Copyright (c)
1999 by the Massachusetts Institute of Technology. All rights reserved.
Perspectives
on Science 6.3 (1998)
209-231
Studying the Study of
Science Scientifically
David L. Hull
Abstract: Testing the
claims that scientists make is extremely difficult. Testing the claims that
philosophers of science make about science is even more difficult, difficult
but not impossible. I discuss three efforts at testing the sorts of claims that
philosophers of science make about science: the influence of scientists' age on
the alacrity with which they accept new views, the effect of birth order on the
sorts of contributions that scientists make, and the role of novel predictions
in the acceptance of new scientific views. Without attempting to test philosophical
claims, it is difficult to know what they mean.
In the summer of 1996, David Bloor (1997,
p. 498) was dismayed to hear a philosopher argue before an international
audience that, according to Kuhn, "communication between scientists in
different, incommensurable paradigms is impossible, but such communication is
indeed possible--and here examples were provided--so Kuhn is wrong." In
response, Bloor (1997, p. 499) argues that Kuhn was "not equating
incommensurability with incommunicability, though he was saying that it can
attenuate communication and may demand an effort to overcome." I do not
know whether the philosopher in question was as obtuse as Bloor claims, but he
or she was doing something right--attempting to test claims about science made
by students of science. If Kuhn is right about paradigms, one would expect that
scientists working in the same paradigm should be able to communicate with each
other more easily than scientists working in different paradigms. This claim
can actually be tested, and the results of this test might reflect positively
or negatively on Kuhn's famous incommensurability [End Page 209] theses--and
without equating incommensurability with incommunicability.
In this paper I urge more students of
science, especially philosophers of science, to test their claims about science
as often and as rigorously as possible. To perform this task, science must be
distinguished from the study of science. History of science poses one set of
problems. In certain respects it is like all other historical disciplines, such
as cosmology, but human history provides all sorts of other problems in
addition. Historians commonly claim that human histories are as much literature
as they are science. Sociologists of science are put in the position of having
to study themselves. After all, sociology of science is part of sociology, and
sociology is itself a science. But of all the disciplines that make up science
studies, philosophy of science is furthest removed from science itself. In this
paper I concentrate on the hardest case of all--philosophy of science.
Those of us engaged in science studies
study science, but what sort of thing is science? In the past, philosophers of
science have taken science to be something like a natural kind, about which general
knowledge is possible. On this view science is a certain sort of activity
distinguishable from other human activities by characteristics such as serious
attempts at falsification. At the other extreme, current advocates of pluralism
claim that science is merely a "loose and heterogeneous collection of more
or less successful investigative practices" (DuprŽ 1990, p. 69). In this
paper I treat science neither as a natural kind nor as a loose heterogeneous
collection, but as an "historical entity," an entity that is variable
both through time and at any one time but which retains sufficient cohesiveness
and continuity in the face of all this variability.
After numerous false starts, science
dribbled into existence and, once established, continues to the present. To be
sure, it cannot be characterized in terms of universally unvarying processes,
but it exhibits much more coherence and continuity than DuprŽ would allow. At
any one time, science is variable. For example, some cognitive psychologists
allow reference to introspection while behavioral psychologists do not. Science
also varies through time. While reference to God was acceptable in the early
years of science, it is not acceptable now. Furthermore, science has not yet
reached its definitive state today. It is very likely to continue changing in
the future, possibly in ways that few of us would like. For example, political
correctness may supersede empirical truth as a criterion for scientific
acceptance. If so, my interest in science will decrease markedly. But, as
variable as science has been at any one time as well as through time, it is not
a hodgepodge. It exhibits enough coherence and continuity to be considered an
historical entity. [End Page 210]
Regardless of the way in which one
construes science, it still can be studied scientifically. If science is a
kind, possibly a natural kind, then one task of those of us who study science
might well be to discern the regularities that characterize it. If science is
an historical entity, we can still study its variability at any one time and
its modifications through time. Finally, if science is just a variable and
heterogeneous collection of investigative practices, then all we can do is to
chronicle its vicissitudes. Thus, on any of these interpretations, science can
be studied scientifically because scientific understanding encompasses both the
specification of lawful regularities and the description of particular
sequences of events. However, if we are to study science scientifically, we
must meet the same standards as those that govern science itself. As Sulloway
and others have remarked, too often those of us who study science tend to
employ methodological practices that we would condemn as inadequate in the work
of those scientists whom we study.
In recent years, science studies has been
characterized by a welter of conflicting schools, philosophies, and
methodologies. According to many students of science, much of what we commonly
take to be important in science consists in little more than public relations
ploys. Scientists do not discover facts; they construct, fabricate, and invent
them. To the extent that these expressions were devised to emphasize the active
role that scientists, both individually and in groups, play in the generation
of knowledge claims, they are unproblematic; but I personally can understand
why many readers, including scientists, take these claims to imply much more,
as if nothing that can be legitimately termed "nature" or "the
world" in any way constrains what scientists come to believe. If any of
the advocates of these philosophies actually hold any of these more extreme
positions, they will surely reject my call for students of science to test
their beliefs about science as one more instance of self-delusion. If all the
time that scientists expend testing their views is just so much show, then
surely any attempt by those of us who study science to test our views about
science scientifically is even more of an illusion.
