The Competitiveness of Nations in a Global Knowledge-Based Economy
Thomas S. Kuhn
Historical Structure of Scientific Discovery
Science,
136 (3518
|
Contemt
Some Discoveries Predictable, Some Not
Adjustment, Adaptation, and Assimilation HHC: Index added |
To the historian discovery is seldom a unit
event attributable to some particular man, time,
and place.
Thomas S. Kuhn
My object in this article is to isolate and
illuminate one small part of what I take to be a continuing historiographic
revolution in the study of science
(1]. The structure of
scientific discovery is my particular topic, and I can best approach it by
pointing out that the subject itself may well seem extraordinarily odd.
Both scientists and, until quite
recently, historians have ordinarily viewed discovery as the sort of event
which, though it may have preconditions and surely has consequences, is itself
without internal structure. Rather
than being seen as a complex development extended both in space and time,
discovering something has usually seemed to be a unitary event, one which,
like seeing something happens to an individual at a specifiable time and
place.
This view of the nature of discovery has, I
suspect, deep roots in the nature of the scientific community.
One of the few historical elements
recurrent in the textbooks from which the prospective scientist learns his
field is the attribution of particular natural phenomena to the historical
personages who first discovered them. As
a result of this and other aspects of their training, discovery becomes for
many scientists an important goal. To
make a discovery is to achieve one of the closest approximations to a property
right that the scientific career affords. Professional
prestige is often closely associated with these acquisitions
[2].
Small wonder, then, that
acrimonious disputes about priority and independence in discovery have often
marred the normally placid tenor of scientific communication.
Even less wonder that many historians
of science have seen the individual discovery as an appropriate unit with
which to measure scientific progress and have devoted much time and skill
The author is professor of the history of
science,
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to determining what man made which discovery at
what point in time. If the study of
discovery has a surprise to offer, it is only that, despite the immense energy
and ingenuity expended upon it, neither polemic nor painstaking scholarship
has often succeeded in pinpointing the time and place at which a given
discovery could properly be said to have “been made.”
Some Discoveries Predictable,
Some Not
That failure, both of argument and of research,
suggests the thesis that I now wish to develop.
Many scientific discoveries,
particularly the most interesting and important, are not the sort of event
about which the questions “Where?” and, more particularly, “When?” can
appropriately be asked. Even if all
conceivable data were at hand, those questions would not regularly possess
answers. That we are persistently
driven to ask them nonetheless is symptomatic of a fundamental
inappropriateness in our image of discovery. That
inappropriateness is here my main concern, but I approach it by considering
first the historical problem presented by the attempt to date and to place a
major class of fundamental discoveries.
The troublesome class consists of those
discoveries - including oxygen, the electric current, x-rays, and the electron
- which could not be predicted from accepted theory in advance and which
therefore caught the assembled profession by surprise.
That kind of discovery will shortly be
my exclusive concern, but it will help first to note that there is another
sort and one which presents very few of the same problems.
Into this second class of discoveries
fall the neutrino, radio waves, and the elements which filled empty places in
the periodic table. The existence of
all these objects had been predicted from theory before they were discovered,
and the men who made the discoveries therefore knew from the start what to
look for. That foreknowledge did not
make their task less demanding or less interesting, but it did provide
criteria which told them when their goal had been reached
[3].
As a result, there have been few
priority debates over discoveries of this second sort, and only a paucity of
data can prevent the historian from ascribing them to a particular time and
place. Those facts help to isolate the
difficulties we encounter as we return to the troublesome discoveries of the
first class. In the cases that most
concern us here there are no benchmarks to inform either the scientist or the
historian when the job of discovery has been done.
As an illustration of this fundamental problem
and its consequences, consider first the discovery of oxygen.
Because it has repeatedly been
studied, often with exemplary care and skill, that discovery is unlikely to
offer any purely factual surprises. Therefore
it is particularly well suited to clarify points of principle [4].
At least three scientists - Carl
Scheele, Joseph Priestley, and Antoine Lavoisier - have a legitimate claim to
this discovery, and polemicists have occasionally entered the same claim for
Pierre Bayen [5].
Scheele’s work, though it was almost
certainly completed before the relevant researches of Priestley and Lavoisier,
was not made public until their work was well known [6].
