The Competitiveness of Nations in a Global Knowledge-Based Economy
Robert
K. Merton
The
Matthew Effect in Science, II: Cumulative Advantage and the Symbolism of
Intellectual Property
Isis, 79 (4)
Dec. 1988, 606-623.
Content
The Accumulation of Advantage and Disadvantage for
Scientists
Accumulation of Advantage and Disadvantage among the
Young
Accumulation of Advantage and Disadvantage Among Scientific Institutions
The Symbolism of Intellectual Property in Science
THE SUBJECT OF THIS ESSAY
is a problem in the sociology of science that has long been of interest to me. That problem, a candid friend tells me, is
somewhat obscured by the formidable title assigned to it. Yet, properly deciphered, the title is not
nearly as opaque as it might at first seem.
Consider first the signal
emitted by the Roman numeral II in the main title. It informs us that the paper follows on an
earlier one, “The Matthew Effect in Science,” which I finally put into print a
good many years ago. [1] The ponderous, not to say lumpy, subtitle goes on to
signal the direction of this follow-on. The
first concept, cumulative advantage, applied to the domain of science, refers
to the social processes through which various kinds of opportunities for
scientific inquiry as well as the subsequent symbolic and material rewards for
the results of that inquiry tend to accumulate for individual practitioners of
science, as they do also for organizations engaged in scientific work. The concept of cumulative advantage directs
our attention to the ways in which initial comparative advantages of trained
capacity, structural location, and available resources make for successive
increments of advantage such that the gaps between the haves and the have-nots
in science (as in other domains of social life) widen until dampened by
countervailing processes.
The second phrase in the
subtitle directs us to the distinctive character of intellectual property in
science. I propose the seeming paradox
that in science, private property is established by having its substance freely
given to others who might want to make use of it. I shall argue further that certain
institutionalized aspects of this property system, chiefly in the form of
public acknowledgment of the source of knowledge and information thus freely
bestowed on fellow scientists, relate to the social and cognitive structures of
science in interesting ways that affect the collective advancement of
scientific knowledge.
That is a long agenda for a
short disquisition. Since that agenda
can only be
* Fayerweather 415, Columbia
University, New York, New York 10027.
This article contains the main part of the inaugural
lecture of the George Sarton Leerstoel,
28 November 1986, University of Ghent. [See p. 669 - Eds,]
By request it includes detailed
bibliographical references to this strand of my work since I served as an
apprentice to George Sarton. The full lecture, with its prefatory pages
devoted to Sarton, is to appear in translation in the
Ghent review Tjjdschrift voor Sociale Wetenschappen.
Earlier versions were presented at
the New York Hospital - Cornell Medical Center, Yale University, Bell
Laboratories, the College of Physicians and Surgeons of Columbia University,
Smith College, Washington University, and the Fox Chase Cancer Center.
1.
Robert K. Merton, “The Matthew Effect in Science,” Science, 5 January
1968, 159 (3810):56-63; rpt. in Merton, The
Sociology of Science, ed. Norman W. Storer
(Chicago: Univ. Chicago Press, 1973), Ch. 20.
606
discharged by dealing with these matters in the large, I shall
not attempt to summarize the detailed findings that derive from a now widely
dispersed program of research on cumulative advantage and disadvantage in the
social stratification of science.
An obscure title can also
have a latent function: to keep one from assuming that the title truly speaks
for itself, and thus to make it necessary to elucidate one’s intent. As for the main title: what, you may well ask,
does “The Matthew Effect in Science” refer to? A mercifully short reprise of the work
introducing this notion will get us into its further elucidation.
We begin by noting a theme
that runs through Harriet Zuckerman’s hours-long interviews with Nobel
laureates in the early 1960s. It is
repeatedly suggested in these interviews that eminent scientists get
disproportionately great credit for their contributions to science while
relatively unknown ones tend to get disproportionately little for their
occasionally comparable contributions. As a laureate in physics put it: “The world is peculiar in this
matter of how it gives credit. It
tends to give the credit to already famous people.” [2] Nor are the laureates alone in stating that the more
prominent scientists tend to get the lion’s share of recognition; less notable
scientists in a cross-sectional sample studied by Warren O. Hagstrom
have reported similar experiences. [3] But it is the eminent scientists, not least those who
have received the ultimate contemporary accolade, the Nobel Prize, who provide
presumptive evidence of this pattern. For
they testify to its occurrence, not as aggrieved victims, which might make
their testimony suspect, but as “beneficiaries,” albeit sometimes embarrassed
and unintentional ones.
The claim that prime
recognition for scientific work, by informed peers and not merely by the
inevitably uninformed lay public, is skewed in favor of established scientists
requires, of course, that the nature and quality of these diversely appraised
contributions be identical or at least much the same. That condition is approximated in cases of
full collaboration and in cases of independent multiple discoveries. The distinctive contributions of collaborators
are often difficult to disentangle; independent multiple discoveries, if not
identical, are at least enough alike to be defined as functional equivalents by
the principals involved or by their informed peers.
In papers jointly published
by scientists of markedly unequal rank and reputation, another laureate in
physics reports, “the man who’s best known gets more credit, an inordinate
amount of credit.” Or as a laureate in
chemistry put it, “If my name was on a paper, people would remember it and
not remember who else
2.
Harriet Zuckerman, “Nobel Laureates: Sociological Studies of Scientific
Collaboration” (Ph.D. diss., Columbia Univ., 1965). The later fruits of Zuckerman’s research
appear in Zuckerman, Scientific Elite: Nobel Laureates in the United States (New
York: Free Press, 1977); an account of the procedures adopted in these
tape-recorded interviews appears in Zuckerman, “Interviewing an Ultra-Elite,” Public
Opinion Quarterly, 1972, 36:159-175. This is occasion for repeating what I have
noted in reprinting the original “Matthew Effect in Science”: “It is now [1973]
belatedly evident to me that I drew upon the interview and other materials of
the Zuckerman study to such an extent that, clearly, the paper should have
appeared under joint authorship.” A
sufficient sense of distributive and commutative justice requires one to
recognize, however belatedly, that to write a scientific or scholarly paper is
not necessarily sufficient grounds for designating oneself as its sole author.
3.
Warren O. Hagstrom, The
Scientjfic Community (New York: Basic Books,
1965), pp. 24-25.