The relation between science and
philosophy of science is usually characterized in terms of "levels."
Science is related to philosophy of science in the same way that ethics is
related to metaethics. Philosophy of science is one level "higher"
than science. The relation between these levels is problematic. For example,
logical empiricist philosophers of science insist that empirical data play a
necessary role in science. However, they need not on this account be committed
to the view that empirical data play any role whatsoever in philosophy of
science. The Covering-Law Model of Scientific Explanation might be a totally
adequate analysis of "scientific explanation" [End Page 211] even if
no scientist ever explained any phenomenon by deriving it from a law of nature.
The central role of evidence in science entails nothing about the importance of
evidence in our study of science. However, this difference between science and
the study of science does, to say the very least, call for an explanation. In
this paper I see to what extent the sort of testing that goes on in science can
profitably be extended to the study of science. Traditionally, historians and
sociologists of science have acknowledged the role of data in their work.
Philosophers should do the same. Not only should we use the data gathered by
historians and sociologists of science, but we should also generate a bit of
this data ourselves. In doing so, we will deepen our understanding of both
science and philosophy of science.
One message that both history and
sociology of science have to teach us is that testing is difficult. These
difficulties have several sources. One difficulty arises from the intricate
interconnections between our basic theories and anything that might count as
empirical data. It is simply not true that we know what our theories mean
independently of any attempt to test them. We may think that we understand a
particular theory, but this illusion can be quickly dispelled by attempting to
test it. No amount of conceptual analysis can serve as a substitute for
empirical investigation--even with respect to meaning. Empirical investigation
requires the operationalizing of the concepts we are attempting to apply.
Philosophers have contributed to our understanding of science by showing that
theoretical terms cannot be operationally defined in a literal sense of
"definition," but this impossibility proof is not enough. We still
need some discussion of how to operationalize our concepts. What difficulties
are we likely to meet? Can they be overcome?
Testing the sorts of claims that
scientists make is difficult enough. Testing the sorts of meta-level claims
made by those of us who study science is even more difficult. Even so, we must
try. In this paper I investigate three attempts to study science
scientifically: my own study of the role of age in determining how quickly
scientists accept new ideas (Hull, Tessner, and Diamond 1978), Sulloway's
(1996) attempt to discover the influence of birth order on the sorts of
contributions that scientists are likely to make to science, and Donovan, Laudan,
and Laudan's (1988) investigation of the role of novel predictions in science.
By discussing these three examples, I intend to show how general claims about
science can be tested and to illustrate how the sorts of difficulties that
arise in such attempts can be overcome. They are overcome in the same ways as
they are in science in general. By emphasizing the role of testing via data, I
do not mean to imply that this is all there is to science. Obviously, science
is much more than empirical testing. However, such testing is an important
aspect of science. Also, in emphasizing the need for philosophers of science
[End Page 212] to attempt to test their views about science, I do not mean to
imply that this is all that philosophers of science should do. Occasional
testing does not entail nothing but testing.
Planck's Principle
In his autobiography, Max Planck (1949,
p. 33) remarked that a "new scientific truth does not triumph by
convincing its opponents and making them see the light, but rather because its
opponents eventually die and a new generation grows up that is familiar with
it." Instance after instance can be given of scientists, who, like Planck,
were involved in a basic conceptual revolution in science, claiming that older
scientists are less willing to adopt new views than their younger colleagues.1
This claim is important because it casts doubt on the role of reason, argument,
and evidence in bringing about change in science. Good evidence should be just
as good for young scientists as for their older colleagues. If older scientists
are more resistant to new ideas than are younger scientists, it might be due to
the biological or psychological effects of aging, to differences in the stage
of a scientist's career, to professional commitments to certain views, or to
greater knowledge of the effects of this change, and so on (for discussion of
the role of age in science, see McCann 1978; Messeri 1988; Rappa and Debackere
1993; and Levin, Stephan, and Walker 1995).
The investigation of Planck's principle
raises two questions: what does it mean? and is it true? Until we begin to
decide what Planck means, we cannot begin to decide whether or not Planck was
right. What counts as a "new scientific truth?" How "new"
must it be? To answer these questions, [End Page 213] I turn to two examples of
scientific revolutions: the Darwinian revolution and the Mendelian revolution.
Inevitably, when scientists publish what they take to be new scientific ideas,
historians will find all sorts of precursors. For example, Matthew (1831)
anticipated Darwin with respect to natural selection, and numerous authors,
including Lamarck and Robert Chambers, anticipated him with respect to
evolution. Why then term the revolution that took off in 1859 the Darwinian
revolution? Why not the Matthewian revolution? The answer is that Matthew did
not produce a revolution of any kind. His allusions to what came to be known
later as "natural selection" went totally unnoticed at the time.
Authors such as Lamarck and Chambers had some impact with respect to the
transmutation of species (e.g., on Wallace), but neither succeeded in producing
anything like a "revolution." Darwin did.
