Phil. SOC.Sci.

11 (1981) 199-213

11. SYMPOSIUM: THE STRONG PROGRAMME IN THE

SOCIOLOGY OF KNOWLEDGE

11.2 The Strengths of the Strong

Programme
DAVID BLOOR, Science Studies unit, Edinburgh

Professor Laudan’s strictures on the strong programme in the sociology

of knowledge do not, I think, call for a defence of that programme so
much as a thorough counter-attack. Nevertheless I am grateful to him
for raising a range of objections and queries of a kind which are typical of
philosophers. I shall therefore combine defence and attack. To ease the
burden on the reader I shall discuss Laudan’s points in the order in
which he raises them. The only departure from this procedure concerns
some general points from the end of his paper that I shall take up
immediately. These deal with what Laudan sees as the excessive em-
phasis on sociological approaches and the neglect of the pragmatic
success of science.
Like Laudan I think that a number of disciplines, such as biology or
psychology, would have to combine with sociology if we were trying to
produce acomprehensive description of all the aspects of an activity like
science. I am surprised that any reader of Knowledge and Social Imag-
ery could imagine that I thought otherwise. I said on page four-and
Laudan quotes the passage-that naturally there will be other types of
cause apart from social ones which will cooperate in bringing about
belief. A few pages later there is, accordingly, an extended discussion of
the role of sense-experience to illustrate this point. The importance of
combining sociology with other disciplines was in fact broached in the
very first paragraph of the book, and is a theme that runs through it.
The fact remains that there are good reasons for a special emphasis on
the social characteristics of science, for stressing its nature as a social
institution. There is nothing special about science that resides in the
biology of scientists, their sensory and memory capacities, or motor
dexterity. There is nothing special about the size of their incomes or the
structure of their professional organizations. There is not even anything
special about their using pieces of apparatus or their taking measure-
ments and samples. It is their goals and the interpretations they put on
their interactions with the world that matter. We only begin,to bring
science as such into focus when we notice, say, certain features of its

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200 David BIoor

training procedure, where esoteric traditions, practices and precedents

are passed on to new members. In short, it is only by examining the
culture of science that we come close to the heart of that activity. To
study the transmission, distribution, maintenance and change of the
accepted beliefs and practices in science is therefore to study one of its
most vital aspects. For this reason I can attach no sense at all to
Laudan’s assertion that he finds it ‘entirely conceivable’ that a ‘com-
prehensive’ study of science could omit sociology.
In an effort tojustify his assertion my critic declares it not proven that
there are any parts of science that are better treated by sociology than
any other forms of study. In that case I wonder how he would analyze
those parts of science which have shown themselves demonstrably
affected by the presence of social interests? I will give more examples
later, but as acase in point take the priority dispute between Newton and
Leibniz over the invention of the calculus. The reason why sociological
variables are important here is because the controversy was a symptom
of intriguing connections between Newtonian philosophy and the prob-
lem of the Hanoverian succession. It was not simply a matter of the
psychological make up of the protagonists. The question of priority was
deliberately made into an issue in an effort to stop the future George the
First bringing Leibnizfrom Hanover to England.’ What was at stake was
Newton’s status as the Court philosopher. In order to press charges
against Leibniz a delicate balance had to be struck between making out
the two forms of the calculus to be similar, so the charge of plagiarism
would stick, and saying that they were diflerenf so that Newton’s work
could be said to be superior. This is what gives the issue a connection
with the detailed internal history of mathematics.
It is conventional to deplore the Newton-Leibnizdispute and hence to
set it outside science proper.* This is the kind of response that would
recommend itself to anyone who is more interested in celebrating the
purity of science than in studying all its connected features in a matter-
of-fact way. If this tactic occurs to my critic as a way of ruling out this
example of sociological variables in ‘science’ I reply as follows. The
connection between Whig politics and the Newtonian philosophy that
surfaces inthis dispute has deep and extensive ramifications in the
theory of matter. Any attempt to rule out my example a priori would
seriously conflict with the general historical picture that is now emerging
of this phase of our scientific de~elopment.~ A ‘comprehensive’ rather
1 Arnold Thackray, “‘The Business of Experimental Philosophy”. The Early Newton-
ian Group and the Royal Society’, Acres du XXIe Congrk Inrernariona1~Histo;redes
Sciences, 3, 1970-71, 153-59.
2 For avaluable analysis of the various responses to this dispute see S. Shapin, ‘Licking
Lcibnit’ (essay review of A. R. Hall, Philosophers at War), History ofdcience, Dec.
1981 (forthcoming).
3 See for example M. C. Jacob, The Neuronions andthe English Rer.olufion, 1689-1720,