607
was involved.” [4] The
biological scientists R. C. Lewontin and J. L. Hubby
have lately reported a similar pattern of experience with a pair of their
collaborative papers, which have been cited often enough to qualify as
“citation classics” (as designated by the Institute for Scientific
Information). One paper was cited some
310 times; the other, some 525 times. The
first paper described a method; the second
gave the detailed result of the application of the method
to natural populations. The two papers
were a genuinely collaborative effort in conception, execution, and writing and
clearly form an indivisible pair,... published
back-to-back in the same issue of the journal. The order of authors was alternated, with the
biochemist, Hubby, being the senior author in the method paper and the
population geneticist, Lewontin, as senior author in
the application paper. Yet paper II has
been cited over 50 percent more frequently than paper I. Citations to paper I
virtually never stand alone but are nearly always paired with a citation to II,
but the reverse is not true. Why? We seem to have a clearcut
case of Merton’s “Matthew Effect” - that the already
better known investigator in a field gets the credit for joint work, irrespective
of the order of authors on the paper, and so gets even better known by an
autocatalytic process. In 1966 Lewontin had been a professional for a dozen years and was
well known among population geneticists, to whom the paper was addressed, while
Hubby’s career had been much shorter and was known chiefly to biochemical
geneticists. As a result, population
geneticists have consistently regarded Lewontin as
the senior member of the team and given him undue credit for what was a
completely collaborative work that would have been impossible for either one of
us alone. [5]
At the extreme, such
misallocation of credit can occur even when a published paper bears only the
name of a hitherto unknown and uncredentialed
scientist. Consider this observation by
the invincible geneticist and biochemist, J. B. S. Haldane
(whose not having received a Nobel Prize can be cited as prime evidence
of the fallibility of the judges sitting in Stockholm). Speaking with Ronald Clark of S. K. Roy, his
talented Indian student who had conducted important experiments designed to
improve strains of rice, Haldane observed that
Roy himseff deserved about
95 per cent of the credit… The other 5 per cent may be divided
between the Indian Statistical Institute and myself,”
he added. “I deserve credit for letting
him try what I thought was a rather ill-planned experiment, on the general
principle that I am not omniscient.” But
[Haldane] had little hope that credit would be given
that way. “Every effort will be made
here to crab his work,” he wrote. “He has not got a Ph.D. or even a first-class
M.Sc. So
either the research is no good, or I did it.” [6]
It is such patterns of the
misallocation of recognition for scientific work that I described as “the
Matthew effect.” The not quite
foreordained term derives, of course, from the first book of the New Testament,
the Gospel according to Matthew (13:12 and 25:29). In the stately prose of the King James
Version, created by what must be one of the most scrupulous and consequential
teams of scholars in Western history, the well-remembered passage reads: “For
unto ev-
4.
Zuckerman, Scientific Elite (cit. n. 2), pp. 140, 228.
5.
R. C. Lewontin
and J. L. Hubby, “Citation Classic,” Current Contents/Life Sciences, 28
Oct. 1985, No. 43, p. 16.
6.
Ronald W. Clark, J.B.S.: The Life and Work of J. B. S. Haldane
(New York: Coward-McCann, 1969), p. 247.
608
eryone that hath shall be given, and he shall have
abundance; but from him that hath not shall be taken away even that which he
hath.” [7]
Put in less stately
language, the Matthew effect is the accruing of large increments of peer
recognition to scientists of great repute for particular contributions in
contrast to the minimizing or withholding of such recognition for scientists
who have not yet made their mark. The
biblical parable generates a corresponding sociological parable. For this is the form, it seems, that the
distribution of psychic income and cognitive wealth in science also takes. How this comes to be and with what
consequences for the fate of individual scientists and the advancement of
scientific knowledge are the questions in hand.
The Accumulation of Advantage and
Disadvantage for Scientists
Taken out of its spiritual
context and placed in a wholly secular context, the Matthew doctrine would seem
to hold that the posited process must result in a
7.
The term and concept “Matthew effect” has diffused widely since its coinage a
quarter century ago. Geographically, it
has become common usage in the West and, my colleague Andrew Walder informs me, has traveled to mainland China where it
is known as “mati xiaoying.”
Substantively, it has diffused into
diverse domains other than the sociology and history of science. As examples, it has been adopted in welfare
economics and social policy (e.g., by Herman Deleeck,
Het Matteuseffect:
De ongelijke verdeling van
de sociale overheidsuitgaven
in België [Antwerp: Kluwer,
1983]); in education (Herbert J. Walberg and Shiow-Ling
Tsai, “Matthew Effects in Education,” American Educational Research Journal,
1983, 20:359-373); in administrative studies (James G. Hunt
and John D. Blair, “Content, Process, and the Matthew Effect among Management
Academics,” Journal of Management, 1987, 13: 191-210); and, to go
no further, in social gerontology (Dale Dannefer,
“Aging as Intracohort Differentiation: Accentuation,
the Matthew Effect and the Life Course,” Sociological Forum, 1987, 2:211-236.)
Despite that wide diffusion, it is also the case that
the term “Matthew effect,” though not the concept, has been questioned from the
start on several grounds. In 1968, soon
after its first appearance in print, my colleague and later collaborator, David
L. Sills, based his reservations about the term upon “(1) the issue of the
priority of the words in Matthew 25:29 (Mark 4:25 said them first [to say
nothing of Luke 8:18 and 19:26 probably being indebted to them both]); (2) the
authorship issue (it is almost certain that Matthew did not write the Gospel
According to Matthew); (3) the attribution issue (the words are Christ’s, not
those of the author-compiler of the gospel); and (4) the interpretation issue
(it is quite unlikely that the point of the parable is ‘the more, the more’)”:
Sills to Merton, 29 Mar. 1968.
These objections have been variously reiterated over
the years. Thus the astronomer Charles D. Geilker (Science,
1968, 159:1185) maintains that since the three evangelists were all
quoting Jesus, I might just as well have called it “the Jesus effect.” But then, this would have precluded my having
neutralized or reduced the Matthew effect of the term by the very act of
calling it “the Matthew effect.” Most
recently, I am indebted to M. de Jonge, professor of
theology at the University of Leyden, who has made
some of the same observations as Sills. He
notes further that “it is highly likely that [Jesus] took over a general
saying, current in Jewish (and/or Hellenistic) Wisdom circles - see, e.g.,
Proverbs 9:9, Daniel 2:21, or Martialis, Epigr. V 81: ‘Semper pauper ens, si
pauper es, Aemiliane. Dantur opes nullis
[nunc] nisi divitibus.’ “And de Jonge
concludes: “The use made of this sentence [in Matthew] by modern authors
neglects the eschatological thrust inherent in the saying in all versions, and
(in all probability) in Jesus’s own version of it. It links up, however, with the Wisdom-saying
taken over by Jesus: ‘Look around you and see what
happens: If you have something, you get more; if you have not a penny, they
will take from you the little you have.’” M. de Jonge, summary
of lecture, “The Matthew Effect,” 24 July 1987.
It is not for me to adjudicate these matters. The priority question of Matthew, Mark, Luke,
Q, or still earlier proverbial wisdom had best be left to historians
specialized in the matter. In coining
the term, I was plainly transferring the pertinent sentence from its
theological context into a secular one. Having studied the various interpretations of
the five similar passages in the synoptic gospels - principally as summarized
and advanced by Ronald Knox, A Commentary on the Gospels (New York: Sheed & Ward, 1952) - I decided to give public
expression to my preference for Matthew. It was a comfort to learn recently that
Wittgenstein had chosen Matthew as his favorite gospel: M. O’C. Drury,
“Conversations with W,” in Ludwig Wittgenstein: Personal Recollection, ed.
Rush Rhees (Oxford: Blackwell, 1981), p. 177.
609
boundlessly growing inequality of wealth, however wealth is
construed in any sphere of human activity. Conceived of as a locally
ongoing process and not as a single event, the practice of giving unto everyone
that hath much while taking from everyone that hath little will lead to the
rich getting forever richer while the poor become poorer. Increasingly absolute and not only relative
deprivation would be the continuing order of the day. But as we know, things are not as simple as
all that. After all, the extrapolation
of local exponentials is notoriously misleading. In noting this, I do not intend nor am I
competent to assess the current economic theory of the distribution of wealth
and income. Instead, I shall report what
a focus upon the skewed distribution of peer recognition and research
productivity in science has led some of us to identify as the processes and
consequences of the accumulation of advantage and disadvantage in science.