Therefore it had no apparent causal
role, and I shall simplify my story by omitting it [7].
Instead, I pick up the main route to
the discovery of oxygen with the work of Bayen, who, sometime before March
1774, discovered that red precipitate of mercury (HgO) could, by heating, be
made to yield a gas. That aeriform
product Bayen identified as fixed air (C02), a substance made
familiar to most pneumatic chemists by the earlier work of Joseph Black
[8].
A variety of other substances were known to yield the same gas.
At the beginning of August 1774, a few months after Bayen’s work had appeared, Joseph Priestley repeated the experiment, though probably independently. Priestley, however, observed that the gaseous product would support combustion and therefore changed the identification. For him the gas obtained on heating red precipitate was nitrous air (N20), a substance that he had himself discovered more than two years before [9]. Later in the same month Priestley made a trip to
The remainder of this story of discovery is
briefly told. During March 1775
Priestley discovered that his gas was in several respects very much “better”
than common air, and he therefore re-identified the gas once more, this time
calling it “dephlogisticated air,” that is, atmospheric air deprived of its
normal complement of phlogiston. This
conclusion Priestley published in the Philosophical Transactions, and
it was apparently that publication which led Lavoisier to reexamine his own
results [12].
The re-examination began during
February 1776 and within a year had led Lavoisier to the conclusion that the
gas was actually a separable component of the atmospheric air which both he
and Priestley had previously thought of as homogeneous.
With this point reached, with the gas
recognized as an irreducibly distinct species, we may conclude that the
discovery of oxygen bad been completed.
Only, to return to my initial question, when
shall we say that oxygen was discovered and what criteria shall we use in
answering that question? If
discovering oxygen is simply holding an impure sample in one’s hands, then the
gas had been “discovered” in antiquity by the first man who ever bottled
atmospheric air. Undoubtedly, for an
experimental criterion, we must at least require a relatively pure sample like
that obtained by Priestley in August 1774. But
during 1774 Priestley was unaware that he had discovered anything except a new
way to produce a relatively familiar species.
Throughout that year his “discovery” is scarcely distinguishable from
the one made earlier by Bayen, and neither case is quite distinct from that of
the Reverend Stephen Hales who had obtained the same gas more than 40 years
before [13].
Apparently to discover something one
must also be aware of the discovery and know as well what it is that one has
discovered.
But, that being the case, how much must one
know? Had Priestley come close enough
when he identified the gas as nitrous air? If
not, was either
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he or Lavoisier significantly closer when he
changed the identification to common air? And
what are we to say about Priestley’s next identification, the one made in
March 1775? Dephlogisticated air is
still not oxygen or even, for the phlogistic chemist, a quite unexpected sort
of gas. Rather it is a particularly
pure atmospheric air. Presumably,
then, we wait for Lavoisier’s work in 1776 and 1777, work which led him not
merely to isolate the gas but to see what it was.
Yet even that decision can be
questioned, for in 1777 and to the end of his life Lavoisier insisted that
oxygen was an atomic “principle of acidity” and that oxygen gas was
formed only when that “principle” united with caloric, the matter of heat
[14].
Shall we therefore say that
oxygen had not yet been discovered in 1777? Some
may be tempted to do so. But the
principle of acidity was not banished from chemistry until after 1810 and
caloric lingered on until the 1860’s. Oxygen
had, however, become a standard chemical substance long be-fore either of
those dates. Furthermore, what is
perhaps the key point, it would probably have gained that status on the basis
of Priestley’s work alone without benefit of Lavoisier’s still partial
re-interpretation.
I conclude that we need a new vocabulary and new
concepts for analyzing events like the discovery of oxygen.
Though undoubtedly correct, the
sentence “Oxygen was discovered” misleads by suggesting that discovering
something is a single simple act unequivocally attributable, if only we knew
enough, to an individual and an instant in time.
When the discovery is unexpected,
however, the latter attribution is always impossible and the former often is
as well. Ignoring Scheele, we can, for
example, safely say that oxygen had not been discovered before 1774; probably
we would also insist that it had been discovered by 1777 or shortly
thereafter. But within those limits
any attempt to date the discovery or to attribute it to an individual must
inevitably be arbitrary. Furthermore,
it must be arbitrary just because discovering a new sort of phenomenon is
necessarily a complex process which involves recognizing both that
something is and what it is. Observation
and conceptualization, fact and the assimilation of fact to theory, are
inseparably linked in the discovery of scientific novelty.
