sciortino 2017.) Skeptics ask what
difference historical epistemology makes to science, history, or
philosophy of science. Is it more than a faddish relabeling of work
already well underway? Are new historical and/or philosophical methods
required to conduct such a study? Given its different strands, is it
coherent as a movement? Various adherents disagree on what it includes
and even what to call it. Although Daston declares that
Hacking'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 doing
whiggish "history of the present". Scholars such as
Nersessian, ABC (Andersen, Barker, & Chen 2006), and Renn rely
heavily on recent work in cognitive science, whereas sociologists
still tend to shun cognitive psychology.



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