(Unkind readers will no
doubt describe this part of my report as rambling; critical ones, as
convoluted; and kindly, understanding ones, as complex. Myself, I should describe it as the slow,
laborious emergence of an intellectual tradition of work in the evolving
sociology of science.)
I first stumbled upon the
general question of social stratification in science in the early 1940s. One paper of that period alludes to “the
accumulation of differential advantages for certain segments of the population,
differentials that are not [necessarilyj bound up
with demonstrated differences in capacity.” [8] It would not be correct or, indeed, just to say that
that text is no clearer to me now than the notoriously obscure Sordello was clear to Robert Browning, when
he confessed: “When I wrote that, God and I knew what it meant, but now God
alone knows.” [9] However, I can report that the notion of the accumulation of
advantage just rested there as only a proto-concept - inert, unnoticed, and unexplicated - until it was taken up, almost a quarter
century later, in my first paper on the Matthew effect. Until then, the notion of cumulative advantage
in science had led only a ghostly existence in private musings, sporadically
conjured up for oral publication rather than put in print. [10]
Further investigation of
the process of cumulative advantage took hold in the latter 1960s with the
formation of a research quartet at Columbia consisting of Harriet Zuckerman,
Stephen Cole, Jonathan R. Cole, and myself. There has since emerged an “invisible college”
- to adopt the brilliant terminological recoinage by
Derek Price - which has grown apace in contributing to a program of research on
cumulative advantage and disadvantage, in social stratification generally and
in science specifically. Notably
including Price himself until his recent lamented death, that college also
numbers Paul D. Allison, Bernard Barber, Ste-
8.
Robert K. Merton, “The Normative Structure of Science” (1942), rpt. in Merton, Sociology
of Science (cit. n. 1), p. 273.
9.
There are other versions of that confession.
Edmund Gosse reports that he “saw him
[Browning] take up a copy of the first edition, and say, with a grimace, ‘Ah! the entirely unintelligible “Sondello”’”:
Gosse, “Robert Browning,” Dictionary of National
Biography, First Supplement (London: Smith, Elder, 1901), Vol. I, pp. 306-319,
on p. 308. The remark has also been
attributed to the eighteenth-century poet Friednich Klopstock and to Hegel. Once again, it is not for me to adjudicate priority
claims.
10.
The central idea was presented briefly in the National Institutes of Health
Lecture in February 1964 and later that year in expanded form at the annual
meeting of the American Association for the Advancement of Science. It then underwent several more editions in a
succession of public lectures, notably one at the University of Leyden in 1965, before it found its way into print in Science
(see n. 1).
610
phen J. Bensman, Judith Blau, Walter Broughton, Daryl E. Chubin,
Dale Dannefer, Simon Duncan, Mary Frank Fox, Eugene
Garfield, Jerry Gaston, Jack A. Goldstone, Warren O. Hagstrom,
Lowell L. Hargens, Karin D. Knorr,
Tad Krauze, J. Scott Long, Robert McGinnis, Volker Meja, Roland Mettermeir, Edgar W.
Mills, Jr., Nicholas C. Mullins, Barbara Reskin,
Leonard Rubin, Dean K. Simonton, Nico Stehr, John A. Stewart, Norman W. Storer,
Stephen P. Turner, and Herbert J. Walberg, among others.”
This, surely, is not the
occasion for providing a synopsis of that now considerable body of research
materials. Rather, I shall only remind
you of a few of the marked inequalities and strongly skewed distributions of
productivity and resources in science, and then focus on the consequences of
the bias in favor of precocity that is built into our institutions for
detecting and rewarding talent, an institutionalized bias that may help bring
about severe inequalities during the life course of scholars and scientists.
First,
then, a quick sampling of the abundance of conspicuously skewed distributions
and inequalities identifiable at a given time.
• The total number of scientific papers published by
scientists differs enormously, ranging from the large proportion of Ph.D.s who
publish one paper or none at all to the rare likes of William Thomson, Lord
Kelvin, with his six hundred plus papers, or the mathematician Arthur Cayley, publishing a paper every few weeks throughout his
work life for a total of almost a thousand. [12]
• The skewed distribution in the sheer number of
published papers is best approximated by variants of Alfred J. Lotka’s “inverse square law” of scientific productivity,
which states that the number of scientists with n publications is
proportional to n2. In
a variety of disciplines, this works out to some 5 or 6 percent of the
scientists who publish at all producing about half of all papers in
their discipline. [13]
• The distributions are even more skewed in the use of
scientists’ work by their peers, as that use is crudely indexed by the number
of citations to it. Much the same
distribution has been found in various data sets: typical is Garfield’s finding
that, for an aggregate of some nineteen million articles published in the
physical and biological sciences between 1961 and 1980,
11.
Price had extended Robert Boyle’s seventeenth-century term “invisible college”
to designate the informal collectives of scientists interacting in their
research on similar problems, these groups being generally limited to a size
“that can be handled by interpersonal relationships”: Derek J. de Solla Price, Little Science, Big Science... and
Beyond (New York: Columbia Univ. Press, 1986; 1st ed., 1963), pp. 76-81, passim.
For a key paper on cumulative
advantage see Price, “A General Theory of Bibliometric
and Other Cumulative Advantage Processes,” Journal of the American Society
for Information Science, 1976, 27:292-306. For detailed analysis and history of the idea
and a substantial bibliography see Harriet Zuckerman, “Accumulation of
Advantage and Disadvantage: The Theory and Its Intellectual Biography,” paper
presented to the Amalfi Conference of the Associazione Italiana di Sociologia, 1987; forthcoming
in L’opera di
Robert K. Merton e la sociologia contemporanea,
ed. Carlo Mongardini (Rome).
12.
Silvanus P. Thompson, The Life of William
Thomson, Baron Kelvin of Largs, 2 vols. (London: Macmillan,
1910), Vol. II, pp. 1225-1274; J. D. North, “Arthur Cayley,”
Dictionary of Scientific Biography, ed. Charles C. Gillispie
(New York: Scribners, 1970-1980), Vol. III, p. 163.
13.
Alfred J. Lotka, “The Frequency Distribution of
Scientific Productivity,” Journal of the Washington Academy of Sciences, 1926,
16:317-323; and Price, Little Science, Big Science... and Beyond (cit.
n. 11), pp. 38-42.
611
0.3 percent were cited more than one hundred times;
another 2.7 percent between twenty-five and one hundred times; and, at the
other extreme, some 58 percent of those that were cited at all were cited only once
in that twenty-year period. [14] This inequality, you will recognize, is steeper than
Pareto-like distributions of income.
When it comes to changes
in the extent of inequalities of research productivity and recognition
during the course of an individual’s work life as a scientist, the needed
longitudinal data are much more scarce. Again, a few suggestive findings must serve.
