The Competitiveness of Nations
in a Global Knowledge-Based Economy
October 2002
Thomas S. Kuhn
The Structure
Postscript - 1969
Third Edition
University of Chicago Press, Chicago,
[1962, 1970] 1996
Index
1. Paradigms and Community Structure
2. Paradigms as the Constellation of Group Commitments
3.
Paradigms as Shared Examples
4.
Tacit Knowledge and Intuition
5. Exemplars, Incommensurability, and Revolutions
HHC: Index added
It has now been almost seven years since this book was first published
.1 In the interim both the response of critics and my own further work have increased my understanding of a number of the issues it raises. On fundamentals my viewpoint is very nearly unchanged, but I now recognize aspects of its initial formulation that create gratuitous difficulties and misunderstandings. Since some of those misunderstandings have been my own, their elimination enables me to gain ground that should ultimately provide the basis for a new version of the book. 2 Meanwhile, I welcome the chance to sketch needed revisions, to comment on some reiterated criticisms, and to suggest directions in which my own thought is presently developing. 3Several of the key difficulties of my original text cluster about the concept of a paradigm, and my discussion begins with them.
4 In the subsection that follows at once, I suggest the desirability of disentangling that concept from the notion of a scientific community, indicate how this may be done, and discuss some signifi-
1. This postscript was first prepared at the
suggestion of my onetime student and longtime friend, Dr. Shigeru Nakayaxna of
the
2. For this edition I have attempted no
systematic rewriting, restricting alterations to a few typographical errors
plus two passages which contained isolable errors.
One of these is the description of the
role of
3.Other indications will be found in two
recent essays of mine: “Reflection on My Critics,” in Imre Lakatos and Alan
Musgrave (eds.), Criticism and the Growth of Knowledge
(Cambridge, 1970); and “Second Thoughts on Paradigms,” in Frederick Suppe
(ad.), The Structure of Scientific Theories (Urbana, Ill., 1970
or 1971), both currently in press. I
shall cite the first of these essays below as “Reflections” and the volume in
which it appears as Growth of Knowledge; the second essay will
be referred to as “Second Thoughts.”
4 For particularly cogent criticism of my initial
presentation of paradigms see: Margaret Masterman, “The Nature of a Paradigm,”
in Growth of Knowledge; and Dudley Shapere, “The Structure of
Scientific Revolutions,” Philosophical Review, LXXIII (1964),
383-94.
174
cant consequences of the resulting analytic
separation. Next I consider what
occurs when paradigms are sought by examining the behavior of the members of a
previously determined scientific community.
That procedure quickly discloses that
in much of the book the term ‘paradigm’ is used in two different senses.
On the one hand, it stands for the
entire constellation of beliefs, values, techniques, and so on shared by the
members of a given community. On the
other, it denotes one sort of element in that constellation, the concrete
puzzle-solutions which, employed as models or examples, can replace explicit
rules as a basis for the solution of the remaining puzzles of normal science.
The first sense of the term, call it
the sociological, is the subject of Subsection 2, below; Subsection 3 is
devoted to paradigms as exemplary past achievements.
Philosophically, at least, this second sense of
‘paradigm’ is the deeper of the two, and the claims I have made in its name
are the main sources for the controversies and misunderstandings that the book
has evoked, particularly for the charge that I make of science a subjective
and irrational enterprise. These
issues are considered in Subsections 4 and 5.
The first argues that terms like ‘subjective’ and ‘intuitive’ cannot
appropriately be applied to the components of knowledge that I have described
as tacitly embedded in shared examples. Though
such knowledge is not, without essential change, subject to paraphrase in
terms of rules and criteria, it is nevertheless systematic, time tested, and
in some sense corrigible. Subsection 5
applies that argument to the problem of choice between two incompatible
theories, urging in brief conclusion that men who hold incommensurable
viewpoints be thought of as members of different language communities and that
their communication problems be analyzed as problems of translation.
Three residual issues are discussed in
the concluding Subsections, 6 and 7. The
first considers the charge that the view of science developed in this book is
through-and-through relativistic. The
second begins by inquiring whether my argument really suffers, as has been
said, from a confusion between the descriptive and the normative modes; it
concludes with brief remarks on a topic deserving a separate
175
essay: the extent to which the book’s main
theses may legitimately be applied to fields other than science.
1. Paradigms and Community Structure
The term ‘paradigm’ enters the preceding pages early, and its manner of entry is intrinsically circular. A paradigm is what the members of a scientific community share, and, conversely, a scientific community consists of men who share a paradigm. Not all circularities are vicious (I shall defend an argument of similar structure late in this postscript), but this one is a source of real difficulties. Scientific communities can and should be isolated without prior recourse to paradigms; the latter can then be discovered by scrutinizing the behavior of a given community’s members. If this book were being rewritten, it would therefore open with a discussion of the community structure of science, a topic that has recently become a significant subject of sociological research and that historians of science are also beginning to take seriously. Preliminary results, many of them still unpublished, suggest that the empirical techniques required for its exploration are non-trivial, but some are in hand and others are sure to be developed
. 5 Most practicing scientists respond at once to questions about their community affiliations, taking for granted that responsibility for the various current specialties is distributed among groups of at least roughly determinate membership. I shall therefore here assume that more systematic means for their identification will be found. Instead of presenting preliminary research results, let me briefly articulate the intuitive notion of community that underlies much in the earlier chapters of this book. It is a notion now widely shared by scientists, sociologists, and a number of historians of science.
5. W. O. Hagstrom, The Scientific
Community (New York, 1965), chaps. iv and v; D. J. Price and D. de B.
