## 1. The Problems of Revolution and Innovative Change



The difficulties in identifying and conceptualizing scientific
revolutions involve many of the most challenging issues in
epistemology, methodology, ontology, philosophy of language, and even
value theory. With revolution we immediately confront the problem of
deep, possibly noncumulative, conceptual and practical change, now in
modern science itself, a locus that Enlightenment thinkers would have
found surprising. And since revolution is typically driven by new
results, or by a conceptual-cum-social reorganization of old ones,
often highly unexpected, we also confront the hard problem of
understanding creative innovation. Third, major revolutions supposedly
change the normative landscape of research by altering the goals and
methodological standards of the enterprise, so we face also the
difficult problem of relating descriptive claims to normative claims
and practices, and changes in the former to changes in the latter.



Comparing the world of business innovation and economic theory
provides a perspective on the difficulty of these problems, for both
the sciences and the industrial technologies change rapidly and
sometimes deeply (in the aforementioned ways), thanks to what might be
termed "innovation push"--both the pressure to
innovate (to find and solve new problems, thereby creating new
designs) and the pressure to accommodate innovation (see, e.g.,
Christensen 1997; Christensen and Raynor, 2003; Arthur 2009). In a
market economy, as in science, there is a premium on change driven by
innovation. Yet most economists have treated innovations as exogenous
factors--as accidental, economically contingent events that come
in from outside the economic system to work their effects. It is
surprising that only recently has innovation become a central topic of
economic theorists. Decades ago, the Austrian-American economist
Joseph Schumpeter characterized economic innovation as



> 
> the process of industrial mutation--if I may use that biological
> term--that incessantly revolutionizes the economic structure
> *from within*, incessantly destroying the old one, incessantly
> creating a new one. This process of Creative Destruction is the
> essential fact about capitalism. [1942, chap. VII; Schumpeter's
> emphasis]
> 



Unfortunately, economists largely ignored this sort of claim (made
also by a few others) until the recent development of economic growth
theory (e.g., Robert Solow, Paul Romer, and W. Brian Arthur: see
Beinhocker 2006 and Warsh 2006). The result was an inability of
economic models to account for economic innovation endogenously and,
thereby, to gain an adequate understanding of the generation of
economic wealth.



The parallel observation holds for philosophy of science. Here, too,
the leading philosophers of science until the 1960s--the logical
empiricists and the Popperians--rejected innovation as a
legitimate topic, even though it is the primary intellectual driver of
scientific change and producer of the wealth of skilled knowledge that
results. The general idea is that the so-called context of discovery,
the context of creatively constructing new theories, experimental
designs, etc., is only of historical and psychological interest, not
epistemological interest, and that the latter resides in the epistemic
status of the "final products" of investigation. On this
view, convincing confirmation or refutation of a claim enables
scientists to render an epistemic judgment that detaches it from its
historical context. This judgment is based on the logical relations of
theories and evidence rather than on history or psychology. According
to this traditional view, there exists a logic of justification but
not a logic of discovery. The distinction has nineteenth-century
antecedents (Laudan 1980). Cohen and Nagel (1934) contended that to
take historical path into account as part of the epistemic assessment
was to confuse historical questions with logical questions and thereby
to commit what they called a "genetic fallacy." However,
the context of discovery / context of justification distinction (or
family of distinctions) is often attributed to Reichenbach (1938).
(See the entry on
 Reichenbach.
 For recent discussion see Schickore and Steinle, 2006.)



Today there are entire academic industries devoted to various aspects
of the topic of scientific revolutions, whether political or
scientific, yet we have no adequate general theory or model of
revolutions in either sphere. This article will focus on Thomas
Kuhn's conception of scientific revolutions, which relies partly
on analogies to political revolution and to religious conversion.
Kuhn's is by far the most discussed account of scientific
revolutions and did much to reshape the field of philosophy of
science, given his controversial claims about incommensurability,
rationality, objectivity, progress, and realism. For a general account
of Kuhn's work, see the entry on
 Kuhn.
 See also Hoyningen-Huene (1993), and Bird (2001).


## 2. History of the Concept of Scientific Revolution



What history lies behind the terms 'revolution' and
'scientific revolution'? The answer is an intriguing mix
of accounts of physical phenomena, political fortunes, and conceptions
of chance, fate, and history. Originally a term applying to rotating
wheels and including the revolution of the celestial bodies (as in
Copernicus' title: *De Revolutionibus Orbium Coelestium*)
and, more metaphorically, the wheel of fortune,
'revolution' was eventually transferred to the political
realm. The term later returned to science at the metalevel, to
describe developments within science itself (e.g., "the
Copernican Revolution"). Christopher Hill, historian of
seventeenth-century Britain and of the so-called English Revolution in
particular, writes:



> 
> Conventional wisdom has it that the word 'revolution'
> acquired its modern political meaning only after 1688. Previously it
> had been an astronomical and astrological term limited to the
> revolution of the heavens, or to any complete circular motion. [Hill
> 1990, 82]
> 



Hill himself dates the shift to the governmental realm somewhat
earlier, pointing out that the notion of *over*turning was also
present in groups of reformers who aspired to return human society to
an earlier, ideal state: *over*turning as *re*turning.
This conception of revolution as overturning was compatible with a
cyclical view of history as a continuous process.



It was in the socio-political sphere that talk of revolution as a
successful uprising and overturning became common. In this sense, a
revolution is a successful revolt, 'revolution' being an
achievement or product term, whereas 'to revolt' is a
process verb. The fully modern conception of revolution as involving a
break from the past--an abrupt, humanly-made overturning rather
than a natural overturning--depended on the linear, progressive
conception of history that perhaps originated in the Italian
Renaissance, gained strength during the Protestant Reformation and the
two later English revolutions, and became practically dogma among the
champions of the scientific Enlightenment. The violent English
Revolution of the 1640s gave political revolution a bad name, whereas
the Glorious Revolution of 1688, a bloodless, negotiated compromise,
reversed this reputation.


### 2.1 Scientific Revolution as a Topic for Historiography of Science



When did the term 'revolution' become a descriptor of
specifically scientific developments? In the most thorough treatment
of the history of the concept of scientific revolution, I. B. Cohen
(1985) notes that the French word *revolution* was being used
in early eighteenth-century France to mark significant developments.
By mid-century it was pretty clear that Clairaut, D'Alembert,
Diderot and others sometimes applied the term to scientific
developments, including Newton's achievement but also to
Descartes' rejection of Aristotelian philosophy. Cohen fails to
note that Emilie Du Chatelet preceded them, in her
*Institutions de Physique* of 1740, where she distinguished
scientific from political revolutions (Chatelet and Zinnser
2009, p. 118). However, the definition of *revolution* in the
*Encyclopedie* of the French *philosophes* was
still political. Toward the end of the century, Condorcet could speak
of Lavoisier as having brought about a revolution in chemistry; and,
indeed, Lavoisier and his associates also applied the term to their
work, as did Cuvier to his. Meanwhile, of course, Kant, in *The
Critique of Pure Reason* (first edition 1781), spoke of his
"Copernican Revolution" in philosophy. In fact, Cohen
(1985) and Ian Hacking (2012) credit Kant with originating the idea of
a scientific revolution, although Kant had read Du Chatelet.
Interestingly, for Kant (1798) political revolutions are, by nature,
unlawful, whereas Locke, in his social contract theory, had permitted
them under special circumstances.



It was during the twentieth century that talk of scientific
revolutions slowly gained currency. One can find scientists using the
term occasionally. For example, young Einstein, in a letter to his
friend Habicht, describes his new paper on light quanta as "very
revolutionary" (Klein 1963, 59). The idea of radical breaks was
foreign to such historians of science as Pierre Duhem and George
Sarton, but Alexandre Koyre, in *Etudes
Galileennes* (1939), rejected inductivist history,
interpreting the work of Galileo as a sort of Platonic intellectual
transformation. (See Zambelli (2016) for a revealing account of
Koyre's own background.) In *The Origins of Modern
Science: 1300-1800* (1949 and later editions), widely used
as a course text, Herbert Butterfield, a political historian working
mainly from secondary sources, wrote a compact summary of the
Scientific Revolution, one that emphasized the importance of
conceptual transformation rather than the infusion of new empirical
information. The anti-whiggism that he had advocated in his *The
Whig Interpretation of History* (1931) became a major constraint
on the new historiography of science, especially in the Anglophone
world. In *Origins*, Butterfield applied the revolution label
not only to the Scientific Revolution and to several of its components
but also to "The Postponed Revolution in Chemistry" (a
chapter title), as if it were a delayed component of the Scientific
Revolution. His history ended there. A revolution for Butterfield is a
major event that founds a scientific field. Taken together, these
revolutions founded modern science. As the title of his book suggests,
he was concerned with origins, not with what comes after the founding.
In the Introduction he famously (or notoriously) stated that the
Scientific Revolution



> 
> outshines everything since the rise of Christianity and reduces the
> Renaissance and Reformation to the rank of mere episodes, mere
> internal displacements, within the system of medieval Christendom.
> 



For Butterfield, the Scientific Revolution was a watershed event on
the scale of total human history, an event that, somewhat ironically
and somewhat like Christianity according to its believers, enabled the
sciences, to some degree, to escape from history and thereby to become
exceptional among human endeavors. Subsequently, A. Rupert Hall, a
full-fledged historian of science who worked from primary sources,
published *The Scientific Revolution: 1500-1800* (Hall
1954). Soon many other scholars spoke of *the* Scientific
Revolution, the achievements of the period from Copernicus to Newton,
including such luminaries as Kepler, Galileo, Bacon, Descartes,
Huygens, Boyle, and Leibniz.



Then Thomas Kuhn and Paul Feyerabend challenged received views of
science and made talk of revolutionary breaks and incommensurability
central to the emerging new field of history and philosophy of
science. They asserted that major conceptual changes lay in the future
of mature, modern sciences as well as in their past. Kuhn (1962, ch.
IX) contended that there will be no end to scientific revolutions as
long as systematic scientific investigation continues, for they are a
necessary vehicle of ongoing scientific progress-necessary to
break out of dated conceptual frameworks. In other words, there are
both founding revolutions, in something like Butterfield's sense
of threshold events to maturity, and a never-ending series of later
revolutions within an ongoing field, no matter how mature it is.
However, soon after *Structure*, Kuhn had second thoughts and
eventually abandoned the Butterfield conception of revolution, on the
ground that even his so-called preparadigm schools had their paradigms
(Kuhn 1974, 460, note 4; details below). So multiple Kuhnian paradigms
in long-term competition now became possible.



The Scientific Revolution was the topic around which the field of
history of science itself came to maturity. Kuhn's
popularization of the idea that even the mature natural sciences
undergo deep conceptual change stimulated much general intellectual
interest in the history of science during the 1960s and 1970s. The
revolution frame of reference was also a boon to historiographical
narrative itself (see Cohen 1985 and Nickles 2006). And by challenging
the received, quasi-foundational, Enlightenment conception of science,
history of science and related philosophies of science gained great
cultural significance for a time.



In recent decades, however, many historians have contested even the
claim that there was a single, coherent development appropriately
called "the Scientific Revolution." Steven Shapin (1996,
1) captured the unease in his opening sentence: "There was no
such thing as the Scientific Revolution, and this is a book about
it." Everyone agrees that a series of rapid developments of
various kinds took place during the period in question, but the
operative word here is 'various'. One difficulty is that
no one has succeeded in capturing a 150-year (or more) period of work
in an insightful, widely accepted characterization that embraces the
important changes in theory, method, practices, instrumentation,
social organization, and social status ranging over such a wide
variety of projects. The very attempt has come to seem reductionist.
Older styles of historical writing were characterized by grand
narratives such as "the mechanization of the world
picture" (Dijksterhuis 1961; original, Dutch edition, 1950) and
humanity's passage from subjective superstition to objectivity
and mathematical precision (Gillispie 1960). Philosophically oriented
writers attempted to find unity and progress in terms of the discovery
of a new, special scientific method. Today even most philosophers of
science dismiss the claim that there exists a powerful, general,
scientific method, the discovery of which explains the Scientific
Revolution and the success of modern science. Quite the contrary:
effective scientific methods are themselves the product of painstaking
work at the frontier--scientific results methodized--and are
hence typically laden with the technical content of the specialty in
question. There is no content-neutral, thereby general and timeless
method that magically explains how those results were achieved
(Schuster and Yeo 1986, Nickles 2009).