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 The Strengths of the Strong Prograninie 201

than an arbitrarily truncated picture of science manifestly does invoke

the social.
Nevertheless, it is reasonable to insist that the most important aspects
of science concern the making and testing of predictions. How does this
relate to the sociology of knowledge? Isn’t success in prediction con-
nected with the pragmatic side of science, and that, surely, has little to
do with factors of the kind investigated by sociologists? The pragmatic
success ofa theory is, I am sure, often connected with its acceptance and
espousal by the scientific community. Given the utilitarian goals which
have long informed our science this is no surprise. Of course, the
connections between these successes and the trittli of a theory is very
tenuous. For the same reason the beliefs about a theory which follow
from its pragmatic success are not strongly constrained. Even the
acknowledgement that a theory is pragmatically successful involves
complex judgements and is frequently a matter of dispute. Success here
has to be weighed against failure elsewhere. The past history and future
prospects of a theory have to bejudged and compared with rivals. When
pragmatic success is put in context its indications are never unequivocal
nor as simple as they may seem in the abstract.
In order to justify preferences and decisions arrived at in these com-
plicated circumstances scientists often invoke ‘formal’ criteria. Profes-
sor Laudan seems to think that these in some way displace or rule out
social factors. As instances of such formal criteria he cites the desire that
theories be ‘simple’, or the preference for, say, causal theories. I can
only marvel at his choice of examples. Simplicity as a formal criterion
has been adisaster for rationalist philosophers. There are many possible
ways of defining and assessing simplicity. What, then, makes a scientist
choose this rather than that definition? What gives an intuition of
simplicity its credibility for this or that group? How and why might
‘simplicity’ be adopted in preference to some other measure of theoreti-
cal virtue which may conflict with it? All that simplicity does is to pose
problems and point to the need for other kinds of explanation. It is more
plausible to see ‘simplicity’ as an after-the-fact justification for opinions
that have their real basis e l ~ e w h e r e . ~
In the case ofcausality as a desirable or undesirable characteristic of a
theory, we have the salutary reminder of Paul Forman’s well
documented study.5 He has demonstrated the political significance of
Ithaca 1976. S. Shapin. ‘Of Gods and Kings: Natural Philosophy and Politics in the
Leibniz-Clarke Disputes’. Isis, 72, 1981. S . Schaffer, Newtonian Cosmology and the
Steady State. unpublished PHD thesis, Cambridge University, 1980. Chap. vii.
4 Mary Hesse. Revolutions and Reconstructions in the Philosophy of Science, Brighton
1980, p. 190. Mary Hesse, The Structure of Scientific Inference. London 1974.
5 P. Forman, ‘Weimar Culture, Causality and Quantum Theory, 1918-1927.Adaptation
by German Physicists and Mathematicians to a Hostile Intellectual Environment’, in
R. McConnmach,ed., HisroricalStudiesinthe PhysicalSciences, vol. 3,1971.1-115.

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202 David Bloor

the rejection of causality in Weimar Germany. After Germany’s defeat

in 1918 there was a massive reaction against science. The immensely
popular Lebensphilosopliie of Oswald Spender fastened on causality as
a symbol of all that it rejected. Forman has shown how energetically
physicists and mathematicians accommodated to this powerful intellec-
tual fashion for denigrating causality. Even if it showed nothing else,
Forman’s study means that we cannot simply proceed, as my critic does,
by contrasting professional judgements with ‘social’ facts, as if they
could not be one and the same thing.
Professor Laudan also points out that when, for whatever reason, our
choice of theories has been narrowed down to two, then experimental
evidence can often tip the balance between them. Indeed it can, but
Laudan’s own work on Pierre Duhem will have told him that in practice
crucial experiments can always be challenged.6 So what is it that sets the
scene for a crucial experiment, holding us to a given outcome or permit-
ting us to exploit the ever present possibility of challenging it? All that
Laudan is doing by starting his discussion at the point where there are
two main contenders for the truth is assuming that social processes have
already done their work and then pretending that they don’t exist.
Before we ever reach the point on which Laudan focusses attention we
need to know how the field has been narrowed down. These are ques-
tions about the cultural inheritance of those who are conducting the
crucial experiment. It is no use trying to invoke previous experimental
results or the constraints of reality as a sufficient ground forthis narrow-
ing process, because this just raises all the same problems over again.
We need to invoke some further processes to work in conjunction with
experiment and observation. It is necessary to introduce some process
such as socialization into a tradition ofnormal science in order to explain
the constraints which limit the acceptable interpretations which can be
put on the facts of experience. And if this applies to the circumstances
which lead up to a crucial experiment, it applies equally to the decisions
that are made about its outcome.
Providing that we do not arbitrarily choose to ignore the necessary
social setting of a crucial experiment there are some extremely interest-
ing case studies at hand. Consider, for example, Farley and Geison’s
account of the clash between Pasteur and Pouchet.’ The question was:
could life be produced by spontaneous generation out of non-living
matter? Pouchet had conducted experiments that pointed to precisely
this conclusion. Pasteur was the spokesman for the scientific establish-
ment who challenged this belief. He claimed that minute living creatures
6 P. Duhem, The Aim and Striicrure of Physical Theory, trans. P. P. Wiener. Princeton
1954.
7 J. Farley and G. L. Geison, ‘Science, Politics and Spontaneous Generation in
Nineteenth Century France: The Pasteur-Pouchet Debate’, Bidleiin of the Hisrory of
Medicine. 48, 1974, 161-98.

