Data and Presentation

A sensitive approach to the study of science, as I pointed out earlier, forces us to dismiss the methodological intermediaries generally used for collecting data. We must renounce the services of interviewers, questionnaires and statistical offices, and expose ourselves, through direct observation and participation, to the savage meaning of the scientists' laboratory action.

However, this is more easily said than done. Having despaired of the task for the

24 The Manufacture of Knowledge

moment, Apostel et a /.⁸⁵ have pointed out that scientists are socially less accessible to being investigated than prison inmates, factory workers, "primitive" cultures, or even students, none of whom really has the resources for a defence against the social scien­tist's demands. And those demands are nothing less than unreasonable. Unlike the stu­dent who may earn college credit, or the factory worker who may be paid for his time, or the prisoner who has nothing but time, or the native who takes the time to enjoy a diversion, scientists feel they have "no time" to lose. While this may be universally true, the problem is particularly acute in the United States where career advancement normally depends upon the number of publications and citations.

The social scientist, on the other hand, is an intruder in the laboratory, especially when armed with what I call a sensitive methodology (which is not to be confused with the "unobtrusive" measurement once proposed by Webb et al., 1966). To refrain from asking questions is against the social scientist's interests, as is refusing to listen to telephone calls or personal conversations, or to check out test-results, or spy at group meetings, or follow the scientists from one scene of action to another.

Consequently, the social scientist will often prove to be a source of embarrassment to the subjects of his or her investigation, startling them by entering the room while they brood over a paper or by looking over their shoulders as they take a measurement. An unexpected question may cause them to mix up their recordings; unsolicited help may end up confusing their samples. They may be forced to apologise to their unattended colleagues for being "shadowed". In short, the social scientist may be accused, as I have been, of becoming a constant "pain in the neck".

The presence of a talkative and ignorant social scientist in small offices and cramped laboratories is somewhat different from that of an anthropologist living in a separate tent in the open "field" of a native gathering place. The anthropologist will train and eventually pay an informant, or associate with different groups and turn for help to whomever is most willing, or even disappear when it seems appropriate, leaving the lit­tle obscurities for some later date. But the social scientist in the laboratory needs to keep track of the activities of one particular group. There is no shopping around for in­sights wherever they are cheapest, because the process of events is an interest in itself. To withdraw for substantial periods of time would mean forfeiting any records of what happened, beyond an occasional recollection offered by the scientist.

The choice of the laboratory used in the present study was dictated by the opportu­nity to be accepted as an intruder (no matter how talkative or ignorant); and the choice of a group to trouble with my constant presence was determined by the willingness of one scientist in particular to serve as my informant throughout the period of observa­tion. The observations were conducted from October 1976 through October 1977 at a government-financed research centre in Berkeley, California. In January 1977, the cen­tre employed approximately 330 scientists and engineers (including technical and ser­vice staff), and an additional 86 students, visiting scientists, temporary employees and other collaborators.

The work of the centre was devoted to basic and applied research in chemical, physical, microbiological, lexicological, engineering and economic areas, conducted under the auspices of seventeen separate research units (the number of which has since been reduced). Two of these units were devoted to chemistry, while others dealt in plant biochemistry, plant phytochemistry, toxicology, microbiology, chemical analysis, instrumental analysis, fibre science and food technology. Two units worked

The Scientist as a Practical Reasoner 25

in the field of food engineering, with the other six being orientated more toward general problems than specific disciplines. Several service groups (such as photographers and illustrators) were at the scientists' disposal, as were the other, reportedly excellent, technical facilities. An internal study of staff productivity (as measured in terms of citation rates and total citations per staff member) was on a par with the average rate of productivity at several large universities. A well equipped research centre engaged in normal science done by a typical aggregation of scientists of whom some were highly recognised and many were not—that was the impression.

My observations focused on plant protein research, an area which turned out to in­clude aspects of protein generation and recovery, purification, particle structure, tex­ture, assessment of biological value, and applications in the area of human nutrition. Note that my observations were not focused on a specific group of individuals: although the scientists and technicians I watched belonged to the same research unit, the working "group" constantly varied in size and administrative composition. At times it reached out toward the facilities, services and cooperation of other research units, while at others it withdrew into itself, sometimes to a point where no more than one scientist, half a technician, and a rarely seen "senior member" actually did the work.