Beaver, “Collaboration in an Invisible College,” American Psychologist,
XXI (1966), 1011-18; Diana Crane, “Social Structure in a Group of Scientists:
A Test of the ‘Invisible College’ Hypothesis,” American Sociological
Review, XXXIV (1969), 335-52; N. C. Mullins, Social Networks among
Biological Scientists, (Ph.D. diss., Harvard University, 1966), and
“The Micro-Structure of an Invisible College: The Phage Group” (paper
delivered at an annual meeting of the American Sociological Association,
Boston, 1968).
176
A scientific community consists, on this view,
of the practitioners of a scientific specialty.
To an extent unparalleled in most
other fields, they have undergone similar educations and professional
initiations; in the process they have absorbed the same technical literature
and drawn many of the same lessons from it. Usually
the boundaries of that standard literature mark the limits of a scientific
subject matter, and each community ordinarily has a subject matter of its own.
There are schools in the sciences,
communities, that is, which approach the same subject from incompatible
viewpoints. But they are far rarer
there than in other fields; they are always in competition; and their
competition is usually quickly ended. As
a result, the members of a scientific community see themselves and are seen by
others as the men uniquely responsible for the pursuit of a set of shared
goals, including the training of their successors.
Within such groups communication is
relatively full and professional judgment relatively unanimous.
Because the attention of different
scientific communities is, on the other hand, focused on different matters,
professional communication across group lines is some times arduous, often
results in misunderstanding, and may, if pursued, evoke significant and
previously unsuspected disagreement.
Communities in this sense exist, of course, at
numerous levels. The most global is
the community of all natural scientists. At
an only slightly lower level the main scientific professional groups are
communities: physicists, chemists, astronomers, zoologists, and the like.
For these major groupings, community
membership is readily established except at the fringes.
Subject of highest degree, membership
in professional societies, and journals read are ordinarily more than
sufficient. Similar techniques will
also isolate major subgroups: organic chemists, and perhaps protein chemists
among them, solid-state and high-energy physicists, radio astronomers, and so
on. It is only at the next lower level
that empirical problems emerge. How,
to take a contemporary example, would one have isolated the phage group prior
to its public acclaim? For this
purpose one must have recourse to attendance at special conferences, to the
distri-
177
bution of draft manuscripts or galley proofs prior to publication, and above all to formal and informal communication networks including those discovered in correspondence and in the linkages among citations
. 6 I take it that the job can and will be done, at least for the contemporary scene and the more recent parts of the historical. Typically it may yield communities of perhaps one hundred members, occasionally significantly fewer. Usually individual scientists, particularly the ablest, will belong to several such groups either simultaneously or in succession.
Communities of this sort are the units that this
book has presented as the producers and validators of scientific knowledge.
Paradigms are something shared by the
members of such groups. Without
reference to the nature of these shared elements, many aspects of science
described in the preceding pages can scarcely be understood.
But other aspects can, though they are
not independently presented in my original text.
It is therefore worth noting, before turning to paradigms directly, a
series of issues that require reference to community structure alone.
Probably the most striking of these is what I
have previously called the transition from the pre- to the post-paradigm
period in the development of a scientific field.
That transition is the one sketched
above in Section II. Before it
occurs, a number of schools compete for the domination of a given field.
Afterward, in the wake of some notable
scientific achievement, the number of schools is greatly reduced, ordinarily
to one, and a more efficient mode of scientific practice begins.
The latter is generally esoteric and
oriented to puzzle-solving, as the work of a group can be only when its
members take the foundations of their field for granted.
The nature of that transition to maturity
deserves fuller discussion than it has received in this book,
particularly from those concerned with the development of the contemporary
social
6. Eugene Garfield, The Use of Citation Data
in Writing the History of Science (Philadelphia: Institute of Scientific
Information, 1964); M. M. Kessler, “Comparison of the Results of Bibliographic
Coupling and Analytic Subject Indexing,” American Documentation, XVI
(1965), 223-33; D. J. Price, “Networks of Scientific Papers,” Science,
CIL (1965), 510-15.
178
sciences. To
that end it may help to point out that the transition need not (I now think
should not) be associated with the first acquisition of a paradigm.
The members of all scientific
communities, including the schools of the “pre-paradigm” period, share the
sorts of elements which I have collectively labelled ‘a paradigm.’
What changes with the transition to
maturity is not the presence of a paradigm but rather its nature.
Only after the change is normal
puzzle-solving research possible. Many
of the attributes of a developed science which I have above associated with
the acquisition of a paradigm I would therefore now discuss as consequences of
the acquisition of the sort of paradigm that identifies challenging puzzles,
supplies clues to their solution, and guarantees that the truly clever
practitioner will succeed. Only those
who have taken courage from observing that their own field (or school) has
paradigms are likely to feel that something important is sacrificed by the
change.
A second issue, more important at least to
historians, concerns this book’s implicit one-to-one identification of
scientific communities with scientific subject matters.
I have, that is, repeatedly acted as
though, say, ‘physical optics,’ ‘electricity,’ and ‘heat’ must name scientific
communities because they do name subject matters for research.
The only alternative my text has
seemed to allow is that all these subjects have belonged to the physics
community. Identifications of that
sort will not, however, usually withstand examination, as my colleagues in
history have repeatedly pointed out. There
was, for example, no physics community before the mid-nineteenth century, and
it was then formed by the merger of parts of two previously separate
communities, mathematics and natural philosophy (physique experimentale).
What is today the subject matter
for a single broad community has been variously distributed among diverse
communities in the past. Other
narrower subjects, for example heat and the theory of matter, have existed for
long periods without becoming the special province of any single scientific
community. Both normal science and
revolutions are, however, community-based activities.
To discover and analyze them, one must
first unravel the changing community structure of the sciences
179
over time. A
paradigm governs, in the first instance, not a subject matter but rather a
group of practitioners. Any study of
paradigm-directed or of paradigm-shattering research must begin by locating
the responsible group or groups.
