Knowledge, Practice and Mere Construction

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682 Social Studies of Science
Responses and Replies (continued)
Knowledge, Practice and Mere Construction
Andy Pickering
The project was motivated by a feeling that the discussions of incommensurability were
locked in problems which were generated more by the framework of discussion, the
ground-rules, than by the phenomenon supposedly under discussion. (Mary Tiles,
Bachelard: Science and Objectivity [1984], xvi)
Philosophers have too often focused on the narrowly intellectual aspects of science...
In this context it is easy to forget that scientific research is also a deeply practical
activity... .Even theory is more practical and craftlike than philosophers usually
recognise. Thus the problem is not the neglect of one part of science (experiment)
in favour of another (theory), but rather a distorting perspective on the scientific
enterprise as a whole. (Joseph Rouse, Knowledge and Power: Toward a Political
Philosophy of Science [19871, x-xi)
Do we prove in the end to be innocent dupes in all this, unwary country bumpkins ...
(R&B, 608)
I. St Louis Blues
The critique by Roth and Barrett (R&B) of Constructing Quarks (CQ)
operates on two levels. ' One is that of explicit argument, as in the third
main section of their essay, where they contest my model of scientific
practice. This level is not very interesting and I deal with it quickly,
mainly in an Appendix. The other level is more diffuse, more that of
insinuating a way of understanding and reading CQ than that of making
a case. I think that R&B's reading of CQ is, in the end, as misguided
as their arguments. But it is more interesting than their arguments, and
elements of it are, I think, widely shared among even sympathetic
commentators on CQ, and on the strong programme in general. The
principal thrust of this essay is therefore to speak to R&B's reading of
CQ and to show why it is wrong. That does not mean that I am about
to quote myself endlessly. I want to be more constructive. CQ's analysis
Social Studies of Science (SAGE, London, Newbury Park and New Delhi),
Vol. 20 (1990), 682-729
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Symposium: Pickering: Response to Roth & Barrett 683
of scientific practice was crude at best, and I seek to refine, elaborate
and extend it here. I want to underpin the original model in a way that
blocks R&B-type readings of CQ and, at the same time, to get to grips
with scientific knowledge and practice better. An outline of my present
understanding bears upon some of the classic philosophical issues that
inhabit or lurk behind R&B's text: I talk about objectivity and relativism,
realism, and the appropriateness (or lack of it) of existing disciplinary
frameworks for studying scientific practice further.
In writing CQ I had two main aims. One was to tell the history of
elementary-particle physics up to and including the establishment in the
late 1970s and early 1980s of the quark/gauge-theory worldview.
Chapters 2 to 13 of the book, which constitute nearly all of the text,
were devoted to this historical account. The other aim was to expound
an interpretative model of what I called the dynamics of scientific practice.
'Opportunism in context' was the slogan here. I set this model out briefly
in Chapter 1 and returned to it in the concluding chapter, Chapter 14.
The two aims were, of course, interconnected. The model of practice
was intended to explain and illuminate the history at issue; the historical
account was intended to exemplify the model, its concepts and their inter-
relations. Now for R&B's critique. The following paragraph, taken from
the early pages of their essay, makes a good point of departure:
Most centrally, all three [Collins, Pinch and Pickering] would consign the explanation
of scientific theory changes to the sociology of science, and not to its philosophy. For,
according to their accounts, when it comes to the decisions of practising scientists,
sociological factors entirely override what philosophers characteristically emphasize
in their idealizations of the logic of science. Whether this is actually so or is no more
than the dream of empire-building social scientists remains to be seen. Our concern
in this paper is simply to show that a good case has not thus far been made. (R&B, 580)
There is a lot going on in this passage, but one aspect of it is easily enough
understood as far as CQ is concerned (Collins and Pinch can reply for
themselves). In the third main section of their essay, R&B develop at
great length an argument that CQ's model of the dynamics of scientific
practice fails in its own terms - that it is 'at best then, a model of stasis
and not of change' (R&B, 613). Hence 'a good case has not thus far been
made' for giving credence to the 'sociology of science', and 'its philosophy'
is left to hold the field. This line of argumentation is faulty in three ways.
First, R&B's argument against my model of practice is itself mistaken
(it hinges upon confusing my discussion of the symbiosis of research
traditions with the model itself). No other commentator has fallen into
this error, and I therefore relegate this aspect of my response to R&B
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684 Social Studies of Science
to an Appendix. Secondly, R&B's argument is at least disingenuous in
dismissing the historical documentation of CQ as 'no central concern of
ours' (R&B, 581), and thus treating my model of practice as pure
theory.2 Even if there were some fatal flaw in my generalizations con-
cerning scientific practice, the historical sections of CQ (I repeat, the
bulk of the book, some 400 pages of text) are, for reasons I expressed
there, refractory in the extreme towards the form of philosophical under-
standing of science that R&B invoke in this paragraph.3 I try to get
clearer on what that form of understanding is as the essay goes on, but
now I should state my third objection to R&B's argumentation. It con-
cerns their implicit suggestion that there is a satisfactory philosophical
scheme for 'the explanation of scientific theory changes' that CQ sought
to displace. To the contrary, I think that such a scheme does not exist.
Even if CQ failed utterly in its self-appointed task, I can see no reason
to assume that its subject matter should revert to philosophy.
So much for R&B's argument. What about their reading of CQ? Here
matters become complex. R&B continually gloss CQ as asserting that
'effectively all of science is free creation', that 'the referents of theoretical
terms in a scientific theory' are 'mere constructs, fabrications in the
imaginations of the scientists who formulate the theory. .. constructs and
nothing more', and so on (R&B, 592, 594-95). These glosses, rather
than the text of CQ itself, seem to be what generate the unwholesome
excitement behind R&B's critique, and some care is required in
unravelling them. It is, of course, true that in CQ I sought to display
scientific knowledge as a 'fabrication', a 'construct'. But how did qualifiers
like 'mere', 'in the imagination of scientists' and 'and nothing more' get
into the act? I certainly did not put them there. To see what is going
on, it helps to go back to the paragraph from R&B quoted above, and
to meditate on its assertion that, according to CQ, 'sociological factors
entirely override what philosophers characteristically emphasize in their
idealizations of the logic of science'. This phrase, together with the
framing of the problematic as 'the explanation of scientific theory change',
and other characteristic locutions that run through their essay, locates
R&B's critique within a particular philosophical tradition. And to get
any further, a brief sketch of the perspective on science of that tradition
is needed. What follows is no doubt crude and debatable, but it is better
than nothing, which is all that R&B provide.
There is a widely shared feeling that science is importantly special.
Other fields of thought - aesthetics, theology, political science, meta-
physics - might be somehow grounded in the history, culture, humanity
of their producers. They might thus display a kind of cultural relativity.
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Symposium: Pickering: Response to Roth & Barrett 685
But science is supposed to be free of the taint of the human; it is supposed
to be objective. And much of twentieth-century philosophy of science
has revolved around the task thus implied, that of explicating the special
objectivity of science. The typical route to such an explication has been
via a series of displacements. First, the objectivity of scientific theory
is located in the control of theorizing by evidence. The nature of this
control is then located in the reasoning faculty of scientists. And finally,
scientific rationality is redescribed as a logic, as a set of rules determining
theory-choice on the basis of evidence. Logic, in this perspective, thus
serves as a kind of rational statics of theory and evidence that guarantees
the objectivity of science. Explication of this logic is the job of philos-
ophers, and the many aspects of scientific practice that fall outside this
job-description are allotted to sociologists and worse.
This, I think, is an adequate summary of the philosophical perspective
that R&B juxtapose to CQ. I say more about some aspects of it in Section
II below, but a few general comments on it and its relation to CQ can
as well be made here as later. First, one can note that this view of science
is very thin. In pursuit of the problematic objectivity, in the philosophical
traditions that adopt this perspective, almost all of the doing of science
is excluded from consideration. That scientists have goals, interests and
desires, craft and tacit knowledge and skills, that they live and work
in the material world and within complex institutional structures - all
of these aspects of science are put to one side in favour of an image of
the scientist as a 'logical' reasoner within a field of theory and evidence.
What one has here is thus an image of science-as-knowledge. This was
not the perspective I adopted in CQ. In CQ, as in all of my other writings,
I sought an understanding of science-as-practice, of science as a way
of being in, getting on with, making sense of, and finding out about the
world. Part of my concern was certainly to address the traditional
problematic of theory-choice, but to do so I found it necessary to take
seriously the material, temporal and social dimensions of practice to
which the philosophical tradition is blind, as well as (not instead of) the
conceptual dimensions to which the tradition is committed.
Thus CQ attempted to get to grips with a phenomenon - science-as-
practice - that can only be partially, at best, represented within a dis-
course on science-as-knowledge. And one aim implicit in this essay is
to urge the virtues of the study of science-as-practice as against those
of the traditional philosophy of science-as-knowledge. I offer no a priori
arguments, but my feeling is this. On the one hand, the science-as-
knowledge image of science is so thin that it bears almost no relation
to its subject matter. The only justification for such an impoverished
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686 Social Studies of Science
vision must therefore lie in the fruitfulness of the problematics framed
within it. But such fruitfulness is conspicuously lacking. No satisfactory
elucidation of 'the logic of science' at present exists, thus the objectivity
of science remains as much of an assumption as it ever was, and the
various sub-problematics spun off from this tradition - including that
of 'scientific realism', which I discuss later - have led nowhere inter-
esting. One is left to conclude, I think, that the continued existence of
this tradition is something of an academic scandal: it talks boringly of
problems constituted in a world of its own making. Conversely, I suggest
that the study of science-as-practice is worthwhile. It speaks immediately
to the found richness of science; it can offer an analysis of theory-change;
it reveals that the objectivity of science is a chimera, but without thereby
reducing scientific knowledge to a 'mere construct'; it offers a new way
of thinking about realism; it does all this by exploring facets of science
rejected from consideration by the philosophical tradition; and in the end,
I believe, it must lead to a radical reconceptualization of what being in
the world is like.
So much for the subtext of my essay. Now back to R&B. One should,
I think, understand their reading of CQ as an attempt to fit a quart into
a pint pot, as an attempt to grasp the analysis of practice in its many
dimensions within the impoverished framework of the philosophy of
science-as-knowledge. In the process, much of the content of CQ just
gets obliterated - especially concerning the temporality and materiality
of practice - while the rest gets distorted. As an example of the latter,
we can go back to R&B's idea that, in CQ, 'sociological factors entirely
override what philosophers characteristically emphasize in their ideal-
izations of the logic of science'. What has happened here is that, in CQ,
I violated the traditional lexicon in speaking a lot about the dynamics
of practice, in contradistinction to the statics of knowledge, and about
sociology, understood in opposition to philosophy. And R&B have got
so excited about this that they read CQ as asserting that 'logic' - meaning
reason, theory and evidence - has nothing to do with the production
of scientific knowledge. What is to be believed is cooked up by scientists
in some social process and then, in effect, projected on to the world.
This is why gratuitous qualifers like 'mere' in 'mere construct' multiply
and propagate through their gloss of my text.
The question arises, of course, of whether R&B have got CQ right
or not here. The answer is no. If I had wanted to call my book Merely
Constructing Quarks I would have done so; that I did not is significant.
There are two ways to make this point. One is brief, but ultimately
unsatisfactory. It is to note that, while I find the word 'logic' a misleading
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Symposium: Pickering: Response to Roth & Barrett 687
word for the process, I did not deny in CQ that reasoned static appraisals
of the relations between theory and evidence were vital to science. I rather
took the position that statics was not enough to explain what was at issue,
and I argued that to understand theory-choice - and much else - it
was necessary to take the dynamics of practice into account. As David
Henderson has recently noted, far from denying that statics had any role
to play, I traded upon a common-sense notion of how the relation between
theory and evidence works in science, sometimes implicitly and
sometimes explicity, as in the frequent references to 'justification and
subject matter' in my analysis of the symbiosis of research traditions.4
So, I could say that R&B are just wrong in their 'mere construct' reading
of CQ - they have done a bad job of squeezing the quart into the pint
pot - and leave it at that. However, with a little imagination R&B could
continue to press me on this point. A thought which lies behind a rather
widespread suspicion of CQ goes, I think, like this.
CQ offers, if the preceding remarks are to be believed, a two com-
ponent model of science. On the one hand, there is a dynamics of practice,
to which attention is continually drawn; on the other hand is a largely
taken-for-granted statics of theory and evidence. Whence a question:
what, if anything, stops the dynamics from overriding the statics? This
is a good question (though instead of asking it R&B assume the wrong
answer). In CQ I did not mean to suggest that dynamics overrode statics,
but neither did I offer any principled argument against this possibility.
This I regard as an important defect of the analysis I offered there, and
I want to take the present opportunity to do better. In Section III of this
essay, I develop an extended model of practice that reduces to that of
CQ in certain circumstances, but in which questions of balance cannot
arise. My aim is a unitary understanding of practice in which statics is
inscribed within dynamics. The key to this model lies in taking the
temporality of practice more seriously than I did in CQ (not less seriously,
as traditional philosophy of science does). This opens a space for a notion
of resistance that was missing in CQ. Recognition of the resistance to
practice that arises in, for example, the material world is enough
definitively to delete the adjective 'mere' from 'mere construct', and thus
to defeat R&B's perverse reading of my book.5
The analysis of scientific practice in Section III is the heart of this
essay. But I want to emphasize that the upshot of this inscription of a
statics of knowledge within the dynamics of practice is not just some
unhappy compromise between philosophy and sociology. To do so, in
Section IV I turn my analysis of practice back upon the defining prob-
lematic of the science-as-knowledge tradition. I argue that my analysis
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688 Social Studies of Science
points not to the objectivity of science as traditionally conceived, but
to a profound relativism and historicism. In Section V, I turn to a sub-
problematic of the same philosophical tradition, realism, and here I argue
that the analysis of practice points towards a fascinating displacement
of the realism debate. The tradition asks about the reality of theoretical
entities appearing within well confirmed theories. Within an analysis that
takes account of the temporal, material and social aspects of scientific
practice, one can ask another question: how does science get its grip
on the world? This seems like the first thing one should think about in
connection with realism, though the science-as-knowledge tradition has
no resources for doing so. I am led to a position I call 'pragmatic realism'
that recognizes that the production and transformation of scientific
knowledge in accommodation to resistance is inseparable from a larger
process of the production and transformation of complex and hetero-
geneous forms of life.
Sections IV and V are, in effect, my response to the second string
of R&B's explicit argument. Besides faulting my model of the dynamics
of practice, R&B are at great pains to suggest that CQ's constructivism
(read 'mere constructivism') was a presumption of my research, not its
conclusion. The second main section of their essay is full of locutions
like, 'To hold that theoretical entities are constructs made by scientists
is, for Pickering, actually tantamount to holding that they are produced
rather than discovered. So, by assuming this from the start, Pickering
has presupposed the most striking and most central of his theses without
having argued for it at all!' (R&B, 596). They are right, in a way. I did
presuppose that knowledge is constructed by scientists - it is, isn't it?
But the point of CQ was not to make this vacuous observation. It was
to address the question of how knowledge is constructed, and it is to
flatter my powers of imagination to suggest that I could have presupposed
an answer to that.6 R&B would have been on safer ground if they had
accused me, not of presupposition, but of stopping thinking too soon.