• In their simulation of longitudinal data (through disaggregation of a cross section of some two thousand
American biologists, mathematicians, chemists, and physicists into several
strata by career age), Paul D. Allison and John A. Stewart found “a clear and
substantial rise in inequality for both [the number of research publications in
the preceding five years and the number of citations to previously published
work] from the younger to the older strata, strongly supporting the
accumulative advantage hypothesis.” [15]
• Allison and Stewart also confirmed the
Zuckerman-Merton hypothesis that decreasing research productivity with
increasing age results largely from differing rates of attrition in research
roles and that this approximates an all-or-none phenomenon. The hypothesis held that “the more productive
scientists, recognized as such by the reward-system of science, tend to persist
in their research roles,” while those with declining research productivity tend
to shift to other indispensable roles in science, not excluding the
conventionally maligned role of research administrator. [16]
• Derek Price pointedly reformulated and developed
that hypothesis, “because there is a very large but decreasing chance that any
given researcher will discontinue publication, the group of workers that
reaches the [research] front during a particular year will decline steadily in
total output as time goes on. Gradually,
one after another, they will drop away from the research front. Thus the yearly output of the group as a whole
will decline, [and now comes the essential point Zuckerman and I tried to
emphasize] even though any given individual within it may produce at a steady
rate throughout his [or her] entire professional lifetime. We need, therefore, to
14.
Eugene Garfield, The Awards of Science and
Other Essays (Philadelphia: ISI Press, 1985), p. 176.
15.
Paul D. Allison and John A. Stewart, “Productivity Differences among
Scientists: Evidence for Accumulative Advantage,” American Sociological
Review, 1974, 39:596-606. But
see Michael A. Faia,
“Productivity among Scientists: A Replication and Elaboration,” Amer. Sociol. Rev., 1975, 40:825-829, and the following
Allison-Stewart “Reply,” pp. 829-831; also Roland Mettermeir
and Karin D. Knorr, “Scientific Productivity and
Accumulative Advantage: A Thesis Reassessed in the Light of International
Data,” R & D Management, 1979, 9:235-239. A later study by Paul D. Allison, J. Scott
Long, and Tad Krauze, based on actual rather than
simulated age-cohort data for chemists and biochemists, finds increasing
inequalities in research publication as a cohort ages but, as yet inexplicably,
finds no such increases in rates of citation: “Cumulative Advantage and
Inequality in Science,” Amer. Sociol. Rev., 1982,
47:615-625.
16.
Allison and Stewart, “Productivity Differences” (cit. n. 15); Harriet Zuckerman
and Robert K. Merton, “Age, Aging and Age Structure in Science” (1972), rpt. in
Merton, Sociology of Science (cit. n. 1), pp. 497-559, on pp. 519-537.
612
distinguish this effect [of mortality at the research front] from
any differences in the actual rates of productivity at different ages among those
that remain at the front.” [17]
With regard to the Matthew
effect and associated cumulation of advantage,
• Stephen Cole found, in an ingeniously designed study
of a sample of American physicists, that the greater their authors’ scientific
reputation, the more likely that papers of roughly equal quality (as assessed
by the later number of citations to them) will receive rapid peer recognition
(by citation within a year after publication). Prior repute of authors somewhat advances the
speed of diffusion of their contributions. [18]
• Cole also found that it is a distinct advantage for
physicists of still small reputation to be located in the departments most
highly rated by peers: their new work diffuses more rapidly through the science
networks than comparable work by their counterparts in peripheral university
departments. [19]
Accumulation of Advantage and
Disadvantage among the Young
I now focus on the special
problems in the accumulation of advantage and disadvantage that derive from an
institutionalized bias in favor of precocity. The advantages that come with early
accomplishment taken as a sign of things to come stand in Matthew-like contrast
to the situation confronted by young scientists whose work is judged as
ordinary. [20] Such early prognostic judgments, I suggest, lead in some
unknown fraction of cases to inadvertent suppression of talent through the
process of the self-fulfilling prophecy. Moreover, this is more likely to be the case
in a society, such as American society, where educational institutions are so
organized as to put a premium on relatively early manifestations of
ability - in a word, on precocity. Since
it was that wise medical scientist Alan Gregg who led me to become aware of
this bias institutionalized in our educational system, and since I cannot
improve on his formulation, I transmit it here in the thought that you too may
find it revealing.
By being generous with time, yes, lavish with it,
Nature allows man an extraordinary chance to learn. What gain can there be, then, in throwing away
this natural advantage by rewarding precocity, as we certainly do when we gear
the grades in school to chronological age by starting the first grade at the
age of six and college entrance for the vast majority at seventeen and a half
to nineteen? For, once you have most
of your students the same age, the academic rewards - from scholarships to
internships and residencies - go to those who are uncommonly bright for
their age. In other
17. Derek de Solla Price,
“The Productivity of Research Scientists,” 1975 Yearbook of Science and the
Future (Chicago: Encyclopedia Britannica, 1975), pp. 409-421, on p. 414. Stephen Cole’s
studies of age cohorts in various sciences confirm this pattern of a steady
rate of publication by a significant fraction of scientists; see Cole, “Age and
Scientific Performance,” Amer. J. Sociol., 1979,
84:958-977.
18.
Stephen Cole, “Professional Standing and the Reception of Scientific
Discoveries,” Amer. J. Sociol., 1970, 76:286-306,
on pp. 291-292.
19.
Ibid., p. 292.
20.
Jonathan R. Cole and Stephen Cole, Social Stratification in Science (Chicago:
Univ. Chicago Press, 1973), pp. 112-122,passim.
613
words, you have rewarded precocity, which may or may not be
the precursor of later ability. So, in
effect, you have unwittingly belittled man’s cardinal educational capital -
time to mature. [21]
The social fact noted by
Gregg is of no small consequence for the collective advancement of knowledge as
well as for distributive justice. As he
goes on to argue, “precocity thus may succeed in the
immediate competitive struggle, but, in the long run, at the expense of mutants
having a slower rate of development but greater potentialities.” [22] By
suggesting that there are such slow-starting mutants who have greater potentialities
than some of the precocious, Gregg is plainly assuming part of what he then
concludes. But, as I noted almost thirty
years ago, Gregg’s
argument cuts deeply, nevertheless. For we know only of the “late bloomers” who
have eventually come to bloom at all; we don’t know the potential late bloomers
who, cut off from support and response in their youth, never manage to come
into their own at all. Judged ordinary
by comparison with their precocious “age-peers,” they are treated as youth of
small capacity. They slip through the
net of our institutional sieves for the location of ability, since this is a
net that makes chronological age the basis for assessing relative ability. Treated by the institutional system as
mediocrities with little promise of improvement, many of these potential late
bloomers presumably come to believe it of themselves
and act accordingly. At least what
little we know of the formation of self-images suggests that this is so. For most of us most of the time, and not only
the so-called “other-directed men” among us, tend to form our self-image - our
image of potentiality and of achievement - as a reflection of the images others
make plain they have of us. And it is
the images that institutional authorities have of us that in particular tend to
become self-fulfilling images: if the teachers, inspecting our Iowa scores and
our aptitude-test figures and comparing our record with [those] of our
“age-peers,” conclude that we’re run-of-the-mine and treat us accordingly, then
they lead us to become what they think we are. [23]
Of even more direct import
for our immediate subject is the further observation back then that the institutionalized
bias toward precocity, noted by Gregg, may have notably different consequences
for comparable youngsters in differing social classes and ethnic groups.