When the analysis of scientific development is
approached in that way, several difficulties which have been foci for critical
attention are likely to vanish. A
number of commentators have, for example, used the theory of matter to suggest
that I drastically overstate the unanimity of scientists in their allegiance
to a paradigm. Until comparatively
recently, they point out, those theories have been topics for continuing
disagreement and debate. I agree with
the description but think it no counter-example.
Theories of matter were not, at least
until about 1920, the special province or the subject matter for any
scientific community. Instead, they
were tools for a large number of specialists’ groups.
Members of different communities
sometimes chose different tools and criticized the choice made by others.
Even more important, a theory of
matter is not the sort of topic on which the members of even a single
community must necessarily agree. The
need for agreement depends on what it is the community does.
Chemistry in the first half of the
nineteenth century provides a case in point. Though
several of the community’s fundamental tools - constant proportion, multiple
proportion, and combining weights - had become common property as a result of
Dalton’s atomic theory, it was quite possible for chemists, after the event,
to base their work on these tools and to disagree, sometimes vehemently, about
the existence of atoms.
Some other difficulties and misunderstandings
will, I believe, be dissolved in the same way.
Partly because of the examples I have chosen and partly because of my
vagueness about the nature and size of the relevant communities, a few readers
of this book have concluded that my concern is primarily or exclusively with
major revolutions such as those associated with Copernicus,
180
is for me a special sort of change involving a
certain sort of reconstruction of group commitments.
But it need not be a large change, nor
need it seem revolutionary to those outside a single community, consisting
perhaps of fewer than twenty-five people. It
is just because this type of change, little recognized or discussed in the
literature of the philosophy of science, occurs so regularly on this smaller
scale that revolutionary, as against cumulative, change so badly needs to be
understood.
One last alteration, closely related to the
preceding, may help to facilitate that understanding.
A number of critics have doubted
whether crisis, the common awareness that something has gone wrong, precedes
revolutions so invariably as I have implied in my original text.
Nothing important to my argument
depends, however, on crises’ being an absolute prerequisite to revolutions;
they need only be the usual prelude, supplying, that is, a self-correcting
mechanism which ensures that the rigidity of normal science will not forever
go unchallenged. Revolutions may also
be induced in other ways, though I think they seldom are.
In addition, I would now point out
what the absence of an adequate discussion of community structure has obscured
above: crises need not be generated by the work of the community that
experiences them and that sometimes undergoes revolution as a result.
New instruments like the electron
microscope or new laws like Maxwell’s may develop in one specialty and their
assimilation create crisis in another.
2.
Paradigms as the Constellation of Group Commitments
Turn now to paradigms and ask what they can possibly be. My original text leaves no more obscure or important question. One sympathetic reader, who shares my conviction that ‘paradigm’ names the central philosophical elements of the book, prepared a partial analytic index and concluded that the term is used in at least twenty-two different ways
. 7 Most of those differences are, I now think, due to stylistic inconsistencies (e.g.,
181
sometimes paradigmatic), and they can be
eliminated with relative ease. But,
with that editorial work done, two very different usages of the term would
remain, and they require separation. The
more global use is the subject of this subsection; the other will be
considered in the next.
Having isolated a particular community of
specialists by techniques like those just discussed, one may usefully ask:
What do its members share that accounts for the relative fulness of their
professional communication and the relative unanimity of their professional
judgments? To that question my
original text licenses the answer, a paradigm or set of paradigms.
But for this use, unlike the one to be
discussed below, the term is inappropriate. Scientists
themselves would say they share a theory or set of theories, and I shall be
glad if the term can ultimately be recaptured for this use.
As currently used in philosophy of
science, however, ‘theory’ connotes a structure far more limited in nature and
scope than the one required here. Until
the term can be freed from its current implications, it will avoid confusion
to adopt another. For present purposes
I suggest ‘disciplinary matrix’: ‘disciplinary’ because it refers to the
common possession of the practitioners of a particular discipline; ‘matrix’
because it is composed of ordered elements of various sorts, each requiring
further specification. All or most of
the objects of group commitment that my original text makes paradigms, parts
of paradigms, or paradigmatic are constituents of the disciplinary matrix, and
as such they form a whole and function together.
They are, however, no longer to be
discussed as though they were all of a piece.
I shall not here attempt an exhaustive list, but noting the main sorts
of components of a disciplinary matrix will both clarify the nature of my
present approach and simultaneously prepare for my next main point.
One important sort of component I shall label
‘symbolic generalizations,’ having in mind those expressions, deployed without
question or dissent by group members, which can readily be cast in a logical
form like (x)(y)(z)
f (x, y, z).
They are the formal or the readily
formalizable components of the disciplinary matrix.
Sometimes they are found already in
sym-
182
bolic form: f = ma or I =
V/R. Others are ordinarily
expressed in words: “elements combine in constant proportion by weight,” or
“action equals reaction.” If it were
not for the general acceptance of expressions like these, there would be no
points at which group members could attach the powerful techniques of logical
and mathematical manipulation in their puzzle-solving enterprise.
Though the example of taxonomy
suggests that normal science can proceed with few such expressions, the power
of a science seems quite generally to increase with the number of symbolic
generalizations its practioners have at their disposal.
These generalizations look like laws of nature, but their function for group members is not often that alone. Sometimes it is: for example the Joule-Lenz Law, H = RI2. When that law was discovered, community members already knew what H, R, and I stood for, and these generalizations simply told them something about the behavior of heat, current, and resistance that they had not known before. But more often, as discussion earlier in the book indicates, symbolic generalizations simultaneously serve a second function, one that is ordinarily sharply separated in analyses by philosophers of science. Like f = ma or I = V/R, they function in part as laws but also in part as definitions of some of the symbols they deploy. Furthermore, the balance between their inseparable legislative and definitional force shifts over time. In another context these points would repay detailed analysis, for the nature of the commitment to a law is very different from that of commitment to a definition. Laws are often corrigible piecemeal, but definitions, being tautologies, are not. For example, part of what the acceptance of Ohm’s Law demanded was a redefinition of both ‘current’ and ‘resistance’; if those terms had continued to mean what they had meant before, Ohm’s Law could not have been right; that is why it was so strenuously opposed as, say, the Joule-Lenz Law was not.