Inevitably, that process extends over
time and may often involve a number of people.
Only for discoveries in my second category – those whose nature is
known in advance - can discovering that and discovering what
occur together and in an instant.
Two last, simpler, and far briefer examples will simultaneously show how typical the case of oxygen is and also prepare the way for a somewhat more precise conclusion. On the night of
Or consider still more briefly the story of the discovery of x-rays, a story which opens on the day in 1895 when the physicist Roentgen interrupted a well-precedented investigation of cathode rays because he noticed that a barium platinocyanide screen far from his shielded apparatus glowed when the discharge was in process [16]. Additional investigations - they required seven hectic weeks during which Roentgen rarely left the laboratory - indicated that the cause of the glow traveled in straight lines from the cathode ray tube, that the radiation cast shadows, that it could not be deflected by a magnet, and much else besides. Before announcing his discovery Roentgen had convinced himself that his effect was not due to cathode rays themselves but to a new form of radiation with at least some similarity to light. Once again the question suggests itself: When shall we say that x-rays were actually discovered? Not, in any case, at the first instant, when all that had been noted was a glowing screen. At least one other investigator had seen that glow and, to his subsequent chagrin, discovered nothing at all. Nor, it is almost as clear, can the moment of discovery be pushed back to a point during the last week of investigation. By that time Roentgen was exploring the properties of the new radiation he had already discovered. We may have to settle for the remark that x-rays emerged in Wiirzburg between 8 November and
The characteristics shared by these examples
are, I think, common to all the episodes by which unanticipated novelties
become subjects for scientific attention.
I therefore conclude these brief remarks by discussing three such
common characteristics, ones which may help to provide a framework for the
further study of the extended episodes we customarily call “discoveries.”
In the first place, notice that all three of our discoveries - oxygen, Uranus, and x-rays - began with the experimental or observational isolation of an anomaly, that is, with nature’s failure to conform entirely to expectation. Notice, further, that the process by which that anomaly was educed displays simultaneously the apparently incompatible characteristics of the inevitable and the accidental. In the case of x-rays, the anomalous glow which provided Roentgen’s first clue was clearly the result of an accidental disposition of his apparatus. But by 1895 cathode rays were a normal subject for research all over
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of a prolonged survey of the northern heavens.
That survey was, except for the
magnification provided by Herschel’s instruments, precisely of the sort that
had repeatedly been carried through before and that had occasionally resulted
in prior observations of Uranus. And
Priestley, too - when he isolated the gas that behaved almost but not quite
like nitrous air and then almost but not quite like common air - was seeing
something unintended and wrong in the outcome of a sort of experiment for
which there was much European precedent and which had more than once before
led to the production of the new gas.
These features suggest the existence of two
normal requisites for the beginning of an episode of discovery.
The first, which throughout this paper
I have largely taken for granted, is the individual skill, wit, or genius to
recognize that something has gone wrong in ways that may prove consequential.
Not any and every scientist would have
noted that no unrecorded star should be so large, that the screen ought not
have glowed, that nitrous air should not have supported life.
But that requisite presupposes another
which is less frequently taken for granted. Whatever
the level of genius available to observe them, anomalies do not emerge from
the normal course of scientific research until both instruments and concepts
have developed sufficiently to make their emergence likely and to make the
anomaly which results recognizable as a violation of expectation
[17].
To say that an
unexpected discovery begins only when something goes wrong is to say that it
begins only when scientists know well both how their instruments and how
nature should behave. What
distinguished Priestley, who saw an anomaly, from Hales, who did not, is
largely the considerable articulation of pneumatic techniques and expectations
that had come into being during the four decades which separate their ‘two
isolations of oxygen [18].
The very number of
claimants indicates that after 1770 the discovery could not have been
postponed for long.
The role of anomaly is the first of the
characteristics shared by our three examples.