In CQ I did not attempt seriously to confront my analysis with some
orthodox philosophical positions on which it evidently bore. If I was
doing philosophy in CQ, it was philosophy by example.7 Sections IV
and V then, rectify this omission.
Finally, in Section VI I turn to the question of 'sociology versus
philosophy'. R&B stage their critique of CQ, in the paragraph quoted
above and throughout, in terms of a battle between sociology and
philosophy. Sociology is the upstart that, in the guise of works like CQ,
seeks to overthrow philosophy as the authorized source of knowledge
about science and to proclaim itself 'the new Queen of the Sciences' (R&B,
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Symposium: Pickering: Response to Roth & Barrett 689
581). From within a tradition that sees logic as the subject matter of
philosophy and throws all but this tiny sliver of science to the dogs, I
suppose they have to see things this way. But, as usual, something funny
is going on here. As a matter of fact, of course, a particular group of
philosophers must be held responsible for propagating an impoverished
image of science and for the sterile problematics that go with it. And,
again as a matter of fact, a particular group of people calling themselves
6sociologists of scientific knowledge' can take the credit for opening up
the spectacle of science-as-practice. But these facts are just historical
contingencies. They have nothing to do with disciplinary essences. As
I argue in Section VI, there is nothing to stop people in philosophy depart-
ments thinking about science-as-practice. One of the scandals of
contemporary philosophy of science is its self-righteous refusal to do
so. This is my modest conclusion, which points towards the potential
fruitfulness of interdisciplinary studies of science rather than towards
exclusive disciplinary claims to proprietorship. But I have a stronger
conclusion that is more ambivalent towards prevailing forms of inter-
disciplinarity. It is that scientific practice has its own peculiar integrity
that analyses within existing disciplinary frameworks can only distort.
To catch that integrity, some new framework is needed that crosses estab-
lished boundaries between disciplines. We need a new 'philosophy', to
use the word in its everyday rather than academic sense.
II. Science as Knowledge
Before I come to CQ, I want to clarify some points concerning the
science-as-knowledge philosophical approach to science that R&B seek
to defend. R&B write as though this approach is a viable competitor for
CQ. I will point to some well known reasons for thinking that it is not,
and elaborate on a couple of less well appreciated ones.
The science-as-knowledge tradition has taken many forms in the
twentieth century. The logical positivism of the Vienna Circle and the
falsification of Karl Popper were perhaps its defining moments, but more
recently a considerable range of positions have been developed - the
methodology of scientific research programmes, Bayesianism, cogni-
tivism, and so on - each aiming to spell out and cash in its own version
of the logic of science.8 I am not concerned with the details of these
positions here. As far as a blanket judgement on what they have achieved
in more than fifty years of work, I can just echo R&B's recognition of
the 'absence of accepted philosophical guidelines' (R&B, 579) for theory-
choice, and Arthur Fine's stronger formulation of the same sentiment:
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690 Social Studies of Science
What constructivitism needs to take from philosophy of science are not specific,
established doctrines. It needs only to take the programs of investigation that sought
after general accounts of the structure and dynamics of theories, of observation, of
confirmation, of hypothesis testing, of explanation, of discovery, and so on, and to
note their widely acknowledged inadequacy.9
In general terms, then, there is no 'logical' account of scientific theory-
choice that needed seriously to be driven from the field before CQ could
get to work. But there are two further observations on these various logics
that I want to make here. First, it is significant to note that much of the
present disarray of the science-as-knowledge tradition was precipitated
by the critique mounted in the 1950s and 1960s by Kuhn, Feyerabend,
Hanson, Toulmin, Quine and the shades of Wittgenstein and Duhem.
Drawing upon considerations of the underdetermination of theory by
evidence, the theory-ladenness of observation and incommensurability,
these authors all contrived to suggest that, in one way or another, the
search for a logic that could satisfactorily explicate important instances
of theory-choice was futile. I entirely agree with this conclusion, but
the best known way of putting the argument is deceptive. Kuhn and
Feyerabend, especially, argued for a kind of 'frame relativism'. That is,
they located the problem for 'logic' in the incommensurability of big,
unitary entities - Kuhn spoke of paradigms, Feyerabend simply of
theories. And thus they effectively split the problematic of the philosophy
of science-as-knowledge into two. One problem became that of trying
to find a logic that could bridge the 'rationality gap' that Kuhn and
Feyerabend had opened up, and thus to salvage the objectivity of science
tout court. Popper, Lakatos and more recently Laudan have essayed this
task. The other, lesser, problematic circled around that of articulating
an image of objectivity-within-a-frame. Bayesianism and cognitivism
address themselves, I think, to this lesser problematic, and this seems
to be typical of the attitude of many contemporary philosophers of
science. The overall objectivity of science has been put on the shelf in
the possibly temporary concession that scientific knowledge is relative
to some frame, but the hope is still to rescue objectivity-within-a-frame.
The point I want to make in this connection is a simple one. There is
no reason in the world to think that the line can be held at objectivity-
within-a-frame. Philosophers have predictably pitched their debates at
the level of grand theories, paradigms or whatever. But the historical
evidence on which they have frequently drawn does not require them
to do so. Historically, the evidence that logic is not enough goes 'all the
way down', to borrow R&B's useful phrase (R&B, 598). CQ, for
example, is full of instances - 'no central concern of ours' - small as
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Symposium: Pickering: Response to Roth & Barrett 691
well as great, that logic is not enough at any level. I develop this point
further in the following sections.
I turn now to the question of explanation. R&B think that there is at
least a format for explanation offered by the science-as-knowledge
tradition - its longed-for 'logic of science' - that could, in principle,
do the job that I attempted in CQ (and do it better). I think that, to the
contrary, once it is recognized that what CQ aimed at was 'real-time'
explanation of practice, it becomes apparent that this is not the case.
To see this, suppose that one had what does not exist, a satisfactory logic
of science that everyone could agree upon. What would follow from it
for scientific practice? The answer, as far as I can see, is nothing. It
would, it is true, issue in judgements like: this theory is better confirmed
on the evidence than that one. But so what? Having arrived at such a
judgement, what should one do next? Should one elaborate the better
confirmed theory, try to falsify it, sit on the porch and admire it (William
James's spectator theory of knowledge), try to think of another theory,
or what? And if one picks, say, the first option, how should one elaborate
the theory? It seems to me that anything that deserves to be called a 'logic'
must, as a species of rational statics, be quite silent on such questions.
But these, of course, are just the kinds of question that one has to answer
if one wants to do real-time explanation. I therefore believe that R&B
are wrong in thinking that any 'logic' had to be contested before CQ could
go into action. 1
Of course, the science-as-knowledge tradition in its various incarnations
has been more-or-less aware of this problem of explanation, and one
response to it is relevant here. It is to supplement the statics of logic
with a dynamics. Thus Popper instructs scientists to identify the best
confirmed theory, then develop it in order to probe its weaknesses, attack
them experimentally whenever possible, falsify the theory eventually,
and finally to make bold conjectures towards the construction of the next
victim. Feyerabend recommends constant proliferation of theories. Kuhn
recommends this strategy only in times of crisis. And so on. Now, it
seems to me that these are moves in the right direction. If one is ever
to understand what science is like, that understanding must go beyond
statics to encompass dynamics. Other than that, however, the different
dynamic maxims of Popper, Kuhn, Feyerabend and others have little
to recommend them. All three that I have mentioned, for example, take
it for granted that the history of science is that of a succession of big
unitary entities, theories or paradigms, and relate to how the process
of succession is to be managed. In my discussion of objectivity-within-
a-frame above, I have already sketched a rationale for not conceptual-
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692 Social Studies of Science
izing the history of science in such terms. At a more fine-grained level,
of course, Thomas Kuhn is one of the few philosophers to have moved
from a critique of the philosophy of science-as-knowledge to a serious
attempt at conceptualizing science-as-practice. His conception of normal
science as a process of open-ended, exemplar-based modelling was the
model for CQ's analysis of the dynamics of scientific practice.
III. Science as Practice
Perhaps the single most conspicuous departure of CQ from the
philosophical tradition is that, in CQ, I paid great attention to the dynamic
aspect of scientific practice. I advanced a general schema for thinking
about this dynamics under the slogan of 'opportunism in context'. The
idea was simple enough. Doing science is real work; real work requires
resources; different scientists have different degrees of access to such
resources; and resources to hand are opportunistically assembled as
contexts for constructive work are perceived. My claim, exemplified
many times over in CQ, was that if one understands scientists as working
this way then one can understand, in some detail, why individuals and
groups acted as they did in the history of particle physics. No one has
seriously disputed that this model indeed illuminates the episodes I
discuss. But this is not to say that the model is beyond criticism. Most
evidently, it is very compressed and schematic. It illuminates the episodes
I discuss in CQ, but does not capture their richness. The model has the
more profound failing, however, that it fails to address the 'balance-
problem'. As I indicated in Section I, it is not clear in CQ how my under-
standing of the dynamics of practice fits together with a statics of reason,
theory and evidence, and why, in R&B's terms, 'sociological factors' do
not 'entirely override . .. the logic of science'. This is the problem I address
here by articulating a better model of practice, one in which statics is
inscribed within dynamics. The image of practice that emerges from this
exercise is one that refines and elaborates that of CQ. It underpins rather
than undermines what I said there.
In CQ, I tried to get to grips with a broad sweep of history, and my
analysis of practice was correspondingly coarse-grained. To get clearer
on the nature of practice, and to explore the limits of CQ's understanding
of it, one needs to examine practice in finer detail. If one does so, one
finds, first, that the opportunism-in-context model of dynamics is not
an exhaustive model of practice. It is rather a model of one phase of
practice, namely that of goal-formation. The model illuminates why
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Symposium: Pickering: Response to Roth & Barrett 693
particular scientists embarked upon particular goal-oriented courses of
research in particular circumstances. It does not illuminate what goal-
oriented practice looks like. The gap between goals and their achieve-
ment is elided in CQ.1' This elision is what I focus on in this section,
since it is where the 'logic of science' escaped from an integral role in
CQ's image of the dynamics of practice, and it is where a notion of
resistance to practice can be articulated. But first the process of goal-
formation itself needs some attention.
CQ's opportunism-in-context model offers at best a very crude and
sketchy understanding of goal-formation. Since writing the book, I have
come to see goal-formation as a fascinating and complex process for
which I do not claim to be able to offer a full analysis. What I have to
say here derives principally from working through a single historical
example, but it is sufficient for present purposes.'2
One can start by noting that the formulation of a research goal is an
imaginative act. It is the construction of a possible future state that does
not presently exist. Nevertheless, this future state is not arbitrary. It is
connected somehow to the present, and I was right in CQ, I think, in
locating this connection between present and future in a process of
modelling: futures are modelled on presents.'3 In CQ, though, I failed
to pay sufficient attention to the open-endedness of modelling, to the
fact that a given model can be projected along any number of axes in
any number of ways. This openness of projection is not just a 'philos-
ophical' problem, it is a problem for the actors. And to understand how
it is managed in practice, one has to pay attention to an aspect of scientific
culture that I only gestured towards in CQ, namely its patchiness,
diversity and heterogeneity.'4 To return to a theme that I broached in
Section II, it is a mistake to think of scientific cultures as unitary entities.
Instead they should be seen as supporting and comprising a rich plurality
of elements of knowledge and practice - theories, models, approximation
techniques, many at any given level of abstraction, instruments, work-
styles, institutional arrangements, and so on - standing in all sorts of
relationships to one another, including, often, no relation at all. The
plurality of elements itself constitutes a plurality of models for projection
forwards in time, and this observation is, I believe, the key to under-
standing scientists' management of the openness of modelling. Goals
situate themselves at the intersection of projections of multiple cultural
elements. I give an example of what I mean by this below, but two points
can be made now.
One is that a notion of coherence appears here: in goal-formation,
elements of culture are not projected independently of one another, but
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694 Social Studies of Science
rather towards the point at which they cohere and hang together. Such
coherence, I am inclined to believe, is a constant telos of scientific
practice. And I suggest below that it is in just this form that 'the logic
of science' can be inscribed within a dynamic understanding of
practice. 15 My second point concerns the contingency of goal-
formation. I believe that one can see an underlying general structure to
goal-formation in science, and that modelling and coherence are important
concepts in unravelling that structure. But I do not think that one can
offer causal explanations of goal-formation on this basis. To the contrary,
there seems to be an ineradicable element of chance here. There is an
explanatory gap that I cannot see how to bridge between possessing a
given range of resources and assembling them into a coherent goal. 16
I come back to this point again in my discussion of objectivity and
relativism.
I turn now to the question of what goal-oriented practice looks like,
a question that I did not address in CQ. The best way to proceed is by
example, so let me retell a story I have told at greater length in The Uses
of Experiment. 17 It is a story of the production of experimental fact
rather than of theory-choice per se, but this is all to the good since the
general suspicion of CQ concerning the balance-problem seems actually
to centre on the prior questions it raises concerning the empirical base
of science.'8
For most of the twentieth century, physicists believed that charge was
quantized in units of e, the charge on the electron. But in 1964, Murray
Gell-Mann and George Zweig proposed that, in fact, the building blocks
of the universe were quarks - hitherto unobserved particles that carried
electric charges that were third-integral (either I or 2 e). Out of this
proposal, the Italian physicist Giacomo Morpurgo constructed for himself
a specific technical goal. He would search for quarks in his laboratory
using a scaled-up version of Millikan's oil-drop apparatus to measure
the charges of relatively large samples of matter.19 His goal thus
situated itself, as indicated above, at a projected intersection of three
elements of his culture. First, he had a space of phenomenal models -
possible understandings of how the world might be: either charge was
quantized in integral or third-integral units. Second, he had an initially
vague idea of what material procedure was needed to decide between
these phenomenal models. Back in the 1910s, Millikan had established
the quantization of charge by suspending tiny oil-drops between two metal
plates and observing their motion in response to an applied electric field.
Morpurgo's material procedure was to be modelled upon Millikan's, but
somehow modified to make possible observations on much larger samples
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Symposium: Pickering: Response to Roth & Barrett 695
(since quarks had never been seen, they were presumably rare). And
third, Morpurgo took it for granted that he would use the laws of classical
electrostatics, suitably implemented, to construct an interpretative model
of his apparatus. This model would allow him to read the measured
responses of samples to applied electric fields as indices of their electrical
charges.
As discussed above, Morpurgo's goal was thus defined by the point
at which these three elements of his practice - his material procedure
and his interpretative and phenomenal models - fitted together and
cohered; at which the interpretative model effected a smooth translation
between the material procedure and one of the two contending
phenomenal models. But this harmonious situation was intially both vague
and imaginary. It existed only in thought, as an imaginative projection.
It remained for Morpurgo to find out whether he could achieve his goal
in practice. At this point, Morpurgo began a series of experimental trials
that continued for fifteen years, and discussion of a few episodes will
serve to bring out a pattern. Morpurgo first attempted to suspend his
experimental samples - small grains of graphite - in a liquid, carbon
tetrachloride. This material procedure failed utterly. The samples moved
around so fast and erratically that there was no hope of carefully observing
their response to an applied electric field and hence determining their
charges. Here, I want to say, we have our first exemplification of the
key concept of resistance to practice, arising, in this instance, in the
material world. Morpurgo had no way of knowing in advance that the
liquid-suspension method would fail. One could easily imagine that it
would have worked perfectly, but it did not. Thus the material world
resisted this first attempt of Morpurgo to approach his goal.