During my stay, the work was conducted in at least four different laboratories of the centre (not counting service laboratories involved in routine chemical analyses). Vir­tually every scientist at the centre had a small lab connected with the office, as well as access to several large facilities shared by members of a unit. Various lines of research were generally conducted simultaneously, and each scientist seemed to be engaged in a host of different projects. Keeping track of these various enterprises was as much a problem for the scientists as it was for me, and there was a lot of rushing back and forth between different facilities to keep an eye on instruments or technicians, and to remedy all sorts of experimental breakdowns.

In addition to observation, I collected the laboratory protocols, drafts of papers, and published results of the relevant research. I also conducted formal interviews with scientists from five other research units, covering a variety of scientific fields, on ques­tions which arose from the observations. Only a small fraction of the material can be analysed here. The examples presented are derived from notes I took during and after the observations, from tape-recorded conversations and interviews, and from the writ­ten materials collected. Where appropriate, this information has been verified with the respective scientists (which often led to efforts as renegotiating what was "really" meant or what should or should not be included in a publication like this).

I have tried to stick, wherever possible, to a verbatim rendering of the scientists' laboratory reasoning. But it would be absurd to claim that a participant-observer's notes can provide a literal account of what happened. Where tape-recording is imprac­tical or impossible (and a year's observation cannot be put on tape), the observer's notes are little more than hurried, incomplete sketches in which many words spoken in the laboratory are omitted and occasionally, some have been confused. Since it is often more useful to listen than scribble frantically in one's book, the observer's notes are best described as on-the-spot reconstructions of what happened, based on the words, interpretations and corrections that emerged from the immediate situation.

As I implied earlier, this procedure does not go very far toward the methodological relativism advocated for a sensitive ethnography of knowledge, even when it is

26 The Manufacture of Knowledge

bolstered by abundant mechanical recording. Remember also that the most disturbing problem in any sensitive approach is not so much that of listening better or understand­ing more, but being able to let the situation speak. In other words, it is a problem of conserving meaning, and being able to reduce and present data in a way which remains faithful to the field of observation. Tape-recordings solve only the preliminary (yet nonetheless crucial) problem of conserving the source.

To avoid the need for excessive reconstruction, I have resisted the temptation to work part of the material into a case history of the research (although my notes do follow some lines of enquiry from the scientist's concept of a beginning to the tem­porary end in publication). Instead, I have selected and summarised examples from the laboratory to remind us of their source, which, as emphasised before, is the scientists' practical reasoning. Since we have taken this practical reasoning to be indicative of the decision-making process through which knowledge is constructed, various aspects of this reasoning can be used to illustrate different points about the "how" of scientific production.

I will first provide examples of the situationally contingent, circumstantial character of knowledge construction—an argument which displays the selections of the laboratory as contextual and the practice of science as local. Chapter 3 digresses into the analogical reasoning of the laboratory, which is linked less to innovation than to the orientation of the process of contextual selection. In Chapter 4, I argue that the contextual selections of the laboratory are also situated in a field of social relationships into which the scientists insert themselves. The chapter results in a critique of the estab­lished concept of scientific community as the unit of cognitive and social organisation in science, and of the quasi-economic models aligned with this conception. It proposes instead the idea of variable transscientific fields, and illustrates the relationships which traverse and sustain these fields as constituted by resource-relationships. In Chapter 5, we observe the transformation of the constructive operations of research as we move from the laboratory to the scientific paper—the single most acclaimed product of research. In other words, we will compare the savage reasoning of the laboratory with the tame (and yet interest-ridden) rhetoric through which the scientists turn their private laboratory constructions into public products. Based on what was said before, Chapter 6 will argue that we might have to reconsider a dichotomy which has become increasingly dear to us in recent years: the distinction between the two sciences, bet­ween the symbolic, decision-laden world of the humanities and social sciences, and the world of technology and nature.

Throughout the rest of the book, I shall talk about "science" and "technology" without any further qualification in the spirit of grounded theorising which proves so seductive to close observational studies. The well-disposed reader may want to remember that these observations have been conducted with a handful of scientists in one problem area at one research laboratory (the ill-disposed readers will recall this on their own). From time to time, I will attempt to exorcise "wrong" social studies of science, hoping to put the "right" ones in their place. I trust in the reader's indulgence in reflecting that it is often the exorcised with which we are most familiar, and from which we have learned most.

