Experiment In Science And Technology Research Paper

1. Development Of New Approaches To Experiment: Challenges To The ‘Received View’

In the 1950s and early 1960s, one of the central assumptions of the ‘received view’ was seriously challenged. The presumed independence of experimental and observational data from contamination by the very theories that the data were intended to judge was challenged by W. V. O. Quine (Quine 1953), Norwood Russell Hanson (Hanson 1958), and Thomas S. Kuhn (Kuhn 1970 [1962]). Quine showed, using an argument similar to one used by Pierre Duhem (1954), early in the twentieth century, that empirical data always underdetermine the theories that can rest upon them. In Duhem’s hands, the argument rested on a position of ‘conventionalism,’ whereby the relationship between items of discrete empirical data and the theories employing those data was seen to be underdetermined; in particular, Duhem argued that there could be no such thing as a ‘crucial experiment’ that could decide definitively between two alternative theories. A result inconsistent with one of the theories need not be attributed to an inadequacy in the target theory itself, but might instead be attributed tOverror in a subsidiary theory (such as one relating to observational instruments) that had not initially been in question. Possibilities of that sort amounted to decisions, according to Duhem, and were consistent with a conventionalist view of scientific theories, whereby pure convention determined which in a network of theories would be preserved and which amended so as to fit experimental results.

Hanson and Kuhn went further, with their arguments in favor of the ‘theory-ladenness of observation.’ They held that a pure observation language was in principle impossible, and that, accordingly, the results of experiments and observations of nature always implicated theoretical concepts in their very formulation. This position blurred the distinction between empirical data on the one hand and the theories that are justified by those data on the other. Both Kuhn and Hanson likened empirical data to the psychologist’s gestalt experiments, wherein, for example, the ‘same’ image can sometimes be seen as a duck and sometimes as a rabbit; the difference, they claimed, was that in science there is no possibility of resting one’s description on an account of the underlying set of lines. Instead, the scientist sees a duck or a rabbit, with no further reduction to a common observational base being possible. All empirical data are already interpreted; that is, seen in a particular way (cf. Fleck 1979 [1935], an acknowledged source for Kuhn).

2. Sociological And Historical Exploitations Of New Theoretical Arguments

These challenges to the ‘received view’ of science provoked much debate in the 1960s and into the 1970s. In its wake, however, there arose attempts to exploit the ideas of such as Hanson and Kuhn in the service of sociological projects aimed at making sense of scientific knowledge seen as a social product. In the early days of the ‘sociology of scientific knowledge’ (SSK), the Duhem–Quine ‘underdetermination’ thesis became a standard in-principle justification for sociological studies of the acceptance of knowledge claims by scientific communities (e.g., Mulkay 1979, KnorrCetina and Mulkay 1983). This was so because it was argued that the inadequacy of empirical evidence to necessitate any particular theoretical belief in science left room for social explanations regarding which belief among the manifold logical possibilities was the one actually chosen. At the same time, however, a more fundamental theoretical challenge to the self-sufficiency of ‘received view’ accounts of the role of experiment in science was being developed by H. M. Collins, drawing on a sociological reading of Wittgenstein (Winch 1958, cf. Bloor 1983).

Wittgenstein had argued that rules do not contain rules for their own application; such a position, in the form of ‘finitism,’ also applies to practices of classification (see, for a summary of its relevance to STS, Barnes et al. 1996). The basic claim amounts to observing that every new situation, every new occurrence of some kind of event, is in its own way unique; it therefore requires indeterminate judgments of similarity and difference to decide whether a new event or instance is or is not a legitimate member of a given category. In articles from the mid-1970s onwards, and culminating in a book of 1985 (Collins 1985), Collins developed empirical case studies that exploited Wittgenstein’s arguments to show how the participants in actual scientific controversies resolve problems of the ambiguity of experimental outcomes. In work on claims to the detection of high-flux gravitational radiation in the 1970s, as well as in the transfer of skills relating to the successful replication of TEA-laser technology, Collins developed the notion of the ‘experimenters’ regress,’ which he saw as an application in the domain of the sociology of science of Wittgenstein’s ‘indeterminacy of rules.’ In the case of an experimental result, a judgment must be made that involves deciding whether the experiment or experimental run was competently conducted. If yes, then the outcome can be used to assess an associated theoretical claim (which would then open up Duhem–Quine issues), whereas if not, then the outcome will be irrelevant to the claim. Collins showed that, routinely, such assessments of experimental competence were central to scientific controversies. The ultimate criterion for judging the competence of an experiment, according to Collins, was whether the experimental outcome was correct or not. In the case of experiments the results of which were taken to depend on unknown or controversial aspects of the natural world, therefore, controversy over nature was coextensive with controversy over which experiments were fit to judge concerning that feature of nature. This, then, is the essential paradox designated by the term ‘experimenters’ regress’: it is only possible to know whether an experiment was competently performed if it is known what the correct outcome should be, but (in an empiricist epistemology) the correct outcome can only be known as a consequence of the performance of competent experiments.