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 The Strengths of the Strong Programme 203

had been introduced into the experiment and contaminated the 'non-
living' matter. The appearance of spontaneous generation was thus an
artifact produced by faulty procedures. This argument was consistently
advanced by Pasteur even when, to our eyes, it seems very strained
indeed. What Farley and Geison show is how judgements of plausibility
about Pouchet's results were the outcome of social and political consid-
erations. In the conservative France of that time the doctrine of spon-
taneous generation had a definite social meaning. It was looked upon as
theologically mischievous and politically dangerous. The capacity to
create life 'was the prerogative of spirit, and spirit was of course the
region which housed all the ultimate justifications of the agencies of
social control and political authority. To reduce life to matter was thus to
attack, in a mediated and metaphorical way, the foundations of a certain
kind of society.
I do not want to claim that the theoretical interpretation of experimen-
tal results is always or necessarily influenced by social factors that bear
on national or dynastic politics. The question of the kind or scope of the
social factors at work in a system of knowledge is entirely contingent and
can only be established by empirical study. The important point, how-
ever, is that where broad social factors are not involved, narrow ones
take over. The sociology of knowledge is still relevant. As well as an
external sociology of knowledge there is also an internal sociology of
knowledge. By this I mean that the social factors concerned may be ones
which derive from the narrowly conceived interests or traditions or
routines of the professional community. To see what this amounts to we
may turn to the literature that deals with professional vested interests in
science. This describes the concern shown by scientists in expanding the
area to which theircompetences apply. Much that goes on in science can
be plausibly seen as a result of the desire to maintain or increase the
importance, status and scope of the methods and techniques which are
the special property of a group. This is how Ospovat analyzes the
different theories of adaptation accepted by early nineteenth Century
biologists and geologists.* The geologists saw organisms as perfectly
adapted to their geophysical surroundings. Organic changes were there-
fore explicable by appeal to prior geological change. Biologists, on the
other hand, emphasized the variability of the connection between an
organism and its environment. This made room for specifically biologi-
cal laws of change which would safeguard the role of their expertise. A
similar set of internal professional interests lies behind the recurrent and
protracted debates in botanical taxonomy described by Dean.9 He
8 Dov Ospovat, 'Perfect Adaptation and Teleological Explanation: Approaches to the
Problemofthe History of Life in the Mid-nineteenthCentury', Sritdies in rhe History of
Biology, 2, 1978, 33-56.
9 J. Dean, 'Controversy Over Classification: A Case Study from the History of

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204 David BIoor

shows how judgements on very specific issues such as the classification

of Cilia and the number of species in the genus can be related to the
interests vested in the skills and practices routine in different groups.
One group will draw its boundaries according to morphological relation-
ships, another according to patterns of gene-exchange, another accord-
ing to evolutionary relationships.
Numerous other examples could be given of factors which are at once
'internal' and yet clearly related to typical sociological variables con-
cerned with autonomy, control, prestige, status, tradition and habit.I0 I
hope, however, that enough has been said for one thing to emerge
clearly., To claim that scientists are educated and socialized into a
certain community, and address their communications to their peers, is
most certainly riot, as Laudan asserts, to invoke a trivial mode of social
involvement. The claim only appears trivial if it is attended by a shallow
or uncertain grasp of the social processes in question. Properly under-
stood, training, socialization and communication are deep and complex
and revealing phenomena. That fact will only be appreciated, however,
if we resolutely engage our accounts of knowledge with the detailed
understanding of these processes that is emerging from specialist re-
searchers.
I will now move to the more specific of Professor Laudan's objections
and take them in order. They fall into three groups.
(i) The first charge, it may be recalled, is that I attack a thesis that has
never been held by any significant philosophers. The thesis in question is
that true or rational beliefs have, in Laudan's words "no explanation
Botany'. in B. Barnes and S. Shapin (eds.). Natural Order, Historical Studies of
Scienril;c Citlture. Beverly Hills and London 1979. Chap. 9.
10 For example see D. MacKenzie. 'Statistical Theory and Social Interests: A Case
Study', SocialStrtdies of Science, 8,1978.35-83. S . Shapin, 'The Politics of Observa-
tion: Cerebral Anatomy and Social Interests in the Edinburgh Phrenology Disputes'. in
R. Wallis (ed.), On the Margins of Science: The Social Constrirction of Rejected
Knowledge, Sociological Reriew Monographs, 27. 1979, pp. 139-78.S. Shapin,
'Phrenological Knowledge and the Social Structure of Early Nineteenthcentury Edin-
burgh'. Annals of Science, 32. 1975.219-43. E. Frankel, 'Corpuscular Optics and the
Wave Theory of Light: The Science and Politics of a Revolution in Physics', Social
Studies ofScience. 6 , 1976. 141-84. J. Hanvood, 'The Race-Intelligence Controversy:
A Sociological Approach. I-Professional Factors; 11-External Factors', Social
Slitdies of Science, 6 , 1976, 369-91; 7, 1977, 1-30. R. S. Turner, 'The Growth of
Professorial Research in Prussia, 1818-1848-Causes and Contexts', Historical
Studies in fhe PhysicalSciences. 3,1971,137-82. R. S . Turner, 'University Reformers
and Professorial Scholarship in Germany, 1760-1806'. in L. Stone (ed.). The University
in Society. Oxford 1975. vol. ii. 495-531. G. Allen, 'Naturalists and Experimentalists:
The Genotype and the Phenotype', Stitdies in the History of Biology, 3 , 1979, 179-209.
T. Brown, 'The College of Physicians and the Acceptance of Iatromechanism in
England, 1665-1695', Biillerin of the History of Medicine, 44, 1970, 12-30. T. Brown,
'From Mechanism to Vitalism in Eighteenth-Century English Physiology', Journal of
the History of Biology. 7 . 1974. 179-216.