A second can be considered more briefly, for it has provided the main
theme for the body of my text. Though
awareness of anomaly marks the beginning of a discovery, it marks only the
beginning. What necessarily follows,
if anything at all is to be discovered, is a more or less extended period
during which the individual and often many members of his group struggle to
make the anomaly lawlike. Invariably
that period demands additional observation or experimentation as well as
repeated cogitation. While it
continues scientists repeatedly revise their expectations, usually their
instrumental standards, and sometimes their most fundamental theories as well.
In this sense discoveries have a
proper internal history as well as prehistory and a posthistory.
Furthermore, within the rather vaguely
delimited interval of internal history, there is no single moment or day which
the historian, however complete his data, can identify as the point at which
the discovery was made. Often, when several individuals are involved, it is
even impossible unequivocally to identify any one of them as the discoverer.
Adjustment, Adaptation, and
Assimilation
Finally, turning to the third of these selected
common characteristics, note briefly what happens as the period of discovery
draws to a close. A full discussion of
that question would require additional evidence and a separate paper, for I
have had little to say about the aftermath of discovery in the body of my
text. Nevertheless, the topic must not
be entirely neglected, for it is in part a corollary of what has already been
said.
Discoveries are often described as mere
additions or increments to the growing stockpile of scientific knowledge, and
that description has helped make the unit-discovery seem a significant measure
of progress. I suggest, however, that
it is fully appropriate only to those discoveries which, like the elements
that filled missing places in the periodic table, were anticipated and sought
in advance and which therefore demanded no adjustment, adaptation, and
assimilation from the profession. Though
the sorts of discoveries we have here been examining are undoubtedly additions
to scientific knowledge, they are also something more.
In a sense that I can now develop only
in part, they also react back upon what has previously been known, providing a
new view of some previously familiar objects and simultaneously changing the
way in which even some traditional parts of science are practiced.
Those in whose area of special
competence the new phenomenon falls often see both the world and their work
differently as they emerge from the extended struggle with anomaly which
constitutes that phenomenon’s discovery.
William Herschel, for example, when he increased by one the time-honored number of planetary bodies, taught astronomers to see new things when they looked at the familiar heavens even with instruments more traditional than his own. That change in the vision of astronomers must be a principal reason why, in the half century after the discovery of Uranus, 20 additional circumsolar bodies were added to the traditional seven [19]. A similar transformation is even clearer in the aftermath of Roentgen’s work. In the first place, established techniques for cathode ray research had to be changed, for scientists found they had failed to control a relevant variable. Those changes included both the redesign of old apparatus and revised ways of asking old questions. In addition, those scientists most concerned experienced the same transformation of vision that we have just noted in the aftermath of the discovery of Uranus. X-rays were the first new sort of radiation discovered since infrared and ultraviolet at the beginning of the century. But within less than a decade after Roentgen’s work, four more were disclosed by the new scientific sensitivity (for example, to fogged photographic plates) and by some of the new instrumental techniques that had resulted from Roentgen’s work and its assimilation
[20].
Very often these transformations in the
established techniques of scientific practice prove even more important than
the incremental knowledge provided by the discovery itself.
That could at least be argued in the
cases of Uranus and of x-rays; in the case of my third example, oxygen, it is
categorically clear. Like the work of
Herschel and Roentgen, that of Priestley and Lavoisier taught scientists to
view old situations in new ways. Therefore,
as we might anticipate, oxygen was not the only new chemical species to be
identified in the aftermath of their work. But,
in the case of oxygen, the readjustments demanded by assimilation were so
profound that they played an integral and essential role - though they were
not by themselves the cause - in the gigantic upheaval of chemical theory and
practice which has since
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been known as the “chemical revolution.”
I do not suggest that
every unanticipated discovery has consequences for science so deep and so
far-reaching as those which followed the discovery of oxygen.
But I do suggest that every such
discovery demands, from those most concerned, the sorts of readjustment that,
when they are more obvious, we equate with scientific revolution.
It is, I believe, just because they
demand readjustments like these that the process of discovery is necessarily
and inevitably one that shows structure and that therefore extends in time.
1. The larger revolution will be discussed in my forthcoming book, The Structure of Scientific Revolutions, to be published in the fall by the
2. For a brilliant discussion of these points
see, R. K. Merton, “Priorities in scientific discovery: a chapter in the
sociology of science,” Am. Sociol. Rev. 22, 635
(1957).