The Mendelian revolution poses a
different set of problems. Was Mendel the author of the Mendelian revolution or
was he simply a precursor like Matthew, Lamarck, and Chambers? Although
Mendel's 1865 paper did not go totally unnoticed, it certainly did not initiate
anything like a revolution in the study of heredity. The Mendelian revolution
did not occur until the turn of the century when others came up with views
similar (though far from identical) to those of Mendel. These authors claimed
independent discovery. If so, then Mendel's paper played no role in the
"rediscovery" of Mendelian genetics. Then why call this revolution
"Mendelian?" One answer is that Mendel's paper includes a careful and
clear exposition of the theory that eventually came to bear his name. It was
not just a vague sketch. Another reason is that it served to stave off a
priority dispute. The two junior rediscoverers were not about to have this
theory named after them. They were able to sabotage any potential effort by the
powerful de Vries to get his name attached to this emerging field by
emphasizing the role of Mendel. Better Mendelian genetics than de Vriessian
genetics. The sense of novelty that is relevant to Planck's Principle concerns
reception, not first discovery or even first publication. Until scientists
notice a new idea, they cannot accept or reject it.
What counts as a scientific truth, and
must it be true? Theologians, art critics, wine connoisseurs, and hosts of
others may or may not be resistant to change, but Planck's principle applies
only to scientists. Who are we to count as scientists? In evaluating Planck's
principle, are we to count scientists as they were conceived of at the time or
as we conceive of them today? After all, who is or is not considered a
scientist has changed during the course of science. For example, Descartes, and
later Newton, were engaged in roughly the same array of activities. They were
engaged in what we today would call philosophy, mathematics, and science, not
to mention theology, alchemy, and other questionable practices, but the
preceding [End Page 214] distinctions were not made at the time the way that we
make them today. Nowadays, college students are likely to come across Descartes
in an introductory philosophy course, while they hear about Newton as a
scientist. Why is this so? The reason is obvious: Descartes generated what we
would now call a philosophical research program (only specialists pay any
attention to Descartes's science), while Newton generated a successful
scientific research program (again, only specialists are much interested in
Newton's philosophy). Hence, today, Descartes is usually characterized as a
philosopher and Newton as a scientist. But such presentist ascriptions are
sorely misleading.
I see no easy way out of the dilemma
posed by the evolution of language. All of us are saddled with the requirement
that we write for present-day readers and must use present-day language to do
so, even if we know that present-day language is sure to mislead. The best we
can do is to warn our readers of the most obvious and important instances of
possible misunderstandings. After all, publishing a book on sixteenth century
Italian science in sixteenth century Italian would be a waste of time. Those
who could make the most sense of such a book have long been dead. Even the most
anti-presentist historians now see the need for what they term "legitimate
anachronisms" (Lightman 1997, p. 10). However, we must constantly remind
ourselves that calling Descartes a philosopher and Newton a scientist in the
absence of such explanations can lead to serious misunderstandings.
With respect to Planck's Principle and
the reception of Darwin's theory of evolution, we cast our net broadly. We
included anyone who was treated as a scientist between 1859 and 1869 by their
contemporaries, even if we had our doubts. Happily, we may term these workers
"scientists" because William Whewell first coined this term in 1833
and published it in 1834, only to reject it as inappropriate (Whewell 1834). It
caught on anyway but not until a half century later. Why we are permitted to
use a term only after it was introduced--even if rejected by its author and by
the relevant audience for half a century--remains, for me, one more
historiographic mystery. In any case, we were well aware that we were not
sampling the scientific community at large. Those scientists who were most
likely to pass judgment on evolutionary theory were those most closely
connected to it conceptually, e.g., zoologists, botanists, geologists, those
physicists working on the age of the earth, etc.
In addition, well-known scientists are
likely to leave more extensive records than their lessor-known brethren. This
second limitation might seem on the surface not to be of great significance,
except for the work of Desmond (1989) and Kim (1994) with respect to the
reception of Darwinian evolution and Mendelian genetics, respectively. They
discovered that [End Page 215] second- and third-tier scientists reacted quite
differently from their more prominent colleagues. Although Darwin valued the
opinion of Charles Lyell over that of an obscure pigeon fancier, Planck clearly
intended to be talking about scientists, not just the scientific elite (for
discussions of the elitist nature of science, see Meltzer 1956; Price 1963;
Cole and Cole 1973; Yoels 1973; Reskin 1977; Ladd and Lipset 1977; Garvey 1979;
and Hull 1988).
Are older scientists resistant only to
new truths? Planck's principle is usually raised only with respect to new
scientific ideas that we now take to be true or at least significant
improvements over past beliefs. How about all the new ideas that are rejected, and,
in retrospect, we think rightly so? Rarely does anyone complain about the
resistance of scientists to phrenology, the Piltdown man, polywater, cold
fusion, and a host of other ideas that we now take to be mistaken. Instead, the
usual question is why serious scientists were taken in. Are older scientists
more able than younger scientists to tell truth from falsity? Or are older
scientists supposedly more resistant to all new ideas, independent of the
eventual fates of those ideas? On my reading, Planck's principle concerns the
latter. Once again, older scientists as they were conceived of at the time are
supposedly more resistant than younger scientists to all new ideas, regardless
of how we judge, in retrospect, the truth-values of these ideas.