Continuity theorists such as Pierre Duhem (1914), John Herman Randall
(1940), A. C. Crombie (1959, 1994), and more recent historians such as
Peter Dear (2001) have pointed out a second major difficulty in
speaking of "the Scientific Revolution." It is hard to
locate the sharp break from medieval and Renaissance practices that
discontinuity historians from Koyre to Kuhn have celebrated.
When examined closely in their own cultural context, all the supposed
revolutionaries are found to have had one foot in the old traditions
and to have relied heavily on the work of predecessors. In this vein,
J. M. Keynes famously remarked that Newton was "the last of the
magicians," not the first of the age of reason (Keynes 1947).
Still, most historians and philosophers would agree that the rate of
change of scientific development increased notably during this period.
Hence, Shapin, despite his professional reservations, could still
write an instructive, synthetic book about the Scientific Revolution.
The most thorough appraisal of historiographical treatments of the
Scientific Revolution is H. Floris Cohen's (1994).



The Scientific Revolution supposedly encompassed all of science or
natural philosophy, as it then existed, with major social
implications, as opposed to more recent talk of revolutions within
particular technical fields. Have there been other multidisciplinary
revolutions? Some have claimed the existence of a "second
scientific revolution" in the institutional structure of the
sciences in the decades around 1800, especially in France, others
(including Kuhn 1977a, ch. 3) of a multidisciplinary revolution in the
"Baconian sciences" (chemistry, electricity, magnetism,
heat, etc.) during roughly the same time period. Enrico Bellone 1980),
Kuhn, and others Kuhn have focused on the tremendous increase in
mathematical abstraction and sophistication during the early-to-mid
nineteenth century that essentially created what we know as
mathematical physics. Still others have claimed that there was a
general revolution in the sciences in the decades around 1900. (See
also Cohen 1985, chap. 6, for discussion of these claims.)



For many historians, 'the Scientific Revolution' now
describes a topic area rather than a clearly demarcated event. They
find it safer to divide the Scientific Revolution into several more
topic- and project-specific developments. However, in their unusually
comprehensive history of science textbook, Peter Bowler and Iwan Morus
(2005) query of practically every major development they discuss
whether or not it was a genuine revolution at all, at least by Kuhnian
standards. More recently, David Wootton's (2015) is a
revisionist account that returns to a more heroic understanding of the
Scientific Revolution.


### 2.2 Scientific Revolution as a Topic for Philosophy



Commitment to the existence of deep scientific change does not, for
all experts, equate to a commitment to the existence of revolutions in
Kuhn's sense. Consider the historically-oriented
philosopher Stephen Toulmin (1953, 1961, 1972), who wrote of
"ideals of natural order," principles so basic that they
are normally taken for granted during an epoch but that are subject to
eventual historical change. Such was the change from the Aristotelian
to the Newtonian conception of inertia. Yet Toulmin remained critical
of revolution talk. Although the three influential college course
texts that he co-authored with June Goodfield recounted the major
changes that resulted in the development of several modern sciences
(Toulmin and Goodfield 1961, 1962, 1965), these authors could write,
already about the so-called Copernican Revolution:



> 
> We must now look past the half-truths of this caricature, to what
> Copernicus attempted and what he in fact achieved. For in science, as
> in politics, the term 'revolution'--with its
> implication that a whole elaborate structure is torn down and
> reconstructed overnight--can be extremely misleading. In the
> development of science, as we shall see, thorough-going revolutions
> are just about out of the question. [1961, 164]
> 



The Toulmin and Goodfield quotation invites us to ask, When did talk
of scientific revolutions enter philosophy of science in a significant
way? And the answer seems to be: there is a sprinkling of uses of the
term 'scientific revolution' and its cognates prior to
Kuhn, but these were ordinary expressions that did not yet have the
status of a technical term.



Given the prominence of the topic today, it is surprising that we do
not find the term in Philipp Frank's account of the positivist
discussion group in Vienna in the early twentieth century. However,
Frank (1957) does speak of their perception of a "crisis"
in modern physics caused by the undermining of classical mechanics by
special relativity and quantum mechanics, and it was common to speak
of this or that worldview or world picture (*Weltanschauung*,
*Weltbild*), e.g., the electromagnetic vs. the Einsteinian vs.
the mechanical picture. Nor do we find talk of scientific revolutions
in the later Vienna Circle, even after the diaspora following the rise
of Hitler. The technical term does not appear in Karl Popper's
*Logik der Forschung* (1934) nor in his 1959 English expansion
of that work as *The Logic of Scientific Discovery*, at least
not important enough to be indexed. Hans Reichenbach (1951) speaks
rather casually of the revolutions in physics. The technical term is
not in Ernest Nagel's *The Structure of Science* (1961).
Nor is it in Stephen Pepper's *World Hypotheses* (1942).
It plays no significant role in N. R. Hanson's *Patterns in
Discovery* (1958), despite its talk of the theory-ladenness of
observation and perceptual Gestalt switches. Meanwhile, there were, of
course, a few widely-read works in the background that spoke of major
ontological changes associated with the rise of modern science,
especially E. A. Burtt's *Metaphysical Foundations of Modern
Physical Science* (1924). Burtt's book influenced
Koyre, who, in turn, influenced Kuhn.



In his retrospective autobiographical lecture at Cambridge in 1953,
Popper did refer to the dramatic political and intellectual events of
his youth as revolutionary:



> 
> [T]he air was full of revolutionary slogans and ideas, and new and
> often wild theories. Among the theories which interested me
> Einstein's theory of relativity was no doubt by far the most
> important. The others were Marx's theory of history,
> Freud's psycho-analysis, and Alfred Adler's so-called
> 'individual psychology'. [Popper 1957]
> 



And during the 1960s and 1970s, Popper indicated that, according to
his "critical approach" to science and philosophy, all
science should be revolutionary--revolution in permanence. But
this was a tame conception of revolution compared to Kuhn's,
given Popper's two logical criteria for a progressive new
theory: (a) it must logically conflict with its predecessor and
overthrow it; yet (b) "a new theory, however revolutionary, must
always be able to explain fully the success of its predecessor"
(Popper 1975). As we shall see, Kuhn's model of revolution
rejects both these constraints (depending on how one interprets his
incommensurability claim) as well as the idea of progress toward
final, big, theoretical truths about the universe. Kuhn dismissed
Popper's notion of revolution in perpetuity as a contradiction
in terms, on the ground that a revolution is something that overthrows
a long and well-established order, in violation of the rules of
that order. Kuhn (1970) also vehemently rejected Popper's
doctrine of falsification, which implied that a theory could be
rejected in isolation, without anything to replace it. According to
Popper, at any time there may be several competing theories being
proposed and subsequently refuted by failed empirical
tests--rather like several balloons being launched, over time,
and then being shot down, one by one. Popper's view thus faces
the difficulty, among others, of explaining the long-term coherence
that historians find in scientific research.



Beginning in the 1960s, several philosophers and historians addressed
this difficulty by proposing the existence of larger units (than
theories) of and for analysis. Kuhn's paradigms, Imre
Lakatos's research programmes, Larry Laudan's research
traditions (Lakatos 1970, Laudan 1977), and the widespread use of
terms such as 'conceptual scheme', 'conceptual
framework', 'worldview', and *Weltanschauung*
(Suppe 1974) instanced this felt need for larger-sized units among
Anglo-American writers, as had Toulmin's old concept of ideals
of natural order. These stable formations correspondingly raised the
eventual prospect of larger-scale instabilities, for an abrupt change
in such a formation would surely be more dramatic, more revolutionary,
than a Popperian theory change. However, none of the other writers
endorsed Kuhn's radical conception of scientific revolution.
Meanwhile, Michel Foucault 1963, 1966, 1969, 1975), working in a
French tradition, was positing the existence of "discursive
formations" or *epistemes*, sets of deep-structural
cultural rules that define the limits of discourse during a period.
Section 5 returns to this theme.


### 2.3 Criteria for Identifying Scientific Revolutions



I. B. Cohen (1985, chap. 2) lays down four historical tests, four
necessary conditions, for the correct attribution of a revolution.
First, the scientists involved in the development must perceive
themselves as revolutionaries, and relevant contemporaries must agree
that a revolution is underway. Second, documentary histories must
count it as a revolution. Third, later historians and philosophers
must agree with this attribution and, fourth, so must later scientists
working in that field or its successors. By including both reports
from the time of the alleged revolution and later historiographical
judgments, Cohen excludes people who claimed in their day to be
revolutionaries but who had insufficient impact on the field to
sustain the judgment of history. He also guards against whiggish, post
hoc attributions of revolution to people who had no idea that they
were revolutionaries. His own four examples of big scientific
revolutions all have an institutional dimension: The Scientific
Revolution featured the rise of scientific societies and journals, the
second was the aforementioned revolution in measurement from roughly
1800 to 1850 (which Kuhn, too, called "the second scientific
revolution"; 1977, 220). Third is the rise of university
graduate research toward the end of that century. Fourth is the
post-World War II explosion in government funding of science and its
institutions. 



Cohen sets the bar high. Given Copernicus' own conservatism and
the fact that few people paid attention to his work for half a
century, the Copernican achievement was not a revolution by
Cohen's lights. Or if there was a revolution, should it not be
attributed to Kepler, Galileo, and Descartes? This thought further
problematizes the notion of revolution, for science studies experts as
well as scientists themselves know that scientific and technological
innovation can be extremely nonlinear in the sense that a seemingly
small, rather ordinary development may eventually open up an entire
new domain of research problems or a powerful new approach. Consider
Planck's semi-classical derivation of the empirical blackbody
radiation law in 1900, which, under successively deeper theoretical
derivations by himself and (mainly) others over the next two and a
half decades, became a pillar of the revolutionary quantum theory. As
Kuhn (1978) shows, despite the flood of later attributions to Planck,
it is surprisingly difficult, on historical and philosophical grounds,
to justify the claim that he either was, or saw himself as, a
revolutionary in 1900 and for many years thereafter. (Kuhn 2000b
offers a short summary.) Augustine Brannigan (1981) and Robert Olby
(1985) defend similar claims about Mendel's alleged discovery of
Mendelian inheritance.



These examples suggest that Cohen's account of scientific
revolution (and Kuhn's) is tied too closely to the idea of
political revolution in placing so much weight on the intentions of
the generators. In the last analysis, many would agree, revolution,
like speciation in biology, is a retrospective judgment, a judgment of
eventual consequences, not something that is always directly
observable as such in its initial phases, e.g., in the stated the
intentions of its authors. On the other hand, a counterintuitive
implication of this consequentialist view of revolutions is that there
can be revolution without revolt (assuming that revolt is a deliberate
course of action), revolutionary work without authors, so to speak, or
at least revolutionary in eventual meaning despite the authors'
intentions. Then why not just speak of evolution rather than
revolution in such cases? For, as we know by analogy from evolutionary
biology, in the long run evolution can be equally transformative, even
moreso (see below).



A related point is that, insofar as revolutions are highly nonlinear,
it is difficult to ascribe to them any particular reason or cause;
for, as indicated, the triggering events can be quite ordinary work,
work that unexpectedly opens up new vistas for exploration. A small
cause may have an enormous effect. To be sure, the state of the
relevant scientific system must be such that the events do function as
triggers, but we need not expect that such a system always be readily
identifiable as one in crisis in Kuhn's sense. Rather, the
highly nonlinear revolutionary developments can be regarded as
statistical fluctuations out of a "noisy" background of
ordinary work. At any rate, on this view it is a mistake to think that
explaining revolutions requires locating a momentous breakthrough
(Nickles 2012a and b).



What of the common requirement that revolutions be rapid, event-like,
unlike the century-and-a half-long Scientific Revolution? Brad Wray
(2011, 42f) answers that there is no reason that a revolution need be
an abrupt event. What is important is how thoroughgoing the change is
and that it be change at the community level rather than a Gestalt
switch experienced by certain individuals. (After the original
publication of *Structure*, Kuhn acknowledged his confusion in
attributing Gestalt switches to the community as a whole as well as to
individuals.) On Wray's view, evolution and revolution are not
necessarily opposed categories. And with this understanding, the
Toulmin and Goodfield comment quoted above becomes compatible with
revolutionary transformation, which, not surprisingly, takes time to
become thoroughgoing. Meanwhile, the Butterfield quotation suggests
that what counts as a striking change is a matter of historical scale.
By our lights today, 150 years is a long time; but, against the long
sweep of total human history, a change of the magnitude of the
Scientific Revolution was quite rapid. Perhaps today's rapid
pace of scientific and technological innovation makes us impatient
with slower-scaled developments in the past. And it is surely the case
the some of the slow, large-scale transformations now underway are
scarcely visible to us.