The potential late bloomers in the less privileged
social strata are more likely to lose out altogether than their counterparts in
the middle and upper strata. If poor
[youths] are not precocious, if they don’t exhibit great ability early in their
lives and so are not
21.
Alan Gregg, For Future Doctors (Chicago: Univ. Chicago Press, 1957),
pp. 125-126 (emphasis added).
22.
Ibid., p. 125.
23.
This sociological extension of Gregg’s biopsychosocial
observation remains as formulated in 1960: R. K. Merton, “‘Recognition’ and
‘Excellence’: Instructive Ambiguities,” in Recognition of Excellence:
Working Papers, ed. Adam Yarmolinsky (New York:
Free Press, 1962), rpt. in Merton Sociology of Science (cit. n. 1), pp.
419-438, on p. 428 (emphasis added). Much
theoretical debate and hundreds of empirical studies of this kind of
self-fulfilling prophecy in American schools have resulted from the pioneering
work of Robert Rosenthal. See, to begin
with, Robert Rosenthal and Lenore Jacobson, Pygmalion in the Classroom:
Teacher Expectation and Pupils’ Intellectual Development (New York: Holt,
Rinehart & Winston, 1968); the critical monograph by Janet D. Elashoff and Richard E. Snow, Pygmalion Reconsidered (Worthington,
Ohio: Jones Publishing, 1971); and a monograph on the “decade of research and
debate” by Harris M. Cooper and Thomas L. Good: Pygmalion Grows Up: Studies
in the Expectation Communication Process (New York/London: Longman, 1983).
614
rewarded by scholarships and other sustaining grants, they
drop out of school and in many instances never get to realize their
potentialities. The potential late
bloomers among the well-to-do have a better prospect of belated recognition. Even if they do poorly in their school work at
first, they are apt to go on to college in any case. The values of their social class dictate this
as the thing to do, and their families can see them through. By remaining in the system, they can
eventually come to view. But many of
their [presumably] more numerous counterparts in the lower strata are probably
lost for good. The bias toward precocity
in our institutions thus works profound [and ordinarily hidden] damage on the
[potential] late bloomers with few economic or social advantages. [24]
Such differential outcomes
need not be intended by the people engaged in running our educational
institutions and thereby affecting patterns of social selection. And it is such unanticipated and unintended
consequences of purposive social action - in this case, rewarding primarily
early signs of ability - that tend to persist. For they are latent, not manifest,
social problems, that is, social conditions and processes that are at odds with
certain interests and values of the society but are not generally recognized as
being so. [25] In identifying the wastage that results from marked
inequalities in the training and exercise of socially prized talent, social
scientists bring into focus what has been experienced by many as only a
personal problem rather than a social problem requiring new institutional
arrangements for its reduction or elimination.
Mutatis mutandis, what holds for the accumulation of advantage and of
disadvantage in the earliest years of education would hold also at a later
stage for those youngsters who have made their way into fields of science and
scholarship but who, not having yet exhibited prime performance, are shunted
off into the less stimulating milieus for scientific work, with their limited
resources. Absent or in short supply are
the resources of access to needed equipment, an abundance of able assistance,
time institutionally set aside for research, and, above all else perhaps, a
cognitive microenvironment composed of colleagues at the research front who are
themselves evokers of excellence, bringing out the best in the people around
them. Not least is the special resource
of being located at strategic nodes in the networks of scientific communication
that provide ready access to information at the frontiers of research. By hypothesis, some unknown fraction
of the unprecocious workers in the vineyards of
science are caught up in a process of cumulative disadvantage that removes
them early on from the system of scientific work and scholarship. [26]
24.
Merton, “‘Recognition’ and ‘Excellence,’” pp. 428-429.
25.
On the first concept see R. K. Merton, “The Unanticipated Consequences of
Purposive Social Action,” Amer. Sociol. Rev., 1936,
1:894-904; on the concept of manifest and latent social problems see R. K.
Merton, Social Research and the Practicing Professions, ed. Aaron
Rosenblatt and Thomas F. Gieryn (Cambridge: Abt Books, 1982), pp. 43-99, esp. pp. 55ff.
26.
Late-bloomer patterns in science remain a largely unexplored area of
research. Jonathan R. Cole and Stephen
Cole found (in a sample of 120 university physicists that by design overrepresents productive and eminent physicists) that
“three-quarters of these physicists began their professional careers by
publishing at least three papers soon after their doctorates. There are few ‘late bloomers’; only five of
the thirty physicists who started off slowly ever became highly productive
(averaging 1.5 or more papers a year)”: Cole and Cole, Social Stratification
in Science (cit. n. 20), p. 112. Whether
one writes that “only” five of thirty (17 percent) or “as many as” 17 percent
proved to be late bloomers is, of course, a matter of tacit judgment. See also Stephen Cole, “Age and Scientific
Performance” (cit. n. 17); Nancy Stern, “Age and Achievement in Mathematics: A
Case-Study in the Sociology of Science,” Social Studies of Science, 1978,
8: 127-140; and Barbara Reskin, “Age and [Scientific Productivity: A Critical Review,” in The
Demand for New Faculty in Science and Engineering, ed. Michael S. McPherson
(Washington, D.C.: National Academy of Sciences, 1979).]
HHC: [bracketed] displayed on page 616 of original.
615
Other social and cognitive
contexts may make for such patterned differentials of cumulative advantage and
disadvantage. Harriet Zuckerman
suggests, as an example, that just as class origins
may differentially affect the rates at which potential late bloomers remain in
the educational system long enough to bloom, so academic disciplines may differ
in an unplanned tolerance for late blooming. Disciplines in which scholars often develop
comparatively late - say, the humanities - presumably provide greater
opportunities for late bloomers than those in which early maturation is more
common - say, mathematics and the physical and biological sciences. Generalized, these conjectures hold that contextual
differences such as social class or fields of intellectual activity as well
as individual differences in the pattern of intellectual growth affect
the likelihood of success and failure for potential late bloomers. [27]
Differences in individual
capabilities aside, then, processes of accumulative advantage and disadvantage
accentuate inequalities in science and learning: inequalities of peer
recognition, inequalities of access to resources, and inequalities of
scientific productivity. Individual
self-selection and institutional social selection interact to affect successive
probabilities of being variously located in the opportunity structure of
science. When the scientific role
performance of individuals measures up to or conspicuously exceeds the standards
of a particular institution or discipline - whether this be a matter of ability
or of chance - there begins a process of cumulative advantage in which those
individuals tend to acquire successively enlarged opportunities for advancing
their work (and the rewards that go with it) even further. [28] Since elite institutions have comparatively large resources
for advancing research in certain domains, talent that finds its way into these
institutions early has the enlarged potential of acquiring differentially
accumulating advantages. The systems of
reward, allocation of resources, and other elements of social selection thus
operate to create and to maintain a class structure in science by providing a
stratified distribution of chances among scientists for significant scientific
work. [29]
27.
Zuckerman, “Accumulation of Advantage and Disadvantage” (cit. n. 11).
28.
In terms of a clinical rather than statistical sociology, I have tried to trace
the process of accumulation of advantage in the academic life course of the
historian of science and my longtime friend Thomas S. Kuhn, as I have done more
recently in tracking my own experience as apprentice to the then world dean of
the history of science who has been honored by the establishment of the George Sarton Chair in the History of Science at the University of
Ghent. For the case of Kuhn see R. K.