8 Probably that situation is typical. I currently suspect that
8. For significant parts of this episode see: T.
M. Brown, “The Electric Current in Early Nineteenth-Century French Physics,”
Historical Studies in the Physical Sciences, I (1969), 61-103, and
Morton Schagrin, “Resistance to Ohm’s Law,” American Journal of Physics,
XXI (1963), 536-47.
183
all revolutions involve, among other things, the
abandonment of generalizations the force of which had previously been in some
part that of tautologies. Did Einstein
show that simultaneity was relative or did he alter the notion of simultaneity
itself? Were those who heard paradox
in the phrase ‘relativity of simultaneity’ simply wrong?
Consider next a second type of component of the
disciplinary matrix, one about which a good deal has been said in my original
text under such rubrics as ‘metaphysical paradigms’ or ‘the metaphysical parts
of paradigms.’ I have in mind
shared commitments to such beliefs as: heat is the kinetic energy of the
constituent parts of bodies; all perceptible phenomena are due to the
interaction of qualitatively neutral atoms in the void, or, alternatively, to
matter and force, or to fields. Rewriting
the book now I would describe such commitments as beliefs in particular
models, and I would expand the category models to include also the relatively
heuristic variety: the electric circuit may be regarded as a steady-state
hydrodynamic system; the molecules of a gas behave like tiny elastic billiard
balls in random motion. Though the
strength of group commitment varies, with non-trivial consequences, along the
spectrum from heuristic to ontological models, all models have similar
functions. Among other things they
supply the group with preferred or permissible analogies and metaphors.
By doing so they help to determine
what will be accepted as an explanation and as a puzzle-solution; conversely,
they assist in the determination of the roster of unsolved puzzles and in the
evaluation of the importance of each. Note,
however, that the members of scientific communities may not have to share even
heuristic models, though they usually do so. I
have already pointed out that membership in the community of chemists during
the first half of the nineteenth century did not demand a belief in atoms.
A third sort of element in the disciplinary
matrix I shall here describe as values. Usually
they are more widely shared among different communities than either symbolic
generalizations or models, and they do much to provide a sense of community to
natural scientists as a whole. Though
they function at all times, their particular importance emerges when the
members of a
184
particular community must identify crisis or,
later, choose between incompatible ways of practicing their discipline.
Probably the most deeply held values
concern predictions: they should be accurate; quantitative predictions are
preferable to qualitative ones; whatever the margin of permissible error, it
should be consistently satisfied in a given field; and so on.
There are also, however, values to be
used in judging whole theories: they must, first and foremost, permit
puzzle-formulation and solution; where possible they should be simple,
self-consistent, and plausible, compatible, that is, with other theories
currently deployed. (I now think it a
weakness of my original text that so little attention is given to such values
as internal and external consistency in considering sources of crisis and
factors in theory choice.) Other sorts
of values exist as well - for example, science should (or need not) be
socially useful - but the preceding should indicate what I have in mind.
One aspect of shared values does, however,
require particular mention. To a
greater extent than other sorts of components of the disciplinary matrix,
values may be shared by men who differ in their application.
Judgments of accuracy are relatively,
though not entirely, stable from one time to another and from one member to
another in a particular group. But
judgments of simplicity, consistency, plausibility, and so on often vary
greatly from individual to individual. What
was for Einstein an insupportable inconsistency in the old quantum theory, one
that rendered the pursuit of normal science impossible, was for Bohr and
others a difficulty that could be expected to work itself out by normal means.
Even more important, in those
situations where values must be applied, different values, taken alone, would
often dictate different choices. One
theory may be more accurate but less consistent or plausible than another;
again the old quantum theory provides an example.
In short, though values are widely
shared by scientists and though commitment to them is both deep and
constitutive of science, the application of values is sometimes considerably
affected by the features of individual personality and biography that
differentiate the members of the group.
To many readers of the preceding chapters, this
characteristic
185
of the operation of shared values has seemed a major weakness of my position. Because I insist that what scientists share is not sufficient to command uniform assent about such matters as the choice between competing theories or the distinction between an ordinary anomaly and a crisis-provoking one, I am occasionally accused of glorifying subjectivity and even irrationality
. 9 But that reaction ignores two characteristics displayed by value judgments in any field. First, shared values can be important determinants of group behavior even though the members of the group do not all apply them in the same way. (If that were not the case, there would be no special philosophic problems about value theory or aesthetics.) Men did not all paint alike during the periods when representation was a primary value, but the developmental pattern of the plastic arts changed drastically when that value was abandoned. 10 Imagine what would happen in the sciences if consistency ceased to be a primary value. Second, individual variability in the application of shared values may serve functions essential to science. The points at which values must be applied are invariably also those at which risks must be taken. Most anomalies are resolved by normal means; most proposals for new theories do prove to be wrong. If all members of a community responded to each anomaly as a source of crisis or embraced each new theory advanced by a colleague, science would cease. If, on the other hand, no one reacted to anomalies or to brand-new theories in high-risk ways, there would be few or no revolutions. In matters like these the resort to shared values rather than to shared rules governing individual choice may be the community’s way of distributing risk and assuring the long-term success of its enterprise.
Turn now to a fourth sort of element in the
disciplinary matrix, not the only other kind but the last I shall discuss
here. For it the term ‘paradigm’ would
be entirely appropriate, both philology-
9. See particularly: Dudley Shapere, “Meaning and
Scientific Change,” in Mind and Cosmos: Essays in Contemporary Science and
Philosophy, The University of Pittsburgh Series in the Philosophy of
Science, III (Pittsburgh, 1966), 41-85; Israel Scheffler, Science and
Subjectivity (New York, 1987); and the essays of Sir Karl Popper and Imre
Lalcatos in Growth of Knowledge.