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 The Strengths of the Strong Programme 205

whatever’ and that ‘literally nothing causes us to believe what is true’. I

agree: this thesis has never been held by anybody. But then, this is not
what I am attacking. My targets in the first chapter of Knowledge and
Social Imagery are Lakatos, Ryle, Hamlyn and Karl Mannheim. Had
Laudan’s book been published then I would certainly have included him
in the list. What I was taking issue with was every approach that makes
‘logic, rationality and truth appear to be their own explanation’. Note:
‘their own explanation’, not ‘requiring no explanation at all’. It is the
self-explanatory or self-moving picture of knowledge, as it is presented
by these writers, which appears to me so pernicious.
- Professor Laudan’s quotation from my book-about the general
structure of the positions that I am attacking-unfortunately misses out
the crucial words. Where I refer to my opponents’ views in terms of
logic, rationality and truth being their own explanation, Laudan leaves a
row of little dots. Had he included the missing words, this might have
inhibited his ‘no explanation whatever’ reading of my position.
The crucial point in all this is that many philosophers, including
Laudan, proceed by first evaluating a belief, and if they find it unsatis-
factory they feel the need for more information to explain it. Here, and
here alone, will they countenance socio-psychological causes. Thus
HarnlyP tells us that ‘the ways in which we may perceive something
can be divided into two classes-the right ways and the wrong ways.
Indeed, one way of perceiving something-the right way-may be dis-
tinguished from all others’ (p. 11). It then emerges that ‘this case pro-
vides no room for scientific explanation, since none is called for’ (p. 22).
Suppose we are looking at two lines of equal length in a psycholgoical
experiment; ‘nothing makes them look of equal length’ says Hamlyn,
‘they just are so’ (p. 13). A good psychologist like Kurt Koffka, who is
of course one of Hamlyn’s targets, does not go through this evaluative
exercise.’* He simply poses the question ‘why do things look as they
do?’ (p. 77).
These were the contrasts that I had in mind when I spoke about a
‘symmetrical’ and an ‘asymmetrical’ stance to evaluation and explana-
tion. This was why I chose to call the symmetrical stances causal-
remember Hamlyn’s words: nothing makes them look equal, they just
are so. The correctness of the perception is its own explanation. But if
Hamlyn’s work is a blatant piece of anti-scientific philosophizing, then
so is this:
When a thinker does what it is rational to do, we need enquire no further into the
causes of his action, whereas when he does what is in fact irrationalAven if he
believes it to be rational-we require some further explanation. [P. 189.]13
1 1 D. W. Harnlyn, The Psychology of Perception, London 1969.
12 K. Koffka, Principles of Gestalt Psychology, London 1936, p. 76.
13 L. Laudan, Progress and IISProblems. Towards a Theory of Scientific Gronqth,
London 1977.