The Scientist as a Practical Reasoner 27

Notes

1. cf. Sohn-Rethel (1972). For a short presentation of his theory in English, see Sohn-Rethel (1973, 1975).
A critical summary of Sohn-Rethel's theory of knowledge can be found in Dombrowski et al. (1978).

2. For an example of this position, see Sellars (1963). Critical discussions from differing perspectives
(leading to different conclusions) can be found in Bhaskar (1978) and Habermas (1971): pp. 67 ff.

3. This is not a naive statement of the empirical realist's position, although it may sound like one. The naive
position would hold that the picture which science gives us of the world is a true one. In contrast, the above
statement emphasises an epistemic attitude, rather than the correspondence of actual results. For a further
discussion of this, see B. van Fraasen (1977): Ch. 2, pp. 2 ff. Suppe's formulation is that the results of scien­
tific enquiry are generalised descriptions of reality which must be true in order for the theory to be adequate,
cf. Suppe (1974): 211.

4. cf. Habermas (1971): 69.

5. See also the definitions of the anti-realist position advanced by Lakatos in his criticism of Toulmin
(1976).

6. For an exposition of Feyerabend's position, see his essays "Explanation, Reduction and Empiricism"
(1962), and "Against Method" (1970). See also the more extensive discussion in Feyerabend (1975).

7. In this connection, Gouldner speaks of the "decontextualisation" upon which idealism thrives, and
which Marx criticised by asking for a recovery of the class-character of social phenomena (1976: 44 ff.). See
also Gidden's formulation, "if men make society, they do so not merely under conditions of their own
choosing" (1976: 102, 126), used in his criticism of ethnomethodology for its tendency toward idealism.

8. In its extreme forms, scepticism implies a type of idealism. Suppe claims that none of the analysis of
science which can be said to have scepticist consequences are necessarily committed to them. To affirm that
the objects of observation exist and have properties independent of conceptualisation is consistent with their
position. But the nature of the objects observed and the properties they are seen to possess are determined in
part by the conceptual frame of the observer, cf. Suppe (1974: 192 ff.) The slogan "anything goes" is the
trademark of Feyerabend's scepticism. He says that "the only principle that does not inhibit progress is that
of anything goes" (1975: 10, 23 ff.).

9. cf. Putnam (1971: 22).

10. See "The Logic of 1873" for a formulation of Peirce's programme. Peirce (1931-35, Volume 2,
paragraphs 227 ff.).

11. For example, see the symposium edited by Suppe (1974) on the question of the meaning variance of
observation sentences and its implications for the philosophy of science. The thesis relies primarily on the
work of Bohm (1957), Hanson (1958), Kühn (1962, 1970) and Feyerabend (e.g. 1962, 1970, 1975).

12. cf. the behavioural therapy proposed and illustrated by Watzlawick, Weakland and Fisch (1974).

13. The example is taken from van Fraasen (1977, Ch. 2: 45).

14. cf. Bhaskar (1978), particularly Ch. 2: 118 ff. for an exposition of this critique. By way of example,
Bhaskar says that to predict the next eruption of Vesuvius would require a complete state-description of an
open system which is multiply determined and controlled above and beyond the constraints imposed by the
laws of physics and chemistry.

15. Bhaskar's argument is based on the transcendental question of what the world must be like for science to
be possible. Briefly stated, Bhaskar argues from the nature of experimental activity, which he holds to be in­
telligible only if the experimenter is conceived of as a causal agent in a sequence of events, but not of the
causal law which the sequence of events identifies. According to Bhaskar, this implies that there is an on-
tological distinction between scientific laws and patterns of events. See the summary of his position in
Bhaskar (1978: 12 ff.).

16. Bhaskar (1978: 54). Bhaskar calls those things which exist independent of men, but of which we can have
knowledge through experimental activity, the "intransitive objects of knowledge", in contrast to the "trans­
itive objects" which constitute the raw material of science: the artificial, antecedent objects dealt with in
scientific investigations, such as established facts and theories, models, methods and techniques. Appar­
ently, the intransitive objects of knowledge can only be characterised by the same names as those of the trans­
itive objects. For example, Bhaskar speaks of "the mechanism of natural selection" which "had been going
on for millions of years" before Darwin, cf. Bhaskar (1978: 22). For an amusing fable on the matter of real
objects, scientific objects, and popular objects see Latour (1980b).