Ideas and theories are very difficult to
individuate. How much of a new theory must other scientists accept in order for
us to count them as accepting that theory? Darwinism, for example, is a very
general, heterogeneous theory. Different elements have had very different
fates. If one of Darwin's contemporaries had to agree with Darwin on all his
basic tenets in order to be counted as accepting Darwin's theory, then very few
scientists could be considered Darwinians. (Numerous evolutionary biologists
can be found making claims about what the "essence" of Darwinism is,
but such pronouncements are simply efforts to throw Darwin's mantle over their
own shoulders.) In order to test Planck's principle for something like
Darwinism, one element of the general theory must be singled out, for example,
the basic claim that species evolve. One might disagree with Darwin about the
role of sexual selection in evolution and still count as accepting his theory,
but it would be difficult to consider anyone a Darwinian who refused to acknowledge
that species evolve. Of course, Darwin's belief that species evolve was the
least original part of his theory (for further discussion, see Hull 1985 and
Numbers 1998).
Must older scientist literally die?
Retirement from scientific life is good enough. The relevant generation time is
professional, not biological. After all, roughly 75 percent of professional
scientists had accepted the evolution of species by 1869 without any upsurge in
the death rates of scientists [End Page 216] (Hull, Tessner, and Diamond 1978).
In different areas of science, periods of productivity vary tremendously. A
scientist who is thirty years old might be considered young in one field, over
the hill in another (see Merton and Zuckermann 1973; McCann 1978; Messeri 1988;
and Rappa and Debackere 1993 for further discussion).
The preceding discussion might sound as
if it were designed to discourage anyone from attempting to test hypotheses
about science, but it is not. In spite of the need to
"operationalize" hypotheses about science in order to test them,
testing can still be done. Scientists do it repeatedly in their various areas
of science. Students of science can do the same. After all, two decades ago,
Tessner, Diamond, and I were able to reach at least some tentative conclusions
about the applicability of Planck's Principle to the Darwinian revolution, and
the sophistication of the literature has only increased since then. For
example, we discovered that when comparisons between the mean age in 1859 of
scientists who accepted evolution between 1859 and 1869 is compared to those
who still held out after 1869, the results are statistically significant (39.6
to 48.1). However, if one looks just at scientists who came to accept evolution
between 1859 and 1869, age accounts for less than ten percent of the variance.
Of course, in studies such as these, 10 percent is substantial. It is also
true, as pointed out by Sulloway, that small variance does not imply small
effect size.
However, the correlation between age and
acceptance of the evolution of species after 1859 is not as dramatic as
participants and later commentators alike have claimed. It is statistically
significant but not so overwhelming that participants should have picked it up
through casual observation. My suspicion is that revolutionaries such as Planck
and Darwin were not reacting to the resistance of older scientists as such but
to the resistance of the leaders in their respective fields--the scientists
whose ideas were under attack. The relevant issue is professional age and
standing in the community, not biological age. Elite scientists reacted
negatively to the views of Planck and Darwin, not because they were old but
because they were the authors of the views that were under attack. For the same
reason, prestigious professional journals tended to ignore Darwin's theory
(Burkhardt 1974).
The message of the preceding example is
that even a claim as apparently straightforward as Planck's principle requires
extensive reformulation and operationalization before it can be tested. As a
result, any attempts to test hypotheses about science are likely to result in
their being modified extensively. In attempting to test Planck's principle, I
was forced to address questions that would have never occurred to me independently
of my attempt to test it. I understand the principle much more deeply and
thoroughly after testing it than before. I now have good reason to think [End
Page 217] that, on certain interpretations, Planck's principle is true; on
other interpretations, it is false. The important consideration involves
differences in interpretations. Although we all thought that we understood
Planck's principle, we were seriously mistaken. Vague ideas floated before our
eyes, and that is all. (For more recent discussions of Plank's principle, see
Rappa and Debackere 1993; as well as Levin, Stephan, and Walker 1995; and
Diamond 1997.)
Birth Order and Science
The issue that I investigated in the
preceding section is as narrow and tractable as any issue is likely to get in the
study of science. Others are sure to be much more complicated. Almost three
decades ago, Sulloway began to investigate the effects of birth order on
science. In the course of his investigations, he has expanded his study to
include over forty variables, twenty-eight scientific controversies, and
hundreds of scientists (Sulloway 1996). Starting with evolutionary theory,
Sulloway discovered a marked tendency for laterborns to accept Darwin's theory,
but as he expanded his investigation to include other scientific controversies,
a more complicated correlation emerged. New theories with a strongly
conservative cast attract firstborns, while those that are ideologically
radical attract laterborns.