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206 David Bloor

Structurally, Laudan's position, quoted above, is identical in its lop-

sidedness to Hamlyn, Ryle or Lakatos. It makes no difference if he
proceeds to call his self-explanatory reasons by the tiante .of 'cause'
because the asymmetry will immediately show itself by a distinction
between two 'species' of cause. We will have rational causes and irra-
tional causes to cope with. I prefer a more uncompromising notion of
causation."
( i i ) The second objection concerns the scientific status of the strong
programme. (There are, I think, some real issues here, notjust a squab-
ble about words.) Again the focus is on the symmetry postulate. How
can it be scientific, asks my critic, to assume apriori that the same kinds
of causal agent are involved in rationally and irrationally held beliefs?
Should not this be a conclusion for which I produce independent evi-
dence rather than something that I treat as a postulate? In fact my
procedure was to move from a brief survey of some current work in the
sociology of knowledge to a statement of the postulates. They were
meant to make explicit what seemed to me good features of the practice
of investigators. I cited some nine pieces of work which did not divide
knowledge into two classes and channel its attention solely onto error.
In other words, I did produce independent evidence, and were I writing
now I would cite twice or three times that number of studies in my
survey.
I think I know why Laudan may have overlooked the role that actual
cases played in the formulation of the programme. He has failed to see
that I am an inductivist. He consistently tries to understand my position
through a haze of deductivist assumptions. For example, he asks: how
could I say that the strong programme is scientific without having aclear
criterion of demarcation? He wonders how on earth we could attempt to
emulate science if we cannot say what features of it are unique? Notice
the very strong verbal bias. It is as if action only seems intelligible to my
critic if it can be made out to follow from stated principles. I have no such
bias. The student of the piano may not be able to say what features are
unique to the playing of his teacher, but he can certainly attempt to
emulate them. In the same way we acquire habits of thought through
exposure to current examples of scientific practice and transfer them to
other areas. Indeed some thinkers such as Kuhn and Hesse believe that
this is exactly how science itselfgrows. Thought moves inductively from
case to case.
My suggestion is simply that we transfer the instincts we have ac-
quired in the laboratory to the study of knowledge itself. Those like
14 Fora fuller account of why I speak of a contrast between causal and teleological styles
ofexplanation. and my reasons for imputingteleological theories to Lakatosandothers
who treat rationality as a self-propelling phenomenon, see D. Bloor, 'Wittgenstein and
Mannheim on the Sociology of Mathematics', Stirdies in History and Philosophy of
Science, 4, 1973. 173-91.

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 The Strengths of the Strong Programnie 207

Laudan who reject the symmetry postulate are trying to stop our induc-
tive intuitions moving from case to case. There are certain cases that
have to be protected. Stop here, they say, think about this in a different
way, acknowledge something as special. So when Laudan asks, “How
can Bloor, who protests against the assimilation of science to the sacred,
be consistent in urging that the only legitimate mode in which to study
science is the scientific mode?’ I reply: you have missed the point. How
could I be consistent if I did otherwise?
(iii) I now come to the heart of Laudan’s attack. Here he offers direct
counter-examples to the symmetry thesis. He argues that, properly
understood, the notion of rationality shows the symmetry requirement
to be misguided. Before stating the alleged counter-examples I must
sound a note of caution. In the course of his argument my critic shifts his
defmition ofrationality. It begins as adescnptive concept but finishes as
an evaluative one, and in the course ofits evolution it also changes its
reference from being a property of an individual to being a property of a
group. I think that Laudan is quite unaware of either the magnitude or
the consequences of this equivocation. In order to cope with this prob-
lem I suggest we distinguish between what may be called ‘natural’ and
‘normative’ rationality. Natural rationality refers to typical human
reasoning propensities; normative rationality refers to patterns of infer-
ence that are esteemed or sanctioned. The one has reference to matters
of psychological fact; the other to shared standards or
The first step in Laudan’s argument is to formulate amodel of rational-
ity. This locates the essence of rationality in the calculation of means-
end relationships. A rational individual has goals and beliefs and com-
putes ways of achieving these goals out of the material provided by
beliefs about the world. (Expressing his verbal bias, Laudan also stipu-
lates that reasons must be statable, but this point plays no significant role
in the argument.) Irrationally held beliefs are those that are adopted or
imposed in the actor in ways that cut across these computations. They
are the result of a disruption in normal thought processes. Reference is
made to the ‘direct action of social and psychological forces’. So threats,
bribes, brain-washing or trauma seem to be what is in mind.
Notice how sparse this model is. It says nothing of the choice of goals
or the character of the prior beliefs. Nor does it specify any standards
whichmust bemet by themeans-end calculations. These would be out of
place in the model. In effect all that it says is that the brain is acalculating
machine. ‘Irrationality’ is a label for when the machine breaks down or is
overridden. None of this is criticism. I am merely stating what is in-
cluded in the model and what is excluded. What we have is a very
elementary representation of man’s natural rationality.
15 1 have taken the term ‘natural rationality’ from S. B. Barnes, ‘Natural Rationality: A
Neglected Concept in the Social Sciences’, Philosophy ofthe Social Sciences, 6,1976,
115-26.