17. Preliminary statements in regard to the interpretation of science as constructive rather than descriptive
can be found in Knorr (1977; 1979a).

18. This has been pointed out to me by Bruno Latour.

28 The Manufacture of Knowledge

19. For example, in his critique of Carnap's failure to translate physicalistic discource into terms of sense ex­
perience, logic and set theory, Quine argues that it would be better to discover how science is in fact
developed and learned; that is, "to settle for psychology" rather than "fabricate fictitious" rational
reconstructions (1969: 78).

While Quine has consistently defended the rights of an "empirical epistemology", he never actually became the anthropological observer he envisioned in a mental experiment in his Word and Object (1960). Other philosophers of science like Toulmin (e.g. 1972) and Feyerabend (e.g. 1975), similarly disenchanted with what can be achieved by pure epistemology, were actually moved to study science historically and sociologically. Examples of more recent calls for an empirical epistemology—understood as an empirical in­vestigation of the questions which traditionally occupy the philosophy of science—are Campbell (1977) and Apostel et al. (1979). Compare Böhme, van den Daele and Krohn (1977). Not surprisingly, there has been an increasing emphasis on close, observational studies—an "anthropology of knowledge"—rather than on em­pirical, macroscopic studies of science.

20. Most familiar, of course, from discussions of the epistemological and methodological state of the social
sciences.

21. In 1907, the eminent physicist Joseph John Thomson said, "From the point of view of the physicist, a
theory of matter is a policy rather than a creed; its object is to connect or coordinate apparently diverse
phenomena, and above all to suggest, stimulate and direct experiment" (1907:10). See also Bachelard (1934).

22. This is a paraphrase of Habermas (1971: 315), whose meaning differs somewhat from what is intended
here.

23. See Callon (1975) and Callon, Courtial and Turner (1979) for a series of examples and for the sort of
quantitative content analysis of problem networks they use. See also Callon (1980) for an English presenta­
tion of some of the material. The concept of translation is elaborated and discussed by Serres (1974).

24. For a comprehensive exposition of Luhmann's systems theory approach, see his Soziologische
Aufklärung I and II (1971, 1975), parts of which have been translated into English and will be published by
Columbia University Press (1981).

25. This explains the occurrence of simultaneous "discoveries" by scientists who in fact did not steal from
one another. Note that scientific institutions and the familiar forms of social control in science can be seen as
a comprehensive structure to assure that selections remain to a large degree fixed, and that the remainder are
made in a similar, compatible and repeatable way. Note also that the descriptivist interpretation of enquiry
can be taken to suggest that the constellations of selections which enter a scientifically produced finding are
in all relevant respects constrained by nature itself.

26. cf. K. Popper (1963:216ff.)

27. See also D. Phillips (1974: 82 ff.). Phillips has pointed out that, as a consequence, we have to assume, in
opposition to Mills and Merton, that the motives and social position of an enquirer are indeed relevant for
the evaluation she gets from fellow scientists.

28. This scientist, a department head at a top university, implied that the reviewers even knew whose pro­
posal they were reviewing. This is not surprising, even when names are eliminated from the proposal: the
amount of money asked, the kind of research proposed, the resources (including instruments) mentioned, all
suggest the source of a proposal in those highly specialised areas where it is a matter of survival for scientists
to know very well "who" (in the widest sense of the word) is in the area.

29. Other areas relevant here are journals and publishers, or contexts in which decisions about the publica­
tion of results are made. Results which are not published or otherwise circulated effectively obviously have a
much smaller chance to even enter the process of general validation.

30. It is tempting to quote Wittgenstein here: "So sagst Du also, dass die Übereinstimmung der Menschen
entscheide, was richtig und was falsch ist?—Richtig und falsch ist, was Menschen sagen; und in der Sprache
stimmen die Menschen überein. Dies ist keine Übereinstimmung der Meinungen, sondern der Lebensform."
The English translation is: "So you are saying that human agreement decides what is true and what is
false?—It is what human beings say that is true and false; and they agree in the language they use. That is not
agreement in opinions, but in form of life." See paragraph 241 of the Philosophical Investigations as
translated by G. E. M. Anscombe (1968).