At first glance, deciding birth order
would seem to be as straightforward a task as determining a scientist's age,
but Sulloway soon discovered that it is much more complicated than one might
expect. For example, the sex of one's siblings, the spacing between siblings,
one's precise birth rank, and overall number of siblings all turned out to
matter. In male-dominated societies, having an older brother is quite different
from having an older sister. In addition, Sulloway discovered that a firstborn
whose closest sibling is more than six years younger functions as if he were an
only child, whereas twelve years have to elapse before a laterborn functions as
an only child. Although Louis Agassiz was his parents' fifth child, he
functioned as a firstborn because the other four died in infancy. Parents also
remarry, combine and separate families, and much, much more. Sulloway had to
make decisions on these and other issues, including some of the same issues
that I had to address with respect to Planck's principle. Who is to count as a
scientist or as accepting Darwin's theory? On the second score, he opted for
more stringent requirements than I did. In addition to accepting the evolution
of species, a Darwinian had to acknowledge natural selection as an important
factor in evolution (Sulloway 1996, p. 29).
More problematic still is rating the
controversies on an ideological scale running from conservative to radical.
Sulloway opted to have experts make these decisions intuitively based on their
own expertise. Although lots of in-principle arguments can be raised against the
use of expert opinions in [End Page 218] making such a rating, the results are
more important than the arguments. In Sulloway's study, the average interrater
reliability turned out to be quite high. At the very least, these authorities
shared common biases. As impressionistic as expert opinion may be, it has
proved to be reliable in certain contexts. For example, practicing taxonomists
are very good at estimating taxonomic relationships--except in very special
circumstances--and those systematists who have attempted to quantify taxonomic
judgments have gradually uncovered what these special circumstances are (see,
e.g., Fernholm, Brener, and Jšrnvall 1989).
The most important bias that present-day
observers are likely to introduce stems from our presentist perspective.
Although Sulloway acknowledges such difficulties, I think they pose one of the
most serious problems for his undertaking. He treats certain themata as if they
were independent of time and place. Firstborns tend to prefer continuity,
order, causality, hierarchy, and essentialism, while laterborns are inclined
toward discontinuity, chaos, acausality, equality, and population thinking.
However, the assertive content of these themata seem to have changed through
time. For example, postmodernist radicals take "essentialism" to be
the primary source of the evils that have afflicted societies throughout
history. Hence, they would be counted as confirming Sulloway's hypothesis. But
as postmodernists use "essentialism," it does not contrast with
population thinking but with realism, and realism is not on Sulloway's list.
Idealism has raised its head periodically in the course of science. In Darwin's
day it was a conservative view, but today it is quite radical (Webster and
Goodwin 1996). How are we to score scientists from one age to the next?
I do not raise these problems in order to
discount or reject Sulloway's studies. To the contrary, these issues arise only
because Sulloway chose to take birth order seriously. Nor do I think that these
problems are insuperable. The reason that certain students of science are
likely to resist studies such as those conducted by Sulloway is that they seem
to imply that certain factors, which we traditionally think do not or should
not have a significant effect on science, actually do. However, the traditional
view of science is not in the least threatened if increased financial support
for science leads to its acceleration, or if firstborns tend to be
overrepresented in the rank of eminent scientists. Truth is truth regardless of
the birth order of those who discovered it. However, the correlations that
Sulloway found between birth order and preference for certain sorts of ideas do
pose problems. If firstborns tend to have disproportionate effects on science
and prefer certain ideas, then the cognitive content of science is likely to
reflect these preferences. If science is to reflect the world in which we live
more strongly than the character of scientists themselves, it must incorporate
one or more mechanisms capable of neutralizing the effects that Sulloway [End
Page 219] has discovered (see Ruse 1996 for an exhaustive detailing of the
effects that a belief in progress has had on science, especially evolutionary
theory).
The Role of Novel Predictions in
Science
Over a decade ago, the people at Virginia
Polytechnic Institute and State University decided that it was about time to
subject some of the key claims made by theorists of scientific change to the
same kind of "empirical scrutiny that has been so characteristic of
science itself" (Donovan, Laudan, and Laudan 1988, p. 3). In the past,
students of science have sporadically attempted not just to illustrate general
principles about science but also to test them by reference to episodes in
science. The trouble is that the results of these studies are not comparable.
They embody different assumptions, attempt to test different principles, and
proceed in very different ways. In this respect, science studies is not all
that different from other areas of science. Certain naive investigators (e.g.,
Collins 1985) were shocked to discover that scientists do not replicate each
other's work all that often or all that precisely. They tend to concentrate on
results that conflict with their own views, and when they do run these experiments,
they are rarely narrow replications. Scientists modify certain aspects of the
experimental setup for a variety of reasons. However, in many cases, these
differences are so slight that the studies can be compared. One problem with
the empirical studies that have been done in the study of science is that they
are so different that they cannot be meaningfully compared.
The folks at Virginia Tech decided to
remedy this situation. They gave over thirty historians, philosophers, and
sociologists of science the task of evaluating a variety of claims commonly
made about science by members of the post-positivist historical school in the
philosophy of science. They ended up publishing the results of only sixteen of
these case studies (Donovan, Laudan, and Laudan 1988). The organizers of this
science studies research program were well aware that their activity was
necessarily reflexive. For example, one of the theses of the historical school
is that no thesis can be expressed in an entirely theory-free vocabulary.