Finally, what of Butterfield's criterion of broader social
impacts? Kuhn retained this criterion in *The Copernican
Revolution*, but revolutions increasingly become changes in
specialist communities in his later work, since those communities
insulate themselves from the larger society. In the chapter on the
invisibility of revolutions in *Structure*, Kuhn tells us that
a tiny subspecialty can undergo a revolution that looks like a
cumulative change even to neighboring fields of the same scientific
discipline. In this respect Kuhn remained an internalist.


## 3. Kuhn's Early Account of Scientific Revolutions



Although virtually no one in the science studies fields accepts
Kuhn's model in *Structure* as correct in detail, there
has been a revival of interest in his views since his death and, more
recently, in connection with the fiftieth anniversary in 2012 of the
book's original publication. Some examples are: the fiftieth
anniversary edition of *Structure* itself, including a valuable
introduction by Ian Hacking; Kuhn (2000a), a collection that records
the later evolution of Kuhn's thought; Sankey (1997); Bitbol
(1997); Fuller (2000); Bird (2001); Friedman (2001); Andersen (2001);
Sharrock and Read (2002); Nickles (2003a); Gonzalez (2004);
Soler et al. (2008); Agazzi (2008); Gattei (2008); Torres (2010); Wray
(2011), Kindi and Arabatzis (2012), De Langhe (2013), Marcum (2015),
and Richards and Daston (2016). Kuhn on revolutions has helped to
shape many symposia on scientific realism and related matters, for
example, Soler (2008) on contingency in the historical development of
science and Rowbottom and Bueno (2011) on Bas van Fraassen's
(2002) treatment of stance, voluntarism, and the viability of
empiricism. Since Kuhn's work is discussed in some detail in
other contributions to this *Encyclopedia* (see, especially,
"Kuhn, Thomas", and "The Incommensurability of
Scientific Theories"), a brief account will suffice here. For a
detailed reading guide to *Structure*, consult Preston
(2008).


### 3.1 Kuhn's Early Model of Scientific Development



According to Kuhn in *Structure*, a loosely characterized group
of activities, often consisting of competing schools, becomes a mature
science when a few concrete problem solutions provide models for what
good research is (or can be) in that domain. These exemplary
problems-cum-solutions become the basis of a "paradigm"
that defines what it is to do "normal science." As its
name suggests, normal science is the default state of a mature science
and of the community of researchers who constitute it. The paradigm
informs investigators what their domain of the world is like and
practically guarantees that all legitimate problems can be solved in
its terms. Normal science is convergent rather than divergent: it
actively discourages revolutionary initiatives and essentially novel
(unexpected) discoveries, for these threaten the paradigm. However,
normal research is so detailed and focused that it is bound to turn up
anomalous experimental and theoretical results, some of which will
long resist the best attempts to resolve them. Given the historical
contingencies involved in the formation of guiding paradigms as well
as the fallibility of all investigators, it would be incredibly
improbable for everything to end up working perfectly. According to
Kuhn, anomalies are therefore to be expected. Historically, all
paradigms and theory complexes face anomalies at all times. If and
when persistent efforts by the best researchers fail to resolve the
anomalies, the community begins to lose confidence in the paradigm and
a crisis period ensues in which serious alternatives can now be
entertained. If one of these alternatives shows sufficient promise to
attract a dominant group of leading researchers away from the old
paradigm, a paradigm shift or paradigm change occurs--and that is
a Kuhnian revolution. The radicals accomplish this by replacing the
former set of routine problems and problem-solving techniques
(exemplars) by a new set of exemplars, making the old practices seem
defective, or at least old fashioned.


### 3.2 Revolution as Incommensurable Paradigm Change



The new paradigm overturns the old by displacing it as no longer a
competent guide to future research. In the famous (or
notorious)chapter X of *Structure*, Kuhn claims that the change
is typically so radical that the two paradigms cannot be compared
against the same goals and methodological standards and values.
Moreover, the accompanying meaning shift of key terms, such as
'simultaneous', 'mass', and
'force' in physics, leads to communication breakdown. In
effect, scientists on different sides of a paradigm debate "live
in different worlds." Kuhn speaks of scientists experiencing a
kind of gestalt switch or religious conversion experience. The heated
rhetoric of debate and the resulting social reorganization, he says,
resemble those of a political revolution. "Like the choice
between political institutions, that between competing paradigms
proves to be a choice between incompatible modes of community
life" (1970, 94). The comparison of scientific with political
revolutions should not surprise, given the entangled history of the
term 'revolution', but claiming such close similarity
enraged philosophical and cultural critics of Kuhn.



The typical paradigm change does not involve a large infusion of new
empirical results, Kuhn tells us (chs. IX and X). Rather, it is a
conceptual reorganization of otherwise familiar materials, as in the
relativity revolution. A paradigm change typically changes goals,
standards, linguistic meaning, key scientific practices, the way both
the technical content and the relevant specialist community are
organized, and the way scientists perceive the world. (For the often
neglected practices dimension in Kuhn's account, see Rouse,
2003.) Nor can we retain the old, linear, cumulative conception of
scientific progress characteristic of Enlightenment thinking; for,
Kuhn insists, attempts to to show that the new paradigm contains the
old, either logically or in some limit or under some approximation,
will be guilty of a fallacy of equivocation. The meaning change
reflects the radical change in the assumed ontology of the world. A
second Kuhnian objection to cumulative progress is what has come to be
called "Kuhn loss" (see Post 1971, 229, n. 38). Rarely
does the new paradigm solve all of the problems that its predecessor
apparently solved. So even in this sense the new paradigm fails
completely to enclose the old. The consequence, according to Kuhn, is
that attempts to defend continuous, cumulative scientific progress by
means of theory reduction or even a correspondence relationship (e.g.,
a limiting relationship) between a theory and its predecessor must
fail. Revolutions produce discontinuities.



Given all these changes, Kuhn claimed that the two competing paradigms
are "incommensurable", a technical term that he repeatedly
attempted to clarify. Traditional appeals to empirical results and
logical argument are insufficient to resolve the debate. For details
of the incommensurability debate, see the entry "The
Incommensurability of Scientific Theories." as well as
Hoyningen-Huene and Sankey (2001) as a sample of the large literature
on incommensurability.



Naturally, many thinkers of a logical empiricist or Popperian bent, or
simply of an Enlightenment persuasion, were shocked by these claims
and responded with a barrage of criticism--as if Kuhn had
committed a kind of sacrilege by defiling the only human institution
that could be trusted to provide the objective truth about the world.
Today there is fairly wide agreement that some of Kuhn's claims
no longer look so radical. Meanwhile, Kuhn himself was equally shocked
by the vehemence of the attacks and (to his mind) the willful
distortion of his views (see, e.g., Lakatos and Musgrave 1970). In
later papers and talks, he both clarified his views and softened some
of his more radical claims. Critics reacted to the radical views of
Paul Feyerabend (1962, 1975) in a somewhat similar manner. (For
details, see the entry "Feyerabend, Paul.")



Given that cyclic theories of history have, for the most part, long
given way to linear, progressive accounts, readers may be surprised at
Kuhn critic, physicist Stephen Weinberg's comment that
Kuhn's overall model is still, in a sense, cyclic (Weinberg
2001). In fact, Kuhn himself had already recognized this. After the
founding paradigm in Kuhn's account in *Structure*, we
have normal science under a paradigm, then crisis, then revolution,
then a new paradigm--a development that brings back a new period
of normal science. At this abstract level of description, the model is
indeed cyclic, but of course the new paradigm heads the science in
question in a new direction rather than returning it to a previous
state. Other commentators, including Marxists, have regarded
Kuhn's mechanism as dialectical, as illustrated by the
succession of self-undermining developments in the theory of light,
from a Newtonian particle theory to a wave theory to a new kind of
wave-particle duality. (For the dialectical interpretation see
especially Krajewski 1977 and Nowak 1980 on the idealizational
approach to science, as originated by Karl Marx.)



Somewhat ironically, Kuhn's attempt to revolutionize the
epistemology of science has had a wider socio-cultural impact than
many scientific revolutions themselves. While some of Kuhn's
doctrines step into the postmodern era, he still had a foot in the
Enlightenment, which helps to explain his dismay at the critical
reaction to his work and to radical developments in the new-wave
sociology of science of the 1970s and '80s. For, unlike many
postmodernists (some of whom make use of his work), Kuhn retained a
scientific exceptionalism. He did not doubt that the sciences have
been uniquely successful since the Scientific Revolution. For him,
unlike for many of his critics, revolutions in his radical sense were
great epistemological leaps forward rather than deep scientific
failures. On the science policy front, he intended his work to help
preserve the integrity of this socially valuable enterprise. It is on
science policy issues that Steve Fuller is most critical of Kuhn
(Fuller 2000).



The general problem presented by Kuhn's critique of traditional
philosophy of science is that, although the various sciences have been
successful, we do not understand *how* they have accomplished
this or even how to characterize this success. Enlightenment-style
explanations have failed. For example, Kuhn and Feyerabend (1975),
preceded by Popper, were among the first philosophers to expose the
bankruptcy of the claim that it was the discovery of a special
scientific method that explains that success, a view that is still
widely taught in secondary schools today. And that conclusion (one
that cheered those postmodernists who regard scientific progress as an
illusion) left Kuhn and the science studies profession with the
problem of how science really does work. To explain how and why it had
been so successful became an urgent problem for him--again, a
problem largely rejected as bogus by many science studies scholars
other than philosophers. 



Another of Kuhn's declared tasks in *Structure* was to
solve the problem of social order for mature science, that is, how
cohesive modern science (especially normal science) is possible
(Barnes 1982, 2003). Yet another was to bring scientific discovery
back into philosophical discussion by endogenizing it in his model,
while denying the existence of a *logic* of discovery. Whereas
the logical empiricists and Popper had excluded discovery issues from
philosophy of science in favor of theory of confirmation or
corroboration, Kuhn was critical of confirmation theory and supportive
of historical and philosophical work on discovery. He argued that
discoveries are temporally and cognitively structured and that they
are an essential component of an epistemology of science. In Kuhnian
normal science the problems are so well structured and the solutions
so nearly guaranteed in terms of the resources of the paradigm that
the problems reduce to puzzles (Nickles 2003b). Kuhn kept things under
control there by denying that normal scientists seek essential
innovation, for, as indicated above, major, unexpected discoveries
threaten the extant paradigm and hence threaten crisis and revolution.
So, even in normal science, Kuhn had to admit that major discoveries
are unexpected challenges to the reigning paradigm. They are
anomalous, even exogenous in the sense that they come as shocks from
outside the normal system.



But this is the working scientists' point of view. As noted,
normal science is bound to turn up difficulties that resist
resolution, at least some of which are sooner or later recognized by
the community. In Kuhn's own view, as a historian and
philosopher standing high above the fray, it is deliberate, systematic
normal research that will most readily sow the seeds of revolution and
hence of rapid scientific progress. According to the old
musicians' joke, the fastest way to Carnegie Hall is slow
practice. For Kuhn the fastest way to revolutionary innovation is
intensely detailed normal science.



When it comes to revolution on Kuhn's account, the social order
breaks down dramatically. And here his strategy of taming creative
normal research so as to make room for articulated discovery (the
reduction of research problems to puzzles) also breaks down. Kuhn had
to acknowledge that he had no idea how the scientists in extraordinary
research contexts manage to come up with brilliant new ideas and
techniques. This failure exacerbated his problem of explaining what
sort of continuity underlies the revolutionary break that enables us
to identify the event as a revolution within an ongoing field of
inquiry. As he later wrote:



> 
> Even those who have followed me this far will want to know how a
> value-based enterprise of the sort I have described can develop as a
> science does, repeatedly producing powerful new techniques for
> prediction and control. To that question, unfortunately, I have no
> answer at all.... [1977b, 332]
> 


### 3.3 Progress through Revolutions



Kuhn's work on scientific revolutions raises difficult questions
about whether science progresses and, if so, in what that progress
consists. Kuhn asks (p. 60), "Why is progress a perquisite
reserved almost exclusively for the activities we call science"
and not for art, political theory, or philosophy? Early critics took
him to deny scientific progress, because he rejected the traditional
correspondence theory of truth and the related idea of cumulative
progress toward a representational truth waiting out there for science
to find it. For Kuhn the internalist, the technical goals of science
are endogenously generated and change over time, rapidly during
revolutions. Yet, somewhat paradoxically, Kuhn regarded revolutions as
the *most* progressive components of his model of science.
Unfortunately, he was not able to articulate fully in what that
progress consists, given the issues of truth, incommensurability and
Kuhn loss, a problem that those who reject convergent scientific
realism still face. However, problem-solving know-how and success,
including predictive precision, are major components of his answer.
"[T]he unit of scientific achievement is the solved
problem...." (p. 169). In a retreat from his most radical
statements, Kuhn responded to critics by saying that we do possess a
general set of scientific values that enables us, usually pretty
easily, to order scientific works in historical time according to the
degree in which they realize these values. A new paradigm, he says,
must always treat successfully a serious anomaly left by the old one
as well as opening up new questions for fruitful investigation.