Also very relevant, though it
did not appear until this article had been prepared, is F. Reif, “The
competitive world of the pure scientist,”
Science
134, 1957 (1961).
3. Not all discoveries fall so neatly as the preceding into one or the other of my two classes. For example,
4. I have developed a less familiar example from
the same viewpoint in “The caloric theory of adiabatic compression,” Isis
49, 132 (1958).
A closely similar analysis
of the emergence of a new theory is included in the early pages of my essay
“Conservation of energy as an example of simultaneous discovery,” in
Critical Problems in the History of
Science, M. Clagett, Ed. (Univ. of Wisconsin Press, Madison,
1959), pp. 321-356. Reference to these
papers may add depth and detail to the following discussion.
5.
The still classic discussion of the discovery of oxygen is A. N. Meldrum, The Eighteenth Century Revolution in Science - The First Phase (Calcutta, 1930), chap. 5. A more convenient and generally quite reliable discussion is included in J. B. Conant, The Overthrow of the Phlogiston Theory: The Chemical Revolution of 1775-1789, “Harvard Case Histories in Experimental Science, Case 2” (Harvard Univ. Press, Cambridge, 1950). A more recent and indispensable review, which includes an account of the development of the priority controversy, is M. Daumas, Lavoisier, théoricien et expérimentaleur (6. For the dating of Scheele’s work, see A. E. Nordenskidld, Carl Wilhelm Scheele, Nachgelassene Briefe und Aufzeichnungen (
7. U. Bocklund [“A lost letter from Scheele to Lavoisier,” Lychnos (1957-58), pp. 39-621 argues that Scheele communicated his discovery of oxygen to Lavoisier in a letter of
8. P. Bayen, “Essai d’expériences chymiques,
faites sur quelques précipités de mercure, dans la vue de découvrir leur
nature, Seconde partie,” Observations sur la physique (1774), vol. 3,
pp. 280-295, particularly pp. 289-291.
9. J. B. Conant (see
5, pp. 34-40).
10. A useful translation of the full text is
available in Conant (see 5).
For this description of the
gas see p. 23.
11. For simplicity I use the term red precipitate throughout. Actually, Bayen used the precipitate; Priestley used both the precipitate and the oxide produced by direct calcination of mercury; and Lavoisier used only the latter. The difference is not without importance, for it was not unequivocally clear to chemists that the two substances were identical.
12. There has been some doubt about Priestley’s
having influenced Lavoisier’s thinking at this point, but, when the latter
returned to experimenting with the gas in February 1776, he recorded in his
notebooks that he had obtained “l’air dephlogistique de M. Priestley” [M.
Daumas (see 5, p. 36)].
13. J. R. Partington (see
5, p. 91).
14. For the traditional elements in Lavoisier’s interpretations of chemical reactions, see H. Metzger, La philosophic de la matière chez Lavoisier (
15. P. Doig, A. Concise History of Astronomy
(Chapman, London, 1950), pp. 115-116.
16. L. W.
17. Though the point cannot be argued here, the
conditions which make the emergence of anomaly likely and those which make
anomaly recognizable are to a very great extent the same.
That fact may help us understand the
extraordinarily large amount of simultaneous discovery in the sciences.
18. A useful sketch of the development of
pneumatic chemistry is included in Partington (see
5, chap. 6).
19. R. Wolf, Geschichte der Astronomic (Munich, 1877), pp. 513-515, 683-693.
The prephotographic discoveries of the asteroids is often seen as an effect of the invention of Bode’s law. But that law cannot be the full explanation and may not even have played a large part. Piazzi’s discovery of Ceres, in 1801, was made in ignorance of the current speculation about a missing planet in the “hole” between Mars and Jupiter. Instead, like Herschel, Piazzi was engaged on a star survey. More important, Bode’s law was old by 1800 (R. Wolf, ibid., p. 683), but only one man before that date seems to have thought it worth while to look for another planet. Finally, Bode’s law, by itself, could only suggest the utility of looking for additional planets; it did not tell astronomers where to look. Clearly, however, the drive to look for additional planets dates from Herschel’s work on Uranus.20. For α-, β and γ-radiation, discovery of which dates from 1896, see
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