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208 David Bloor

The reason why this is held to be a counterexample to the requirement

of symmetry is because the precise causal story to be told when the
calculating machine is working will be different from when its workings
are disrupted. This is certainly true. But is this really a denial of what is
required by the symmetry postulate? Only ifthat postulate is interpreted
as the demand for identical causal stories for discriminably different
behaviour would this be a counter-example. That is certainly not what I
said.
I would want to reverse Laudan’s judgement. The computer model of
means-end rationality surely satisfies the requirement of symmetry.
The problem of understanding the working and the breakdown of a
machine does not seem to me to hinge on any prior evaluation. Of course
the language of ‘working’ and ‘not working’ embodies an evaluation.
Nevertheless, from the point of view of the general laws and physical
principles involved, whether it be the law of the lever or the laws of
electronics, working and not working are just two of the possible physi-
cal states of a device.
To make the example more realistic let me go back to the procedures
of experimental psychologists. This is the science of natural rationality
because it develops models of our typical cognitive processes. Its
theories fulfil the requirement of symmetry because, despite Hamlyn
and Ryle, psychologists do not offer different accounts for, say, veridi-
cal and illusory percpetion. They offer single models which under ap-
propriate conditions produce the various observed outcomes. Thus
Richard Gregory’s model of perception describes the brain’s utilization
of perspective cues and its mechanism of constancy scaling. He then
shows under what conditions the brzin will be tricked into computing
these conclusions that we call optical illusions of the geometrical kind,
e.g., the Miiller-Lyer arrows.*6If the kind of model of natural rationality
proposed by Laudan were meant seriously it would be devleoped in
exactly the same way. In fact such models which focus on means-end
calculations h a w been explored in great and fascinating detail but not,
of course, by philosophers. The real home of these models is learning
theory and its great exponents are, in their different ways, Hull and
Tolman. It would be pleasant to see rationalists acknowledging
psychologists as the true leaders in their field and reading their works
with the appreciation they deserve.
Now let us see what happens when Laudan’s schematic model of
rationality is put to use in explanations that involve groups of people.
The issue that must be faced here is this. Do all cultures proceed from the
unhampered working of our natural rationality, or do some belief sys-
tems depend upon its systematic distortion if they are to maintain their
credibility? The empirical evidence suggests that all institutionalized
16 R. L. Gregory, Concepts and Mechanisms of Perception, London 1974.

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 The Strength of the Strong Programme 209

systems of belief are compatible with plausible models of natural ration-

ality. Even the belief systems that are at a maximum distance from
western scientific cultures (such as magical cosmologies) do not depend
on any slackeningofmen’s native wit. Anthropological authorities ofthe
stature of Evans-Pritchard attest to this.”
Professor Laudan touches briefly on these topics when he considers
the case of two imaginary social groups, one of which he calls a rational
society, the other an irrational society. In one, beliefs are rendered
acceptable in so far as they satisfy certain shared ‘rules’. The other is an
‘anarchic’ society in which a not of personal preferences is permitted.
Laudan’s main concern is to use this example to show that even if a
sociology of rational belief were possible, it would be different from a
sociology of irrational belief. The very fact that the different cognitive
policies of the two groups is grounded in different forms of social
organization-and hence perhaps caused by different conditions-is
taken to refute the symmetry postulate. This is clearly just a repetition of
the previous mistake. Symmetry is read as identity or, in Laudan’s
words, ‘complete causal homogeneity’.
The fact that such an example has been considered, however, seems
to constitute some small concession to the procedures of the sociology
of knowledge. Indeed Laudan goes so far as to say that he could envision
a sociology of the rational ‘which would be concerned to explain why in
certain cultures certain things counted as good reasons’. Unfortunately,
just at the point at which these interesting themes are being broached the
exposition becomes opaque. The example of the two social groups is
meant to remind us that rationality is not static and that ‘social factors
play a role in shaping the manner in which rationality itself evolves*.
Rationality itself? How can these locutions be squared with the defini-
tion of rationality given by the model of means-end calculation? Laudan
has simply left his definition behind. He has shifted from talking about
natural rationality and has moved on to normative rationality. ‘Rational-
ity’ now refers to the standards which say what counts as a good or
acceptable reason;-Surely, there is nothing in the original model which
really justifies calling the anarchic society less rational than the other.
Their difference simply lies in the standards, or lack of them, that are
imposed on the workings of the means-end calculations of their mem-
bers. Calling one society ’rational* is simply endorsing the standards
used by one group and repudiating those used by the other.
For my part I am as happy to see the word ‘rationality’ used to refer to
a set of standards as to see it used to refer to man’s innate cognitive
competences. I just wish my critic would make up his mind on the
question. For interesting reasons ordinary usage hovers between a
17 E. E. Evans-Pritchard, Witchcraft, Oracles and Magic Among the Azande. Oxford
1937.