10. See the discussion at the beginning of
Section XIII, above.
186
cally and autobiographically; this is the
component of a group’s shared commitments which first led me to the choice of
that word. Because the term has
assumed a life of its own, however, I shall here substitute ‘exemplars.’
By it I mean, initially, the concrete
problem-solutions that students encounter from the start of their scientific
education, whether in laboratories, on examinations, or at the ends of
chapters in science texts. To these
shared examples should, however, be added at least some of the technical
problem-solutions found in the periodical literature that scientists encounter
during their post-educational research careers and that also show them by
example how their job is to be done. More
than other sorts of components of the disciplinary matrix, differences between
sets of exemplars provide the community fine-structure of science.
All physicists, for example, begin by
learning the same exemplars: problems such as the inclined plane, the conical
pendulum, and Keplerian orbits; instruments such as the vernier, the
calorimeter, and the Wheatstone bridge. As
their training develops, however, the symbolic generalizations they share are
increasingly illustrated by different exemplars.
Though both solid-state and
field-theoretic physicists share the Schrodinger equation, only its more
elementary applications are common to both groups.
3.
Paradigms as Shared Examples
The paradigm as shared example is the central
element of what I now take to be the most novel and least understood aspect of
this book. Exemplars will therefore
require more attention than the other sorts of components of the disciplinary
matrix. Philosophers of science have
not ordinarily discussed the problems encountered by a student in laboratories
or in science texts, for these are thought to supply only practice in the
application of what the student already knows.
He cannot, it is said, solve problems at all unless he has first
learned the theory and some rules for applying it.
Scientific knowledge is embedded in
theory and rules; problems are supplied to gain facility in their application.
I have tried to argue, however, that
this localization of
187
the cognitive content of science is wrong.
After the student has done many
problems, he may gain only added facility by solving more.
But at the start and for some time
after, doing problems is learning consequential things about nature.
In the absence of such exemplars, the
laws and theories he has previously learned would have little empirical
content.
To indicate what I have in mind I revert briefly
to symbolic generalizations. One
widely shared example is
In practice, though this aspect of the situation
is seldom or never noted, what students have to learn is even more complex
than that. It is not quite the case
that logical and mathematical manipulation are applied directly to f =
ma. That expression proves on
examination to be a law-sketch or a law-schema.
As the student or the practicing
scientist moves from one problem situation to the next, the symbolic
generalization to which such manipulations apply changes.
For the case of free fall, f = ma
becomes
;
for the simple pendulum it is
transformed to
;
for a pair of interacting harmonic oscillators it becomes two equations,
the first of which may be written
188
and for more complex situations, such as the
gyroscope, it takes still other forms, the family resemblance of which to f
= ma is still harder to discover. Yet,
while learning to identify forces, masses, and accelerations in a variety of
physical situations not previously encountered, the student has also learned
to design the appropriate version of f = ma through which to
interrelate them, often a version for which he has encountered no literal
equivalent before. How has he learned to do this?
A phenomenon familiar to both students of
science and historians of science provides a clue.
The former regularly report that they
have read through a chapter of their text, understood it perfectly, but
nonetheless had difficulty solving a number of the problems at the chapter’s
end. Ordinarily, also, those
difficulties dissolve in the same way. The
student discovers, with or without the assistance of his instructor, a way to
see his problem as like a problem he has already encountered.
Having seen the resemblance, grasped
the analogy between two or more distinct problems, he can interrelate symbols
and attach them to nature in the ways that have proved effective before.
The law-sketch, say f = ma, has
functioned as a tool, informing the student what similarities to look for,
signaling the gestalt in which the situation is to be seen.
The resultant ability to see a variety
of situations as like each other, as subjects for f = ma or some other
symbolic generalization, is, I think, the main thing a student acquires by
doing exemplary problems, whether with a pencil and paper or in a
well-designed laboratory. After he has
completed a certain number, which may vary widely from one individual to the
next, he views the situations that confront him as a scientist in the same
gestalt as other members of his specialists’ group.
For him they are no longer the same
situations he had encountered when his training began.
He has meanwhile assimilated a
time-tested and group licensed way of seeing.
The role of acquired similarity relations also
shows clearly in the history of science. Scientists
solve puzzles by modelng them on previous puzzle-solutions, often with only
minimal recourse
189
to symbolic generalizations. Galileo found that a ball rolling down an incline acquires just enough velocity to return it to the same vertical height on a second incline of any slope, and he learned to see that experimental situation as like the pendulum with a point-mass for a bob. Huyghens then solved the problem of the center of oscillation of a physical pendulum by imagining that the extended body of the latter was composed of Galilean point-pendula, the bonds between which could be instantaneously released at any point in the swing. After the bonds were released, the individual point-pendula would swing freely, but their collective center of gravity when each attained its highest point would, like that of Galileo’s pendulum, rise only to the height from which the center of gravity of the extended pendulum had begun to fall. Finally, Daniel Bernoulli discovered how to make the flow of water from an orifice resemble Huyghens’ pendulum. Determine the descent of the center of gravity of the water in tank and jet during an infinitesimal interval of time. Next imagine that each particle of water afterward moves separately upward to the maximum height attainable with the velocity acquired during that interval. The ascent of the center of gravity of the individual particles must then equal the descent of the center of gravity of the water in tank and jet. From that view of the problem the long-sought speed of efflux followed at once
. 11
That example should begin to make clear what I
mean by learning from problems to see situations as like each other, as
subjects for the application of the same scientific law or law-sketch.
Simultaneously it should show why I
refer to the consequential knowledge of nature acquired while learning the
similarity relationship and thereafter embodied in a way of viewing
11.