Popperians use one vocabulary, Kuhnians another, Laudanians yet another, and so
on. If the claims to be tested are set out in Popperian terms, then the
Popperians are likely to have an edge. Hence, if these claims withstand a test,
it may simply be a function of the bias built into the formulation of the
problem situation in the first place. Of course, one of the best ways to refute
the principles of a particular school is to set them out in their own terms and
then show that they are mistaken. If you can refute the views of a particular
school using the vocabulary of that school, then you certainly have presented a
strong refutation.
The people at Virginia Tech took another
tack--setting out and classifying [End Page 220] the principles to be tested as
neutrally as possible. The hope was that any significant biases built into
their terminology and evaluative procedures would be discovered in the course
of the study. Of all the principles that they proposed to test, I will discuss
only one--the role of novel predictions in science. Controversies in the
English-speaking community over the role of novel predictions in science go
back from Popper (1962), Hempel (1966), and Lakatos (1970), to at least Mill
(1843) and Whewell (1849). The problem is not just that these philosophers
meant different things by "novel predictions" but that they were not
all that good about telling their readers what they actually meant by this
phrase. One important distinction is between the phenomenon actually being observed
(i.e., "known") and whether it follows from a particular theory. Four
possibilities present themselves:
(i) Some phenomena are well known (they
have been observed) and follow from one or more accepted theories. They are
explained.
(ii) Some phenomena are not known (they
have never been observed) but follow from a particular theory. These are
epistemologically novel predictions.
(iii) Some phenomena are known to occur
but have yet to be explained by current theories. They are curiosities.
(iv) Finally, some phenomena have not
been experienced by anyone, and no theory implies that they should exist. They
are unknown.
The situations relevant to our discussion
are (ii) and (iii). In (ii) a phenomenon has yet to be noticed by the relevant
scientists. Hence, it cannot contribute to the construction of a theory.
However, once the theory has been sufficiently well constructed, it might well
imply that such a phenomenon should occur. These scientists go check and viol‡,
they confirm this epistemologically novel prediction. In (iii) a phenomenon has
been observed, but it has yet to be derived from any theory. Perhaps no theory
currently exists from which it can be derived, or it could be the case that a
theory exists, but no one has yet to produce the derivation. It is derivable
but not yet derived. After the fact, a scientist shows how this phenomenon can
be derived from this new theory. The phenomenon is not novel, but the
derivation is. This situation is termed "use novelty".
Why should the prediction of epistemologically
novel phenomena be all that special? The usual answer turns on the avoidance of
ad hoc hypotheses. If
scientists are already aware of a particular phenomenon, they can build it into
their theory from the start. Hence, no one is much impressed when they extract
from a theory the very phenomenon that they built into it in the first place.
However, if the scientists constructing a theory are not aware of this
particular phenomenon, they cannot incorporate it into their [End Page 221]
theory in advance. Hence, the derivation of this unknown phenomenon and its
later observation can be very persuasive.
This line of reasoning can be found in
Hempel's discussion of novel predictions. According to Hempel (1966, p. 37),
"it is highly desirable for a scientific hypothesis to be confirmed by
'new' evidence--by facts that were not known or not taken into account when the
hypothesis was formed." But immediately thereafter, Hempel (1966, p. 38)
brings himself up short:
from a logical point of view, the
strength of the support that a hypothesis receives from a given body of data
should depend only on what the hypothesis asserts and what the data are: the
question of whether the hypothesis or the data were presented first, being a
purely historical matter, should not count as affecting the confirmation of the
hypothesis.
In the first quotation, Hempel
distinguishes between (ii) epistemological novelty (facts that were not known)
and (iii) use novelty (facts that were not taken into account). According to
the "positivist" school that Hempel represents, scientists might take
the prediction of phenomena that have yet to be observed as providing greater
support to a hypothesis than the explanation of phenomena that have already
been observed, but they are mistaken to do so. Similar observations follow for
use novelty. Either an observation is derivable from a set of premises or it is
not, regardless of whether anyone has ever actually derived it. Science must be
extracted from the contingencies of history and rationally reconstructed
entirely in terms of inference. An observation statement follows from a set of
premises or it does not, period. Attitudes such as this one are precisely what
advocates of the historical school have attempted to combat.
However, when we turn to the work of
Lakatos (1970) as a representative of the historical school, his views on this
score are not as different from those of Hempel as one might expect.2
Lakatos's methodology of scientific research programmes is
"historical" in the sense that the unit of evaluation is a temporal
sequence of theories. Such a sequence of theories is theoretically progressive
if each new theory in the sequence predicts "some novel, hitherto
unexpected fact" (Lakatos 1970, p. 118), but as was his habit, Lakatos
immediately transforms this apparently straightforward claim in
counterintuitive ways. According to Lakatos (1970, p. 156), when a new research
programme explains "old facts" in novel ways, they count as [End Page
222] "new facts"! In addition, all such appraisals are a matter of
hindsight. It may take a long time before a research programme can be
"seen to produce 'genuinely novel' facts" (Lakatos 1970, p. 156).
Unlike Hempel, Lakatos's scientific research programmes have a temporal
dimension but one that is crucially retrospective. Even determining which
statements are part of a particular scientific research programme is a function
of hindsight. Lakatos's method of scientific research programmes may be
historical, but it is Whig history.