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2 10 David Bloor

psychological cum causal reference and a normative cum justificatory

reference, but for theoretical purposes let us keep them apart. If we do
treat reasons as shared standards then we can pursue the programme of
tracking back differences in standards to differences in forms of social
organization-such as Laudan’s degree of ‘anarchy’. But then we will
find that endorsing a set of standards has no role to play in its explana-
tion. Laudan’s calling one of his groups ‘rational’ and the other ‘irra-
tional’ added nothing to his description.
Professor Laudan does not, however, pursue these themes so none of
these points emerge. Instead he makes a sudden retreat back to his
history of ideas approach. He proclaims his faith in what he calls an
‘asociological model of “good reasons” ’. This wretched mongrel of a
concept symbolizes beautifully the muddle between matters of
psychological fact and matters of shared standards that pervades his
work. Since my critic declares himself impatient with anything but a
naturalistic approach, the ‘asociological’ aspect of his model can only
refer to natural rationality. On the other hand, the reference to ‘good’
reasons points towards a concern with normative rationality. Alas, he
cannot have both at once.lB
In order to justify the sudden retreat to a history of ideas which
proudly eschews any foundation in sociology, Laudan then makes a
truly remarkable assertion. He declares that sociologists have yet to
articulate a plausible model for the social grounding of reasoned be-
haviour’. He repeats with emphasis that ‘ n o such model is at hand’. I
have pondered these claims, trying to work out how they could be made
with such confidence. I confess myself baffled. The fact is that there
certainly ore plausible models which show how and why our reasoning
is socially grounded.
To keep the issue simple let me merely state my own preferences on
this question. One way of grounding our reasoning behaviour in society
is to study the way in which it is harnessed to particular social interests.
The ‘interest model’ has been shown to work convincingly and in detail
in a large number of cases. It certainly does not say everything that
needs to be said, but it says a lot. The writings of Barnes, Shapin and
Mackenzie have been prominent in exhibiting the workings of the in-
terest model by relating it to historical material, both through their
original research and through their interpretive surveys of the research
of others.l9
18 As evidence that this confusion is endemic and does not merely represent a momentary
lapse, see the following review of Laudan’s book S. B. Barnes, ‘Vicissitudes of
Belief, Social Studies of Science, 9, 1979, 247-63.
19 As well as the previous references to their work, see B. Barnes, Inrerests and the
Growth of Knowledge, London 1977. D. MacKenzie. Sraristics in Brirain, 1865-1930.
The Social Constrrtcrion of Scientific Knowledge, Edinburgh 1981. S . Shapin, ‘Social
Uses of Science’, in G. Rousseau and R. Porter (eds.). The Fermenf of Knowledge:

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 The Strengths of the Strong Programme 21 1

The examples described above that bear upon the role ofprofessional
vested interests in science hint at the rich supply of exemplars or
model-cases that are available to guide further work. Nevertheless my
critic, with his verbal and deductivist bias, may not count these as real
models at all. He may feel the need for an explicit body of statements
that he can point to as the single, definitive formulation of the model.
Can this further need be met? Yes it can. All that is necessary is to make
reference to Mary Hesse’s ‘network model of classification’ that is
derived from the work of Duhem and Quine and is developed in her
Strrrctirre of Scientific Itr?feretice.20All theories and all systems of
knowledge ultimately depend on systems of classification. Properly
understood this model spells out in detail exactly how and why there is a
social component to’every single classificatory predicate in our lan-
guage.
Essentially the model is built on the fact that predicates are learnt on
the basis of afinite number of instances. These are provided by teachers
or authorities who must simultaneously inform and control the be-
haviour of the learner. The learner’s task is to acquire a sense of the
similarity between the cases to which he is exposed as instances of a
given concept. His sense of similarity and difference must be matched to
those of other language users. This involves grasping the com~entions
which are involved in the judgements about similarity and difference.
One way ofconveying the character of the network model is to say that it
takes Duhem’s arguments so seriously that it represents every act of
concept application as acrucial experiment. Just as decisions are needed
to fix the outcome of every experimental test, so a decision of sorts is
needed about every act of concept application. And just as no
hypothesis can be tested in isolation, so no concept can be used in
isolation from the network of which it is a part. Since language is a
shared practice that can be transmitted to new members of a social
group, the decisions involved in concept application must be systematic
and to a degree predictable. This is what is meant by calling them
conventions. The conventional character of language is what makes the
profound involvement of society a pervasive and inescapable feature of
knowledge.
The particular form taken by the conventions of a classificatory net-
work are the result of what Hesse calls ‘coherence conditions’. This is
the point at which it is most easy to relate the network model to case
studies of the role of social interests in science. The crucial formula is
that social interests are coherence conditions imposed on the clas-
sificatory network. They are factors which determine how new and
Stirdies in the Historiography of Eighteenth-centrity Science, Cambridge 1980. Also,
the very valuable collection of papers in B. Barnes and S. Shapin (eds.). Nurural
Order: Historical Studies of Scientific Citltrrre, op. cit., note 9. above.
20 M. Hesse, The Stritctrire ofScientific Inference. op. cit., note 4, Chapters 1 and 2.