Kuhn's emphasis on scientific practices, relative to the
philosophical state of play in the 1960s, takes up some of the slack
left by the rejection of strong realism. His emphasis on skilled
practice may have been influenced by Michael Polanyi's
*Personal Knowledge* (1958), with its "tacit
knowing" component, although Kuhn denied that he found
Polanyi's account appealing (see, e.g., Baltas et al., 2000, pp.
296f).



If there have been so many revolutions, then why did the world have to
wait for Kuhn to see them? Because, he said, they are largely
invisible. For, after a revolution, the winners rewrite the history of
science to make it look as if the present paradigm is the brilliant
but rational sequel to previous work. The implication is that only
someone of Kuhn's historical sensitivity could be expected to
notice this. (Skeptical critics reply that Kuhn invented the problem
for which he had a solution.) Indeed, in his large book on the history
of the early quantum theory (Kuhn 1978), he moved the origin of the
quantum theory revolution forward five years, from Planck in 1900 to
Einstein and Ehrenfest in 1905. Revisionist historiography by whiggish
scientists, he claimed, had smoothed out the actual history by
crediting Planck with a solution that he actually rejected at the time
to a problem that he did not then have--and by diminishing the
truly radical contribution of Einstein. Kuhn's move again raises
the question whether the authors of a revolution must knowingly break
from the received research tradition.


### 3.4 Revolution or Evolution?



At the end of *Structure*, Kuhn drew an analogy between the
development of science and evolutionary biology. This was surprising,
since 'evolution' is commonly employed as a contrast term
to 'revolution'. Kuhn's main point was that
evolution ramifies rather than progressing toward a final goal, yet
its degree of specialization through speciation can be regarded as a
sort of progress, a progress *from* a historically existing
benchmark rather than a progress *toward* a preordained,
speculative goal. So specialization is an indicator of progress. As
for revolutions, they correspond to macromutations.



> 
> The process described in Section XII as the resolution of revolutions
> is the selection by conflict within the scientific community of the
> fittest way to practice future science. The net result of a sequence
> of such revolutionary selections, separated by periods of normal
> research, is the wonderfully adapted set of instruments we call modern
> scientific knowledge. Successive stages in that developmental process
> are marked by an increase in articulation and specialization. And the
> entire process may have occurred, as we now suppose biological
> evolution did, without benefit of a set goal... . [1970, 172f]
> 



At the time, it was striking that Kuhn compared revolutionary
transitions, rather than normal scientific developments, with
evolutionary change. It seems clear that he did not consider
revolution and evolution to be mutually incompatible. But keep in mind
that, for him, normal science represents periods of stasis, whereas
revolutions are short, highly creative periods that more closely
resemble the exploration by random trial and error (p. 87) that we
associate with biological evolution. Examined on a minute time scale,
however, normal science arguably also involves a (more constrained)
variation and selection process, as scientific practitioners search
for ways to articulate the paradigm. So, given the inevitability of
evolution under such conditions, Kuhn's treatment of normal
science would appear to be too static. The important point here is
that, in Kuhn's view revolution and evolution are compatible
when considered on the correct time scales (see Wray 2011 and
Kuukkanen 2012). Examined from afar, revolutions are simply the more
noteworthy episodes in the evolution of the sciences. Examined up
close, they (like discoveries in general for Kuhn) have a detailed
structure that is evolutionary, even something as revolutionary as the
quantum theory (Kuhn 1978).



But how, then, the reader is entitled to ask, can Kuhn accommodate the
sharp discontinuities that he advertised in chapter X of the book? We
cannot equate revolutions simply with speciation in Darwin's own
sense, given that Darwin's favorite mechanism of speciation was
anagenesis, not cladogenesis--just the long-term gradual
evolution within a single line rather than the splitting of lines.
Interestingly, the later Kuhn will opt for cladogenesis.



As many commentators have pointed out, the theory of punctuated
equilibrium of Niles Eldredge and Stephen Jay Gould (1992) raises the
question of evolution versus revolution, now precisely in the
biological (paleontological) context. In fact, Gould and Eldredge were
themselves influenced by Kuhn, whom Gould once described as "a
dear friend"; but they denied that they had deliberately
fashioned themselves as Kuhnian revolutionaries (Gould 1997). Gould
and Eldredge end their later review article on punctuated equilibrium
by remarking:



> 
> [C]ontemporary science has massively substituted notions of
> indeterminacy, historical contingency, chaos and punctuation for
> previous convictions about gradual, progressive, predictable
> determinism. These transitions have occurred in field after field;
> Kuhn's celebrated notion of scientific revolutions is, for
> example, a punctuation theory for the history of scientific ideas.
> [1993, 227]
> 



Here, as with Kuhn, those who resist Gould's attempt to sound so
revolutionary as to be contrary to Darwin's phyletic gradualism
note that it is only on a geological timescale that such developments
as the Cambrian explosion appear to be episodic. When examined on the
timescale of the biological generations of the life forms in question,
the development is evolutionary--more rapid evolution than during
other periods, to be sure, but still evolutionary.



Stuart Kauffman (1993) and Brian Goodwin (1994) defended
reorganization in the form of self-organization as the primary
macro-biological mechanism, with evolutionary adaptation adding only
the finishing touches. Gould and Richard Lewontin had raised this
possibility in their famous paper of 1979, "The Spandrels of San
Marco and the Panglossian Paradigm." Applied to the development
of science, this view implies that revolutions determine the overall
shape, while ordinary scientific work applies the adaptive
microevolution. Meanwhile, Michael Ruse (1989) defended the view that
the Darwinian paradigm (with its emphasis on function and adaptation)
and the punctuated equilibrium paradigm (with its emphasis on Germanic
ideas of form and internal constraints) are complementary.



David Hull ended his book, *Science as a Process* (1988), with
the remark that the book can be regarded as an attempt to fulfill both
Kuhn's and Toulmin's ambitions to provide a evolutionary
account of scientific development. Hull's is the most
thoroughgoing attempt to date to provide an evolutionary account of
scientific practice, at least in a specific field. However, nothing
like Kuhnian paradigms, normal science, and revolutions are to be
found in Hull's book, and this was deliberate on his part.
Whereas Kuhn originally said that paradigms correspond one-to-one with
scientific communities, Hull rejected Kuhn's idea of a
scientific community as too loose. A scientific community, he said,
does not consist of people who merely happen to agree on certain
things (anymore than the members of a species are individuals who
happen to share a set of traits). Mere consensus is not enough.
Rather, communities are tightly causally linked in the right sorts of
ways, just as species are. There is no community of biologists or even
of evolutionary biologists but only a patchwork of cliques. It is
here, locally, that the seeds of innovation are sown, most of which
are weeded out in a selective process by the larger group of
specialists. Hull's is a story of the socio-cultural evolution
of science without revolution.


## 4. Kuhn's Later Account of Scientific Revolutions



In "The Road Since Structure," his 1990 Presidential
Address to the Philosophy of Science Association, Kuhn reported on a
book in progress, a project that would remain unfinished at his death.
(See also Kuhn 1993.) In this and other fragments of that work, he
develops the biological metaphor broached at the end of
*Structure*. He retains his old parallel to biological
evolution, that science progresses or evolves away from its previous
forms rather than toward a final truth about the world; but he now
extends the biological analogy by regarding scientific specialties
themselves as akin to biological species that carve out research and
teaching niches for themselves. In the process, he significantly
modifies his conception of scientific revolutions and attendant claims
concerning crises and incommensurable breaks. No longer do we hear of
revolutions as paradigm change, certainly not in the sense of large
paradigms. In fact, Kuhn prefers to speak of "developmental
episodes" instead of revolutions. However, he does retain
something of his original idea of small paradigms, the concrete
problem solutions that he had termed "exemplars" in the
"Postscript-1969" to *Structure*. Most revolutions,
he tells us, are not major discontinuities in which a successor theory
overturns and replaces its predecessor. Rather, they are like
(allopatric) biological speciation, in which a group of organisms
becomes reproductively isolated from the main population.



> 
> 
> [R]evolutions, which produce new divisions between fields in
> scientific development, are much like episodes of speciation in
> biological evolution. The biological parallel to revolutionary change
> is not mutation, as I thought for many years, but speciation. And the
> problems presented by speciation (e.g., the difficulty in identifying
> an episode of speciation until some time after it has occurred, and
> the impossibility even then, of dating the time of its occurrence) are
> very similar to those presented by revolutionary change and by the
> emergence and individuation of new scientific specialties.
> ...
> 
> 
> 
> Though I greet the thought with mixed feelings, I am increasingly
> persuaded that the limited range of possible partners for fruitful
> intercourse is the essential precondition for what is known as
> progress in both biological development and the development of
> knowledge. When I suggested earlier that incommensurability, properly
> understood, could reveal the source of the cognitive bite and
> authority of the sciences, its role as an isolating mechanism was
> prerequisite to the topic I had principally in mind. ... [Kuhn
> 2000, 98-99]
> 
> 
> 



In short, specialization is speciation, a scientific progress
heightens communication breakdown. Experts doing similar kinds of
research come to realize that their use of key taxonomic terms no
longer jibes with mainline usage, in the sense that what Kuhn calls
"the no overlap principle" is violated: the group is using
a taxonomic hierarchy for crucial kind terms and the associated
categories that is incompatible with that of the established
tradition. The group splits off and forms a distinct specialty with
its own professional journals, conferences, etc., while leaving the
rest of the field largely intact. The incommensurability is now a
local, community-licensed, taxonomic one that creates something of a
barrier to communication with neighboring specialties. One thinks, for
example, of the way different biological specialties employ the
species concept itself, and the concept of gene. This linguistic
sensitivity as a group identifier permits the kind of fullness of
communication, both linguistic and practical, within the group that
Kuhn had stressed already in *Structure* and thus permits the
group to progress more rapidly. This multiplication of specialties is
the key to Kuhn's new conception of scientific progress. Two
recent books that directly engage these issues are Andersen et al.
(2006) and Wray (2011), the first from a cognitive science point of
view, the second with emphasis on Kuhn's social epistemology.
See also Nersessian (2003, 2008) and Kuukkanen (2012).



Another striking fact about Kuhn's last project is the demotion
to "a historical perspective" of the history of science as
a detailed source of data or phenomena upon which philosophers of
science should draw. While *Structure* was already a curious
mix of an inductive, history-based, bottom-up approach to modeling
scientific development and a more formal, top-down approach based on
Kuhn's Kantianism (see below), he now concludes that his core
position follows from first principles alone.



> 
> With much reluctance I have increasingly come to feel that this
> process of specialization, with its consequent limitation on
> communication and community, is inescapable, a consequence of first
> principles. Specialization and the narrowing of the range of expertise
> now look to me like the necessary price of increasingly powerful
> cognitive tools. [2000, p. 98]
> 



Thus Kuhn's new emphasis is on synchronic revolutions, in which
a field splits into subfields, rather than on the diachronic
replacement of one paradigm complex by another that his early account
featured. His conception of a science is therefore less monolithic. A
vibrant field such as evolutionary biology can tolerate several
distinct species concepts at the same time, a fact that contributes
rather than detracts from its vibrancy. The overall result is a less
tightly integrated, less dogmatic conception of normal science under
an overarching paradigm, a view that has implications also for the
necessity and size of future revolutions. For no longer need an
esoteric discrepancy get the leverage to trigger a crisis that
eventuates in the replacement of an entire, tightly integrated system.
In this respect, Kuhn's conception of physics becomes somewhat
closer to Godfrey-Smith's characterization of progress in
biology as "a deluge" rather than a full-scale Kuhnian
revolution (see below and Godfrey-Smith 2007). Given that progress in
biological evolution is better regarded as the remarkable
proliferation of intricate, useful design rather than movement toward
a goal, the explicit parallels that Kuhn draws to biological evolution
suggest that he is moving toward the same conception of scientific
progress as some see in biological evolution--as the
proliferation of adaptive design. We may know more about his final
position once more of the book manuscript, left incomplete at his
death, is published.