Before proceeding further, a word must be
said about the "rational reconstructions" of which
"positivist" philosophers of science are so fond, especially when we
have emphasized all the reconstruction that must be carried out if hypotheses
are to be tested empirically. The purpose of rational reconstructions is to
make logical connections more apparent. Real science tends to be very messy, so
messy that its logical structure is obscured. Rational reconstructions lay bare
the logical structure by eliminating all historical, psychological, and
sociological contingencies. The sort of reconstruction that I discussed
previously involves formulating rough-and-ready operational criteria to aid in
the testing of more general and abstract hypotheses. In this respect, these
reconstructions are the exact opposite of rational reconstructions. They
reintroduce the very contingencies that rational reconstructions are designed
to exclude.
All of the preceding concerns what the
principle of novel prediction actually asserts and whether it should play an
important role in science. It is quite another question whether scientists
actually do make recourse to this principle. The three authors in Donovan,
Laudan, and Laudan (1988, pp. 18-20) who discuss this principle at any length
all conclude that it did not play a very significant role in the scientific
episodes that they studied (Hoffman 1988, Frankel 1988, and Nunan 1988).3
Hence, the views of "positivists" on this score do not conflict with
actual scientific practice. However, such coincidences do not function as
confirmation for "positivists" because they do not think that
philosophical views such as theirs can be tested empirically in the first
place.
Initially, the function of epistemically
novel predictions was to guard against the introduction of ad hoc hypotheses. If scientists give no
special weight to novel predictions, then perhaps they are not as worried about
ad hoc theorizing as
they and students of science claim that they should be. [End Page 223] Was the
introduction of so many epicycles in Ptolemaic astronomy part of the legitimate
articulation of this scientific theory or an instance of blatant ad hocery? How about the introduction of
epistatic genes by Mendelian geneticists when transmission patterns did not
accord with the basic principles of Mendelian genetics? Was the postulation of
epistatic genes ad hoc?
More often than not, claims about which hypotheses are ad hoc, and which are not, are largely a
function of public relations. "My hypotheses are firmly grounded in
careful observation, while yours are invented merely for the purposes at
hand."
More fundamentally, claims about ad
hoc hypotheses need not
turn on the content of these claims but on a commitment to do something with
them. A scientist can introduce what looks very much like an ad hoc hypothesis. If that is all that the
scientist does with it, then it may well turn out to be ad hoc. However, if this scientist continues to
work on the processes and entities postulated, developing and modifying them as
he or she continues to work on the overall theory, then they may become a
legitimate part of the theory. They may well have been introduced to neutralize
a particular problem but were expanded to become an integral part of the
theory, implying much more than the phenomenon that they were introduced to
handle.
Conclusion
The main lessons to be learned from the
preceding summaries of three different attempts to test hypotheses about
science are that formulating hypotheses about science in ways that can be
tested empirically is very difficult and that the necessary clarifications
cannot be anticipated prior to our attempts at testing. One reason that novel
predictions cannot play the clear-cut epistemological role that some have
attributed to them is that the course of science does not run smoothly. On the
basis of minimal data (some of which is likely to turn out to be mistaken or
misleading) and very hazy theories, tests are run. Before these tests are
completed, the scientists running them have already reformulated some of their
hypotheses and made adjustments in their investigative techniques. Frequently,
early test runs are not worth completing. Instead, new sequences of tests are
devised and carried to partial completion, each more sophisticated and
determinate than the ones before. Order is introduced only long after the fact,
when it comes time to publish the results of one's research.
If scientists already knew everything
that they needed to know before they started their empirical investigations, a
single experiment might prove conclusive. Of course, scientists do not know in
advance everything that they need to know. As a result, sequences of tests need
to be run in order to make proper use of the ad hoc hypotheses that scientists formulate,
[End Page 224] and in the process some of these ad hoc hypotheses become transmuted into
legitimate scientific hypotheses. Lakatos is right about this much. We can
decide which hypotheses are ad hoc,
and which are not, only in retrospect. In a genuinely historical view of
science, many decisions can be made only in retrospect.
Parallel lessons hold for the study of
science itself. I did my study on age in my spare time, with the help of two
graduate students toward the end. (Incidentally, I did the data collecting
because these graduate students did not know enough about the period under
investigation to do it properly.) Sulloway was fortunate to be awarded a
five-year grant from the MacArthur Foundation. In a paper that Rachel Laudan
delivered at the History of Science Society meetings in 1990, she remarked on
the inability of the people at Virginia Tech to get adequate funding for their
project. The methods that Sulloway and I used did not require large research
teams and massive financial expenditures. We could carry out our investigations
in relative isolation for very little money, but if science teaches us anything
about science, it implies that the investigation of certain problems requires
large numbers of people working in close cooperation over many years.
Haphazard, local, short-term investigations are not good enough. The people at
Virginia Tech learned a lot about their research program as it progressed. By
the time that the first cycle was complete, they knew enough to make the second
cycle even more determinate. Unfortunately, no second cycle was possible. The
funding ceased, and the members of this research team went their separate ways.