For the example, see: René Dugas, A History of
Mechanics, trans. J. It. Maddox (Neuchatel, 1955), pp. 135-36, 186-93, and
Daniel Bernoulli, Hydrodynamica, sive de viribus et motibus fluidorum,
commentarii opus academicum (
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physical situations rather than in rules or
laws. The three problems in the example, all of them exemplars for
eighteenth-century mechanicians, deploy only one law of nature.
Known as the Principle of vis
viva, it was usually stated as:
“Actual descent equals potential ascent.” Bernoulli’s
application of the law should suggest how consequential it was.
Yet the verbal statement of the law,
taken by itself, is virtually impotent. Present
it to a contemporary student of physics, who knows the words and can do all
these problems but now employs different means.
Then imagine what the words, though
all well known, can have said to a man who did not know even the problems.
For him the generalization could begin
to function only when he learned to recognize “actual descents” and “potential
ascents” as ingredients of nature, and that is to learn something, prior to
the law, about the situations that nature does and does not present.
That sort of learning is not acquired
by exclusively verbal means. Rather it
comes as one is given words together with concrete examples of how they
function in use; nature and words are learned together.
To borrow once more Michael Polanyi’s
useful phrase, what results from this process is “tacit knowledge” which is
learned by doing science rather than by acquiring rules for doing it.
4.
Tacit Knowledge and Intuition
That reference to tacit knowledge and the
concurrent rejection of rules isolates another problem that has bothered many
of my critics and seemed to provide a basis for charges of subjectivity and
irrationality. Some readers have felt
that I was trying to make science rest on unanalyzable individual intuitions
rather than on logic and law. But that
interpretation goes astray in two essential respects.
First, if I am talking at all about
intuitions, they are not individual. Rather
they are the tested and shared possessions of the members of a successful
group, and the novice acquires them through training as a part of his
preparation for group-membership. Second,
they are not in principle unanalyzable. On
the contrary, I am currently experimenting with a
191
computer program designed to investigate their
properties at an elementary level.
About that program I shall have nothing to say here
, 12 but even mention of it should make my most essential point. When I speak of knowledge embedded in shared exemplars, I am not referring to a mode of knowing that is less systematic or less analyzable than knowledge embedded in rules, laws, or criteria of identification. Instead I have in mind a manner of knowing which is miscontrued if reconstructed in terms of rules that are first abstracted from exemplars and thereafter function in their stead. Or, to put the same point differently, when I speak of acquiring from exemplars the ability to recognize a given situation as like some and unlike others that one has seen before, I am not suggesting a process that is not potentially fully explicable in terms of neuro-cerebral mechanism. Instead I am claiming that the explication will not, by its nature, answer the question, “Similar with respect to what?” That question is a request for a rule, in this case for the criteria by which particular situations are grouped into similarity sets, and I am arguing that the temptation to seek criteria (or at least a full set) should be resisted in this case. It is not, however, system but a particular sort of system that I am opposing.
To give that point substance, I must briefly
digress. What follows seems obvious to
me now, but the constant recourse in my original text to phrases like “the
world changes” suggests that it has not always been so.
If two people stand at the same place
and gaze in the same direction, we must, under pain of solipsism, conclude
that they receive closely similar stimuli. (If
both could put their eyes at the same place, the stimuli would be identical.)
But people do not see stimuli; our
knowledge of them is highly theoretical and abstract.
Instead they have sensations, and we
are under no compulsion to suppose that the sensations of our two viewers are
the same. (Sceptics might remember
that color blindness was nowhere noticed until John Dalton’s description of it
in 1794.) On the contrary, much
12. Some information on this subject can be found
in “Second Thoughts.”
192
neural processing takes place between the
receipt of a stimulus and the awareness of a sensation.
Among the few things that we know
about it with assurance are: that very different stimuli can produce the same
sensations; that the same stimulus can produce very different sensations; and,
finally, that the route from stimulus to sensation is in part conditioned by
education. Individuals raised in
different societies behave on some occasions as though they saw different
things. If we were not tempted to
identify stimuli one-to-one with sensations, we might recognize that they
actually do so.
Notice now that two groups, the members of which
have systematically different sensations on receipt of the same stimuli, do in
some sense live in different worlds. We
posit the existence of stimuli to explain our perceptions of the world, and we
posit their immutability to avoid both individual and social solipsism.
About neither posit have I the
slightest reservation. But our world
is populated in the first instance not by stimuli but by the objects of our
sensations, and these need not be the same, individual to individual or group
to group. To the extent, of course,
that individuals belong to the same group and thus share education, language,
experience, and culture, we have good reason to suppose that their sensations
are the same. How else are we to
understand the fulness of their communication and the communality of their
behavioral responses to their environment? They
must see things, process stimuli, in much the same ways.
But where the differentiation and
specialization of groups begins, we have no similar evidence for the
immutability of sensation. Mere
parochialism, I suspect, makes us suppose that the route from stimuli to
sensation is the same for the members of all groups.
Returning now to exemplars and rules, what I
have been trying to suggest, in however preliminary a fashion, is this. One of
the fundamental techniques by which the members of a group, whether an entire
culture or a specialists’ sub-community within it, learn to see the same
things when confronted with the same stimuli is by being shown examples of
situations that their predecessors in the group have already learned to see as
like
193
each other and as different from other sorts of
situations. These similar situations
may be successive sensory presentations of the same individual - say of
mother, who is ultimately recognized on sight as what she is and as different
from father or sister. They may be
presentations of the members of natural families, say of swans on the one hand
and of geese on the other. Or they
may, for the members of more specialized groups, be examples of the Newtonian
situation, of situations, that is, that are alike in being subject to a
version of the symbolic form f = ma and that are different from
those situations to which, for example, the law-sketches of optics apply.