## 5. Larger Formations and Historical A Prioris: The Germanic and French Traditions



We pass now from the smaller-scale revolutions of Kuhn's later
work to large-scale movements that, in several cases, exceed the
bounds of the early Kuhnian paradigms and the revolutionary
transformations linking them. Other thinkers have gone even further
than Kuhn, by positing the existence of cognitive formations that are
both broader and deeper than his. One prominent line of thought here
is the neo-Kantian one up through Reichenbach and Carnap, discussed
and further developed by Michael Friedman (2001, 2003). Another, not
entirely distinct, idea is that of a thought style or discursive
formation found variously in such writers as Ludwik Fleck (1935),
Alistair Crombie (1994), Michel Foucault (1969), and Ian Hacking
(1990, 2002, 2012). Especially in the accounts of Foucault and
Hacking, new conceptual spaces are constructed and may
"crystallize" (Hacking) rapidly. Once they become
canonical, they seem to be such obvious frameworks for making true or
false claims that the corresponding categories of thought and action
appear to be *given* as part of the nature of things, as
written in the language of nature, so to speak, when they are in fact
a product of the cultural conditioning of our socio-cognitive systems.
In the limit we project our deeply ingrained cultural categories not
only onto our world as we encounter it but also onto all
(historically) conceivable worlds. The historical change in question,
once called to our attention, seems revolutionary--in a manner
that is both broader and deeper than the transition to a new paradigm
within a particular scientific specialty. Once again, the magnitude of
the change is practically invisible to all but the most sensitive
archeologist of knowledge. Feyerabend was alive to this perspective in
his work on Galileo. But, unlike his treatment of the Copernican
Revolution (Kuhn 1957), Kuhn's revolutions in *Structure*
and beyond are more limited in scope, typically occurring more or less
wholly within a single discipline. Nor is it obvious that the
emergence of a new thought style must overturn a distinct predecessor.
Of course, we should not regard social constructionist /
deconstructionist projects (whether or not deliberately designed) as,
automatically, ongoing, enlightened processes that
"unfreeze" the stones inherited from the past; for it was
these very processes that created essentialist constructions in the
first place. The claim is that our constructions today are no
different.



The four main characteristics of Hacking's "big
revolutions" are that they lead to whole new interdisciplinary
complexes, replete with new social institutions and corresponding
social changes, and they alter that period's overall take on, or
"feel" for, the universe. For critical discussion of
Hacking on styles of reasoning, see Kusch (2010) and Scortino (2016).
For more on Hacking, see section 5.3 below.


### 5.1 Thomas Kuhn: Kantian or Hegelian?



Kuhn several times described himself as "a Kantian with moveable
categories." Hoyningen-Huene (1993) provides a broadly Kantian
interpretation of Kuhn (endorsed by Kuhn himself), as does Friedman
(2001, 2003, 2010). Given the historical approach of
*Structure*, other commentators have likened Kuhn to Hegel
instead of Kant. And given the early Kuhn's view that scientific
reason is manifested more clearly in historical change as well as in
normal scientific practices than in symbolic logical structures,
Kuhn's early theory of scientific change can be termed very
broadly Hegelian. Also fitting the broadly Hegelian frame is
Kuhn's internalist account of normal scientific research as
sowing the seeds of its own destruction through unintended innovation,
resulting eventually in a kind of dialectical conflict that drives the
enterprise forward. However, there is no Hegelian Spirit lurking
within Kuhn's model, nor a permanent logic of science as its
replacement as there was for Lakatos (Lakatos 1970;
Hoyningen-Huhne 1993; Bird 2008; Worrall 2003, 2008; Nickles
2009).



Kuhn disliked being compared to Hegel, whose work he found obscure and
characterized by a non-naturalistic philosophy of history, but it is
worth commenting further on the partial resemblance. Both Kant and
Hegel rejected naive empiricism, according to which all human
knowledge arises, somehow, from the accumulative aggregation of
individual sensations or perceptions. Kant argued that we need
transcendental structures such as a system of processing rules in
order to organize sensory input into something coherent and
intelligible, e.g., as physical objects interacting causally in space
and time. These were Kant's forms of intuition (in space and
time) and categories (substance, causality, etc.). They represent the
human mind's contribution to knowledge. (In this regard Kant can
be regarded as a forerunner of cognitive psychology.) Thus, our
experience of the world is shaped to fit a priori forms, and this is
where the Kantian version of idealism enters the picture: the world of
human experience is not the world of ultimate reality (Kant's
unknowable, noumenal world of things-in-themselves); rather, it is a
world shaped by our own cognitive structures.



Hegel, one of the founders of the deep conception of historical change
broadly characteristic of nineteenth-century German scholarship,
proceeded to historicize Kant's innovation, in effect by
historicizing Kant's categories. They are not inborn, permanent,
and universal; on the contrary, they are socio-historically acquired
or lost and hence differ from one historical epoch to another. People
living in different epochs cognize the world differently. It is
tempting to read the Kuhn of *Structure* as further
relativizing and localizing Hegel to specific scientific domains and
their paradigms. Kuhn's model provides endogenous, dynamic
mechanisms of (inadvertent) scientific innovations that sow the seeds
of the paradigm's eventual destruction in a vaguely Hegelian
sort of dialectical process. It thus becomes possible to experience a
change in categorical scheme within one's own lifetime--the
victory of the new paradigm being the small-scale scientific
counterpart of Hegel watching Napoleon march in victory through the
streets of Jena! Thus it is tempting to regard Kuhnian revolutions as
Hegelian revolutions writ small.



Nonetheless, in terms of historical genealogy, Kuhn is better aligned
with the Kantian tradition, especially the neo-Kantian relativization
of Kant. Interestingly, some logical empiricists (especially
Reichenbach) were influenced by the neo-Kantianism of the German
Marburg School of philosophy to develop a historically relativized but
constitutive a priori (see below and Friedman 2001.)


### 5.2 The German Neo-Kantian Tradition



There is a long historical gap between Kant/Hegel and Kuhn, and this
space is not empty. Many other thinkers, especially those in the
various nineteenth-century idealist traditions, were Kantian or
Hegelian or neo-Hegelian or neo-Kantian opponents of empiricist
positions that they considered naive, such as that of John Stuart
Mill. The neo-Kantian label applies even to prominent logical
positivists of the Vienna Circle and logical empiricists of the Berlin
Circle, who have too often been caricatured as simple, cumulative
empiricists. As Friedman (2001) and others have shown, several
founders of twentieth-century academic philosophy of science extended
the neo-Kantian attack on simple empiricism. The basic idea here is
that, just as Kant regarded any account of perception and knowledge as
naively empiricist insofar as it left no room for underlying
cognitive organizing principles, so any account of the sciences that
provided no analogous underlying social-cognitive framework was a
continuation of simple empiricism, i.e., a version of
"positivism." In this particular respect, W. V.
Quine's "Two Dogmas of Empiricism" and *Word and
Object* (Quine 1951, 1960) were throwbacks to simple empiricism in
their attempt to eliminate the Kantian formal component.



The German Marburg School of Hermann Cohen, Paul Natorp, and Ernst
Cassirer was especially important in the emergence of modern
philosophy of science in the form of the logical positivism and
logical empiricism. Friedman (2001 and elsewhere) has explored its
influence on young Reichenbach's attempt to interpret the
significance of the new relativity theory. Rudolf Carnap had been
influenced by Ernst Cassirer, among others. (See the entries on
logical empiricism, Reichenbach, Carnap, Cohen, Natorp, and Cassirer.)
Cassirer's central theme was the fundamental epistemological
implications of the replacement of Aristotle's subject-predicate
logic and substance ontology by the new relational logic of the
modern, mathematical-functional approach to nature. This could not be
a priori in Kant's original sense, since the emergence of
non-Euclidean geometry had shown that there are alternative organizing
principles. But the very fact that we still needed organizing
structures that are constitutive or definitive of the cognitive
enterprise in question meant that Kant was still basically correct.
Like Moritz Schlick, the first leader of the Vienna Circle,
Reichenbach of the Berlin school parlayed his engagement with
relativity theory and non-Euclidean geometries into a conception of
the "relativized a priori." All of this by around 1920,
with the younger Carnap's views developing during the 1920s and
'30s. In the USA, meanwhile, C. I. Lewis (1929) was defending
his "pragmatic a priori."



In his famous paper of 1950, "Empiricism, Semantics, and
Ontology," Carnap made his two-tiered view of inquiry quite
explicit. Starting from the problem of the existence of abstract
entities, Carnap distinguished internal questions, that is, questions
that can arise and be answered within a particular logico-linguistic
framework, from external questions, that is, meta-level questions
about which framework to prefer. External questions cannot be answered
in the same, disciplined manner as internal, for choice of framework
is ultimately a pragmatic decision based on the expected fertility of
using one framework rather than another. Although it is difficult to
equate Carnap's fruitfulness decisions with Kuhn's
revolutionary breaks (Kuhn 1993, 313f), Carnap regarded his vision of
science as similar to Kuhn's, and he liked the manuscript of
*Structure* that Kuhn submitted to the *International
Encyclopedia of Unified Science*, as George Reisch (1991) has
shown. Thus the clash of Kuhn's work with that of Carnap and the
positivist movement has been exaggerated.



Although both defended two-tiered conceptions of inquiry, there are
important differences between Kuhn and Carnap (as Friedman, 2001,
2003, 2010, among others, observes). For Carnap, as for Reichenbach,
the choice of framework or coordinating definitions was conventional,
a matter of convenience or heuristic fertility, whereas for committed
Kuhnian normal scientists the foundational tenets of their paradigm
are deep truths about the world, principles not subject to empirical
test. (However, in a crisis situation, fertility becomes a key element
in theory and paradigm choice.) In Carnap's frameworks these
were explicit systems of logical rules, whereas Kuhn's account
of normal science largely jettisoned rule-based knowledge in favor of
a kind of case-based tacit knowledge, the cases being the concrete
exemplars. Third, Kuhn himself emphasized that his approach was
historical, whereas Carnap's was not. Although a Carnapian
change from one logical framework to another could, in principle, be
quite revolutionary, Carnap himself never emphasized this point,
suggested nothing of Kuhn's radical discontinuity, and was
simply not interested in the history of science.



Meanwhile, Friedman himself has extensively developed the idea of
historically contingent but constitutive a prioris (e.g., 2001, 2003,
2008). He is sympathetic to Kuhn's view that revolutions occur
when the constitutive principles change. From the old point of view,
there is disruptive and incommensurability, but defenders of the new
viewpoint manages to establish a kind of continuity. Friedman goes
well beyond Kuhn in stressing the role of philosophical ideas in
establishing this continuity.



> 
> Since deep conceptual revolutions or paradigm-shifts are a fact of
> scientific life (and, I would argue, a necessity), we are never in a
> position to make our present constitutive principles as truly
> universal principles of human reason-as fixed once and for all
> throughout the evolution of science.
> 

 In recent work, Friedman devotes more attention to the
social dimension, and he notes that even the standards of rationality
may continue to change historically. (See the entry "Historical
Theories of Rationality". See also DiSalle 2002.)


Another development that appeals to Germanic themes in its criticism
of naive empiricism is the idealization movement of the Poznan
School in Poland, associated especially with Leszek Nowak. This group
regards science as developing in an idealizational and dialectical
manner, ideas that they trace back to Karl Marx's analysis of
economics, inspired by his own study of Galileo's fruitful use
of abstract, idealized models against the Aristotelians. The
Poznan group regards idealization as the secret to modern science
and finds it remarkable that virtually all previous analytic
philosophy of science remains Aristotelian in treating proposed laws
and theories not as ideal models but as true or false statements
directly about the real world (Nowak 1980 and later writings; see also
Krajewsky 1977). As models, these constructions must be concretized to
some degree before they can be applied to the real world. While the
idealizationists tend to reject Kuhnian revolutions as too
discontinuous and irrational, they do see a resemblance to their
internalistic, dialectical conception of scientific development. For
them a revolution consists in a new theory or model that reveals a
previously unnoticed idealizing assumption built into its predecessor,
a change that alters scientists' conception of what is essential
versus peripheral to the domain of phenomena in question. Hence there
can be a significant change of world-conception.