Merton, The Sociology of Science: An Episodic Memoir (Carbondale:
Southern Illinois Univ. Press, 1979), pp. 71-109; for my own case see Merton,
“George Sarton: Episodic Recollections by an Unruly
Apprentice,” Isis, 1985, 76:470-486.
29.
On processes of stratification in science see Harriet Zuckerman,
“Stratification in American Science,” Sociological Inquiry, 1970, 40:235-257;
Zuckerman, Scientific Elite (cit. n. 2); Cole and Cole, Social
Stratification in Science (cit. n. 20); Jonathan R. Cole, Fair Science:
Women in the Scientific Community (New York: Free Press, 1979); Jerry
Gaston, The Reward System in British and American Science (New York:
Wiley, 1978); G. Nigel Gilbert, “Competition, Differentiation and Careers in
Science,” Social Science lnformation, 1977, 16:
103-123; Hagstrom, Scientific Community (cit.
n. 3); Lowell Hargens, Nicholas C. Mullins, and
Pamela K. Hecht, “Research Areas and Stratification Processes in Science,” Soc.
Stud. Sci.,
1980, 10:55—74; Hargens
and Diane Felmlee, “Structural Determinants of
Stratification in Science,” Amer. Sociol.
Rev., 1984, 49:685-697; Norman W. Storer, The
Social System of Science (New York: Holt, Rinehart & Winston, 1966);
Jack A. Goldstone, “A Deductive Explanation of the Matthew Effect in Science,”
Soc. Stud. Sci., 1979, 9:385-392; and Stephen
P. Turner and Daryl E. Chubin, “Chance and Eminence
in Science: Ecclesiastes II,” Soc. Sci. Info., 1979,
3:437-449.
616
Accumulation of Advantage and Disadvantage
Among Scientific Institutions
Skewed distributions of
resources and productivity that resemble those we have noted among individual
scientists are found among scientific institutions. These inequalities also appear to result from
self-augmenting processes. Clearly, the
centers of historically demonstrated accomplishments in science attract far
larger resources of every kind, human and material, than research organizations
that have not yet made their mark. These
skewed distributions are well known and need only bare mention here.
• In 1981, some 28 percent of the $4.4 billion of
federal support for academic research and development went to just ten
universities. [30]
• Universities with great resources and prestige in
turn attract disproportionate shares of the presumably most promising students
(subject to the precocity restriction we have noted): in 1983, two thirds of
the five hundred National Science Foundation graduate fellows elected to study
at just fifteen universities. [31]
• Those concentrations have been even more conspicuous
in the case of outstanding scientists. Zuckerman
found, for example, that at the time they did the research that ultimately
brought them the Nobel Prize, 49 percent of the future American laureates
working in universities were in just five of them: Harvard, Columbia,
Rockefeller, Berkeley, and Chicago. By
way of comparison, these five universities comprised less than 3 percent of all
faculty members in American universities. [32]
• Zuckerman also found that these resource-full and
prestige-full universities seem able to spot and to retain these prime movers
in contemporary science. For example,
they kept 70 percent of the future laureates they had trained, in comparison
with 28 percent of the other Ph.D.s they had trained. Much the same pattern, though less markedly,
held for a larger set of sixteen elite institutions. [33]
But
enough about these details of great organizational inequalities in science. This only
raises the question anew: If the processes of accumulating advantage and
disadvantage are truly at work, why are there not even greater inequalities
than have been found to obtain?
Or to put the question more
concretely and parochially, why have not Harvard, rich in years - 350 of them -
and in much else, and Columbia, with its 230 years, and, to remain parochial,
the Rockefeller, with its 75 years of prime reputation both as research
institute and graduate university, jointly garnered just about all the
American Nobel laureates rather than a “mere” third of them within five
30. National
Science Foundation, Federal Support to Universities, Colleges, and Selected
Nonprofit Institutions, Fiscal Year 1981 (Washington, D.C.: U.S. Government
Printing Office, 1983), pp. 79-80.
31. National
Science Foundation, Grants and Awards for Fiscal Year 1983 (Washington, D.C.: U.S. Government Printing Office,
1984), pp. 215-217.
32. Zuckerman,
Scientific Elite (cit. n. 2), p. 171.
33. Ibid., Ch. 5.
617
years after the prize? [34] Put
more generally, why do the posited processes of accumulating advantage and
disadvantage not continue without assignable limit?
Even Thomas Macaulay’s
ubiquitous schoolboy would nowadays know that exponential processes do not
continue endlessly. Yet some of us make
sensible representations of growth processes within a local range and then
mindlessly extrapolate them far outside that range. As Derek Price was fond of saying in this
connection, if the exponential rate of growth in the number of scientists
during the past half century were simply extrapolated, then every man, woman,
and child - to say nothing of their cats and dogs - would have to end up as
scientists. Yet we have an intuitive
sense that somehow they will not.
In much the same way, every
schoolgirl knows that when two systems grow at differing exponential rates, the
gap between them swiftly and greatly widens. Yet we sometimes forget that as such a gap
approaches a limit, other forces come into play to constrain still further
concentrations and inequalities of whatever matters are in question. Such countervailing processes that close off
the endless accumulation of advantage have not yet been systematically
investigated for the case of science - more particularly, for the distribution
of human and material resources in research universities and of scientific
productivity within them. Still, I would
like to speculate briefly about the forms countervailing processes might take.
Consider for example the
notion of an excessive density of talent. It is not a frivolous question to ask: How
much concentrated talent can a single academic
department or research unit actually stand? How many prime movers in a particular research
area can work effectively in a single place? Perhaps there really can be too much of an
abstractly good thing.
Think a bit about the
patterned motivations of oncoming talents as they confront a high density of
talented masters in the same department or research unit. The more autonomous among them might not entirely
enjoy the prospect of remaining in the vicinity and, with the Matthew effect at
work, in the shadow of their masters, especially if they felt, as youth
understandably often comes to feel - sometimes with ample grounds - that those
masters have seen their best days. Correlatively,
some of the firmly established masters, in a pattern of master-apprentice
ambivalence, may not relish the thought of having exceedingly talented younger
associates in their own or competing research terrains, who they perceive might
subject them to premature replacement, at least in local peer esteem, when, as
anyone can see, they, the masters, are still in their undoubted prime. [35] Not every one of us elders has the same powers of
critical self-appraisal, and the same largeness of spirit, as Isaac Barrow, the
first occupant of the Lucasian Chair of Mathematics
at Cambridge, who stepped down from that special chair at the advanced age of
thirty-nine in favor of his twenty-seven-year-old student - a chap named Isaac
Newton. In our time, of course, at least
during the years of seemingly limitless academic affluence and expansion,
Barrow would have stayed on and Newton would have been given a new chair. But again, as we
34.
Ibid., p.241.
35.
R. K. Merton and Elinor Barber, “Sociological
Ambivalence” (1963), rpt. in Merton, Sociological Ambivalence (New York:
Free Press, 1976), pp. 3-31, esp. pp. 4-6; Vanessa Merton, R. K. Merton, and Elinor Barber, “Client Ambivalence in Professional Relationships,”
in New Directions in Helping, ed. B. M. DePaulo
et al. (New York: Academic Press, 1983), Vol. II, pp. 13-44, on pp. 26-27.