Two further general points can be made concerning this rather trivial
episode. First that the resistance Morpurgo encountered was a situated
one. It was situated relative to his goal. If instead of searching for quarks
he had, say, been seeking to observe some features of the interaction
of solid particles with liquids, this method might have counted as a
success, not as a failure. Second, Morpurgo's response to encountering
this resistance was one of accommodation. He revised his understanding
of what was going on to accord with his experience. To be precise, he
revised his interpretative model of the liquid-suspension method. Before,
he had thought of the liquid as simply buoying up the test samples; now
he came to believe that the samples were freely exchanging charge with
the suspending medium. This was why the particles behaved so erratic-
ally, and this was why the liquid-suspension method was unsuited to his
purposes.
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696 Social Studies of Science
Morpurgo then moved to a magnetic-suspension method, suspending
particles of graphite in an appropriately formed magnetic field, and after
a period of largely trial-and-error experimentation he developed a new
material procedure that worked - one in which it was possible to observe
systematic responses to electric fields applied to the test particles. He
could thus begin to make observations that would lead to conclusions
on the existence of quarks. In the first observation deploying this pro-
cedure he found something odd. The grain under observation moved in
the same direction when the direction of the applied field was reversed.
This behaviour was unaccountable under Morpurgo's existing inter-
pretative model of how the apparatus worked, but he found that, under
a revised interpretation, he could understand it in terms of nonuniformities
in the applied electric field (previously assumed to be uniform). Under
the revised interpretation, this first grain proved to carry integral charge,
as did the five which followed, and in 1966 Morpurgo published the
fact that he had established the absence of quarks on these grains. Once
more, we can understand this sequence of events in terms of a dialectic
of resistance and accommodation. The motion of the first grain initially
constituted yet another situated resistance arising in material practice to
the achievement of Morpurgo's goal. And, as before, Morpurgo accom-
modated himself to this resistance in a revision of his interpretative model.
This time, though, the revision led to the achievement of his goal. The
three elements of his practice that had once, imprecisely conceived,
cohered in his imagination now cohered in detail in his practice: his
revised interpretative model now did effect a smooth translation from
his most recent material procedure to one of his possible phenomenal
models - the no-quark variant.
Some discussion of this mundane passage of scientific practice is appro-
priate. The first point to note is that just as resistances are situated and
unpredictable, so are successful accommodations to them. Morpurgo had
no way of knowing in advance that having encountered the unexpected
motion of the first grain he would be able to repair his interpretative
model in such a way as to emerge with the coherence he desired. He
may never have found such an interpretative model. At this stage, as
at all others, his experiment could simply have failed.20 Again, an
element of contingency, analogous to that of goal-formation, appears
in the process of accommodation.21 My second point is that one can see
in this example how CQ's balance-problem is to be solved, but this needs
more explanation.
Consider the situation when Morpurgo had achieved coherence between
the three elements of his practice, his material procedure and his two
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Symposium: Pickering: Response to Roth & Barrett 697
conceptual models. This was the point at which he could first feel rela-
tively confident that he knew something: that there was not a quark upon
the grain he was examining. And this confidence derived from the fact
that the achieved coherence could be phrased as an argument, a reason
to believe in his findings: on the basis of this material procedure and
this interpretation he had reason to believe that no quark was present
in this instance. Inasmuch, then, as 'logic' is a traditional shorthand for
the offering of reasons and arguments in science, to speak of coherence
here is, as indicated earlier, a way of explicating the 'logic of science'
(not of denying it any role). Beyond this, one can see how achieved
coherence functions, like 'logic', as a kind of statics of knowledge. When
the three elements of Morpurgo's practice were incoherent, there was
always something more for him to do. The achievement of coherence,
in contrast, marked a static limit to practice. Achieved coherence is the
place where practice can rest and findings can be reported. However,
I have already argued that coherence is not just a static attribute of a
particular limit to practice. It should instead be seen as a telos, running
through practice right up to the moment of goal-formation. And thus
'logic', construed as achieved coherence, is not something that lies apart
from the dynamic aspect of practice, that one hopes might come after
and check the dynamic, 'sociological' aspects of practice, but that one
fears, with R&B, might become an optional extra to be overridden by
'sociological factors'. In the example of Morpurgo, one can see that the
search for coherence is constitutive of practice in its full temporality,
and thus that no balance-problem of statics and dynamics can arise.
Recognition of the temporality of practice in terms of a goal-oriented
dialectic of resistance and accommodation thus makes it possible to
inscribe a statics of reason and knowledge within a dynamics of practice
and to solve the balance-problem of CQ. To see coherence as a telos
of practice is to see that the balance-problem is a fake.
Having sketched out this solution to the balance-problem, a further
point needs to be discussed. I have suggested that my notion of coherence
bears upon the same issues in the statics of knowledge that the philosophy
of science-as-knowledge has sought to catch in a 'logic'. The question
thus arises of whether an equation of 'coherence' with 'logic' as
traditionally conceived would be useful. Oddly enough, the answer to
this question does not matter very much as far as the remainder of this
essay is concerned. When I come to discuss objectivity, realism and
disciplinary divisions of labour, I will emphasize the situatedness and
contingency of practice along the lines already indicated, and the 'logical'
properties of coherence will be largely irrelevant to my conclusions. It
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698 Social Studies of Science
may be useful to go a little further, though. My feeling is that one should
not attempt to reduce coherence to logic, if by 'logic' one refers to a
set of content and context-free rules for the association of propositions.
Obviously, such a logic could not apply to the non-propositional, material
dimension of Morpurgo's practice.22 But even if one focusses just on
the propositional aspect - articulated observations, interpretations,
findings - 'logic' still seems wrong. Better as indicated above, I think,
to see the coherence that Morpurgo sought as constituting a 'good'
argument within the framework of classical electrostatics for the existence
or nonexistence of quarks, and to see such arguments as themselves
modelled in an open-ended fashion upon exemplary instances found in
textbooks and the research literature. This, of course, is a line of thought
articulated in Kuhn's Structure of Scientific Revolutions.23 It seems to
me to point towards a fine-grained analysis of scientific argument to which
traditional 'logics' could never aspire and, moreover, to a degree of
situatedness and open-endedness at the very place where the philosophical
tradition has looked for transcendence and fixity. But, as I say, my
subsequent discussion does not depend upon how one attempts to cash
in the notion of coherence, so I return to the discussion of Morpurgo
and his experiments. This will help to fill out my present understanding
of practice and to give substance to the following sections of the essay.
Morpurgo's first no-quark publication marked only a temporary limit
to his practice. He continued making observations, and the seventh grain
he examined was peculiar. Its charge was 'one fourth (or with "some
goodwill".. . one third)' of e - that is, it looked as if it might carry a
quark. Morpurgo continued examining grains, and found that several
carried peculiar charges, neither integral or third-integral. It looked as
if charge might not be quantized at all. But then he found that if he
changed his material procedure he could get sensible results. On widening
the separation of the metal plates he found that all of his grains appeared
to carry integral charge. Making sense of this finding through a revision
of his interpretative model - again revolving around non-uniformities
in the applied field and imperfections in the test samples - he published
in 1972 his new findings, to the effect that he had been unable to detect
quarks on a relatively large quantity of matter. This sequence of events
leading up to Morpurgo's second publication is reminiscent of that which
led up to the first. Initially, a resistance arose in Morpurgo's material
practice. The coherence between material procedure and interpretative
and phenomenal models was broken by the apparent observation of non-
quantized charges. One can note once more that this resistance was
situated relative to Morpurgo's goal: if he had been prepared to find non-
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Symposium: Pickering: Response to Roth & Barrett 699
quantized charges, it would not have counted as a resistance at all, it
might instead have counted as an important result. But, in this passage
of practice, Morpurgo's accommodation to resistance took the form of
a contingent revision of his material procedure, in the first instance, rather
than of his interpretative model. Tinkering with his apparatus, with no
guarantee of future success, Morpurgo found that widening the plate
separation led to the production of credible findings. Only subsequently,
and again contingently, did Morpurgo find that he could accommodate
this discovery in a revised interpretative model, and thus once more arrive
at a relation of coherence between the three elements of his practice that
could sustain a new publication of his findings.
This pattern - the finding of anomalous results followed by revisions
in material procedures and interpretative understandings - was repeated
over the years. Thus, in the mid-1970s, beginning a more powerful and
sophisticated version of his experiment on samples of iron, Morpurgo
found charges that varied with time, until he revised his material
procedure, making measurements on spinning instead of stationary
samples, when constant and integral charge measurements emerged. This
behaviour was understood in a further revision of Morpurgo's inter-
pretation of his apparatus. Continuing with this same version of the
experiment, Morpurgo once more began to find non-integral (and non-
third-integral) charges, until he yet again revised his interpretative model
of his apparatus, revealing integral charges once more. The pattern was
constant: the emergence in material practice of situated resistances,
contingently accommodated in revised material procedures and inter-
pretations, and always with the same upshot: the absence of quarks on
ever increasing quantities of matter.
This is as far as I want to take my discussion of Morpurgo's experi-
ments. The important points have been made. I have analyzed Morpurgo's
work in terms of a set of concepts that can, I think, form a more adequate
basis for a general understanding of scientific practice than that of CQ,
an understanding that can take the temporality of practice seriously. I
have identified CQ's model of the dynamics of practice as a crude model
of goal-formation in science, and I have indicated how the model could
be further refined. Goal-formation should be thought of as a process of
modelling organized around a telos of coherence within a heterogeneous
and patchy culture, a process that has structure but to which contingency
remains endemic. Further, I have gone beyond CQ in analyzing what
lies between goals and their attainment in terms of a concept of resistance.
Again, I have stressed the contingency and situatedness of resistance.
And I have argued that goal-oriented practice needs to be understood
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700 Social Studies of Science
in terms of situated accommodations to resistances as they arise, with
no advance guarantee of success. All of this seems to me to be right;
with only straightforward modifications I believe that one can analyze
and illuminate any number of instances of practice within this conceptual
frame. Here, then, we have an understanding of scientific practice that
can at once underpin the model of the dynamics of practice put forward
in CQ - it reduces to the latter if one seems to explain successful practice
at a low level of temporal resolution - while, as I have explained, it
solves the balance-problem of CQ by inscribing the statics of knowledge
within an analysis of the dynamics of practice: the pursuit of coherence
runs through practice; it is not some optional extra that could, for
example, be sacrificed to 'sociological factors'.
So, the only serious problem that R&B might have raised concerning
CQ has been solved, and in what follows, therefore, I will assume that
the way of accounting for scientific practice just sketched is fully general.
My goal in the remainder of the essay is to ask how such an analysis
of practice relates to the problematics of objectivity and realism, and
how it bears upon the possibilities for disciplinary analyses of science.
Before moving on, though, I had better clear up some points of potential
confusion concerning my Morpurgo example.
First, I have spoken repeatedly of resistance as arising in material
practice. This is appropriate in this instance - Morpurgo had a vision
of what he wanted to accomplish, and was continually frustrated in trying
to carry through the material dimension of his project. But there is a
symmetry here that needs to be brought out. I noted that the resistances
that Morpurgo encountered were situated with respect to his goals, and
this points more generally to a constitutive interplay between the material
and the conceptual, social and whatever dimensions of practice. The
easiest way to see this is to consider the accommodation to resistance
that Morpurgo never made in the course of his experiments. He never
once questioned the fact that charge was quantized, despite the fact that
his experiments, straightforwardly interpreted, frequently pointed in this
direction. If he had questioned the quantization of a charge, of course,
he would have run into another axis of resistance - the resistance of
his colleagues, mobilized as arguments in favour of the orthodoxy of
charge quantization. Charge quantization was, in effect, a 'fixed point'
of Morpurgo's culture, and resistance to modification of this fixed point
was a constitutive precondition of the resistance he encountered in the
material world. A similar comment applies to Morpurgo's continually
changing electrostatic interpretation of his experiment. Here, in a more
complex fashion, one should see Morpurgo as threading his way through
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Symposium: Pickering: Response to Roth & Barrett 701
incipient culturally conditioned resistances to his various interpretative
models. This is why he did not act as if he were free simply to tailor
his interpretations to whatever results he wanted to find. What follows,
then, is that one should not think of practice as evolving in accom-
modation to resistances arising solely in the material world. One should
think instead symmetrically, of resistances as arising in attempts to
engineer coherence across otherwise disconnected elements - material,
conceptual, social - of a heterogeneous and patchy culture. This remark
will be of importance when I come to discuss the question of realism.
It also points to the possibility of analyzing theoretical and mathematical
practice within the conceptual framework I have sketched.24
The second qualification I want to enter concerning my Morpurgo story
is that it has, at least as I have told it so far, an untypical simplicity.
Morpurgo found a way to thread his way through all of the resistances
he enountered without treading on anyone's toes. In producing his findings
on the absence of quarks in his laboratory, he reinforced the received
wisdom on the quantization of charges without challenging existing lore
on how to perform Millikan-type experiments, how to apply the laws
of classic electrostatics to them, and so on. But, even in this instance,
the appearance of a smooth accumulation of knowledge and technique
is deceptive. After all, in reporting the absence of quarks, Morpurgo
was in effect challenging a straightforward interpretation of Gell-Mann
and Zweig's quark proposal. Thus Morpurgo's practice cut across that
of Gell-Mann and Zweig, and hence laid the foundations for a new set
of goals, circling around the problematic of how quarks could be both
real and unobservable.25 One should, I believe, think of all practice as
potentially involving this destabilizing aspect, wherein particular local
coherences - such as those achieved by Morpurgo - are bought at the
price of introducing incoherences elsewhere - thus creating a space for
further goal-oriented practice. And, to return to the traditional philos-
ophical problematic, one should think of theory-choice (as well as the
production of facts, phenomena and instruments) as emerging from the
complicated interplay thus set in motion.26
IV. Objectivity and Relativism
The defining aim of the philosophy of science-as-knowledge has been
that of displaying the objectivity of science, its freedom from the taint
of the human. The means to that end has been the attempted articulation
of a 'logic of science' - ideally a set of content- and context-free rules
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702 Social Studies of Science
determining the conditions for acceptance or rejection of theory on the
basis of static comparisons with evidence. In Section II, I set out some
reasons for not holding one's breath until a satisfactory logic was forth-
coming - including the admitted and long standing lack of success in
articulating such a logic, the well-known historical and philosophical
arguments that point up the difficulty of the project, and the fact that
it is hard to see how any rational statics could explain theory-choice in
a meaningful sense. In Section III, in contrast, I outlined a conceptual
framework for understanding scientific practice that can, I claim, explain
theory-choice and much else about science. What happens if one turns
that framework back upon the original philosophical problematic? What
becomes of objectivity within the understanding of science-as-practice
offered here?