There is some affiliation of Poznan with the European
structuralist account of theories, based on a set-theoretical analysis
of theory structure and theory relations. Kuhn himself was much
attracted to Joseph Sneed's approach (Sneed 1971), soon extended
by Wolfgang Stegmuller (1974/1976) and others. Given the
informality of Kuhn's own approach and his explicit shunning of
rules and rational reconstructions, his attraction to the
structuralist line was initially puzzling. However, the structuralists
were and are interested in intertheory relations, and models are
central to their non-sentential conception of theories. These are
models in the formal sense, but Kuhn found insightful connections to
his own use of models in the form of exemplars. For both Kuhn and the
structuralists it is the collection of exemplars or models, not an
abstract statement of a theory, that carries the weight in scientific
inquiry.



Already the early Kuhn, especially in the postscript to the second
edition of *Structure*, largely abandoned the traditional
conception of theories as deductive systems, even in physics, and
substituted informal collections of models of various, exemplary
kinds, along with a toolbox of expert practices for constructing and
applying them (Cartwright 1983, Giere 1988, Teller 2008). He always
liked Margaret Masterson's remark that "a paradigm [in the
sense of preferred models or exemplars] is what you use when the
theory is not there" (Baltas et al. 2000, 300). Such a view,
like Nowak's, anticipates the move from theory-centered to
model-centered accounts of scientific work. However, Kuhn's
normal scientific practitioners presumably hold the models to be true
in their original application, as is the grand theory incorporated in
the paradigm, whereas today the emphasis is on modeling practices
across the sciences, in which the models are almost always known in
advance to be false because of their employment of idealizations,
approximations, abstractions, etc.


### 5.3 The French Discontinuity Theorists



Meanwhile, important French thinkers had already taken a historical
approach, one that explicitly characterizes science as a series of
breaks or *coupures*. The principal genealogy includes
Leon Brunschvicg, Gaston Bachelard and his student, Georges
Canguilhem, and the latter's student, Michel Foucault. Neither
Kuhn's historicism nor his talk of revolutionary breaks was news
to the French (Gutting, 2001, 2003). The French tradition of science
studies, going back to Auguste Comte and including later figures such
as Pierre Duhem and Henri Poincare, possessed a historical
dimension that positivism lost after Ernst Mach, as it became logical
positivism. However, the French and Germanic traditions have some
roots in common. As Gutting points out, Brunschvicg, like Emile
Meyerson, was a science-oriented idealist. For him the mind is not a
passive wax tablet; rather, it actively forges internal links among
ideas, yet it is also often surprised by the resistant exteriority of
the natural world. Against traditional metaphysics, philosophy of
science should limit itself to what the science of the time
allows--but not dogmatically so. For dogmatic attempts to extract
timeless principles and limitations (such as Kant's denial of
the possibility of non-Euclidean geometry) may soon be embarrassed by
further scientific advances. Einstein's general theory of
relativity exemplifies the revolutionary nature of the most impressive
developments.



Bachelard, French physicist and philosopher-historian of science, also
believed that only by studying history of science can we gain an
adequate understanding of human reason. He stressed the importance of
epistemological breaks or discontinuities (*coupures
epistemologiques*). In *Le Nouvel Esprit
Scientifique* (1934), Bachelard argued that the worldview of
classical physics, valuable in its own time, eventually became an
obstacle to future progress in physics. Hence a break was needed.
Here, then, we already find the idea that a successful theory can lose
its luster by being considered exhausted of its resources and thus
lacking in fertility. Like Brunschvicg, Bachelard held that a
defensible, realist philosophy had to be based on the science of its
day. Hence, scientific revolutions have (and ought to have) brought
about epistemological revolutions. The reality we posit, he said,
ought to be that of the best science but with the realization that our
concepts are active constructs of our own minds, not imported from
nature's own language, as it were. Future mental activity as
well as future empirical findings are likely to require another
rupture. As Gutting points out, Bachelard's account of
discontinuity was not as radical as Kuhn's. Bachelard was
willing to speak of progress toward the truth. He made much of the
fact that successor frameworks, such as non-Euclidean geometry or
quantum physics, retain key predecessor results as special cases and,
in effect, contextualize them.



Canguilhem was more interested in the biological and health sciences
than Bachelard and gave great attention to the distinction between the
normal and the pathological, a distinction that does not arise in
physical science. For this and other reasons, in his view, we can
expect no reduction of biology to physics. Canguilhem provided a more
nuanced conception of obstacles and ruptures, noting, for example,
that an approach such as vitalism that constitutes an obstacle in one
domain of research can simultaneously play a positive role elsewhere,
as in helping biological scientists to resist reductive thinking. Here
we find context sensitivities and heuristic resources difficult to
capture in terms of a context- and content-neutral logic of science
such as the logical empiricists espoused.



Bachelard and Canguilhem also had less disruptive conceptions of
scientific objectivity and scientific closure than Kuhn. Canguilhem
criticized Kuhn's (alleged) view that rational closure could not
amount to more than group consensus. Both Frenchmen emphasized the
importance of norms and denied that disciplinary agreement was as weak
as Kuhnian consensus. Kuhn replied to this sort of objection (in
"Postscript" and elsewhere) that his scientific
communities do possess shared values, that their agreement is not
something arbitrary, say, as whipped up by political ideologues.



Foucault's archaeology of knowledge (Foucault 1966, 1969) posits
a distinction between a superstructure of deliberately made
observations, claims, and arguments and a deep structure, most
elements of which we are probably unconscious. Once again we meet a
two-level account. Writes Hacking:



> 
> Foucault used the French world *connaissance* to stand for such
> items of surface knowledge while *savoir* meant more than
> science; it was a frame, postulated by Foucault, within which surface
> hypotheses got their sense. *Savoir* is not knowledge in the
> sense of a bunch of solid propositions. This "depth"
> knowledge is more like a postulated set of rules that determine what
> kinds of sentences are going to count as true or false in some domain.
> The kinds of things to be said about the brain in 1780 are not the
> kinds of things to be said a quarter-century later. That is not
> because we have different beliefs about brains, but because
> "brain" denotes a new kind of object in the later
> discourse, and occurs in different sorts of sentences. [2002, 77]
> 



Given the influence of Foucault, we may also locate our discussion of
Hacking's own work on historical ontology here (Hacking 2002).
Hacking (1975, 1990, 1995, 2012) has studied in depth the emergence of
probability theory and (later) of statistical thinking and the
construction of the modern self as key examples of what he terms
"historical ontology." He acknowledges inspiration from
both Foucault's discursive formations and Crombie's styles
of thinking (Crombie 1994), with a dose of Feyerabend thrown into the
mix. Like Kuhn (and Friedman), Hacking returns to Kant's
"how possible?" question, the answer to which sets out 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. Hacking, too, historicizes the Kantian
conception. He likes the term 'historical a priori', which
Canguilhem once applied to the work of his erstwhile student,
Foucault.



> 
> 
> 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]
> 
> 
> 



Hacking describes changes in historical *a prioris* as
"significant singularities during which the coordinates of
'scientific objectivity' are rearranged" (2002,
6).



Although reminiscent of Kuhn's positions in some ways, there are
striking differences. As noted above, Hacking's constructed
formations are much broader than Kuhn's. Thus he feels free to
employ telling bits of popular culture in laying out his claims, and
he admits to being whiggish in starting from the present and working
backward to find out how we got here. Moreover, in mature, modern
science, 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 (rather than subjectivism) 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). This sort of unintelligibility
runs deeper than a Kuhnian translation failure. It is not a question
of determining which old style statements match presumed new style
truths; rather, it is a question of the conditions for an utterance to
make a claim that is either true *or* false at all. 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]
> 



By contrast, Kuhnian paradigms include a set of positive assertions
about the world. Yet Kuhn himself was attracted by Hacking's way
of putting the point about truth-and-falsity (Kuhn 2000, p. 99).


### 5.4 Kuhn's Relation to the Germanic and French Traditions



To what extent was Kuhn indebted to these thinkers? As noted above, he
took Kant but not Hegel very seriously. He was largely self-taught in
philosophy of science. Among his contemporaries, he was familiar with
Popper but not in any detail with the various strains of logical
positivism and logical empiricism, in particular the positions of
Carnap and Reichenbach. Apparently, he was only slightly acquainted
with the work of Bachelard while writing *Structure*, and they
never engaged in a fruitful interchange (Baltas et al. 2000, 284f).
Kuhn did acknowledge, in print and in his classes, the crucial
influence on his historical and philosophical thinking of the two
Russian emigres, Emile Meyerson, author of
*Identite et Realite* (1908) and Alexandre
Koyre, especially his *Etudes Galileenes*
(1939), and that of Annaliese Maier, the German historian of medieval
and early modern science. He had read Ludwik Fleck's *Genesis
and Development of a Scientific Fact* (originally published in
German in 1935) and Michael Polanyi's *Personal
Knowledge* (1958) and had had some discussion with Polanyi (Baltas
et al. 2000, 296). Kuhn was also indebted to Wittgenstein, early
("The limits of my language are the limits of my world,"
1922, 148) and late (on language games and forms of life). (See
Sharrock and Read 2002, the introduction to Harris 2005, and Kindi
2010 for Kuhn's relation to Wittgenstein and others.) He knew
something of Toulmin's work.



Kuhn more than anyone in the Anglo-American world pointed out the need
for larger-sized units than individual theories in making sense of
modern science. Nonetheless, as we have seen, others in the Teutonic
and Francophone worlds had previously postulated even larger
socio-intellectual units and correspondingly deeper changes than
Kuhn's, on somewhat different scales of intellectual space and
time. If we think of authors such as the *Annales* historian
Fernand Braudel, with his distinct time-scales, we recognize that the
attribution of transformative change clearly depends heavily on the
choice of time-scale and on how fine- or course-grained is our
approach. Hacking (2002, 76) makes this point with reference to the
French context:



> 
> There are two extremes in French historiography. The *Annales*
> school went in for long-term continuities or slow
> transitions--"the great silent motionless bases that
> traditional history has covered with a thick layer of events"
> (to quote from the first page of Foucault's 1969 *Archeology
> of Knowledge*). Foucault takes the opposite tack, inherited from
> Gaston Bachelard, Georges Canguilhem, and Louis Althusser. He posits
> sharp discontinuities in the history of knowledge.
> 



Although Kuhn emphasized the importance of skilled scientific
practice, his paradigms remained closer to the articulate surface of
scientific culture than Foucault's discursive formations, which
are better located in the unconscious than in the Kuhnian
subconscious. Foucault does not speak of revolution.


## 6. Other Revolution Claims and Examples



Oliver Wendell Holmes, Jr. (1861) remarked that "Revolutions
never follow precedents nor furnish them." Given the
unpredictability, the nonlinearity, the seeming uniqueness of
revolutions, whether political or scientific, it is therefore
surprising to find Thomas Kuhn attempting to provide a General Theory
of Scientific Revolutions (Kindi 2005). Early Kuhn did seem to believe
that there is a single, underlying pattern to the development of
mature sciences that is key to their success, and late Kuhn a
different pattern. Has either early or late Kuhn found such a pattern,
or has he imposed his own philosophical structure on the vagaries and
vicissitudes of history? Kuhn's Kantianism always did live in
tension with his historicism, and in his late work (e.g., 2000c) he
surprisingly gave up the pretense of deriving his pattern of taxonomic
change and speciation from history of science, on the ground that it
largely followed "from first principles."



Numerous philosophers, scientists, and other commentators have made
claims about scientific change that differ from Kuhn's. (For a
recent selection see Soler et al. 2008.) Some, as we have seen, are
skeptical of revolution talk altogether, others of Kuhn's in
particular. Still others accept that some revolutions are Kuhnian but
deny that all of them are. One common criticism is that not all
revolutionary advances are preceded by an acute crisis, that is, by
major failures of preceding research. Kuhn himself allowed for
exceptions already in *Structure*. Another is that
revolutionary changes need not involve discontinuities in all of
Kuhn's levels at once (especially Laudan 1984). Yet another is
that there need be little logical or linguistic discontinuity. A
rapid, seemingly transformative change in research practices may
involve simply a marked gain in data accessibility or accuracy or
computational processing ability via new instrumentation or
experimental design. And on the later Kuhn's own view,
revolution need not be a game of creative destruction. Only a few
examples can be considered here.