31. I am referring here to Feyerabend's contention that the interpretations which scientists choose are
relative to a cultural and historical context, and can only be understood if we look at these contexts. The
thesis rules out the possibility of specifying a set of context-independent criteria according to which consen­
sus formation proceeds. In contrast, Kühn does not rule out the possibility of such criteria. See Feyerabend
(1975) and Kühn (1970), particularly the discussion in the postscript.

The Scientist as a Practical Reasoner 29

32. Note that Toulmin's model of scientific evolution (the closest adaptation of the biological model) goes to
some length to avoid such consequences. First, as we shall see later, Toulmin restricts the idea of en­
vironmental selection to a form of scientific selection. Secondly, as Lakatos points out in his critique of
Toulmin, he invokes a "Cunning of Reason" in history which somehow secures the final validity of the selec­
tions that have been made. For these and other reasons which will become clear later, Toulmin's model is not
a contextual model as proposed here. cf. Toulmin (1972) and Lakatos (1976).

33. For a summary presentation of the whole discussion, see Lakatos and Musgrave (1970).

34. In stochastic processes on the molecular level, in which the smaller the number of interacting molecules,
the greater the role of fluctuation, it has been shown that the absence of "errors" or indeterminacy cor­
responds not only to an absence of innovation and hence of an increase of information, but to an actual loss
of information. Without chance fluctuations, the system cannot maintain itself in a stationary state. This
means that without the intervention of "error", chance or indeterminacy in biological evolution, for exam­
ple, all species would disappear without being replaced by others, cf. Allan (1979: 54f.). For a propagation of
the idea as a principle of order relevant to science see particularly Latour and Woolgar (1979). For the most
illuminative philosophical analysis which deals with the topic see Serres (1980).

35. The second principle of thermodynamics postulates that natural systems show an evolution toward in­
creasing entropy or maximum molecular disorder, which is identical to a distribution of equal probability.
The recent developments to which we have alluded above show that self-organising systems do have the
capacity to react to perturbations by using them as a factor of organisation, by making them beneficial to the
survival of the system. As will become more clear in the examples that follow, the point is not to deny the
potentially disruptive effect of noise, or indeterminacy, but to say that whether or not the effect will be
disruptive depends on the reaction of the system.

36. This reinterpretation is crucial because it suggests that the point is not, as Von Foerster's terminology
tells us, the construction of "order" out of disorder (indeterminacy, chance), but the emergence or organisa­
tion as defined by an increase in complexity or system differentiation. According to Allan, Von Foerster en­
visioned an increase of repetilion or redundancy with which Ihe nolion of order is associated in information
theory. Only if we see indeterminacy as resulting in greaier organisation or complexity, ralher than in order,
can we define this effeci as an increase of information for the system and understand Ihe adaptive power
which derives from this organisation, cf. Von Foersler (1960) and Allan (1979).

37. In natural language, "order" and "organisation" are often used indiscriminately, and this often occurs
in philosophical Irealmenls of the subject as well (Morin 1977). Yet il should be noled that there is one im­
portant difference to be kepi in mind even if we merely use the principle of "organisation by chance" as an
analogy. While order implies stability, an organisalion toward increasing complexity is inherently linked to
change and a system-inlernal increase of information. It is this pari of Ihe analogy which I take to be par­
ticularly well suiled when we apply it to science, and not Ihe interpretation of "order from disorder".

38. As a simple example, consider the leak in the communicative network of the Nixon administration with
regard to the bombing of Cambodia (kept secret by the administration). While the leak was without doubt
disruptive for some core members of the administration, it may well have benefited the more global system of
American democracy. The implication is that we have to take into account different levels of organisation in
order to distinguish between the disruptive and integrative (or organising) effects of noise.

39. Of course, science produces new problems at the same time, which is part of the process of reconstruc­
tion.

40. The quantity of information within a system is taken to be a measure of the improbability that the com­
bination of the different constituents of the system is the result of chance. This is why the quantity of infor­
mation could have been proposed as a measure of complexity. Strictly speaking, there are three different ver­
sions of writing the quantity of information which correspond to three kinds of complexity, all defined in
relation to our knowledge. The first refers to a variety of which we do not know the distribution (Я = log N),
the second expresses disorder (H = £p log p), and the third measures a lack of knowledge of the internal
constraints or redundancies of a system (H = //max(l-R)), where H = the quantity of information, p = the
probability that a certain sign is present, and R = the redundancy—all according to the summary by Allan
(1979: 79 f.). Note that the characterisation is formal and does noi take into account Ihe content of the signs.