Objectivity vanishes. On my analysis of practice, the philosophy of
science-as-knowledge has been pursuing a chimera for years. Even
though my analysis incorporates a teleological principle of coherence
that runs through and structures practice, and that marks successful
practice as the accomplishment of a harmonious set of static interrelations
between cultural elements, the upshot of the analysis is as relativistic
as can be, and possibly more so. The pursuit and achievement of co-
herence - and the production of knowledge that coherence sustains -
is, I claim, radically situated. The taint of the human is etched into the
body of knowledge in at least two ways. First, there is a kind of radically
situated structure to practice. Thus goal-formation has to be seen as
dependent upon a process of modelling that ties imaginary futures back
to concrete and particular presents. Whatever culture is now structures
whatever it might become. Beyond that, the pursuit of goals itself brings
forth resistances - resistance- that are themselves situated with respect
to the situated goals in question. And beyond that, the uncertain process
of accommodation to resistance is itself trebly situated: with respect to
the particularities of the resistances encountered, with respect to the
context within which the accommodations are made and, of course, with
respect to the defining goals.27
Thus, even at the level of goal-formation and the dialectic of resistance
and accommodation, where one can discern patterns and regular structure
to practice, one can see that future knowledge production is intimately
and irrevocably tied to the culture in which it is produced and which
it is produced from. This, it seems to me, is an inescapably relativistic
perspective on science. I can imagine no way in which scientific
knowledge could somehow float free of practice thus described. If the
objectivity of science is not somehow given in advance in its very foun-
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Symposium: Pickering: Response to Roth & Barrett 703
dations - and it would require some new argument to show that it was
- I cannot see how it could ever be achieved. And the prospects for
such an achievement become gloomier still if one moves from the level
of structure to that of contingency. Throughout Section III I pointed to
the contingency - the sheer chanciness - of scientific practice. There
is an element one cannot explain in goal-formation; the resistances that
emerge in pursuit of goals cannot be foreseen or understood in advance;
the possibilities for, and contours of, successful accommodations to resist-
ances are likewise contingently discovered. This means that in telling
the history of science, one has in the end to say - more and more often
as one looks in increasingly fine-detail - 'it just happened'. It just
happened that the seventh grain Morpurgo examined seemed to have a
charge of one-quarter or one-third; it just happened that widening the
separation of two metal plates made such anomalous findings go away;
it just happened that Morpurgo was able to construct an acceptable
account of this discovery within the framework of classical electro-
statics.28 And so on, for ever and ever. Explanation comes to an end.
Thus we arrive, by a more circuitous but also a more satisfying route,
at the conclusion that Barry Barnes has long argued: that culture does
not determine the contours of its own extension.29 One can see patterns
in the extension of culture. That is what I have offered an analysis of
here. But the patterns are not enough to determine. The future is shot
through with contingency and chance in becoming the present. And, to
return to a topic I raised in Section II, this observation is enough to put
paid to any residual hopes of articulating a vision of objectivity-within-
a-frame - or frame-relativism, to put the emphasis differently. Even
if one imagined that scientific culture was some unitary thing - a
paradigm or whatever - it would remain the case that no set of rules,
no 'logic', could hope to contain the sheer chanciness of the evolution
of scientific culture. What follows, then, is an ultra-relativistic image
of science, in which the appropriateness of the term 'relative' itself starts
to seem doubtful. As far as the structural regularities of practice are
concerned, it would seem to make sense to speak of knowledge as
knowledge relative to the culture of the scientific community that has
produced it. But once one admits contingency as endemic to the
constitution of knowledge, this structured relativity gets diluted towards
relativity to chance, which is relativity to nothing. It might be better at
this point to stop speaking of relativism at all, and to speak instead of
the full-blown 'historicity' of science - a historicity which goes 'all the
way down' - as a way of acknowledging that facts and phenomena,
concepts and theories, as well the instruments and institutions of science,
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704 Social Studies of Science
all owe their existence and character to a genuinely historical process.
They are bound to the wheel of what happened.30.
At any rate, whatever form of words one chooses, the conclusion of
this phase of the argument is that the objectivity of science, as tradition-
ally conceived within an understanding of science-as-knowledge, is dead.
Or, at least and put more circumspectly, that resort to something other
than a 'logic of science' is needed to bring it back to life. However, it
is worth noting that if 'objectivity' in this philosophical sense is dead,
one can easily resuscitate it in an everyday sense.31 The picture I have
sought to paint of goals, resistance and accommodation is hardly one
of 'free creation'. It is a picture in which the brute difficulty of producing
anything that might conceivably count as knowledge is thrown into sharp
relief - much sharper relief than is achieved in any disembodied
discussion of the 'logic of science' and comparisons of theory with evi-
dence. The more I think about it, the more monumental becomes
Morpurgo's achievement in his single programme of experiment. And
more monumental by far becomes, say, the production of the entire new-
physics worldview with which I was concerned in CQ, with all of its
theories, models, interpretations and instrumentation eventually arranged
and circulating within a relatively coherent community-wide constellation
of practices. To draw attention to the radical historicity of the new
physics, as I did in CQ, it is not to represent the new physics as some
kind of collective projection of beliefs on to the world. But to appreciate
this one has to think of science as practice as well as knowledge.32
V. Realism
The primary problematic of the philosophy of science-as-knowledge has
traditionally been that of explicating the objectivity of science through
articulation of a logic of theory-choice. But various subsidiary problem-
atics have run alongside this one, including a debate over scientific realism
that has flourished as attempts to understand theory-choice have them-
selves gone into decline. I want now to clarify how CQ and, especially,
the analysis of scientific practice sketched out in Section III, might bear
on this latter problematic.
The standard philosophies of realism and antirealism are framed within
the traditional view of science-as-knowledge. The problematic is that
of whether reason gives us access to the real, or, put more prosaically,
whether (some or any) unobservable entities appearing in well-confirmed
(whatever that means) theories should be seen as (approximately) cor-
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Symposium: Pickering: Response to Roth & Barrett 705
responding to items of the furniture of the world. Scientific realists answer
that they do so correspond; antirealists deny this. The arguments put
forward on each side are clever and ingenious but, speaking as an
outsider, one has to note that a pall of unreality hangs over the whole
scene. The realists have the intuition of practising scientists on their side,
but they face an insuperable obstacle: how to get at the furniture of the
world independently of science, as is necessary if the correspondence
of theory is to be determined in any direct fashion. This is an impossible
task, and thus the realists fall back on various indirect arguments, often
hinging on the idea that science progresses. For all of these arguments,
though, the antirealist seems able to find a counter. Scientific intuition
is on the side of the realists but the antirealists have the arguments. And
thus what has ensued seems to be a dreary stalemate, in which the best
defended position is a deflationary 'not realism and not antirealism
either'.33
Now, how might an analysis of science-as-practice weigh into this
debate? R&B read CQ as asserting that theoretical entities are 'mere
constructs, fabrications in the imaginations of scientists', and so on, and
they accordingly understand CQ as an attempt to come down as heavily
as possible on the side of scientific antirealism. But I have been at pains
to explain why talk of 'mere constructs' in connection with CQ is perverse,
and I have laid out an understanding of practice that makes such a reading
not just perverse but impossible. How, then, does this latter understanding
- which, as I have said, underpins the analysis of CQ - bear upon
the question of scientific realism? In the first instance, I have to say that
the answer is not clear to me. Scientific realism (and its negation) rep-
resents a retrospective judgement that belief in the correspondence to
reality of this or that theoretical entity is somehow warranted, whereas
my analysis of practice aims at real-time explanation. The two enterprises
are disjoint in their conception, and I have only the most tentative thoughts
on what an appropriate retrospective gloss on my understanding of
practice would be.34 I postpone those thoughts to the end of this section
because, as it happens, I am more inclined to talk about a way of thinking
about realism that is framed quite differently from that of the current
philosophical debate.
By focusing upon well-confirmed theories, the traditional realism
debate tries to explore the connections between articulated knowledge
and the material world when those connections have already been made.
This is the way that it has to be within the philosophy of science-as-
knowledge. But within an analysis of science-as-practice that can
represent within itself the temporal, material and social dimensions of
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706 Social Studies of Science
science, one can constitute a problematic prior to that of scientific realism,
a problematic that also deserves to come under the heading of 'realism'
on any reasonable usage of the term, though it is quite different from
the traditional one. One can ask how the connections between knowledge
and the world are made. One can, in particular, begin to examine the
specifically material dimension of the engagement of science with the
world, a dimension which is systematically obscured in understandings
of science-as-knowledge.
The example of Giacomo Morpurgo's quark-search experiments can
serve again to address this new problematic of realism. The first point
to stress is that the history of Morpurgo's experiments reveals a continuing
and intimate engagement with the material world, an engagement con-
sisting in resistances arising in material practice - the constant frustration
of his plans when realized in material form - and in accommodations
in material practice to such resistances - the widening of the separation
of the plates in one instance, spinning the samples in a later one. This
dialectic of resistance and accommodation in material practice surely
justifies calling the resulting picture of scientific practice a realist one.
But, I repeat, 'realist' here means something different from 'realist' as
it appears in the standard realism debate. It points to a constitutive role
for 'reality' - the material world - in the production of knowledge,
but it carries no necessary connotation of correspondence (or lack of
correspondence) for the knowledge produced.
One can take this line of thought further. In his struggle against resist-
ances, Morpurgo was, as I put it in CQ, 'tuning' his material procedures
against the production of credible phenomena.35 Nothing in his existing
culture instructed Morpurgo how exactly to set up his apparatus. 36 His
task was to learn how to stand with respect to the material world - to
learn what might count as a proper material performance - in his own
uncertain and open-ended interaction with the world. This, it seems to
me, is a fascinating discovery about the material practice of science, and
one that it is unspeakable within the science-as-knowledge tradition. It
becomes even more fascinating if one recognizes both the omnipresence
of the tuning of material practice and the frequency of 'retunings' in the
history of science. In exploring the history of particle physics, for
example, I was struck by how many episodes hinged upon significant
shifts in how experimenters stood with respect to the world. The
importance of gross and subtle changes in material procedures was a
major component of what I tried to convey in my discussion of the
incommensurability of the old and new physics in CQ.37 Needless to
say, it was lost on philosophers of R&B's stripe, who think that the sole
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Symposium: Pickering: Response to Roth & Barrett 707
thrust of my analysis and argument concerned changes in interpretative
practice.38 Of course, I was interested in these interpretative shifts, too;
I will now bring them into the discussion.
So far I have tried to motivate a kind of 'pragmatic-realist' under-
standing of scientific knowledge and practice by stressing the material
engagement of scientists with the world in a dialectic of resistance and
accommodation. But I emphasized in Section III that this material engage-
ment does not proceed independently of the nonmaterial elements of
practice. The resistances that are at the heart of material engagement
are themselves situated with respect to such non-material elements -
goals, theories, models, facts, what have you. Whence it follows that
'we never go away'. Scientists' engagement with the material world is
never unmediated and direct: it has always to be understood as con-
ditioned by the culture within which it takes place, and as reacting back
upon that culture. Morpurgo's repeated revisions of his interpretative
model of his apparatus - conceptual rather than material tunings - can
stand as an emblem of the latter. And thus, in getting to grips with the
realistic aspect of scientific practice, one has to think of a complex process
of reciprocal and interdependent tunings and refigurings of material
procedures, interpretations and theories - all in the face of situated
resistances spanning a multitude of dimensions - rather than of the tuning
of material procedures alone. Further, one needs to add to the picture
a concomitant tuning and refiguring of social entities and their relations
- as in my discussion in CQ (406-07) of the making and breaking of
symbiotic relations between research traditions, old and new. And so
on: work-styles, institutional forms and more are all progressively
implicated in this process as one examines higher and higher levels of
aggregation. What shifts and responds to the material world in science,
then, is not simply knowledge or material practice. It is rather a set of
heterogeneous elements - only some of which I have just listed'- that
sometimes come together in a loose and fragile unity one could call a
'form of life'.39 On a large scale, the old and new physics discussed in
CQ constitute, in all their dimensions, examples of such forms of life.
My argument is, then, that from an examination of practice one can
approach the question of realism from a new and interesting angle. One
can obtain some appreciation of how the connections between scientific
knowledge and the world are forged. It is a realistic picture, since it
acknowledges a sensitive engagement in material practice between scien-
tists and the world. This engagement is the point at which scientists
maintain their purchase on the world and the world maintains its purchase
on them. But nevertheless, it is a picture in which 'we never go away':
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708 Social Studies of Science
within forms of life, facts, phenomena, material procedures,
interpretations, theories, social relations, etc., are, in Latour's word
(borrowed from Marx) 'coproduced'.40 Much more thought, study and
argument could be devoted to this pragmatic realism than I can offer
here. But enough has been said, I think, to indicate that attention to the
forbidden zone of the philosophy of science-as-knowledge - to the
temporal, material and social aspects of practice - can serve to constitute
a rich and promising problematic centred on the relation of scientific
knowledge to the world. This, as I stressed at the start, is not the same
problematic as that at the heart of the traditional realism debate in
philosophy. And no doubt the safest thing to do at this point would be
to leave it at that - to say, here are some new problems connected with
realism that are interesting to think about and that are just different from
the old ones. But, to return to my earlier remark, I want to close by
noting that one might be able to generate a further set of interesting
problems in a confrontation of pragmatic and correspondence realism.
A challenging way to start thinking about this confrontation would be
to note that within pragmatic realism observable facts and phenomena,
as well as theoretical entities, have to be seen as constituted within a
form of life. Thus the observable/unobservable distinction at the heart
of classical debates on correspondence is erased. And this erasure seems
to push one towards an all-encompassing antirealism about scientific
knowledge in general: facts and phenomena now seem less secure than
scientific antirealists think, rather than theory seeming more secure.41
Conversely, however, the acknowledgement of a constitutive role for
the material world in the maintenance and evolution of a form of life
pushes one in the opposite direction. Getting a viable grip on the world
is a non-trivial achievement, and I cannot see why, after the fact, one
should not see such an achievement as pointing to a degree of corre-
spondence between the structure of the real world and empirical and
theoretical knowledge of it. On the other hand again, the non-uniqueness
of scientists' grip on the world - manifest in shifts such as that between
the old and the new physics in the history of elementary-particle physics
- suggests that to maintain a correspondence perspective consonant with
pragmatic realism one needs to think of the structure of the material world
as fundamentally more complex than any particular scientific account
of it. It is no good imagining that the world is pretty much as scientists
represent it today, and that the progress of science consists in just approxi-
mating itself better to that structure. One thus arrives by this route at
a notion of correspondence that depends upon a very rich conception
of the structure of the world. (The furniture metaphor has to go, for
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Symposium: Pickering: Response to Roth & Barrett 709
a start.) Some of Ian Hacking's writings on the equivalence of any
relativism with a suitably framed realism seem to point in the direction
of this line of thought - but I can take it no further here.42
VI. Sociology versus Philosophy?
It should be evident by now that my analysis of practice jumbles a lot
of categories that are customarily held to be distinct. I close by reflecting
upon the consequences of this for disciplinary practice. R&B are very
keen on discipline. They see CQ as the site of a battle between Sociology
and Philosophy, where I capitalize the names to emphasize the essentialist
tendency of R&B's writing. For them there seems to be just one Philos-
ophy of Science, with its single goal of rescuing Objectivity in a 'Logic
of Science'. Likewise there is a single Sociology of Scientific Knowledge,
again with its one aim of reducing knowledge to The Social (very
narrowly conceived, as I explain in the Appendix). They take CQ to
be a prominent, but fatally and typically flawed, exemplar of the latter.
I can see no grounds for this disciplinary essentialism.43 I think R&B
are just wrong here. The tension that underlies R&B's essay should, I
believe, be seen as that between the particular philosophical approach
to science (with a small 'p') that I have called the philosophy of science-
as-knowledge and the different approach of CQ that takes scientific
practice as a unitary subject of enquiry. I want now to discuss how well
my image of practice maps on to existing disciplinary boundaries. The
answer is, not very well at all.