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212 David BIoor

problematic cases will be assimilated into the network. They reveal what
is at stake when the boundaries and scope of a classificatory term are
being negotiated-whether it be a term like Cilia or a term like poly-
hedra.** These are the factors which explain why different groups might
diverge in the way that they extend and articulate their systems or
networks of knowledge.22
In a paper called 'Durkheim and Maws Revisited' I have set out the
network model in a way that is designed to be useful to sociologists of
knowledge.23I have done this by building it up in a step by step fashion
and relating it, on the one hand, to illustrative material from the history
of science and, on the other hand, to the Durkheimean Tradition in
anthropology. When Durkheim and Mauss said that the classification of
things reproduces the classification ofmen, they were nearer to the truth
than their critics have allowed.z4For present purposes the details of the
argument are not as important as the point of principle. The kind of
model I have described, and the kind of connection between society and
reasoning that it indicates are by no means novel. All that is new is the
increased quantity and quality of empirical evidence in its favour. To
21 D. Bloor. 'Polyhedra and the Abominations of Leviticus', British Joitrnal f o r the
History of Science, 11, 1978. 245-71. This is a sociological reading of I. Lakatos'
brilliant book Proofs and Refitations: The Logic of Mathematical Discovery, Cam-
bridge 1976.
22 Hesse's network model was designed, in part, to attack the empiricist idea of an
independent observation language. It explains why all predicates are 'theory-laden' by
showing that they all depend on a negotiable 'network'. But at the same time this
explains why it is correct to equate the theoretical aspect of knowledge with its social
aspect. This is because txamination of the model shows that the network is a set of
conventions.
23 D. Bloor, 'Klassifikation und Wissenssoziologie: Durkheim und Mauss neu bet-
rachtet'. in N. Stehr und V. Meja(Hrsg.), Wissenssoziologie-Studienund Materialen,
Sonderheft 22 der Kolner Zeitschrvt fur Soziologie iind Sozialpsychologie. Opladen:
Westdeutscher Verlag. 1980. An English version will, I hope, be published before too
long. In this paper I develop the ideas fint formulated in my review of Hesse's
Structure of Scientfic Inference, D.Bloor, 'Epistemology or Psychology?'. Studies in
History and Philosophy of Science, 6 , 1975. 382-95.
24 The slogan comes of course from E. Durkheim, and M. Mauss, Primitive Classifica-
tion. trans. R. Needham, London 1%3. p. 11. The material from the history of science
that I have used to illustrate the network model and, in particular, its capacity to
provide anew theoretical underpinning for Durkheim and Mauss's ideas, is taken from
the growing literature on Boyle and Newton's corpuscular philosophy. This work is
one of the best sustained studies in the sociology of knowledge that is currently
available. For a small sample see, for instance: P. M. Rattansi, 'Paracelsus and the
Puritan Revolution', Ambix. 11, 1%3,24-32; P. M. Rattansi, 'The Intellectual Origins
of the Royal Society', Notes and Records of the Royal Society of London. 23. 1%8.
129-43; J. R. Jacob, 'The Ideological Origins of Robert Boyle's Natural Philosophy',
Joiirnalof Eltropeon Studies. 2,1972.1-21. J. R. Jacob, 'Robert Boyle and Subversive
Religion in the Early Restoration', Albion, 6. 1974. 175-93; J. R. Jacob, 'Boyle's
Atomism and the Restoration Assault on Pagan Naturalism', Social Studies of Sci-
enre. 8, 1978. 211-33.

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 The Strengths of the Strong Programme 213

declare that no model is at hand which shows how reasoned behaviour is

socially grounded is simply to display a lack of awareness of a tradition
of work that has long been available. The failure is therefore not one of
sociologists to produce such models, but one of their philosophical
critics to appreciate the significance and potential of an easily accessible
body of literature. But then, there is one important psycho-social law
that everybody knows: that there are none so blind as those who do not
want to see.25
25 I realize. that my critic has shown that he is aware of some of this literature by his brief
discussion of Forman. Shapin and Brown in his book. But instead of putting the cases
that he considers in their proper context, he considers them in isolation and produces
ad hoc responses to them. This is of course always possible, and is simply a technique
for evading the cumulative significance of a growing body of work. This method of
response is well illustrated by his reply to the valuable work that has been done on the
reception of the mechanical philosophy. 'It niight just be that Walter Charleton
accepted the mechanical philosophy because-as he explains in 400 turgid pages-that
theory was rationally preferable to its alternatives' (p. 217). Yes it might, especially if
you make sure that you use an historically relevant criterion of rationality. But when
you have found out what Charleton thought it was rational to take into account, and
when you have explained why Charleton's judgements differed from those of others
around him-and his own earlier views-you will have engaged in the very exercise
that Laudan is criticizing. If. on the other hand, there are ahistoricnl criteria that
explain the changes, then why not give the rival account, rather than just say that it
might exist?

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