41. According lo Ashby, il is logically impossible lhai a self-organising syslem be closed, i.e. a syslem which
does not interacl with an environment. If Ihe syslem could change ils organisation solely as a function of ils
internal siaies, this change would be governed by a constanl. True change has lo be induced eilher ihrough a
program of change injected from Ihe oulside or ihrough external chance interferences, cf. Ashby (1962).

42. See Toulmin (1967) for a short presentation of his model and of the non-metaphoric reading intended
(p. 470 f.). A more exlensive analysis is found in Toulmin (1972). Compare Campbell (1974).

30 The Manufacture of Knowledge

43. Toulmin seems to suggest that this is normally and ideally the case, although he points out that historical
cases do not always follow the pattern he proposes. Hence his distinction between "compact" traditions
which follow his systematic pattern, and "diffuse" traditions which may not. cf Toulmin (1967), particularly
paragraph 4.

44. This makes sense, since it does not presuppose that the observer holds some criterion as to what counts as
an innovation. In the above case, all results counted as new by the scientists themselves would presumably be
part of the "pool of scientific innovations".

45. Since change and particularisation are built into scientific products, we can also say that scientific work
allows for differentiation effects, and these differentiation effects can be appropriated by scientists. It is clear
that the individuation provided by scientific work need not necessarily go to individual persons. Many would
argue that the increasing socialisation of science means that we have an increasing appropriation of differen­
tiation effects by groups, and more importantly, by institutions. This tendency toward a greater anonymity
for individual authors of scientific products can also be seen as an indication of a progressive "proletarisa-
tion" of scientists, to which we will return in Chapter 4.

46. In particular, see his essay on the origin of geometry (1962).

47. For a short presentation, see the chapter on "Logic as Semiotic" in the Dover edition of Peirce's selected
writings (1955: 98 ff.).

48. In Of Orammatology (1976: 27).

49. See particularly p. 45 ff., where Latour and Woolgar introduce the notion of "literary inscription" for
taking a measurement in the laboratory (1979).

50. There has been a particular focus on studies of citation, examples of which are too numerous to be listed
here. For two recent reviews which point to potential new directions, see Chubin and Moitra (1975) and
Sullivan, White and Barboni (1977). For other aspects of patterns of communication among scientists, see
Zuckerman (1977), Ziman (1968), Studer and Chubin (1980) or Gaston (1973, 1978).

51. Böhme has concluded that a concept of the scientific community within a theory of scientific action
needs to be based on a theory of the process of argumentation in science. See Böhme (1975).

52. For an exposition of Luhmann's notion of differentiation in English, see his article on the "Differentia­
tion of Society" (1977a).

53. Another possibility would be to search for system borders somewhere within the process of research pro­
duction itself. The selectivity incorporated in scientific products allows for a problematisation of constitutive
decisions, and problematisation could come to be seen as a form of environment-triggered increase of com­
plexity. The complexifying new selections of the laboratory counter these challenges of problematisation.

54. For a summary of this and other criticisms of systems theory as applied to social systems, see Habermas
(1979), particularly p. 141 f. in Chapter 4, "Toward a Reconstruction of Historical Materialism".

55. Cited in Johnston (1976: 195). Johnston summarises some of the uses of the internal/external distinction
which he traces back to assumptions enshrined in the history and philosophy of science that have been un-
questioningly adopted by subsequent analyses of science.

56. For example, see Kuhn's criticism of Lakatos' use of the distinction (1971: 139 f.). To Lakatos, the inter­
nal seems to be coextensive with the rational part of science. Kühn, in contrast, appears to equate the inter­
nal/external dichotomy with the distinction between the cognitive and the social, a practice he claims is
shared by all historians of science.

57. The fact that in the end only individuals can institute intentional action has led to an argument for a
methodological individualism, to which we shall return in Section 1.9.

58. See, for example, Galtung's critique of some kinds of survey research (1967:148 ff.). Cicourel (1964) has
provided the most comprehensive and influential criticism. See also the new methodological developments
based upon this and other criticisms which are summarised in Brenner, Marsh and Brenner (1978) and Bren­
ner (1980), particularly in the Introduction.