The subtitle of CQ is A Sociological History of Particle Physics. This
was rather forced upon me by the publishers - I wanted 'The Road to
Unity in Particle Physics' as a more expressive formulation and as an
oblique reference to the old Hope, Crosby and Lamour films. But I make
no apologies for the suggestion in the title and throughout the book that
I was doing sociology. I was studying the evolution of an almost con-
temporary culture, which is an acknowledged topic of that discipline.
A question that can be raised, though, is whether I was doing just
sociology. I think not. My model of practice - as expressed in CQ and
as elaborated here - seems to me to touch upon the legitimate interests
of a variety of disciplines: sociology, certainly, but also psychology,
cognitive science, anthropology and even, to return to R&B, philosophy.
Concerning the last of these, I can see no reason whatsoever why people
working in philosophy departments should stick to the played-out
problematics of science-as-knowledge. The objectivity of science there
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710 Social Studies of Science
presupposed does not exist; the search for a 'logic of science' that could
display that objectivity has run philosophers into the ground; the debate
over scientific realism is moving the same way; and, more generally,
the tradition's violent inipoverishment of its ostensible subject matter
becomes more evident with every day that passes. Apart from petty
disciplinarity, then, nothing stands between philosophers of science and,
for example, the problematic that I sketched out under the heading of
pragmatic realism. They would not have to accept my name for it, my
formulation of the problematic, or the particular analysis of practice that
underlies it. They would have only to admit that there is something inter-
esting to be learned from a study of scientific practice, as opposed to
that of Knowledge and Reason alone. To repeat my earlier remarks: there
is no essence of Philosophy that was challenged in CQ; the scandal is
that so many philosophers, the likes of R&B, continue to speak, write
and act as if there were.44
My minimal conclusion is thus the obvious one. Scientific practice
is an extremely rich and multifaceted topic for enquiry, ripe for inter-
disciplinary study from within all of the existing disciplines mentioned
above, and more. Many students of these disciplines, of course, have
known this for some time, and the philosophy of science-as-knowledge
should perhaps simply be exhibited as a curiosity from a bygone era.
But there is a stronger conclusion that I feel like drawing, one that owes
a lot to Bruno Latour.4s Though interdisciplinary study of science is
clearly a step in the right direction, I wonder how far one can go within
any of the existing disciplines. My suspicion is that scientific practice
has its own unity and integrity that cuts very deeply across present
disciplinary boundaries. Thus, on my analysis, scientific culture is
situated and evolves right on the boundary, at the point of intersection,
of the material, social, conceptual (and so on) worlds. It is not in any
one of them in particular. And thus the deployment of existing disciplinary
concepts and categories is liable to produce a serious misunderstanding
of what science is like. These concepts and categories have typically been
formulated and refined with an eye to the delineation of autonomous
disciplinary subject matters, and the danger of insensitivity to the nature
of phenomena at disciplinary boundaries is evident. I do not know
whether it is inevitable, but the upshot of disciplinary analyses of science
has typically been the construction of disciplinary master-narratives in
which a schema drawn from a single discipline constitutes an explanatory
backbone around which all else revolves.46
Such disciplinary master-narratives, I feel, are what we don't need.47
To get to grips with scientific practice as a unitary subject matter, it would
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Symposium: Pickering: Response to Roth & Barrett 711
be better to work with concepts and categories that span the dimensions
that disciplines hold apart - the material, the conceptual, the social and
so on. Unfortunately, the truly remarkable fact about such concepts is,
of course, that of their present non-existence. Even everyday language
enforces the distinctions one needs to erase. It is very hard, for example,
to speak of 'culture' without contriving the appearance that one is speaking
of a unitary something proper to us and somehow separate from the
material world. One can try speaking of 'material culture', which brings
in the realm of objects, but natural facts and phenomena still seem to
stand outside the domain of reference. This difficulty lies behind a recent
proliferation of jargon in the study of practice. 'Forms of life', 'actor
networks', 'cyborgs' are all concepts that seek to span the boundaries
that disciplinary and everyday thought seek to preserve.48 An
evolutionary epistemologist would probably remark that if these
boundaries are so well entrenched they must have a lot going for them.
I prefer to look at things the other way around. To break down such
well entrenched distinctions promises a radically new view of the world.
? APPENDIX
The ABC Model
The crucial positive assertion of R&B's critique of CQ is that the model
of the dynamics of scientific practice I developed there is untenable.
Actually, two claims are intertwined in R&B's essay: that the model
simply fails, and that it fails as causal explanation. I address these claims
in turn, starting with the former.
In CQ, I set out my understanding of the dynamics of scientific practice
under the heading of 'opportunism in context'. I explained what was at
issue in general terms - along the lines indicated in Section III above
- and I claimed that the model explained and was exemplified in
countless episodes in the history of physics. R&B are not interested in
these many exemplifications - 'no central concern of ours' - but, they
say, the general explanatory schema fails. After a long discussion, they
conclude that '[Pickering's] account is, at best then, a model of stasis
and not of change' (R&B, 613). I would regard this charge as fatal if
it could be upheld, but it cannot. I need to rehearse a bit of R&B's
argument' to show this. R&B begin thus:
[CQ's] analysis of the dynamics of research practice is embedded within an account
of theory change in which Pickering advances the following three-stage model:
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712 Social Studies of Science
(A) A symbiotic (circular and self-reinforcing) relation between theory and
[experimental] practice obtains ..
(B) A rift in this symbiotic relation occurs.
(C) Opportunism in context dictates how the rift is resolved. . (R&B, 610).
Having summarized my model thus, R&B belabour the obvious: the 'ABC
model' leans heavily upon the notion of symbiosis (point A); at the same
time it alludes to a fact that is crucial to CQ, that symbioses are from
time to time broken and reformed on new bases (points B and C); but,
and this is the crux of R&B's argument, the model contains no resources
for explaining the breaking of symbiosis. Thus, if the ABC model explains
anything, it must be stasis and not change. Therefore my model of
practice cannot do what it claims, which is to explain the evident changes
in scientific knowledge and practice that CQ is about. The logic of the
argument is impeccable, though R&B manage to spin it out for twenty-
one pages of manuscript before reaching a climax in their assertion that
'[p]erhaps the easiest way out for Pickering lies in his pulling back,
granting that an essential premise of his showpiece explanation is false
and acknowledging that there is no symbiosis as he has pictured it' (R&B,
624).
There is, however, an easier way out. It is to notice that the first
sentence of R&B's critique is backwards. My analysis of the dynamics
of practice is not embedded in any three-stage model that centres on a
notion of symbiosis. It is the other way around. Symbiosis, as I used
the term in CQ, is just one possible upshot of the dynamics of practice.
The opportunism-in-context model of the dynamics of practice is the
primary explanatory device of CQ, and that model is quite indifferent
to the making or breaking of large-scale symbioses. It is true that in CQ
I first explained what I had in mind in referring to 'opportunism in context'
by talking in the abstract about the symbiosis of research traditions (CQ,
10-12), but I immediately continued (CQ, 12-13):
In discussing the development of established traditions, then, my primary explanatory
variables are the shared material resources of experimenters and the shared expertise
of theorists. However, there remains the problem of accounting for the founding of
new traditions and the first steps towards the establishment of new phenomena. Such
episodes are not to be understood in terms of the gross distribution of shared material
resources or expertise, but they pose no special problems because of that ... The only
difference between my accounts of the development of traditions and their founding
is that to discuss the latter I move, perforce, from the macro-level of the group to
the micro-level of the individual. I aim to show that the founding of new traditions
can be understood in terms of the particular resources and context of the individuals
concerned, just as the elaboration of those traditions can be understood in terms of
the shared resources and contexts of the groups involved.
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Symposium: Pickering: Response to Roth & Barrett 713
This paragraph, from the introductory chapter of CQ, explicitly
contradicts R&B's ABC reading of my model of practice. It expresses
my belief that the opportunism-in-context model of practice could explain
practice at the individual level, and my intention to demonstrate this
whenever necessary - that is, whenever distinctive breaks in established
patterns of practice ('the founding of new traditions') were at stake.49
R&B actually quote the key sentence concerning )particular resources
and context' immediately before they lay out their ABC model (R&B,
610), but it seems to me to make completely untenable their claim that
the ABC model has any relevance to CQ at all. There is no reference
to symbiosis in my discussion of individual practice, and none was
intended. R&B could try to hang on, I suppose, by claiming that the
paragraph is an idle cog in the mechanism and refers to rio instances
in my historical account -- or, more wildly, that the founding of new
traditions has nothing to do with the breaking of symbioses. Given that
the historical aspect of CQ is 'no central concern of ours', neither of these
moves seems likely but, to be on the safe side, I will quickly indicate
that they fail. To take the example that R&B discuss in the third section
of their essay, I will talk about the history of electroweak unification.
I argued in CQ that a key event in the history of particle physics was
the renormalization of gauge theory by Gerard t'Hooft in 1971. This event
gave rise to several new traditions of theoretical practice, including those
devoted to the construction and elaboration of unified electroweak models
and to QCD, the gauge theory of the strong interaction. Because these
traditions were so important, I paid considerable attention to explaining
their origins in the work done during the 1960s by Martin Veltman,
t'Hooft's supervisor (CQ, 173-80). 1 documented and discussed Veltman's
work, beginning with his dissertation research, moving through his
attempts to relate this research, on the one side, to properties of the weak
interaction and, on the other, to the work of a few other theorists on
questions of the renormalizability of massless gauge theory, and ending
with his development of the technical apparatus that t'Hooft used to show
the renormalizability of so-called spontaneously broken gauge theory.
All of this discussion was framed within the parameters of my oppor-
tunism-in-context model, but I was quite clear throughout that it was
Veltman's particular resources and context that were important in under-
standing what he was up to. No reference to symbiosis appears in this
passage, and there are many others like it.50 And yet what I offered is
undeniably an analysis and explanation of dynamics and change, not just
of stasis. R&B are simply wrong on this point.
So, my promise in the introduction to CQ to explain the dynamics of
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714 Social Studies of Science
practice at the individual level, independently of any ABC-type model
of symbiosis, was not an idle cog. For R&B's benefit, though, I had
better reconnect the story of Veltman and t'Hooft with the story I did
tell of the breaking and remaking of symbiosis. t'Hooft's demonstration
of the renormalizability of gauge theory constituted, I argued, a site for
the recycling of shared expertise in renormalizable field-theory technique
(note the move towards an aggregated level of analysis here). This
recycling lay at the origin of the growth of the gauge-theory traditions.
One particular tradition was that which aimed at the articulation of
realistic unified models of the electroweak interaction. And this is where
a mismatch arose with traditions of experiment. As it happened, the
unified models that were developed required the existence of some entity
that was unknown to experiment - either the weak neutral current or
heavy leptons. Thus the profitable symbiosis of theory and experiment
that sustained non-gauge-theory understandings of the weak interaction
was interrupted at a key point with respect to the gauge-theory tradition.
As I argued in CQ, this symbiosis was re-established in an even more
profitable form in the discovery in neutrino experiments of the weak
neutral current.51 My argument was, then, that to understand this
passage in the history of particle physics one has first to understand the
practice of Veltman, t'Hooft and others at the individual level. This
practice led up to the renormalization of gauge theory, which as a site
for the recycling of shared expertise, gave birth to various gauge-theory
traditions. Here it becomes possible and appropriate to move to a more
macro-level analysis (and thus to save many pages of explanatory text).
The growth of one of these traditions precipitated a breakdown of
symbiosis with experimental traditions bearing upon the weak interaction,
a breakdown that was healed in the discovery of the neutral current. This
is a story of change, not stasis, and I continue to claim that it is a story
that can be explained in terms of the opportunism-in-context model of
the dynamics of practice. And, to go back to R&B, it is clear that their
ABC model catches only a miserable part of my explanation. R&B have
misunderstood the explanatory framework of CQ.
Before leaving this topic, it might be useful to enquire why R&B make
the mistake of thinking that the notion of symbiosis lies at the bottom
of my analysis of practice (instead of at the top). The answer is probably
simple, and returns to the discussion of Section VI above. R&B are
fighting a boundary dispute over property rights to science.52 They want
to make clear what belongs to Philosophy and what to Sociology, and
it is in their conception of the nature of these two disciplines that the
problem arises. Since they never spell out in their text or through citation
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Symposium: Pickering: Response to Roth & Barrett 715
just what they mean by 'philosophy' and 'sociology', it is hard to speak
precisely here. It is clear, though, that their conception of 'sociology'
is much narrower than that of CQ. 'The social', for R&B, seems to be
what is directly and visibly social, right on the surface. It is people dealing
with one another more-or-less directly. It is the 'merely social'.53 Thus
they describe CQ as offering 'an account of how certain socio-political
interactions among the scientists involved give rise to this production
[of the world]' (R&B, 591). And thus, for R&B, most of my account
of practice, though they have apparently read it and can even retell bits
of it, cannot be part of a 'sociological' explanation of the history of particle
physics. This explains why, for example, they assimilate my analysis
of the history of the renormalization of gauge theory to their ABC model
(R&B, 616-23), despite the fact that much of that analysis is devoted
to the work of Martin Veltman that I have just reviewed as a
demonstration of the irrelevance of the ABC model. Since Veltman's work
was relatively solitary and idiosyncratic, my explanation of it cannot be,
as far as R&B are concerned, part of a 'sociological' explanation of the
history of particle physics. It also explains why R&B only seem to latch
on to my history of the renormalization of gauge theory at the point where
I start discussing the symbiosis eventually achieved between gauge
theorists and neutrino experimenters. Symbiosis - the interaction of
groups of scientists - is sociological right on the surface so, for R&B,
this must be the crux of my 'sociological' explanation. And hence the
travesty of the ABC model: the foundations of my model of practice slip
through the net, and only grossly sociological concepts like symbiosis
remain for R&B to tie up in knots.54
R&B's assertion that CQ's model of the dynamics of practice is at best
a model of stasis is, then, a simple case of mistaken identity in an imagin-
ary boundary war. The ABC model which they hunt down and destroy
is their own creation, predicated on an extremely narrow conception of
'the social', not mine. But besides their correct diagnosis that the ABC
model fails to explain change, R&B also develop a second line of attack
upon this hapless creature. As I indicated above, they fault it for not
being a causal explanation: to quote one of many such instances, as they
thrash the ABC model, they exclaim that my analysis 'is merely to assume
in advance, and without the hint of proof, the causal efficacy of social
factors' (R&B, 620). I could just say 'who cares?' about this presumed
deficiency of an imaginary model. But I want to confess that if R&B
had pressed this aspect of their critique against the model that I actually
proposed in CQ, I would have been forced to plead guilty. As I have
sought to make clear in the present essay, I think that the pursuit of causal
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716 Social Studies of Science
explanations of scientific practice is misguided. There is structure there
to be conceptualized, but there is contingency, too, and there is no way
of ridding explanation of the latter.55 I know that in David Bloor's 1976
statement of the four tenets of the strong programme the first was that
'the sociology of scientific knowledge ... would be causal', so it is not
surprising that R&B thought that they must somehow be on to a winner
in at once setting CQ up as an exemplar of the strong programme, and
then pointing to its lack of causality.56 All that I can say is that they
were wrong. Perhaps this means that I am not a real strong programmer
after all - and neither is Harry Collins, for instance. My own resolution
of this tension is to be no more essentialist about the strong programme
than about sociology or philosophy. Unlike Groucho Marx, if the strong
programme will have me I will be happy to be a member.