Grant for the moment that something of this sort does occur. Ought we say that what has been acquired from exemplars is rules and the ability to apply them? That description is tempting because our seeing a situation as like ones we have encountered before must be the result of neural processing, fully governed by physical and chemical laws. In this sense, once we have learned to do it, recognition of similarity must be as fully systematic as the beating of our hearts. But that very parallel suggests that recognition may also be involuntary, a process over which we have no control. If it is, then we may not properly conceive it as something we manage by applying rules and criteria. To speak of it in those terms implies that we have access to alternatives, that we might, for example, have disobeyed a rule, or misapplied a criterion, or experimented with some other way of seeing
. 13 Those, I take it, are just the sorts of things we cannot do.
Or, more precisely, those are things we cannot
do until after we have had a sensation, perceived something.
Then we do often seek criteria and put
them to use. Then we may engage
in interpretation, a deliberative process by which we choose among
alternatives as we do not in perception itself.
Perhaps, for example, something is odd
about what we have seen (remember the anomalous playing cards).
Turning a corner we see mother
13.
This point might never have needed making if all
laws were like
194
entering a downtown store at a time we had
thought she was home. Contemplating
what we have seen we suddenly exclaim, “That wasn’t mother, for she has red
hair!” Entering the store we see the
woman again and cannot understand how she could have been taken for mother.
Or, perhaps we see the tail feathers
of a waterfowl feeding from the bottom of a shallow pool.
Is it a swan
or a goose? We
contemplate what we have seen, mentally comparing the tail feathers with those
of swans and geese we have seen before. Or,
perhaps, being proto-scientists, we simply want to know some general
characteristic (the whiteness of swans, for example) of the members of a
natural family we can already recognize with ease.
Again, we contemplate what we have
previously perceived, searching for what the members of the given family have
in common.
These are all deliberative processes, and in
them we do seek and deploy criteria and rules.
We try, that is, to interpret sensations already at hand, to analyze
what is for us the given. However we
do that, the processes involved must ultimately be neural, and they are
therefore governed by the same physico-chemical laws that govern
perception on the one hand and the beating of our hearts on the other.
But the fact that the system obeys the
same laws in all three cases provides no reason to suppose that our neural
apparatus is programmed to operate the same way in interpretation as in
perception or in either as in the beating of our hearts.
What I have been opposing in this book
is therefore the attempt, traditional since Descartes but not before, to
analyze perception as an interpretive process, as an unconscious version of
what we do after we have perceived.
What makes the integrity of perception worth
emphasizing is, of course, that so much past experience is embodied in the
neural apparatus that transforms stimuli to sensations.
An appropriately programmed perceptual
mechanism has survival value. To say
that the members of different groups may have different perceptions when
confronted with the same stimuli is not to imply that they may have just any
perceptions at all. In many
environments a group that could not tell wolves from dogs could not endure.
Nor would a group of nuclear
physicists today survive as scien-
195
tists if unable to recognize the tracks of alpha
particles and electrons. It is just
because so very few ways of seeing will do that the ones that have withstood
the tests of group use are worth transmitting from generation to generation.
Equally, it is because they have been
selected for their success over historic time that we must speak of the
experience and knowledge of nature embedded in the stimulus-to-sensation
route.
Perhaps ‘knowledge’ is the wrong word, but there
are reasons for employing it. What is
built into the neural process that transforms stimuli to sensations has the
following characteristics: it has been transmitted through education; it has,
by trial, been found more effective than its historical competitors in a
group’s current environment; and, finally, it is subject to change both
through further education and through the discovery of misfits with the
environment. Those are characteristics
of knowledge, and they explain why I use the term.
But it is strange usage, for one other
characteristic is missing. We have no
direct access to what it is we know, no rules or generalizations with which to
express this knowledge. Rules which
could supply that access would refer to stimuli not sensations, and stimuli we
can know only through elaborate theory. In
its absence, the knowledge embedded in the stimulus-to-sensation route remains
tacit.
Though it is obviously preliminary and need not
be correct in all details, what has just been said about sensation is meant
literally. At the very least it is a
hypothesis about vision which should be subject to experimental investigation
though probably not to direct check. But
talk like this of seeing and sensation here also serves metaphorical functions
as it does in the body of the book. We
do not see electrons, but rather their tracks or else bubbles of vapor
in a cloud chamber. We do not see
electric currents at all, but rather the needle of an ammeter or
galvanometer. Yet in the preceding
pages, particularly in Section X, I have repeatedly acted as though we did
perceive theoretical entities like currents, electrons, and fields, as though
we learned to do so from examination of exemplars, and as though in these
cases too it would be wrong to replace talk of seeing with talk of criteria
and interpretation. The metaphor that
transfers ‘seeing’
196
to contexts like these is scarcely a sufficient
basis for such claims. In the long run
it will need to be eliminated in favor of a more literal mode of discourse.
The computer program referred to above begins to suggest ways in which that may be done, but neither available space nor the extent of my present understanding permits my eliminating the metaphor here
. 14 Instead I shall try briefly to bulwark it. Seeing water droplets or a needle against a numerical scale is a primitive perceptual experience for the man unacquainted with cloud chambers and ammeters. It thus requires contemplation, analysis, and interpretation (or else the intervention of external authority) before conclusions can be reached about electrons or currents. But the position of the man who has learned about these instruments and had much exemplary experience with them is very different, and there are corresponding differences in the way he processes the stimuli that reach him from them. Regarding the vapor in his breath on a cold winter afternoon, his sensation may be the same as that of a layman, but viewing a cloud chamber he sees (here literally) not droplets but the tracks of electrons, alpha particles, and so on. Those tracks are, if you will, criteria that he interprets as indices of the presence of the corresponding particles, but that route is both shorter and different from the one taken by the man who interprets droplets.
Or consider the scientist inspecting an ammeter
to determine the number against which the needle has settled.