59. Such close inspections have primarily occurred within various microsociological perspectives, such as
ethnomethodology, cognitive sociology, symbolic interactionism, ethnogenics and phenomenology. For a
summary presentation of some of the studies relevant here, see Mehan and Wood (1975). Harre (1977),
Cicourel (1973), Berger and Luckmann (1967), and the earlier works of Goffman (e.g. 1961), all include
representative statements about the problematic character of everyday interaction.

60. Whitley's whole argument with respect to "black-boxism" and the sociology of science is found in his
article of the same title (1972).

The Scientist as a Practical Reasoner 31

61. Ethnoscientists distinguish between an "emic" (from phonemic) structural approach, and an "etic"
(from phonetic) intercultural approach which imposes the concepts and distinctions of "scientific" an­
thropology (Pike, 1967: 37 ff.). For recent reviews of developments in ethnoscience or cognitive an­
thropology, see Bernabe and Pinxten (1974) and Pinxten (1979).

62. See Schoepfle, Topper and Fisher (1974: 382).

63. The best example of the use of such terms may be Garfinkel himself (1967).

64. Consequently, it is not enough to require that the student of social science be familiar with the speciality
under study, or be a trained member of the respective scientific discipline. Anthropology demonstrates that,
while this may be a necessary prerequisite for a decentred analysis, it is by no means a sufficient condition for
its achievement. In light of the problem concerning the decentring of scientific speech, the battle over the
hermeneutic or non-hermeneutic character of ethnographic observation seems to be somewhat obsolete. My
own summary presentations of the current state of anthropological methodology and of its challenges can be
found in Knorr (1973; 1980).

65. The term is drawn from Werner (1969), who, like many others, believes that it is the unfortunate, but
unavoidable fate of ethnography to record systematically the structuring of the world contained in the
linguistic expressions of a culture.

66. By which I mean the ugly consequences to which ethnomethodologists' efforts to preserve subject-
centred speech often lead: tormented language and a tormented reader who tries in vain to decipher the hid­
den meaning of the new professional idiom.

67. For this formulation, see Agassi (1973: 185 f.). See also the collection of essays edited by John O'Neill
(1973) on Modes of Individualism and Collectivism, which contains many contributions relevant to these two
methodological orientations.

68. One of the chief critics of methodological individualism in recent years has been Steven Lukes. See his
collection of essays (1978), particularly the essay on "Methodological Individualism Reconsidered" (Chap­
ter 9).

69. The point here is a methodological orientation relative to methodological individualism and wholism,
and not a plea for carrying sociological "symbolic interactionism" over into social studies of science (which,
by the way, has already been introduced into science studies). While the present endeavour is undoubtedly in­
formed by developments in symbolic interactionism, it cannot claim to be a species of that orientation. As
the reader may note, I feel a greater debt to other microscopic—and some macroscopic—orientations.

70. For a brief summary of how ethnomethodology has reinterpreted some traditional problems of sociology
along these lines, see Zimmerman and Wieder (1970). For example, norms and rules interest the
ethnomethodologist not as an explanatory concept for social action, but as a topic of analysis, as a resource
which members use to structure and orient everyday life, and to convince themselves of the orderly structure
of this world.

71. For a number of relevant analyses, see Cicourel (1973). The reason we often learn something about the
"why" by answering the "how", of course, is that both questions are often connected by a series of transla­
tions. To trace "how" something came about often points to its origin, or yields a genetic "explanation". A
similar relationship holds between "what" (the traditional question faced by the anthropological observer)
and "why". As Lukes (1978: 184 f.) has reminded us, to identify an item of behaviour or a set of beliefs is
sometimes enough to explain it: explanation often resides precisely in a successful and sufficiently wide-
ranging identification of behaviour or types of behaviour. The ethnoscientist's attempt to identify cultural
knowledge in the terms in which it is couched by a particular culture should teach us something about why
certain patterns of behaviour exist in that culture, and about similar questions.

72. See the comprehensive discussion of the thesis of symmetry in Stegmüller (1969, Vol. 1, Part 2: 153 ff.).

73. See Luhmann (1977b: 16, 28), who argues that the binary schematisation between true and false may be
inadequate for the instrumental applicability of a theoretical explanation in practical action. Luhmann refers
to the example of the Coleman report which cites the racial and social composition of school classes as the
most important variable in explaining educational success. Busing was widely introduced in the United States
to alter that composition, but educational success did not follow, for reasons which support Luhmann's
point but are not relevant here.