* NOTES
This material is based in part upon work supported by the US National Science Foundation,
History and Philosophy of Science Program, Grant No. DIR-8912095. For helpful comments
and discussion of this paper, I would like to thank Davis Baird, Robert Batterman, David
Bloor, Steve Fuller, Jan Gorecki, Ted O'Leary, Barbara Herrnstein Smith, David Stump,
Peter Winch and members of the University of Illinois History, Philosophy and Sociology
of Science Seminar.
1. Paul Roth and Robert Barrett, 'Deconstructing Quarks', Social Studies of Science,
Vol. 20, No. 4 (November 1990), 579-632; Andrew Pickering, Constructing Quarks:
A Sociological History of Particle Physics (Chicago, IL & Edinburgh: The University of
Chicago Press/Edinburgh University Press, 1984). Page references in the text and notes
are to Roth and Barrett's article and my book.
2. The passage from which the quotation is taken goes as follows:
There are two sustained enterprises that intertwine throughout Pickering's book and
vie with one another for the role of its primary focus. One is a detailed historical narrative
[that is] ... highly informative. Since it is no part of the common cause joined by the
other strong programmers, however, it is no central concern of ours, and we allude
to it only peripherally. (R&B, 580-81)
It is clear that some funny business is in store. The manoeuvre of pointing to the particularity
of the subject matter of CQ can be applied to any of the case studies associated with the
strong programme, and has the effect of turning them all into works of pure theory that
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Symposium: Pickering: Response to Roth & Barrett 717
can be criticized as such. Since a central 'common cause' of the 'strong programmers' is
that the way to understand science is through empirical study and since, indeed, a large
part of the fascination of the strong programme lies in its empirical findings, this is like
pretending that one can sensibly criticize quantum mechanics without mentioning black-
body radiation, atomic spectra or the photo-electric effect.
3. The pecular effects that R&B can achieve by turning an empirical study into pure
theory are at their most spectacular in the third section of their essay. Here they intersperse
quotations from my account of the development of electroweak gauge theory with locutions
like 'Suppose that these [the factors that led to the disruption of the old-physics weak-
interaction symbiosis between theorists and experimenters] should turn out to be factors,
such as recalcitrant data, of the kind philosophers of science have long emphasized' (R&B,
614); 'But, as sketched above, the account of the initial change reads suspiciously like
the standard philosophical account Pickering has been at such pains to malign' (R&B, 617);
'Thus, as he sees it, it was a social factor... and not the alleged conceptual force of
't Hooft's evidential results, that was the key to the change' (R&B, 621); and so on. Several
unjustifiable presuppositions are being insinuated by R&B here. The entire thrust of the
documentation of Chapter 6 of CQ was that the 'initial change' that led to the breaking
of the weak-interaction symbiosis was a programme of theoretical work culminating in
't Hooft's proof (which cannot be sensibly called an 'evidential result') of the renormaliz-
ability of spontaneously broken gauge theory, and that 'factors, such as recalcitrant data,
of the kind philosophers of science have long emphasized' had nothing to do with the genesis
and development of this programme. That R&B have failed to understand what is at issue
becomes crystal clear in their assertion that 'the authority of Lee and others (supplementing
the disruptive experimental results) is supposed [in CQ] to prove decisive and overcome
the symbiosis' (R&B, 622). Gauge theory, as developed by 'Lee and others', flew in the
face of, rather than supplemented, contemporary 'experimental results': the theory was
straightforwardly false on the basis of the data then existing. Only by treating the historical
subject matter of CQ as not just 'no central concern of ours', but as no concern at all,
could R&B have allowed themselves to write as they do here. Their supposition that 'the
standard philosophical account' might be adequate to this phase of the historical development
of particle physics is their fantasy and nothing more.
4. David Henderson, 'On the Sociology of Science and the Continuing Importance of
Epistemologically Couched Accounts', Social Studies of Science, Vol. 20, No. 1 (February
1990), 113-48. Henderson's reading is much closer to the spirit of CQ than is R&B's,
though I find his notion of 'epistemic values' as misleading as R&B's 'logic' - see section
III - and he fails to grasp the 'balance-problem' outlined in the next paragraph. The first
reference to 'justification and subject matter' in CQ is on p.10.
5. The problem of balance alluded to here is, in a way, a classic problem within the
strong programme around which cluster the endless discussions of 'the sociology of error'.
David Bloor and Barry Barnes both got to grips with this problem long ago, in a way
that parallels that which I develop here. See, for example, the entries under 'Manichaean
mythology' in the index to Barry Barnes, T. S. Kuhn and Social Science (London: Macmillan,
1982). Neither Barnes nor Bloor, however, sought to develop the kind of analysis of practice
that I aim at, so I cannot simply resort to a stock response.
6. Connected with their diagnosis of my presuppositions is R&B's repeated attempt
to read CQ as advancing the 'methodological thesis' that 'logical and epistemological consider-
ations traditionally invoked by scientists to account for the acceptability of scientific theories
are inadequate to that task, if not entirely irrelevant to it' (R&B, 581). The only methodo-
logical thesis that informed CQ was that one should explain as much as possible, that one
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718 Social Studies of Science
should keep asking why for as long as possible. My perception of the inadequacy of the
'scientist's account' is one product of this latter method; it was not presupposed. R&B seem
to think that what appears in the first chapter of a book is temporally and logically prior
to the contents of later chapters; this was not the case with CQ.
7. Despite R&B's attempt to treat CQ as a failed philosophical tract, I was very clear
there that my explicit arguments were directed against what I called 'the scientist's account',
and not against any worked-out philosophical position. R&B do, of course, make great
play of the couple of footnotes where I did explicitly mention philosophy of science,
especially the 'inexhaustibly solecistic passage' (R&B, 607), the footnote (CQ, Chapter
1, fn 9) to which they devote five pages of their manuscript. There I said that 'almost
any philosophical position would serve as a foil for this argument'. I stick by this, though
now I would be more precise and specify the science-as-knowledge philosophies as those
to be opposed. Where R&B go wrong is in thinking that the argument against such traditions
is already spelled out in CQ. To see how the argument would go one has to do some work,
and especially to think about the empirical instances of knowledge production that I discuss
- 'no central concern of ours'. It is hard to believe that in their very long essay R&B
have only two critical points to make (this one concerning my presuppositions, and the
one already mentioned concerning the intrinsic failings of my model of practice) - but
as far as I can make out, this is the case.
8. Note that I list here the science-as-knowledge traditions that have retained a concern
for logic, objectivity and so on. These are the traditions I address in the present essay.
A more interesting variant of the science-as-knowledge approach survives in the writings
of philosophers including Quine, Goodman, Putnam, Rorty, Davidson, Feyerabend and
Hanson, all of whom are willing to explore the relativistic implications of their positions
to some extent. Typically, these philosophers make some minimal gesture towards science-
as-practice in attempting to account for theory-choice, but their unwillingness to go very
far in this direction leaves them in some awkward positions. Thus Rorty's pragmatism,
for example, ends up reducing practice to a vague notion of 'conversation' - a softened
and relativized version of the science-as-knowledge view that he otherwise opposes -
and his prototypical actor becomes the poet rather than, say, the scientist. (In empirically
inclined research, discourse analysis, the reflexivity programme and studies of the rhetoric
of enquiry likewise fall into the trap of letting the philosophy of science-as-knowledge
define the parameters of debate, as if the statics of knowledge were all that matters.)
Similarly, Goodman wants to emphasize the open-endedness of 'world-making', but in trying
to defend the idea that there are better and worse ways of world-making his only resource
is to the 'standards' and 'criteria' of traditional philosophy. His distinctive twist on standards-
talk is to note (like Feyerabend) that standards hang together with substance in world-
making, but this seems to cut the ground from under his own feet. The analysis of practice
developed in Section HI gets around this dilemma by substituting situated notions of resistance
and accommodation for non-situated standards. See note 26, below, for more discussion
of making arguments 'better'.
9. Arthur Fine, 'Science Made Up: Constructivist Sociology of Scientific Knowledge'
to appear in J. Margolis (ed.), Realism (Princeton, NJ: Princeton University Press), 5
(in draft).
10. An interesting slide concerning explanation seems to have taken place between the
logical positivists and their successors, hinging on the notion of 'reconstruction'. As I
understand it, the logical positivists aimed at a reconstruction of the contemporary exact
sciences along the lines in which Frege and Russell had reduced mathematics to logic.
This straightforward sense of logical reconstruction did not carry any connotations of
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Symposium: Pickering: Response to Roth & Barrett 719
explaining how, say, relativity theory had been histotically constructed: it was an after-
the-fact process. More recent reconstructions have lost any such fastidiousness, most notably
in the hands of Imre Lakatos who first reconstructs history and then counts his reconstructions
as exemplars of explanation. But Lakatos's 'explanations' are vulnerable to the argument
sketched above: research programme A is more progressive than programme B: so what?
It seems to me that the most Lakatos can explain is why scientist A gets out of bed singing
at dawn and scientist B wakes at noon with a hangover. In short, I disagree with R&B's
assertion that 'it very much mattered that [Pickering] argue againist serious, current, viable
philosophical positions that pose a threat to his own view ... he appears to have refrained
from shouldering this necessary burden, and thus to have forfeited the game for failure
to compete in it at all' (R&B, 608).
11. A problem of writing 'Big History'is that one is almost forced to focus upon instances
of successful practice and to pass quickly over the details of such practice. A good antidote
to this skewing of perspective is, of course, ethnographic study, in which one takes practice
as one finds it. What follows here is particularly indebted to Karin Knorr-Cetina's ethno-
graphic study, 7he Manufacture of Knowvledge: An Essav on the Constructivist and Con-
textual Nature of Science (Oxford & New York: Pergamon, 1981), especially Chapter 3.
12. A. Pickering, 'Openness and Closure: On the Goals of Scientific Practice', to appear
in H. Le Grand (ed.), Experimental Enquiries, Australian Studies in the History and
Philosophy of Science (Dordrecht: Reidel). This study analyzes Luis Alvarez's decision
in the early 1950s to attempt to build a large liquid-hydrogen bubble chamber for particle
physics experiment.
13. In CQ, I particularly emphasized the importance of modelling in theory development
but, as my analysis of Alvarez and the bubble chamber (ibid.) should make clear, I think
that modelling is, in fact, constitutive of all forms of practice.
14. In CQ, I pointed to the existence of three broad and relatively distinct categories
of practice in particle physics (experiment, phenomenology and theorv), I emphasized the
plurality of traditions within each category, and I discussed the symbiotic relations sometimes
existing between those traditions. I now want to extend the image of patchiness and
heterogeneity, both to a much finer level within the traditions I discussed in CQ, and to
a much broader range of practices.
15. I should emphasize that coherence in the abstract is not enough to define a goal.
There is a second constitutive but situated aspect of goal-formation to which I cannot do
justice in what follows, the aspect of circulation. In all of the instances I can think of,
scientists have aimed at a product that will somehow move and circulate other elements
of culture and that will itself move and circulate. This is an idea that is strictly unavailable
within unitary understandings of scientific culture, but that becomes crucial to an under-
standing of practice once the fragmentation of culture is recognized. I discussed circulation
under the heading of symbiosis in CQ; Bruno Latour, in Science in Action (Cambridge,
MA: Harvard University Press, 1987) speaks to similar concerns with notions such as
'inscription' and 'immutable mobiles'. How best in general to conceptualize circulation within
the complex cultural space of science seems to me a very difficult question, though I find
the use of concepts such as 'vortex' in Michel Serres, Hermes: Literature, Science, Philosophy
(Baltimore, MD & London: Johns Hopkins University Press, 1982), very suggestive.
16. See Pickering, op. cit. note 12, and A. Pickering, 'Models in/of Scientific Practice',
Philosophy and Social Action, Vol. 13 (1987), 69-77. To give a simple and stylized example
of what is at stake here, in Chapter 4 of CQ I sought to explain George Zweig's formulation
of the quark model within an existing tradition of group-theoretic explorations of hadron
systematics. Zweig's key move was to imagine that the 'fundamental representation' of
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720 Social Studies of Science
the group SU(3) referred to physical particles - quarks - rather than to purely mathematical
entities. Given that higher representations of the group were themselves routinely construed
as referring to physical particles - the known hadrons - this move does not seem, after
the fact, very surprising or perplexing. Nevertheless, Zweig need not have made it. And
this remark remains true however closely one examines Zweig's resources and context:
at some time he had the idea of quarks as real particles while, at some adjacent but preceding
time, he did not. If one were so inclined, one might, I suppose, look forward to some
future neurophysiological theory as a means of causally explaining Zweig's transition between
these two states. But such a theory would add little to any real-time explanation of his
practice: it would amount to asserting that Zweig came up with the quark concept because
we think that way. At present, it seems to me that there comes a point in explanation where
it is best to say that 'it just happened'; that, for example, it just happened that Zweig tried
to give a physical interpretation to the fundamental representation of SU(3). I return to
this idea in Section IV.
17. A. Pickering, 'Living in the Material World: On Realism and Experimental Practice',
in D. Gooding, T. J. Pinch and S. Schaffer (eds), The Uses of Experiment: Studies of
Experimentation in the Neutral Sciences (Cambridge: Cambridge University Press, 1989).
275-97. See also my 'The Hunting of the Quark', Isis, Vol. 72 (1981), 216-36.
18. The locus classicus for such suspicion has become my account of the discovery
of the weak neutral current (CQ, 180-95), as I discussed at greater length in 'Against Putting
the Phenomena First: The Discovery of the Weak Neutral Current', Studies in History
and Philosophy of Science, Vol. 15 (1984), 85-117; see also my 'Editing and Epistemology:
Three Accounts of the Discovery of the Weak Neutral Current', in L. Hargens, R. A.
Jones and A. Pickering (eds), Knowledge and Society: Studies in the Sociology of Science,
Past and Present, Vol. 8 (1989), 217-32. The neutral-current discovery hinged upon shifts
in interpretative and material experimental procedures, and my argument is that these shifts,
and the discovery to which they gave rise, should be understood within the context of
the contemporary development of electroweak gauge theory. Several authors have offered
R&B-type 'mere construct' readings of this argument. Thus Yves Gingras and S. S.
Schweber, in their Essay Review of CQ, 'Constraints on Construction', Social Studies of
Science, Vol. 16 (1986), 372-83, and Peter Galison, in How Experiments End (Chicago,
IL & London: The University of Chicago Press, 1987), read my account of the discovery
as asserting that theory-choice is cooked up in a quite extra-empirical process and then
projected on to the world of experiment. The analysis of experimental practice given below
blocks such readings, but leaves my argument intact. To return the compliment to Galison,
I should say first that I find his historical accounts of scientific practice fascinating. Second,
that he makes the same mistake as R&B when he reads CQ as asserting that experimentation
is reducible to 'a calculus of interests' (ibid., 258) - read, 'the dynamics of practice': I
deliberately stopped using the word 'interest' long before I wrote CQ - at the expense
of acknowledging any force of what he calls 'persuasive argument'. 'Persuasive argument'
is Galison's softened, historicized and sociologized equivalent of the philosopher's 'logic',
and can easily find a place in the analysis of practice sketched out below. And, again,
Galison makes the same mistake as R&B in thinking that a statics of 'persuasive argument',
any more than a statics of 'logic', is enough to explain scientific practice. I discuss the
way in which the dynamics of practice is backgrounded in Galison's historiography, and
the correspondence-realist presuppositions that I think underpin his accounting strategy,
in my review of his book, Isis, Vol. 79 (1988), 472-73. and, at greater length, in 'Editing
and Epistemology', op. cit. above.