### 6.1 Some Alternative Conceptions of Scientific Revolution



Do revolutions consist, according to Kuhn, of major new materials
(experimental facts, theories, models, instruments, techniques)
entering a scientific domain or, instead, of a major restructuring or
rearrangement of materials, practices, and community affiliations
already present? Kuhn states that the relativity revolution might
serve as



> 
> a prototype for revolutionary reorientation in the sciences. Just
> because it did not involve the introduction of additional objects or
> concepts, the transition from Newtonian to Einsteinian mechanics
> illustrates with particular clarity the scientific revolution as a
> displacement of the conceptual network through which scientists view
> the world. [1970, 102]
> 



The reader may find this claim confusing, however, because in the
just-preceding paragraphs Kuhn had emphasized the ontological and
conceptual changes of precisely this revolution, e.g., the radical
change in the concept of mass. Einstein's masses are not
Newtonian masses, he insisted. They are newly introduced entities;
hence, we may infer, new content. Yet Kuhn surely does have a point
worth saving, in that relativity theory still deals with most of the
same kinds of phenomena and problems as classical mechanics and
employs immediate successors to the classical concepts. But, if so,
then reorganization of familiar materials implies a disciplinary
continuity through revolution that Kuhn minimized.



That reorganization dominates Kuhn's conception of revolutions
is apparent throughout his work. As a young scholar he had an epiphany
when Aristotle's seemingly radically false or unintelligible
claims suddenly came together for him as a coherent, comprehensive
worldview. This experience became Kuhn's psychological model for
revolutionary transformation from one paradigm to its successor and
informed his later talk of Gestalt switches. But he also emphasized
that revolution involves *social* reorganization of the field
(not merely the cognitive reorganization of an individual), from one
form of scientific life to another, incompatible with it. By
implication, his structural or formal conception of revolution
excluded the alternative idea of revolution as extraordinary bursts in
substantive content.



In *Conceptual Revolutions*, Paul Thagard (1992) retains
something of Kuhn's idea of conceptual transformation and the
more specific idea of taxonomic transformation. He distinguishes two
kinds of reclassification, in terms of the language of tree structures
used in computer science: branch jumping and tree switching. Branch
jumping reclassifies or relocates something to another branch of the
same tree, e.g., reclassifying the whale as a mammal rather than a
fish, the earth as a planet, or Brownian motion as a physical rather
than a biological phenomenon. New branches can appear and old branches
can be eliminated. Meanwhile, tree switching replaces an entire
classification tree by a different tree structure based on different
principles of classification, as when Darwin replaced the static
classification tree of Linnaeus by one based on evolutionary genealogy
and when Mendeleev replaced alternative classification systems of the
chemical elements by his own table. Taking a computational approach to
philosophy of science, Thagard employs his computer program ECHO to
reconstruct and evaluate several historical cases of alleged
conceptual revolution and arrives at a tamer conception of
revolutionary breaks than Kuhn's.



*The Cognitive Structure of Scientific Revolutions* by Hanne
Andersen, Peter Barker, and Xiang Chen (2006) also devotes a good deal
of attention to cognition and categorization issues, in a defense of
the later Kuhn's approach. The work of cognitive psychologist
Lawrence Barsalou and of philosopher-historian Nancy Nersessian (the
founder of the "cognitive historical" approach to science)
plays a significant role in their account. Nersessian herself (2003,
2008) emphasizes model-based reasoning. These are no longer static
cases or exemplars, for they possess an internal dynamic.



Howard Margolis (1993) distinguishes two kinds of revolutions,
depending on which kinds of problems they solve. Those revolutions
that bridge gaps, he contends, differ from those that surmount or
penetrate or somehow evade barriers. His focus is on barriers, a
neglected topic even though it fits Kuhn's account of cognition
well. Margolis develops Kuhnian themes in terms of deeply ingrained
"habits of mind." While such habits are necessary for
efficient scientific work within any specialty discipline, they
constitute barriers to alternative conceptions. More broadly, deeply
ingrained cultural habits of mind can close off opportunities that,
according to the perspective of later generations, were staring them
in the face. Margolis is struck by the apparent fact that all the
materials for Copernicus' new model of the solar system had been
available, in scattered form, for centuries. No new gap-crossing
developments were needed. He concludes that, rather than a gap to be
bridged, the problem was a cognitive barrier that needed to be
removed, a barrier that blocked expert mathematical astronomers from
bringing together, as mutually relevant, what turned out to be the
crucial premises, and then linking them in the tight way that
Copernicus did. If Margolis' account of the Copernican
Revolution is correct, it provides an example of revolution as
holistic reorganization of available materials, hence the
non-piecemeal, noncumulative nature of revolutions. The developments
that lead to a barrier's removal can be minor and, as in the
case of Copernicus, even quite peripheral to the primary subject
matter that they ultimately help to transform. Here one thinks of a
model popular with mystery writers, where an everyday observation
leads to a sudden change in perspective.



Davis Baird (2004) contends that there can be revolutions in practice
that are not conceptual revolutions. He emphasizes the knowledge
embodied in skills and in instruments themselves. His central example
is analytic chemistry.



> 
> There is little doubt that analytical chemistry has undergone a
> radical change. The practice of the analyst, who now deals with large,
> expensive equipment, is different than it was in 1930. Modern
> instrumental methods are by and large more sensitive and accurate,
> have lower limits of detection, and require smaller samples; different
> kinds of analyses can be performed. Analytical chemistry is much less
> a science of chemical separations and much more a science of
> determining and deploying the physical properties of substances.
> ... The revolutionary phase of Thomas S. Kuhn's Structure
> of Scientific Revolutions starts with a crisis, a problem that the
> established methods of normal science cannot solve (Kuhn [1962] 1970;
> 1996, ch. 5). There was no such crisis in analytical chemistry. While
> one might imagine that analytical chemistry underwent a change of
> paradigm, there was no crisis that provoked this change. Pre-1930
> analytical chemists did not bemoan the inability of their chemistry to
> solve certain problems. Instead, new methods were developed that could
> solve established "solved" problems, but solve them
> better: more efficiently, with smaller samples, greater sensitivity,
> and lower limits of detection. These changes in analytical chemistry
> do not suffer from any kind of incommensurability: today, one can
> easily enough understand what analytical chemists were doing in
> 1900-although the idea that the analytical chemist is one who
> can quantitatively manufacture pure chemicals is startling on first
> encounter. ... The transformation in analytical chemistry passes
> all of Cohen's tests.
> 



Recently, Rogier De Langhe (2012, 2014a and b, 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. De Langue
employs economic arguments to illuminate such themes as the division
of cognitive labor, models of scientific progress, and
scientists' decisions about whether to specialize or to
innovate. 


### 6.2 Some Biological Cases



The account of the dynamics of science in *Structure* ill fit
the rapid splitting and recombining of fields in the post-World War II
era of Big Science, as Kuhn recognized. So he excluded from his
account the division and recombination of already mature fields such
as happened with the emergence of biochemistry. (This exclusion is
troubling, given the universal thrust of his account. It is as if Kuhn
admitted that his account applies only to a particular historical
period that is now largely past; yet he also wrote as if the
normal-revolutionary model would apply to mature disciplines into the
long future.) In his later work he did devote careful attention to the
division of fields into specialties and subspecialties (see SS5).
However, he still gave little attention to the more-or-less reverse
process of new fields coming into existence by combinations of
previously distinct fields as well as to cross- and trans-disciplinary
research, in which a variety of different specialists somehow succeed
in working together (Galison 1997, Kellert 2008, Andersen 2013).



And what can we make, on Kuhn's account, of the explosion of
work in molecular biology following the Watson-Crick discovery, in
1953, of the chemical structure of DNA and the development of better
laboratory equipment and techniques? Molecular genetics quickly grew
into the very general field of molecular biology. Less than two
decades after Watson and Crick, Gunther Stent could already write in
his 1971 textbook:



> 
> How times have changed! Molecular genetics has ... grown from the
> esoteric specialty of a small, tightly knit vanguard into an
> elephantine academic discipline whose basic doctrines today form part
> of the primary school science curriculum. [Stent 1971, ix]
> 



There is something paradigmatic about molecular biology and also
something revolutionary about its rapid progress and expansion. It is
not clear how to characterize this and similar developments. Was this
a Kuhnian revolution? It did involve major social and intellectual
reorganization, one that conflicted with the previous ones in some
respects but without undermining the Darwinian paradigm. Quite the
contrary. Or is molecular biology more like a style of scientific
practice than a paradigm? Such an explosive development as molecular
biology hardly fits Kuhn's description of steady, normal
scientific articulation of the new paradigm by puzzle solving.
Instead, it seems better to regard it as a large toolkit of methods or
techniques applicable to several specialty fields rather than as an
integrative theory-framework within one field.



Should we then focus on practices rather than on integrative theories
in our interpretation of Kuhnian paradigms? The trouble with this move
is that practices can also change so rapidly that it is tempting to
speak of revolutionary transformations of scientific work even though
there is little change in the overarching theoretical framework (see
Part II of Soler et al. 2008). Moreover, as Baird (2004) points out,
the rapid replacement of old practices by new is often a product of
efficiency rather than intellectual incompatibility. Why continue to
do gene sequencing by hand when automated processing in now available?
Replacement can also be a product of change in research style, given
that, as Kuhn already recognized, scientific communities are cultural
communities.



Similar points can be made about the rise of statistical physics,
mentioned above in relation to Hacking's work. (See also Brush
1983 and Porter 1986.) This was an explosion of work within the
classical mechanical paradigm rather than a slow, puzzle-by-puzzle
articulation of precisely that paradigm in its own previous terms. Or
was it? For Kuhn himself recognized that modern mathematical physics
only came into existence starting around 1850 and that Maxwellian
electrodynamics was a major departure from the strictly Newtonian
paradigm. In any case, there was much resistance among physicists to
the new style of reasoning. The kinetic theory of gases quickly grew
into statistical mechanics, which leapt the boundaries of its initial
specialty field. New genres as well as new styles of
mathematical-physical thinking quickly replaced old--and
displaced the old generation of practitioners. Yet on Kuhn's
official theory of science it was all just "classical
mechanics."



Furthermore, the biological and chemical sciences do not readily
invite a Kuhnian analysis, given the usual, theory-centered
interpretation of Kuhn. For biological fields rarely produce lawful
theories of the kind supposedly found in physics. Indeed, it is
controversial whether there exist distinctly biological laws at all.
And yet the biological sciences have advanced so rapidly that their
development cries out for the label 'revolutionary'.



What of the emerging field of evolutionary-developmental biology
(evo-devo)? It is too soon to know whether future work in this
accelerating field will merely complete evolutionary biology rather
than displacing it. It does seem unlikely that it will amount to a
complete, revolutionary overturning of the Darwinian paradigm. (Kuhn
might reply that the discovery of homeobox genes overturned a smaller
paradigm based on the expectation that the genetic makeup of different
orders of organisms would have little in common at the relevant level
of description.) And if it complements the Darwinian paradigm, then
evo-devo is, again, surely too big and too rapidly advancing to be
considered a mere, piecemeal, puzzle-solving articulation of that
paradigm. Based on work to date, evo-devo biologist Sean B. Carroll,
for example, holds precisely the complement view--complementary
yet revolutionary:



> 
> Evo-Devo constitutes the third major act in a continuing evolutionary
> synthesis. Evo-Devo has not just provided a critical missing piece of
> the Modern Synthesis--embryology--and integrated it with
> molecular genetics and traditional elements such as paleontology. The
> wholly unexpected nature of some of its key discoveries and the
> unprecedented quality and depth of evidence it has provided toward
> settling previously unresolved questions bestow it with a
> revolutionary character. [2005, 283]
> 

 Eva Jablonka and Marion Lamb (2005) make even stronger
Kuhnian-revolutionary claims for evo-devo, which they see as a partial
return to a Lamarckian perspective. It was in his review of their book
that Godfrey-Smith (2007) suggested that recent biological progress is
a deluge rather than a Kuhnian revolution.