618
have ample cause to know, continued expansion of that kind
in any one institution also has its limits.
Apart from such forces
generated within universities that make for dispersion of human capital
in science and learning, there is also the system process of social and
cognitive competition among universities. Again, a brief observation must stand for a
detailed analysis. Entering into that
external competition is the fact that the total resources available to a
university or research institute must be allocated somehow amongst its
constituent units. Some departments wax
poor even in rich universities. This provides
opportunities to institutions of considerably smaller resources and reputation.
These may elect to concentrate their limited
resources in particular fields and departments and so to provide competitively
attractive microenvironments to talents of the first class in those fields.
As another countervailing
process, populist and democratic values may be called into play in the wider
society, external to academic institutions and to science, and lead
governmental largesse to be more widely spread in a calculated effort to
counteract cumulating advantage in the great centers of learning and research.
But
enough of such speculations. I must not further defer examination of the
symbolism of intellectual property in science by continuing with observations
on countervailing forces that emerge to curb the accumulation of advantage that
might otherwise lead to a permanent institutional monopoly or sustained oligopoly
in fields of science and the sustained domination of a few individuals in those
fields. Just as there is reason to know
that the preeminence of individual scientists will inexorably come to an end,
so there is reason to expect that various preeminent departments of science
will decline while others rise in the fullness of time. [36]
The Symbolism of Intellectual Property
in Science
To explore the forms of
inequality in science registered by such concepts as the Matthew effect and the
accumulation of advantage, we must have some way of thinking about the
distinctive equivalents in the domain of science of income, wealth, and
property found in the economic domain. How do scientists manage to perceive one
another simultaneously as peers and as unequals, in
the sense of some being first among equals - primus inter pares, as the
ancients liked to say? What is the
distinctive nature of the coin of the realm and of intellectual property in
science?
The tentative answer to the
coinage question I proposed back in 1957 seems to have gained force in light of
subsequent work in the sociology of science. [37] The system of coinage is taken to be based on the public
recognition of one’s scientific contributions by qualified peers. That coinage comes in various denominations:
largest in scale and shortest in supply is the towering recognition
36. Surveys of
the quality of graduate departments in American universities have been
conducted from time to time, with the last three of them, in 1966, 1970, and
1982, having adopted more-or-less similar methods of inquiry. I am indebted to an unpublished study by
Donald Hood that identifies patterns of substantial change in the assessed
quality of academic departments in the course of quite short intervals.
37.
R. K. Merton, “Priorities in Scientific Discoveries” (1957), rpt. in Merton, Sociology
of Science (cit. n. 1), pp. 286-324.
619
symbolized by eponyms for an entire epoch in science, as when we
speak of the Newtonian, Darwinian, Freudian, Einsteinian,
or Keynesian eras. A considerable plane
below, though still close to the summit of recognition in our time, is the
Nobel Prize. Other forms and echelons of
eponymy, the practice of affixing the names of scientists to all or part of
what they have contributed, comprise thousands of eponymous laws, theories,
theorems, hypotheses, and constants, as when we speak of Gauss’s theorems,
Planck’s constant, the Heisenberg uncertainty principle, a Pareto distribution,
a Gini coefficient, or a Lazarsfeld
latent structure. Other forms of peer recognition
distributed to far larger numbers take further graded forms: election to
honorific scientific societies, medals and awards of various kinds, named
chairs in institutions of learning and research, and, moving to what is surely
the most widespread and altogether basic form of scholarly recognition, that
which comes with having one’s work used and explicitly acknowledged by
one’s peers.
I shall argue that
cognitive wealth in science is the changing stock of knowledge, while the
socially based psychic income of scientists takes the form of pellets of peer
recognition that aggregate into reputational wealth. This conception directs us to the question of
the distinctive character of intellectual property in science.
As I suggested at the
outset, it is only a seeming paradox that, in science, one’s private property
is established by giving its substance away. For in a long-standing social reality, only
when scientists have published their work and made it generally accessible,
preferably in the public print of articles, monographs, and books that enter
the archives, does it become legitimately established as more or less securely
theirs. That is, after all, what we mean
by the expression “scientific contribution”: an offering that is accepted,
however provisionally, into the common fund of knowledge.
That crucial element of
free and open communication is what I have described as the norm of “communism”
in the social institution of science - with Bernard Barber going on to propose
the less connotational term “communality.” [38] Indeed,
long before the nineteenth-century Karl Marx adopted the watchword of a fully
realized communist society – “from each according to his abilities, to each
according to his needs” - this was institutionalized practice in the communication
system of science. This is not a matter
of human nature, of nature-given altruism. Institutionalized arrangements have evolved to
motivate scientists to contribute freely to the common wealth of knowledge
according to their trained capacities, just as they can freely take from that
common wealth what they need. Moreover,
since a fund of knowledge is not diminished through exceedingly intensive use
by members of the scientific collectivity - indeed, it is presumably augmented
- that virtually free and common good is not subject to what Garrett Hardin has
aptly analyzed as “the tragedy of the commons”: first the erosion and then the
destruction of a common resource by the individually rational and collectively
irrational exploitation of it. [39] In the commons of science it is structurally the case
that the give and the take both work to enlarge the common resource of
accessible knowledge.
38. R.
K. Merton, “The Normative Structure of Science” (1942), rpt. ibid., pp.
267-278, esp. pp. 273-275; and Bernard Barber, Science and the Social Order (New
York: Free Press, 1952), pp. 130-132.
39. Garrett Hardin, “The Tragedy of the Commons,” Science,
1968, 162:1243-1247.
620
The structure and dynamics
of this system are reasonably clear. Since
positive recognition by peers is the basic form of extrinsic reward in
science, all other extrinsic rewards, such as monetary income from
science-connected activities, advancement in the hierarchy of scientists, and
enlarged access to human and material scientific capital, derive from it. But, obviously, peer recognition can be widely
accorded only when the correctly attributed work is widely known in the
pertinent scientific community. Along
with the motivating intrinsic reward of working on a scientific problem
and solving it, this kind of extrinsic reward system provides great incentive
for engaging in the often arduous and tedious labors required to produce
results that enlist the attention of qualified peers and are put to use by some
of them.
This system of open
publication that makes for the advancement of scientific knowledge requires
normatively guided reciprocities. It can
operate effectively only if the practice of making one’s work communally
accessible is supported by the correlative practice in which scientists who
make use of that work acknowledge having done so. In effect, they thus reaffirm the property
rights of the scientist to whom they are then and there indebted. This amounts to a pattern of legitimate
appropriation as opposed to the pattern of illegitimate expropriation
(plagiary).
We thus begin to see that
the institutionalized practice of citations and references in the sphere of
learning is not a trivial matter. While
many a general reader - that is, the lay reader located outside the domain of
science and scholarship - may regard the lowly footnote or the remote endnote
or the bibliographic parenthesis as a dispensable nuisance, it can be argued
that these are in truth central to the incentive system and an underlying sense
of distributive justice that do much to energize the advancement of knowledge.