19. For some background on Morpurgo's route to the formulation of this goal, see CQ,
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Symposium: Pickering: esponse to Roth & Barrett 721
117, fn 32. Again, an elerir-ait of contingency enters here: Morpurgo was an elementary-
particle theorist, and his move into experiment was unprecedented.
20. I thank Malcolm Nicolson for reminding me to stress this point.
21. Note that after-the-fact glosses to the effect that Morpurgo had now got his
interpretative model right and that quarks do not in fact exist are of no use to real-time
explanation of his practice: such glosses are the products of practice, not its explanation.
22. The temptation to read 'coherence' as 'logic' disappears when what is at stake is
the construction of an instrument per se rather than the production of articulated fact -
as, for example, in Alvarez's work on the hydrogen bubble chamber (Pickering, op. cit.
note 12). Here, the primary sense of 'coherence' has to be the harmonious functioning
of the various parts of the instrument - the chamber, cryogenics, optics and photography,
safety devices, and so on. One sees here an irnportant connection between the notions
of coherence and circulation (see note 15 above): a significant criterion of the material
coherence of Alvarez's chamber was its success in effecting a circulatioln, first between
the silent world of beams and particles and the articulated world of data and representations,
and then within various fields of practice in particle physics.
23. T. S. Kuhn, The Structure of Scientific Revolutions (Chicago, IL: The University
of Chicago Press, 2nd edn, 1970), Chapter 5, 'The Priority of Paradigms'; R. N. Giere,
Explaining Science: A Cognitive Approach (Chicago, IL & London: The University of
Chicago Press, 1988), especially Chapter 3. Galison's situated notion of 'persuasive argument'
continues the same line of thought: see note 18 above.
24. For an analysis of mathematical practice along these lines, see A. Stephanides and
A. Pickering, 'Constructing Quaternions: On the Analysis of Conceptual Practice', to appear
in A. Pickering (ed.), Science as Practice (Chicago, IL: The University of Chicago Press).
On the need for a symmetric understanding of the evolution of heterogeneous systems,
see Latour, op. cit. note 15, 144.
25. The tension between the growing centrality of quarks to elementary-particle theory
and their continued nonobservation in the laboratory was eventually resolved in the doctrine
of 'confinement': quarks were said to be real entities but subject to forces of a kind that
prohibited their existence in isolation. No proof that present theories of interquark forces
lead to confinement has been forthcoming, however: see CQ, 224-26.
26. There remain many points to be thought through here; I can discuss a few. First,
the Morpurgo case, as I have presented it, as an instance of 'top-down" stabilization of
coherence: the most theoretical element of Morpurgo's practice - the pair of phenomenal
models - was held fixed, while the other elements of his practice were pragmatically
moulded around them. One should not think of this as typical. Instead, one should think
of all the elements between which coherence is sought as, in principle, deformable, revisable,
substitutable. What one has here is a generalized Duhem problem - encounters with
resistance point to the revision of the disparate elements brought together without singling
out any particular one as the source of the problem: see P. Duhem, The Aim and Structure
of Phvsical Theory (Princeton, NJ: Princeton University Press, 1954), 132-270. In my
account of Morpurgo's work, I implicitly extended Duhem's theory-oriented analysis of
such situations to include the material dimension of practice (which, I stress, should not
be conflated with its conceptualization in an interpretative model: such conflation is the
product of the achievement of coherence). In Section V, I point to the need to extend Duhem's
analysis still further, to accommodate social and institutional aspects of practice. In order
to understand which particular elements of practice stand to be revised in the face of
resistance, it helps to think not about the kind of 'vertical' coherence between conceptual
and material practices that I focused on in the text, but about 'horizontal' coherences across
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722 Social Studies of Science
practices of the same kind. Thus, a kind of horizontal coherence was at stake in fixing
Morpurgo's phenomenal models in line with those already accepted within his community.
Horizontal coherence was likewise in question when I suggested that one aspect of the
coherence that Morpurgo aimed at was, in effect, a 'good' argument modelled upon textbook
applications of classical electrostatics. One should imagine that he attempted to show, for
example, that his calculations of the electric field between the plates of his apparatus reduced
to standard results when appropriately specified. One can take this line of thought further
by asking what it might mean to make an argument 'better'. The answer, 1 think, must
lie in the piling up of horizontal coherence - in, say, Morpurgo's tying his interpretative
models not just to textbook instances but to more complicated treatments of real metal
plates to be found in the research literature, and so on. The building of horizontal coherence,
like the building of vertical coherence, should not be thought of as a trivial process; it
should itself be conceptualized as a goal-oriented process subject to situated resistances
and chancy accommodations. In general, therefore, one should think of scientific practice
as continually aiming at the construction, strengthening and extension of particular horizontal
and vertical locally coherent constellations of knowledge and practice. often in opposition
to other such constellations, with no necessary priority going to the maintenance of any
particular element. And thus, to return to my book, while many people (including R&B)
have read CQ as asserting that, as a matter of principle, coherence is stabilized from the
top down - quarks and gauge theory were 'mere constructs' imposed on the world -
they are mistaken. I argued in CQ that from, say, the mid-1970s, top-down stabilization
seems to have been the order of the day in particle physics, but this should be seen as
a contingent historical fact about the field, to be explained along the lines that I attempted
in CQ. One can think of too many disciplines that are obsessed with method and care little
about theory - mainstream US sociology is a case in point - to want to insist upon top-
down stabilization as a universal rule.
Connected with this point, it is worth emphasizing that I am articulating here a local
version of Duhem's analysis, while many commentators take CQ as presupposing a global
formulation of the so-called Duhem-Quine thesis. It is the latter that informs contemporary,
philosophical debate. My feeling is that the whole debate needs to be rethought. Certainly,
Clark Glymour's argument against global versions of the Duhem-Quine thesis pass by
my analysis of its local version: see C. Glymour, Theory and Evidence (Princeton, NJ:
Princeton University Press, 1980). I mention this because both R&B, 600, and Gingras
& Schweber, op. cit. note 18, 380-81, refer to Glymour as a possible philosophical antidote
to CQ; Gingras & Schweber virtually accuse me of Duhem-Quine abuse - the analysis
of practice set out in this essay originated in an effort to understand what they were talking
about. An extended but preliminary account of the thoughts offered so far in this note
is to be found in my Positivism/Holism/Constructivism' (unpublished manuscript, Institute
for Advanced Study, Princeton, 1986). To go a little further, the following observation
might be helpful. I suggested above that the clash of locally coherent bodies of knowledge
and practice can itself serve partially to constitute new goals for scientific research. Peter
Galison's historical studies (for example, op. cit. note 18) are very valuable in illustrating
how this can work out. But I think that, inasmuch as they contrive the effect that repairs
and strengthening of coherence are sufficient to account for practice, they are misleading.
Even when speaking of such passages of practice, one needs some dynamics to understand
how and why repairs are attempted in particular ways.
Turning to a different point, it might be useful to clarify how my analysis of science-as-
practice relates to the various 'criteria' of theory-choice that are much discussed within
the philosophy of science-as-knowledge. Evidently, talk of coherence as a telos of practice
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Symposium: Pickering: Response to Roth & Barrett 723
is somehow related to the frequent appearance of 'coherence' in lists of such criteria. I
should acknowledge that the philosophy of science-as-knowledge is on to something here,
but a couple of points of difference are worth noting. First, on my analysis, the search
for coherence runs through all forms of practice in their full temporality; it is not just
one criterion among many to be invoked in rituals of theory-choice. In short, coherence
is more important to my analysis than it is in the philosophy of science-as-knowledge.
Second, especially in discussions of modern physics, the notion of coherence implicit in
the unification of theory (equivalently, unification of forces) often takes on a particular
significance. David Henderson (op. cit. note 4), for example, takes theoretical unification
to be a paramount 'epistemic value' of science, alongside contact between theory and
experiment, and R&B make similar gestures throughout the third main section of their
essay: thus the rhetorical question, 'in the presence of such conceptual unification, how
is [Pickering] to make good his claim that the social benefits of the theory are also needed
to account for its ultimate ascendancy in the HEP community?' (R&B, 619). My position
here is that, as a species of coherence, theoretical unification indeed constitutes a possible
goal for practice, but I cannot see that it has any special virtue beyond that. As evidence
for the lack of any such special virtue, and in reply to R&B's rhetorical question, I cite
the total apathy with which Weinberg and Salam's 1967 formulation of unified electroweak
theory was greeted. This apathy was replaced by great excitement in 1971, but the change
had nothing to do with unification (the model was no more or less unified than it had been)
or indeed with empirical data (it was as false as ever); it derived instead from the fact
that t'Hooft's proof of the renormalizability of gauge theory opened up an enormous space
of technical goals for practice (see CQ, 180-87).
This brings me to another 'criterion' and my last remark. The philosophy of science-as-
knowledge often takes on a pragmatist flavour when it appeals to criteria like 'fruitfulness'
for theory-choice. I am all in favour of moving philosophy in this direction; I would only
add that 'fruitfulness' is not something that can be read off from the face of a theory. Theories
have to be understood as fruitful for a particular community and within a particular culture,
and my analysis of practice is intended precisely to illuminate what is at stake here. The
'fruitfulness' of a theory is, in my view, something to be explained; it is not itself an
explanation.
27. To avoid misunderstandings, let me note that I do not suggest that goals once
formulated are themselves unrevisable. Very often they are revised in the course of practice,
but there is nothing to gain in continually spelling this out in the text.
28. Remember that after-the-fact glosses (in terms, say, of the actual absence of quarks
from Morpurgo's laboratory) are useless for real-time explanation: see note 21 above.
29. The first four chapters of Barry Barnes's T. S. Kuhn and Social Science (London:
Macmillan, 1982) constitute a sustained argument to this effect. But Barnes's analysis is
largely framed within the science-as-knowledge idiom - his paradigm for the attachment
of knowledge to the world is an unelaborated notion of ostension, rather than of practice.
In the concluding fifth chapter of his book, Bames does gesture towards practice, suggesting
that the openness of modelling is closed down by reference to goals and interests. But
here I think he moves too fast. There is no space in his analysis for the dialectic of resistance
and accommodation that appears when one takes the temporal extension of practice seriously,
and this elision has the effect of both oversimplifying the relation between knowledge and
goals and of strangely reifying goals themselves. In Barnes's work, goals and interests
tend to pop up in the last act as the deus ex machina that save actors from openness.
30. Perhaps the easiest way to mark a difference between the kind of historicism I have
in mind and relativism is to think about the notion of incommensurability. In the Kuhn-
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724 Social Studies of Science
Feyerabend schema one has an incommensurable mismatch between paradigms, but an
unproblematic commensuration within them: hence knowledge is relative to a paradigm.
On my analysis such commensuration always had to be made, even within a single culture.
One upshot of this is a continually widening incommensurability between present and past
culture, even in the absence of the types of big, discontinuous breaks that Kuhn and
Feyerabend talk about. This poses no particular difficulties for scientists, since history
is made forwards; but it does for the historian. My own experience in exploring the history
of particle physics is that to go back in the research literature as far, say, as the 1950s
is to enter a strange land: it requires a considerable act of the imagination to figure out
how physicists were thinking in those days. J.-F. Lyotard, The Differend: Phrases in Dispute
(Minneapolis, MN: University of Minnesota Press, 1988), seems to be getting at a similar
conception of historicity, but as usual within an analysis of language rather than practice,
and without any concept of resistance.
This is an appropriate point to comment on my review of Harry Collins's book, Changing
Order, in 'Forms of Life: Science, Contingency and Harry Collins', British Journal for
History of Science, Vol. 20 (1987), 213-21, that R&B discuss at some length (R&B,
614-16). I abide by the letter of the review, but I regret that I did not then appreciate
the significance of the contingencies that Collins dwells upon for philosophy, social theory
and historiography. I briefly discuss the implications of the recognition of contingency
for the strong programme in my Appendix.
31. One can also resuscitate 'objectivity' within philosophy if one is willing to give the
word a new sense within a historicized understanding of practice. This seems to have been
Gaston Bachelard's intention: see M. Tiles, Bachelard: Science and Objectivity (Cambridge:
Cambridge University Press, 1984).
32. Not to disappoint the critics, I should say that I continue to defend the closing
sentiment of CQ: 'World-views are cultural products; there is no need to be intimidated
by them' (414). I am puzzled by R&B's self-restraint in not quoting this passage.
33. J. Leplin (ed.), Scientific Realism (Berkeley, CA: University of California Press,
1984) is a good collection of essays for and against scientific realism. For the deflationary
'postrealist' position in philosophy of science, see Arthur Fine, The Shaky Game: Einstein
Realism and the Quantum Theory (Chicago, IL & London: The University of Chicago
Press, 1986), Chapter 7, 'The Natural Ontological Attitude', and Chapter 8, 'And Not
Antirealism Either'; and J. Rouse, Knowledge and Power: Toward a Political Philosophy
of Science (Ithaca, NY: Cornell University Press, 1987), Chapter 5, 'Against Realism and
Antirealism'.
34. To avoid unnecessary confusion, I note that the discussion that follows differs
significantly from that which I offered in 'Living in the Material World', op. cit. note 17.
35. CQ, 14. See also my 'The Hunting of the Quark', op. cit. note 17, 236, and
'Constraints on Controversy: The Case of the Magnetic Monopole', in H. M. Collins (ed.),
Knowledge and Controversy: Studies of Modern Natural Science, special issue of Social
Studies of Science, Vol. 11 (1981), 63-93, at 88-89.
36. Neither Morpurgo's theoretical understanding of the apparatus in terms of the laws
of electrostatics, nor the example of earlier versions of Millikan's oil-drop experiment,
were sufficient to specify how he should proceed.
37. See CQ, Chapters 12 and 14.
38. R&B continually gloss the analysis of CQ as hinging upon 'interpretive [sic] practices',
even within paragraphs where they quote me as referring to 'interpretive and instrumental
practices' (R&B, 590). The paragraph which precedes that quoted by R&B explains that,
'As an example of such an instrumental practice, one can think of the episode in which
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Symposium: Pickering: Response to Roth & Barrett 725
the HPW group "improved" their apparatus, replacing the 4 foot iron shield with 13 inches
of steel'. The disappearance of the latter aspect of practice in R&B's glosses illustrates
the blindness of the science-as-knowledge tradition.