His sensation probably is the same as
the layman’s, particularly if the latter has
14.
For readers of “Second Thoughts” the following
cryptic remarks may be leading. The
possibility of immediate recognition of the members of natural families
depends upon the existence, after neural processing, of empty perceptual space
between the families to be discriminated. If,
for example, there were a perceived continuum of waterfowl ranging from geese
to swans, we should be compelled to introduce a specific criterion for
distinguishing them. A similar point
can be made for unobservable entities. If
a physical theory admits the existence of nothing else like an electric
current, then a small number of criteria, which may vary considerably from
case to case, will sufficce to identify currents even though there is no set
of rules that specifies the necessary and sufficient conditions for the
identification. That point suggests a
plausible corollary which may be more important.
Given a set of necessary and
sufficient conditions for identifying a theoretical entity, that entity can be
eliminated from the ontology of a theory by substitution.
In the absence of such rules, however,
these entities are not eliminable; the theory then demands their existence.
197
read other sorts of meters before.
But he has seen the meter (again often
literally) in the context of the entire circuit, and he knows something about
its internal structure. For him the
needle’s position is a criterion, but only of the value of the current.
To interpret it he need determine only
on which scale the meter is to be read. For
the layman, on the other hand, the needle’s position is not a criterion of
anything except itself. To interpret
it, he must examine the whole layout of wires, internal and external,
experiment with batteries and magnets, and so on.
In the metaphorical no less than in
the literal use of ‘seeing,’ interpretation begins where perception ends.
The two processes are not the same,
and what perception leaves for interpretation to complete depends drastically
on the nature and amount of prior experience and training.
5.
Exemplars, Incommensurability, and
Revolutions
What has just been said provides a basis for clarifying one more aspect of the book: my remarks on incommensurability and its consequences for scientists debating the choice between successive theories
. 15 In Sections X and XII I have argued that the parties to such debates inevitably see differently certain of the experimental or observational situations to which both have recourse. Since the vocabularies in which they discuss such situations consist, however, predominantly of the same terms, they must be attaching some of those terms to nature differently, and their communication is inevitably only partial. As a result, the superiority of one theory to another is something that cannot be proved in the debate. Instead, I have insisted, each party must try, by persuasion, to convert the other. Only philosophers have seriously misconstrued the intent of these parts of my argument. A number of them, however, have reported that I believe the following: 16 the proponents of incommensurable theories
15. The points that follow are dealt with in more
detail in Secs. v and vi of “Reflections.”
16.
See the works cited in note 9, above, and also the essay by Stephen Toulmin in
Growth of Knowledge.
198
cannot communicate with each other at all; as a
result, in a debate over theory-choice there can be no recourse to good
reasons; instead theory must be chosen for reasons that are ultimately
personal and subjective; some sort of mystical apperception is responsible for
the decision actually reached. More
than any other parts of the book, the passages on which these misconstructions
rest have been responsible for charges of irrationality.
Consider first my remarks on proof.
The point I have been trying to make
is a simple one, long familiar in philosophy of science.
Debates over theory-choice cannot be
cast in a form that fully resembles logical or mathematical proof.
In the latter, premises and rules of
inference are stipulated from the start. If
there is disagreement about conclusions, the parties to the ensuing debate can
retrace their steps one by one, checking each against prior stipulation.
At the end of that process one or the
other must concede that he has made a mistake, violated a previously accepted
rule. After that concession he has no
recourse, and his opponent’s proof is then compelling.
Only if the two discover instead that
they differ about the meaning or application of stipulated rules, that their
prior agreement provides no sufficient basis for proof, does the debate
continue in the form it inevitably takes during scientific revolutions.
That debate is about premises, and its
recourse is to persuasion as a prelude to the possibility of proof.
Nothing about that relatively familiar thesis
implies either that there are no good reasons for being persuaded or that
those reasons are not ultimately decisive for the group.
Nor does it even imply that the
reasons for choice are different from those usually listed by philosophers of
science: accuracy, simplicity, fruitfulness, and the like.
What it should suggest, however, is
that such reasons function as values and that they can thus be differently
applied, individually and collectively, by men who concur in honoring them.
If two men disagree, for example,
about the relative fruitfulness of their theories, or if they agree about that
but disagree about the relative importance of fruitfulness and, say, scope in
reaching a choice, neither can be con-
199
victed of a mistake.
Nor is either being unscientific.
There is no neutral algorithm for
theory-choice, no systematic decision procedure which, properly applied, must
lead each individual in the group to the same decision.
In this sense it is the community of specialists rather than its
individual members that makes the effective decision.
To understand why science develops as
it does, one need not unravel the details of biography and personality that
lead each individual to a particular choice, though that topic has vast
fascination. What one must understand,
however, is the manner in which a particular set of shared values interacts
with the particular experiences shared by a community of specialists to ensure
that most members of the group will ultimately find one set of arguments
rather than another decisive.
That process is persuasion, but it presents a
deeper problem. Two men who perceive
the same situation differently but nevertheless employ the same vocabulary in
its discussion must be using words differently.
They speak, that is, from what I have
called incommensurable viewpoints. How
can they even hope to talk together much less to be persuasive.
Even a preliminary answer to that
question demands further specification of the nature of the difficulty.
I suppose that, at least in part, it
takes the following form.
The practice of normal science depends on the
ability, acquired from exemplars, to group objects and situations into
similarity sets which are primitive in the sense that the grouping is done
without an answer to the question, “Similar with respect to what?”
One central aspect of any revolution
is, then, that some of the similarity relations change.
Objects that were grouped in the same
set before are grouped in different ones afterward and vice versa.
Think of the sun, moon, Mars, and
earth before and after Copernicus; of free fall, pendular, and planetary
motion before and after Galileo; or of salts, alloys, and a sulpuhur -iron
filing mix before and after