### 6.3 Nonlinear Dynamics



Kuhn treated a scientific field (and perhaps science as a whole) as a
system with a far more interesting internal dynamics than either
Popper or the logical empiricists had proposed. The famous opening
paragraphs of *Structure* read as though Kuhn had analyzed a
historical time series and extracted a pattern from it inductively as
the basis for his model of scientific development. The broadly cyclic
nature of this pattern immediately jumps out at dynamical systems
theorists. Yet despite this perhaps promising start as an early
dynamical modeler of science, Kuhn apparently paid little attention to
the explosion of work in nonlinear dynamics that began with
"chaos" theory and widened into such areas as complex
adaptive systems and network theory. This is unfortunate, since the
new developments might have provided valuable tools for articulating
his own ideas.



For example, it would appear that, as Kuhnian normal science becomes
more robust in the sense of closing gaps, tightening connections, and
thereby achieving multiple lines of derivation and hence mutual
reinforcement of many results. However, that very fact makes normal
science increasingly fragile, less resilient to shocks, and more
vulnerable to cascading failure (Nickles 2008). Kuhn claimed, contrary
to the expectations of scientific realists, that there would be no end
to scientific revolutions in ongoing, mature sciences, with no reason
to believe that such revolutions would gradually diminish in size as
these sciences continued to mature. But it would seem to follow from
his model that he could have made a still stronger point. For
Kuhn's position in *Structure* arguably implies that,
when considering a single field over time, future revolutions can
occasionally be even larger than before. The reason is that just
mentioned: as research continues filling gaps and further articulating
the paradigm, normal science becomes more tightly integrated but also
forges tighter links to relevant neighboring fields. Taking these
developments into account predicts that Kuhnian normal science should
evolve toward an ever more critical state in which something that was
once an innocuous anomaly can now trigger a cascade of failures
(Nickles 2012a and b), sometimes rather quickly. For there will be
little slack left to absorb such discrepancies. If so, then we have an
important sort of dynamical nonlinearity even in normal science, which
means that Kuhnian normal science itself is more dynamic, less static,
than he made it out to be.



It seems clear that Kuhnian revolutions are bifurcations in the
nonlinear dynamical sense, and it seems plausible to think that
Kuhnian revolutions may have a fat-tailed or power-law distribution
(or worse) when their size is plotted over time on an appropriate
scale. Each of these features is a "hallmark of nonlinear
dynamics" (Hooker 2011A, 5; 2011B, 850, 858). To elaborate a
bit: one intriguing suggestion coming from work in nonlinear dynamics
is that scientific changes may be like earthquakes and many other
phenomena (perhaps including punctuated equilibrium events of the
Gould-Eldredge sort as well as mass extinction events in biology) in
following a power-law distribution in which there are exponentially
fewer changes of a given magnitude than the number of changes in the
next lower category. For example, there might be only one magnitude 5
change (or above) for every ten magnitude 4 changes (on average over
time), as in the Gutenberg-Richter scale for earthquakes. If so, then
scientific revolutions would be scale free, meaning that large
revolutions in the future are more probable than a Gaussian normal
distribution would predict. Such a conclusion would have important
implications for the issue of scientific realism.



To be sure, working out such a timescale of revolutions and their
sizes in the history of science would be difficult and controversial,
but Nicholas Rescher (1978, 2006) has begun the task in terms of
ranking scientific discoveries and studying their distribution over
time. Derek Price (1963) had previously introduced quantitative
historical considerations into history of science, pointing out, among
many other things, the exponential increase in the number of
scientists and quantity of their publications since the Scientific
Revolution. Such an exponential increase, faster than world population
increase, obviously cannot continue forever and, in fact, was already
beginning to plateau in industrialized nations in the 1960s. Among
philosophers, Rescher was probably the first to analyze aggregate data
concerning scientific innovation, arguing that, as research
progresses, discoveries of a given magnitude become more difficult.
Rescher concludes that we must eventually expect a decrease in the
rate of discovery of a given magnitude and hence, presumably, a
similar decrease in the rate of scientific revolutions. Although he
does not mention Schumpeter in this work, he expresses a similar
view:



> 
> Scientific progress in large measure annihilates rather than enlarges
> what has gone before--it builds the new on the foundations of the
> ruins of the old. Scientific theorizing generally moves ahead not by
> addition and *enlargement* but by demolition and
> *replacement*. [1978, p. 82, Rescher's emphasis]
> 



This broadly Kuhnian position position on the number and magnitude of
revolutions contrasts sharply with Butterfield's, who saw
revolutions only as founding revolutions, and also with that of those
epistemological realists who grant that revolutionary conceptual and
practical changes have occurred but who believe that they will become
successively smaller in the future as science approaches the true
theory. Kuhn's own later position, in which specialties are
insulated from one another by taxonomic incommensurability, presents
us with a somewhat less integrated conception of science and thus one
less subject to large-scale revolutionary disruption. Since we can
regard scientific practices and organization as highly designed
technological systems, the work of Charles Perrow and others on
technological risk is relevant here. (See Perrow 1984 for entry into
this approach.)



Margolis (1993) notes the importance of the phenomenon of
"contagion," in which new ideas or practices suddenly
reach a kind of social tipping point and spread rapidly. Contagion is,
of course, necessary for a revolt to succeed as a revolution. Today,
contagion is a topic being studied carefully by network theorists and
popularized by Malcolm Gladwell's *The Tipping Point*
(2000). Steven Strogatz, Duncan Watts, and Albert-Laszlo
Barabasi are among the new breed of network theorists who are
developing technical accounts of "phase changes" resulting
from the growth and reorganization of networks, including social
networks of science--a topic dear to the early Kuhn's heart
as he struggled with the themes of *Structure* (see Strogatz,
2003, chap. 10; Watts 1999; Newman 2001; Barabasi 2002;
Buchanan 2002).



Does the emergence to prominence of "chaos theory"
(nonlinear dynamics) itself constitute a scientific revolution and, if
so, is it a distinctly Kuhnian revolution? In recent years several
writers, including both scientists and science writers, have attempted
to link Kuhn's idea of revolutionary paradigm shifts to the
emergence of chaos theory, complexity theory, and network theory
(e.g., Gleick 1987, chap. 2, on the chaos theory revolution; Ruelle
1991, chap. 11; Jen in Cowan et al. 1999, 622f, on complexity theory;
and Buchanan 2002, 47, on network theory). Interestingly, some authors
reapply these ideas to Kuhn's account itself, theoretically
construing revolutionary paradigm shifts as phase changes or as
nonlinear jumps from one strange attractor or one sort of network
structure to another.



Steven Kellert (1993) considers and rejects the claim that chaos
theory represents a Kuhnian revolution. Although it does provide a new
set of research problems and standards and, to some degree, transforms
our worldview, it does not overturn and replace an entrenched theory.
Kellert argues that chaos theory does not even constitute the
emergence of a new, mature science rather than an extension of
standard mechanics, although it may constitute a new style of
reasoning.



Kellert's position hangs partly on how we construe theories. If
a theory is just a toolbox of models, something like an integrated
collection of Kuhnian exemplars (Giere 1988, Teller 2008), then the
claim for a revolutionary theory development of some kind becomes more
plausible. For nonlinear dynamics highlights a new set of models and
the strange attractors that characterize their behaviors. In addition,
complex systems theorists often stress the holistic, anti-reductive,
emergent nature of the systems they study, by contrast with the
linear, Newtonian paradigm. Kuhn wrote that one way in which normal
science articulates its paradigm is by "permitting the solution
of problems to which it had previously only drawn attention."
But had not classical dynamics suppressed rather than drawn attention
to the problems of chaos theory and the various sorts of complexity
theory and network theory that are much studied today? Still, it is
easy to agree with Kellert that this case does not fit Kuhn's
account neatly. To some readers it suggests that a more pluralistic
conception of scientific revolutions than Kuhn's is needed.



Kellert also questions whether traditional dynamics was really in a
special state of crisis prior to the recent emphasis on nonlinear
dynamics, for difficulties in dealing with nonlinear phenomena have
been apparent almost from the beginning. Since Kuhn himself
emphasized, against Popper, that all theories face anomalies at all
times, it is unfortunately all too easy, after an apparently
revolutionary development, to point back and claim crisis.


### 6.4 The Essential Tension between Tradition and Innovation



Kuhn's work called attention to what he called "the
essential tension" between tradition and innovation (Kuhn 1959,
1977a). While he initially claimed that his model applied only to
mature natural sciences such as physics, chemistry, and parts of
biology, he believed that the essential tension point applies, in
varying degrees, to all enterprises that place a premium on creative
innovation. His work thereby raises interesting questions, such as
which kinds of social structures make revolution necessary (by
contrast with more continuous varieties of transformative change) and
whether those that do experience revolutions tend to be more
progressive by some standard.



Some analysts agree that casting the net more widely might shed
comparative light on scientific change, and that Kuhn's model is
too restrictive even when applied only to the mature sciences. We have
already met several alternative conceptions of transformative change
in the sciences. Kuhn believed that innovation in the arts was often
too divergent fully to express the essential tension. By contrast, the
sciences, he claimed, do not seek innovation for its own sake, at
least normal scientists do not.



But what about technological innovation (which is often closely
related to mature science) and what about business enterprise more
generally? There are, of course, important differences between the
products of basic scientific research and commercial products and
services, but there are enough similarities to make comparison
worthwhile--the more so with today's emphasis on
translational science. And in the sciences as well as economic life
there would seem to be other forms of displacement than the logical
and epistemological forms commonly recognized by philosophers of
science. Consider the familiar economic phenomenon of obsolescence,
including cases that lead to major social reorganization as
technological systems are improved. Think of algorithmic data mining
and statistical computation, robotics, and the automation to be found
in any modern biological laboratory. In *The Innovator's
Dilemma* (1997), economist Clayton Christensen denies that major
technological breakthroughs are either necessary or sufficient for
disruptive innovation. In that and later work he distinguishes
sustaining technologies that make incremental improvements of a
company's sales leaders from two kinds of disruptive
technologies. "New-market disruptions" appeal to a
previously *non-existent* market, whereas
"low-market" or "low-end disruptions" provide
simpler and cheaper ways to do things than do the leading products and
services. Such companies can sometimes scale up their more efficient
processes to displace the major players, as did Japanese steel makers
to the big U.S. corporations. There would seem to be parallels in the
history of science.



Speaking of technological developments, philosophers, including Kuhn,
have undervalued a major source of transformative developments,
namely, material culture, specifically the development of new
instruments. There is, however, a growing literature in history and
sociology of science and technology. A good example is Andy
Pickering's discussion of the conception and construction of the
large cloud chamber at Lawrence Berkeley Laboratory (Pickering 1995).
Pickering's *Constructing Quarks* (1984), Peter
Galison's *How Experiments End* (1987) and *Image and
Logic* (1997), and Sharon Traweek's *Beamtimes and
Lifetimes* (1988) describe the cultures that grew up around the
big machines and big theories of high-energy physics in the U.S.,
Europe, and Japan. As he himself recognized, Kuhn's model of
rapid change runs into increasing difficulty with the Big Science of
the World War II era and beyond. But a similar point extends to
smaller-scale material practices as documented by much recent
research, as in Baird (2004), discussed above. One line of fruitful
investigation has been that of the Social Construction of Technology
(SCOT) program of Trevor Pinch and Wiebe Bijker (see Bijker et al.
1987 and a good deal of later work). Such work takes place on all
scales.



In *Structure* and later writings, Kuhn locates revolutionary
change both at the logico-semantical and methodological level
(incompatibility between successor and predecessor paradigm) and at
the level of form of community life and practice. But does the latter
always require the former? Perhaps expressions such as "the
problem of *conceptual* change" and "breaking out
of the old conceptual framework" have led philosophers to
over-intellectualize historical change. As we know from the history of
economics and business, one form of life can replace another in
various ways without being based directly upon a logical or semantic
incompatibility. The old ways may be not wrong but simply obsolete,
inefficient, out of fashion--destroyed by a process that requires
more resources than simple logical relations to understand it. There
can be massive displacement by non-logical means. Many have argued
that Kuhn's semantic holism, with its logical-relational
underpinnings, led him to underappreciate how flexible scientists and
technologists can be at the frontiers of research (Galison 1997).
Having distinguished the working scientists' point of view from
those of the historian and the philosopher, looking down from above,
he proceeded to confuse them. Retrospectively, as many commentators
have noted, we can view Kuhn on scientific revolutions as a
transitional figure, more indebted to logical empiricist conceptions
of logic, language, and meaning than he could have recognized at the
time, while departing sharply from the logical empiricists and Popper
in other respects.