74. See Lofland (1976: 2) on the whole matter mentioned here.

75. Although the case study approach is widely favoured at present (not only in social studies of science, but
in sociology in general), it is surprising that so few sociologists have as yet done what Lofland advocates in
his codification of a qualitative methodology (1976)—that is, actually to enter the field as a (participant)
observer.

76. The essay can be found in Garfinkel (1967: 272 ff.). See also Schutz (1943) on the "Problem of
Rationality in the Social World", to which Garfinkel refers.

32 The Manufacture of Knowledge

77. Merton has been attacked on this subject so often that we need not repeat the criticism here. Those un­
familiar with the subject are referred to Barnes and Dolby (1970) and Stehr (1978). Note, however, that Mer­
ton postulated norms, and not stable properties of scientific action. In this respect Garfinkel, who talks
about rules which routinely manifest themselves in action, goes far beyond Merton.

78. For selected examples of such arguments, see Whitley (1972), Nowotny's call for a cognitive approach to
the study of science (1973), Mulkay's argument that the sociological study of science must include its
technical culture (1974a) or Weingart's specification of cognitive/technical and social variables (as well as
their interrelationship) in the study of the production of knowledge (1976). Most recent "social" studies of
science in Western Europe have tried to include the "cognitive" side of science. The studies published under
the title Cognitive and Historical Sociology of Scientific Knowledge Ъу Elkana and Mendelsohn (1981) pro­
vide the most recent example of the trend. For a relevant, general presentation and discussion of the
"cognitive paradigm", see de Mey (1981).

79. There have been several recent attempts to move beyond science and explore the relationship between
knowledge and society. In particular, see Barnes (1977), and Mulkay (1979). See also the work of Foucault
from a historical perspective (e.g. 1975, 1977), the work of Holzner and Marx (1979) from a general,
sociological perspective, and Stehr and Meja (1982) on classical vs. recent sociology of knowledge.

80. For a representative collection of such studies, see Lamaine, MacLeod, Mulkay and Weingart (1976).
Other studies can be found in Mendelsohn, Weingart and Whitley (1977), particularly Parts 1 and 2. See also
the studies by Edge and Mulkay (1976), Küppers, Lundgreen and Weingart (1978), or Studer and Chubin
(1980).

81. Published studies based upon direct anthropological observation of scientists are still scarce. The
monograph by Latour and Woolgar (1979) is to my knowledge the most extensive study of the sort within the
tradition of social studies of science. See also Latour (1980a) and my earlier articles based upon the same
observational study drawn upon here (Knorr, 1977; 1979a, b; and Knorr and Knorr, 1978). An interesting
antecedent of such studies is the work, not of a sociologist of science, but a theologian (himself a physicist)
whose observations of scientists were financed by a group of progressive Catholics not involved in academia
(Thill, 1972). Preliminary results of some anthropological studies of science still in progress can be found in
Jurdant (1979), Apostel et al. (1979) (to whom I owe the information about Thill), and in McKegney (1979),
Lynch (1979) and Zenzen and Restivo (1979), whose results were presented at a conference on the social pro­
cess of scientific investigation organised by Roger Krohn at MacGill University, Montreal. For the thesis that
we are experiencing a general "anthropological turn" in the social sciences and in science studies, see
Lepenies (1981). See also the work begun by Williams and Law (1980).

82. Note that Bourdieu is not talking about the motives for a scientist's conscious objectives, although the
choice of an area of work is often consciously motivated by career considerations.

83. In delineating a strong programme for the sociology of science, Bloor has criticised the asymmetric treat­
ment which offers a social explanation for recognised scientific mistakes, but not for scientific achievements
so long as they are held to be sound. The central thesis of his book is that "objectivity is a social
phenomenon", "logical necessity is a species of moral obligation" and the "ideas of knowledge are based on
social imagery". Cf. Bloor, 1976: 141. In his later work Bloor returns to the distinction between a social and
cognitive sphere in science by empirically correlating variables which he associates with them. See Bloor
(1978).

84. For a similar argument with regard to "the supposed norms of science", see Mulkay (1976).

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