The conceptual obstacles confronting
science studies are formidable. The disciplinary obstacles are even more
formidable. Not only are those of us who study science subdivided into numerous
factions, each fighting to maintain its own turf, but also we do not have a
tradition of the sort of funding necessary to make headway on the kinds of
problems that we are addressing. It also does not help that science studies is
seen by many scientists as a threat, a perception that is not totally without
foundation. Many of those who study science are more interested in debunking it
than in understanding it. The result has been "Science Wars." 4 Relativist
students of science present numerous case studies to show how unimportant
anything that might be termed evidence is in changing scientists' minds, [End
Page 225] but something is desperately wrong with presenting evidence to show
how irrelevant evidence actually is. Now that students of science have retraced
all the familiar ground that generations of philosophers have trod before them,
perhaps we can abandon our intense fascination with philosophical puzzles and
return to studying science.
Northwestern University
David Hull is
Dressler Professor in the Humanities in the Department of Philosophy,
Northwestern University, Evanston, Ill. He is past president of the Philosophy
of Science Association, the Society of Systematic Zoology, and the International
Society for the History, Philosophy and Social Studies of Science. He has
written or edited eleven books, including Darwin and His Critics (1973),
Philosophy of Biological Science (1974), Science as a Process (1988), The
Metaphysics of Evolution (1989), and Philosophy of Science (1998) with Michael
Ruse.
Notes
1. The following authors
discuss or at least mention Planck's principle: Lavoisier ([1777] 1862, 2:505);
Whewell (1837, 2:157); Whewell (1851, p. 139); Comte (1853, 2:152); Darwin
(1859, pp. 481-82); Lyell (1881, 2:253); Darwin (1899, 2:85, 218); Huxley
(1901); Loewenberg (1932, p. 687); Planck (1936, p. 97); Planck (1949, pp.
33-34); Barber (1961, p. 596); Kuhn (1961, pp. 161-90); Kuhn (1962, pp. 89-90,
150-51); Oakley (1964); Hagstrom (1965, pp. 283, 291); Samuelson (1966,
2:1517-18); Greenberg (1967, p. 45); Scheffler (1967, pp. 18-19); Feyerabend
(1970, p. 203); Dolby (1971, p. 19); Cole and Cole (1973, p. 82); Holton (1973,
p. 394); Merton and Zuckermann (1973, pp. 497-559); Montgomery (1974, p. 115);
Paul (1974, p. 412); Wisdom (1974, 2:829); Bondi (1975, p. 7); Cantor (1975, p.
196); Cole (1975, p. 181); Gunther (1975, p. 458); Brush (1976, p. 640); Chubin
(1976, p. 464); Garber (1976, p. 96); Knight (1976, p. 14); Stegmuller (1976,
p. 148); Rosenkrantz (1977, p. 251); Blackmore (1978, pp. 347-49); Blua (1978,
p. 197); Hull, Tessner, and Diamond (1978, pp. 717-23); McCann (1978, pp. 21,
34, 61-62, 79-80, 90-91, 101, 119); Nitecki, Lemke, Pullman, and Johnson (1978,
pp. 661-64); Barash (1979, p. 240); Garvey (1979, p. 15); Hufbauer (1979, p.
744); Mahoney (1979, p. 372); Coats (1980, pp. 190-92); Diamond (1980, pp.
838-41); Newton-Smith (1981, p. 235); Broad and Wade (1982, p. 135); Cock
(1983, p. 40); Grayson (1983, p. 208); Messeri (1988, pp. 91-112); Perrin
(1988, pp. 105-24); Darwin (1991, p. 279); Stephan and Levin (1992); Margolis
(1996, p. 136).
2. The classificatory
criteria that I am using in placing particular philosophers in particular
schools are extremely crude and not very faithful to history. In many important
respects, Hempel is anything but a positivist, and Lakatos retains many
positivistic elements.
3. One feature of
empirical testing is that results may conflict with one's own preferences. For
example, I think that novel predictions should lend greater support to a
hypothesis than the derivation of the commonplace. I also thought that
practicing scientists have more sense than their positivist commentators and
treat novel predictions as special. Unfortunately, on the basis of these three
studies, I am forced to admit that I was wrong.
4. Several publications
have really heated up the war between the relativist, deconstructionist critics
of science and their realist, "positivist" defenders: Gross and
Levitt (1994); Gross, Levitt, and Lewis (1996); and Sokal (1996a, 1996b).
Gross, Levitt, and Lewis assay what they take to be left-wing,
deconstructionist, postmodernist critics of science, while Sokal wrote a parody
of the sort of prose that he thought characterizes this same literature and got
it published, not as a parody but as a genuine contribution. The reactions have
been numerous and heated: see Richards and Ashmore (1996); Fish (1996); Fuller
(1997); Dickson (1997a, 1997b); Gottfried and Wilson (1997); Macilwain (1997a,
1997b); Gross (1997); Edge (1997); Forman (1997a, 1997b); Robinson (1997);
Levitt (1997); Trefil (1997); Herschbach (1997); Sandler (1997); Ziegler
(1997); and Gibbons (1997). One characteristic of the various defenses of the
new science studies is that these defenders are rapidly taking back everything
that was new about the "new" science studies. No matter how crystal
clear their prose may have been, their critics have totally misconstrued them
as saying something novel and interesting.
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