39. See also my 'Big Science as a Form of Life', in M. De Maria and M. Grilli (eds),
The Restructuring of the Physical Sciences in Europe and the United States, 1945-1960
(Singapore: World Scientific Publishing, 1989), 42-54. Latour has much more vivid
examples of the refiguring of social entities and relations in and through scientific practice:
see his 'Give Me a Laboratory and I Will Raise the World', in K. D. Knorr-Cetina and
M. Mulkay (eds), Science Observed: Perspectives on the Social Study of Science (Beverly
Hills, CA: Sage, 1983), 141-70; Latour, op. cit. note 15; and Latour, The Pasteurization
of French Society followed by Irreductions, A Politico-Scientific Essay (Cambridge, MA:
Harvard University Press, 1988). Another point that Latour makes vividly is that the analysis
of science-as-practice can flow without a break into the analysis of technological practice
and science-technology-society relationships. This is in contrast with the science-as-
knowledge view, where such connections become highly problematic.
40. B. Latour, 'Do We Really Need the Notion of Ideology? A Case to Get Rid of the
Notion by Using Pasteur's Historiography', paper presented at the conference on Ideology
and Nineteenth-Century Science, Harvard University, April 1989, 23.
41. In the traditional realism debate, the unproblematic nature of observable facts is
taken for granted in the discussion of well confirmed theories. Thus the possibility of shifting
unobserved entities into the observable category is usually taken as a point in favour of
realism. I am running the argument backwards here.
42. Ian Hacking, 'The Participant Irrealist at Large in the Laboratory', British Journal
for the Philosophy of Science, Vol. 39 (1988), 277-94. At this point, the extended symmetry
(Latour, op. cit. note 24) implicit in the notion of coproduction seems to call for some
kind of metaphysics. If one gives up the notion that one can reduce the analysis of a form
of life to that of a single aspect - see my discussion of master-narratives in Section VI
- one is led towards the kind of alchemical microcosm-macrocosm analogies to which
Latour repeatedly appeals. See also P. K. Feyerabend, 'Aristotle not a Dead Dog', in his
Science in a Free Society (London: New Left Books, 1978), 53-65.
43. Richard Rorty's Consequences of Pragmatism (Essays: 1972-1980) (Minneapolis,
MN: University of Minnesota Press, 1982) argues an anti-essentialist view of philosophy
at great length.
44. I should be careful not to suggest that all philosophy of science is the philosophy
of science-as-knowledge. Here is a very incomplete list of philosophical or philosophically
oriented authors and representative writings that take aspects of science-as-practice seriously
into account: R. J. Ackerman, Data, Instruments, and Theory: A Dialectical Approach
to Understanding Science (Princeton, NJ: Princeton University Press, 1985); Gaston
Bachelard (see Tiles, op. cit. note 31); D. Baird, 'Instruments on the Cusp of Science
and Technology: The Indicator Diagram', in Hargens, Jones & Pickering, op. cit. note
18, 107-22; P. Barker, 'The Reflexivity Problem in the Psychology of Science', to appear
in B. Gholson (ed.), Psychology of Science: Contributions to Metascience (Cambridge:
Cambridge University Press), 92-114; H. M. Collins, Changing Order: Replication and
Induction in Scientific Practice (Beverly Hills, CA: Sage Publications, 1985); M. Foucault,
Discipline and Punish: The Birth of the Prison (New York: Vintage Books, 1979); Galison,
op. cit. note 18; H. Garfinkel, M. Lynch and E. Livingston, 'The Work of a Discovering
Science Construed with Materials from the Optically Discovered Pulsar', Philosophy of
the Social Sciences, Vol. 11 (1981), 131-58; R. N. Giere, Explaining Science: A Cognitive
Approach (Chicago, IL & London: The University of Chicago Press, 1988); D. Gooding,
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726 Social Studies of Science
'Putting Agency back into Observation', to appear in A. Pickering (ed.), Science as Practice
(Chicago, IL & London: The University of Chicago Press); I. Hacking, Representing and
Intervening (Cambridge: Cambridge University Press, 1983); J. Hadamard, 7he Psychology
of Invention in the Mathematical Field (New York: Dover, 1945); F. L. Holmes, Lavoisier
and the Chemistry of Life: An Exploration of Scientific Creativity (Madison, WI & London:
University of Wisconsin Press, 1985); W. James, Pragmatism and The Meaning of Truth
(Cambridge, MA & London: Harvard University Press, 1978); Knorr-Cetina, op. cit. note
11; Kuhn, op. cit. note 23; Latour, works cited, note 39; M. Lynch, 'Extending Wittgenstein:
The Pivotal Move from Epistemology to the Sociology of Science', to appear in A. Pickering
(ed.), Science as Practice (Chicago, IL & London: The University of Chicago Press);
M. Polanyi, Personal Knowledge: Towards a Post-Critical Philosophy (Chicago, IL: The
University of Chicago Press, 1958); Rouse, op. cit. note 33; M. J. S. Rudwick, The Great
Devonian Controversy (Chicago, IL: The University of Chicago Press, 1985); Serres, op.
cit. note 15; A. P. Usher, A History of Mechanical Inventions (Cambridge, MA: Harvard
University Press, Revised Edition, 1954).
45. See Latour's works cited in note 39.
46. Philosophers and natural scientists themselves are the classic villains here. The
scientists have the 'scientist's account', as I called it in CQ. In this version, the natural
world drives history: both 'the facts' and the entities behind the facts tell scientists what
to believe. In the science-as-knowledge tradition, philosophers carve out their own space
in stories that revolve around reason. Mertonian sociology of science reinforces the scientists'
and philosophers' narratives by accepting some version of them, while proceeding to find
space for its own proper sociological narrative of norms, values, stratification and so on.
More recently, Barry Barnes's 'interest model' and David Bloor's 'grid-group' approach
have done much to challenge these other master-narratives but, again, at the cost of
introducing a new one and making the action revolve around the social. One recent way
of trying to force the kind of account of practice I have given here back into traditional
disciplinary moulds is to speak not of 'resistance' to practice but of 'constraint'. I do not
want to quibble about words, but it seems to me that a lot of constraint-talk has an unsituated,
unsymmetric and teleological sentiment behind it: it is as if there are elastic bands in the
world, or in culture, or in both, that pull practice and knowledge in one way or another,
and around which the traditional master-narratives can be reorganized. To mention an
example of this strategy applauded by R&B (625-26), one can note how Martin Rudwick's
response to critics of The Great Devonian Controversy (op. cit. note 44) works in a notion
of constraint first by appeal to the world and then to communal standards to explain the
achievement of partial consensus: see Rudwick, 'The Closure of the Great Devonian
Controversy', Programme, Papers and Abstracts for the Joint Conference, British Society
for the History of Science and History of Science Society, Manchester, England, 11-15
July 1988, 155-59, at 157:
The fundamental issue, however, is whether this cumulative [empirical] base effectively
constrained the actors ... towards the (almost) consensual resolution of the controversy.
My conclusion that it did ... demonstrated to Harry Collins that I had 'not quite managed
to go native'. He, Trevor Pinch and . . . Roy Porter all commented on the problem posed
by the two lightweight or 'marginal' actors (Weaver and Williams) who obstinately
[note the qualifiers here] declined to join the consensus ... [But as] his criticism of
Weaver shows, the judgement that Williams was wrong (or at least unwise) to rely
on such an area is a judgement based on tacit communal standards to which Williams
himself claimed to adhere.
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Symposium: Pickering: Response to Roth & Barrett 727
In their critique of CQ, Gingras & Schweber (op. cit. note 29, 379-80) deploy a similarly
asymmetric notion of constraint that relies upon an unexplicated translation to a concept
of the 'rigidity' of a theoretical 'network':
More fundamentally, Pickering's frequent statements about the possibility of alternative
theories are based on the assumption that it is easy to construct a theory to fit any
set of data [I don't know where they got this idea from]. Again this may be true for
any set of data taken in isolation, but the constraints are more imposing when the theory
must fit a great number of different phenomena or data. In other words, we believe
that the rigidity of the network is much greater than Pickering allows, and this rigidity
makes it difficult to construct alternative theories ..
The longest discussion of 'constraint' I know is Peter Galison's (op. cit. note 18, 246-62).
Galison draws his inspiration from Fernand Braudel in differentiating between what he
calls 'long-ierm', 'middle-term' and 'short-term constraints' each operating at different cultural
levels ranging from 'metaphysical commitments' (246) to 'faith in a type of [experimental]
device' (254). Galison does not, I think, spell out very clearly his general understanding
of 'constraint' and its operation. The most explicit positive statement I canl find is: 'I want
to use the notion of constraint the way historians often do - to designate obstacles that
while restrictive are not absolutely rigid' (257). On the one hand, the reference to 'obstacles'
is reminiscent of my usage of -resistance'; on the other these obstacles already exist in
a given level of culture rather than, as I would have it, arising between cultural elements
in situated attempts to bring them together. Galison's positive statement is imnmediately
followed by a kind of negative definition: 'Here my reading of the process of experimentaion
differs sharply from that of some sociologists of science who want to reduce laboratory
decisions to the fulfillment of primarily theoretical "interests".' Then com.es a castigation
of my account of the discovery of the weak neutral current that takes for granted a traditional,
R&B-type, science-as-knowledge reading: see note 18 (note added in proof: these remarks
on 'constraint' are developed further in A. Pickering, 'Beyond Constraint: The Temporality
of Practice and the Historicity of Knowledge', to appear in J. Buchwald [ed.], Philosophical
and Historiographic Problems about Small-Scale Experiments [Chicago, IL: The University
of Chicago Press]).
47. For an analysis of their detrimental effects in the historiography of modern physics,
see my 'Anti-Discipline or Narratives of Illusion', paper presented at the Dibner Institute
Workshop on the Historiography of Twentieth-Century Science and Technology, Brandeis
University, Waltham, MA, 12-13 June 1989.
48. For a discussion of 'Technologies as Forrns of Life', see Langdon Winner, The Whale
and the Reactor: A Search for Limits in an Age of High Technology (Chicago, IL & London:
The University of Chicago Press, 1986), 3-18. 'Actor-network' is a term of art of the Paris
school of Callon, Latour and Law; the term 'actor' is defined to be indifferent to the hulmanity
(or lack of humanity) of its reterent. Likewise, the Paris school speaks of 'translationi',
meaning the making of equivalences between heterogeneous entities. The science-fiction
term 'cyborg'. denoting an entity that is part human and part machine, is put to good use
in Donna Haraway, 'A Manifesto for Cyborgs: Science, Technology, and Socialist Feminism
in the 1980s', Socialist Review, Vol. 80 (1985), 65-107.
49. Just to be clear on this, my idea was not that any special explanation was required
for instances of individual practice that contributed to such breaks. I think that the kind
of explanations I gave of those instances could be given of individual practice quite generally.
But there are countless instances of practice I could have discussed in CQ, and I had to
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728 Social Studies of Science
devise some scheme of simplification. My discussion of traditions and symbiosis in terms
of shared resources and contexts was that scheme.
50. The lack of symbiotic feedback experienced by Veltman is brought out, for example,
in his comment that he felt he 'was so much out of line with the rest of the world that
very likely one was producing specialists [that is, training students] in a subject that nobody
was interested in' (CQ, 178). Looking back on my account of Veltman's work, it does
seem that I nowhere explicitly stated that my analysis was intended as an exemplification
of the opportunism-in-context model, so perhaps there is some excuse for R&B not grasping
this. But there are certainly other instances of my analysis of the dynamics of individual
practice that are quite independent of notions of symbiosis and that are explicitly stated
to be exemplifications of the model: see, for example, the 'Three Transitional Biographies'
(CQ, 238-47).
51. I now see that this historical development could bear more explanation than I offered
in CQ. One could, I believe, offer a much more fine-grained analysis of why theorists
concluded that some new entity was needed, and of how the neutral current was discovered,
in terms of the analysis of goal-formation, resistance and accommodation that I sketched
out in Section III.
52. Their remarks quoted above on 'empire-building social scientists' (R&B, 580) speak
of such a concern.
53. Alas, R&B never quite use this phrase. That it is what they have in mind is clear
from the ambiguity they find in Harry Collins's concept of 'the social' (R&B, 596-98).
They fault him for not distinguishing between 'arbitrary social constructs' (R&B, 597) -
like, for example, the convention that one drives on the right in the United States and
the left in Britain - and conventional judgements that can be argued - the 'mathematical
simplicity of 'Euclidean geometry' (R&B, 597), or the judgenient of the Budapest String
Quartet to 'drop some inept would-be stringed instrumentalists' (R&B, 598). R&B seem
to believe that only 'arbitrary social constructs' are the proper subject matter for sociology.
It surprises me, therefore, that they can find any 'sociology' whatsoever in Collins's work.
or Pinch's, or CQ, or in the strong programme in general.
54. R&B's narrow conception of sociology presumably also lies behind the excessive
significance they attribute to the few instances in which I mention a connection between
the ascribed authority of scientists and the credibility of their pronouncements (Lee's role
in arguing for the renormalizability of gauge theory is the case in point here: see R&B,
621). It should be clear to any reader of CQ that I had little interest there in surface
phenomena like 'authority. I mentioned such 'social factors' only when I felt that historical
evidence obliged me to do so, and they find no part in my general analysis. It is totally
misleading of R&B to speak of 'Pickering, with his opportunism in context on the one
hand and his appeal to authorities on the other' (R&B, 621), as though I placed equal weight
on each. Some more literate reviewers than R&B have, in fact, taken me to task for my
neglect of conspicuously social factors like authority in my analysis of particle physics:
see, for example, the reviews of CQ by Bruce Wheaton, Isis, Vol. 77 (1986), 525-27;
John Polkinghome. 'Real or Imagined?', Tirnes Higher Education Supplement (20 July 1984),
23: and, especially, John Ziman, 'Deconstructing the Physical World', Minerva, Vol. 25
(1987), 517-22. I do not feel too guilty about this neglect: I was after fish that are harder
to catch.
55. Note 13 (CQ, 248) to the 'Three Transitional Biographies' discussed in CQ prefigures
my present position on this issue, that one can explain without the imputation of causality.
56. David Bloor, Knowledge and Social Imagerv (London & Boston, MA: Routledge
& Kegan Paul, 1976), 4.
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Symposium: Roth & Barrett: Replies 729
Andy Pickering is a member of the Department of Sociology
and the Unit for Criticism and Interpretive Theory of the
University of Illinois at Urbana-Champaign.
Author's address: Department of Sociology, University of
Illinois, 326 Lincoln Hall, 702 South Wright Street, Urbana,
Illinois 61801, USA.
Responses and Replies (continued)
Reply: Aspects of Sociological Explanation
Paul Roth and Robert Barrett
Nickles's Conception of Cognitive Significance
Tom Nickles advises us that the 'trick for communicating with
people ... is to talk about things of mutual interest'.' In so doing, he
strongly suggests that what we did talk about does not (or need not?)
interest sociologists.2 Well, we have always assumed that one good way
to find common ground with others is to talk about what they do. And
that, after all, is what we did. We directed our attention precisely to
the positions developed by those we criticized. Indeed we accepted the
initial assumptions of those positions; our question was whether the
conclusions reached by Collins, Pinch and Pickering could be justified
on their own assumptions and by application of their own chosen
principles. We never invoked any principles of our own alleging some
'proper' division of disciplinary labour that we took the sociologists to
have transgressed. In working out a number of details and implications
of their positions, including some troubles with them, we confess to
having taken for granted that those thinkers would find our analyses of
interest. Our strategy apparently violates Nickles's sense of the protocols
for fruitful academic exchange. We are quite at a loss to understand just
why.
Social Studies of Science (SAGE, London, Newbury Park and New Delhi),
Vol. 20 (1990), 729-45
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