As part of the intellectual
property system of science and scholarship, references and citations serve two
types of functions: instrumental cognitive functions and symbolic institutional
functions. The first of these involves
directing readers to the sources of knowledge that have been drawn upon in
one’s work. This enables
research-oriented readers, if they are so minded, to assess for themselves the
knowledge claims (the ideas and findings) in the cited source; to draw upon
other pertinent materials in that source that may not have been utilized by the
citing intermediary publication; and to be directed in turn by the cited work
to other, prior sources that may have been obliterated by their incorporation
in the intermediary publication.
But citations and
references are not only essential aids to scientists and scholars concerned to
verify statements or data in the citing text or to retrieve further
information. They also have
not-so-latent symbolic functions. They
maintain intellectual traditions and provide the peer recognition required for
the effective working of science as a social activity. All this, one might say, is tucked away in the
aphorism that Newton made his own in that famous letter to Hooke
where he wrote: “If I have seen further, it is by standing on ye sholders of Giants.” [40]
The very form of the
scientific article as it has evolved over the last three centuries normatively
requires authors to acknowledge on whose shoulders
40.
George Sarton was long interested in the history of
the aphorism. Since it says much in
little about one of the ways in which scientific knowledge grows, I indulged in
a Shandean account of its historical adventures: R.
K. Merton, On the Shoulders of Giants (1965; New York: Harcourt Brace
Jovanovich, 1985).
621
they stand, whether these be the shoulders of giants or,
as is often the case, those of men and women of science of approximately
average dimensions for the species scientificus.
Thus, in our brief study of the
evolution of the scientific journal as a sociocognitive
invention, Harriet Zuckerman and I have taken note of how Henry Oldenburg, the
editor of the newly invented Transactions of the Royal Society in
seventeenth-century England, induced the emerging new breed of scientist to
abandon a frequent long-standing practice of sustained secrecy and to adhere
instead to “the new form of free communication through a motivating exchange:
open disclosure in exchange for institutionally guaranteed honorific property
rights in the new knowledge given to others.” [41]
That historically evolving
set of complementary role obligations has taken deep institutional root. A composite cognitive and moral framework
calls for the systematic use of references and citations. As with all normative constraints in society,
the depth and consequential force of the moral obligation to acknowledge one’s
sources become most evident when the norm is violated (and the violation is
publicly visible). The failure to cite
the original text that one has quoted at length or drawn upon becomes socially
defined as theft, as intellectual larceny or, as it is better known since at
least the seventeenth century, as plagiary. Plagiary involves expropriating the one kind
of private property that even the dedicated abolitionist of private productive
property, Karl Marx, passionately regarded as inalienable (as witness his
preface to the first edition of Capital and his further thunderings on the subject throughout that revolutionary
work).
To recapitulate: the
bibliographic note, the reference to a source, is not merely a grace note,
affixed by way of erudite ornamentation. (That it can be so used, or abused, does not
of course negate its core uses.) The
reference serves both instrumental and symbolic functions in the transmission
and enlargement of knowledge. Instrumentally,
it tells us of work we may not have known before, some of which may hold
further interest for us; symbolically, it registers in the enduring archives
the intellectual property of the acknowledged source by providing a pellet of
peer recognition of the knowledge claim, accepted or expressly rejected, that
was made in that source.
Intellectual property in
the scientific domain that takes the form of recognition by peers is sustained,
then, by a code of common law. This
provides socially patterned incentives, apart from the intrinsic interest in
inquiry, for attempting to do good scientific work and for giving it over to
the commonwealth of science in the form of an open contribution available to
all who would make use of it, just as the common law exacts the correlative
obligation on the part of the users to provide the reward of peer recognition
by reference to that contribution. Did
space allow - which, happily for you, it does not - I would examine the special
case of tacit citation and of “obliteration by incorporation” (or, even more
briefly, OBI): the obliteration of the sources of ideas, methods, or findings
by their being anonymously incorporated in current canonical knowledge. [42] Many
of
41. Harriet
Zuckerman and R. K. Merton, “Patterns of Evaluation in Science:
Institutionalization, Structure and Functions of the Referee System,” Minerva,
1971, 9:66-00.
42. I
easily resist the temptation to begin a discourse on this pattern in the
transmission of knowledge. Short proleptic discussions of “obliteration by incorporation”
are found in Merton, Social Theory and Social Structure (New York: Free
Press, 1968), pp. 25-38; Merton, foreword to Eugene Garfield, Citation
Indexing: Its Theory and Application in Science, Technology, and Humanities (New
York: Wiley, 1979); and Garfield, Essays of an Information Scientist (Philadelphia:
ISI Press, 1977), pp. 396-399.
622
these cases of seemingly unacknowledged intellectual debt,
it can be shown, are literally exceptions that prove the rule, that is to say,
they are no exceptions at all since the references, however tacit, are evident
to knowing peers.
Once we understand that the
sole property right of scientists in their discoveries has long resided in peer
recognition of it and in derivative collegial esteem, we begin to understand
better the concern of scientists to get there first and to establish their
priority. [43] That concern then becomes identifiable as a “normal”
response to institutionalized values. The complex of validating the worth of one’s
work through appraisal by competent others and the seeming anomaly, even in a
capitalistic society, of publishing one’s work without being directly
recompensed for each publication have made for the growth of public knowledge
and the eclipse of private tendencies toward hoarding private knowledge
(secrecy), still much in evidence as late as the seventeenth century. Current renewed tendencies toward secrecy, and not alone in what Henry Etzkowitz
has described as “entrepreneurial science,” [44] will, if extended and prolonged, introduce major
change in the institutional and cognitive workings of science.
Since I have imported, not
altogether metaphorically, such categories as intellectual property, psychic
income, and human capital into this account of the institutional domain of
science, it is perhaps fitting to draw once again upon a chief of the tribe of
economists for a last word on our subject. Himself an inveterate observer of human
behavior rather than only of economic numbers, and also himself a practitioner
of science who keeps green the memory of those involved in the genealogy of an
idea, Paul Samuelson cleanly distinguishes the gold of scientific fame from the
brass of popular celebrity. This is how
he concluded his presidential address, a quarter century ago, to an audience of
fellow economists: “Not for us is the limelight and
the applause [of the world outside ourselves]. But that doesn’t mean the game
is not worth the candle or that we do not in the end win the game. In the long run, the economic scholar works
for the only coin worth having - our own applause.” [45]
43.
For the claim that the race for priority derives from
the culture of science itself see Merton, “Priorities in Scientific
Discoveries” (cit. n. 37), pp. 286-308.
It is further proposed (pp. 309-324)
that the extreme emphasis upon significant originality in the culture of
science can become pathogenic, making for such occasional side effects as the
cooking of fraudulent evidence, the hoarding of one’s own data while making
free use of others’ data, and the breaching of the mores of science by failing
to acknowledge the work of predecessors one has drawn upon.
44. Henry Etzkowitz,
“Entrepreneurial Scientists and Entrepreneurial Universities in American Academic
Science,” Minerva, 1983, 21:198-233.
45. Paul Samuelson, “Economics and the History of
Ideas” (delivered in 1961), rpt. in The Collected Scientific Papers of PaulA.
Samuelson, ed. Joseph E. Stiglitz (Cambridge, Mass.: MIT Press, 1966), Vol. II, pp.
1499-1516.
623
The Competitiveness of Nations
in a Global Knowledge-Based Economy
October 2002