The sort of empirical studies of scientific practice conducted by Collins also yielded fruitfully to analysis in terms of the Duhem–Quine thesis. Trevor Pinch’s Towards an Analysis of Scientific Observation (Pinch 1985) introduced the idea of ‘externality’ in understanding the role and fate within the scientific community of experimental work. Pinch noted that knowledge-claims made on the basis of experimental studies could themselves be couched in alternative ways that maximized or minimized the likelihood that the competence and reliability of the experiments themselves would be questioned. An experimentally based assertion with high externality would be one that used the experimental outcome to make far-reaching inferences about some domain of existing knowledge; an assertion with low externality would depart but little from a bald statement of the local circumstances of the experimental situation, and could provoke but little controversy. Andrew Pickering (Pickering 1984) examined similar professional dynamics in the work that established the existence and characteristics of quarks in the 1970s.

Together, the Duhem–Quine thesis, finitism, and the experimenters’ regress had opened up, by the mid-1980s, a vast terrain within which sociologically informed study of the experimental dimensions of scientific knowledge could be conducted. A landmark study that fully exploited the new possibilities was Steven Shapin and Simon Schaffer’s Leviathan and the Air-Pump (Shapin and Schaffer 1985). This historical study directly challenged the older ‘received view’ conception of the role of experiment in making scientific knowledge, and did so by investigating a classic, oft-cited historical example usually held to exemplify that view. The subject chosen in the book was the air-pump work of Robert Boyle in the 1660s. Boyle’s work had been presented (Conant 1970 [1948]) in one of the Harvard Case Histories in Experimental Science, dating from the late 1940s and 1950s. These were publications that, importantly, had shaped the teaching and scholarship in the history of science for many years, and which were consistent with the usual conception of experiments as unequivocal arbiters of theoretical ideas. Shapin and Schaffer thus accepted Boyle’s air-pump experiments, for the sake of argument, as an exemplary model of scientific procedure. They then attempted to show how a close examination revealed that Boyle’s experiments and their associated knowledge claims were far from unequivocal—were, in fact, strongly contested—and that the interpretation of them advanced by Boyle and his allies could also be understood as part of a political vision of the proper social constitution and conduct of a philosophical community. In order to achieve this purpose, Shapin and Schaffer used the criticisms of Boyle advanced by the philosopher and mathematician Thomas Hobbes, a man whose view of the proper way to make natural knowledge differed significantly from that of Boyle and whose associated conception of the place and legitimacy of knowledge in a polity also differed markedly from Boyle’s. Hobbes’s detailed criticisms of Boyle’s air-pump work revealed an alternative set of values and commitments regarding the best way to achieve social stability and consensus, a way that invalidated experimental work as an effective means of securing knowledge claims. An alternative approach to similar issues (Dear 1985, 1987, 1995) focuses on conventions of knowledge making that were less local than those examined by Shapin and Schaffer, and which support a view of much more mediated connections with social organization. Dear’s main argument is that the modern ‘experiment’ as a historically specific, contrived event was a development of seventeenth-century Europe, and had close filiations with disciplinary approaches employed in mathematical sciences that stressed operationalism.

3. Laboratory Studies And Naturalistic Approaches

By the mid-1980s, in addition to the work already discussed, a number of so-called ‘laboratory studies’ were being published. These studies also had a strong influence on views of experiment in science, but, in contrast to the approaches considered above, they tended to eschew, often explicitly, an overt engagement with the ‘received view’ philosophies of science. Instead, the methodological and/or epistemological approaches that were central to laboratory studies drew from such traditions as those of anthropology, ethnomethodology, and phenomenology. The three crucial and exemplary lab studies from this period were Latour and Woolgar’s Laboratory Life (Latour and Woolgar 1979 1986), Karin Knorr-Cetina’s The Manufacture of Knowledge (Knorr-Cetina 1981), and Michael Lynch’s Art and Artifact in Laboratory Science (Lynch 1985). These three have in common a naturalistic stance towards the work of the laboratory, rejecting presuppositions as to the character of that work. Thus, they have no a priori interest in studying laboratory work as a means of learning how ‘reliable,’ or ‘true,’ or ‘epistemologically privileged’ knowledge results from laboratory practices. Instead, they treat their particular laboratories as sites where activities are carried out, and attempt to describe and account for the nature of those activities. A notable feature of the rapidly changing intellectual landscape on which these laboratory studies were performed is the existence, in the first edition of Laboratory Life, of the subtitle The Social Construction of Scientific Facts, and its replacement in the second edition, seven years later, by the less doctrinaire The Construction of Scientific Facts. The change signals the way in which, in the years surrounding 1980, the rhetoric of SSK, with its insistence on ‘social construction’ as the crucial mechanism by which scientific knowledge was made, dominated science studies. By 1986, this insistence was already looking rather hackneyed and uninformative in some quarters.

The place of experiment in the tradition of laboratory studies is less clear-cut than it was in the mainstream SSK tradition, because the former were not reacting directly to the epistemological highlighting of experiment characteristic of the philosophical ‘received view.’ Thus, experiments were less likely to be seen as obviously individuated events, instead falling within an overall passage of scientific activity. The highlighting of particular experiments as especially significant cognitive elements of such passages now became contingent on the behavior and utterances of the scientists being studied, rather than being self-evidently central to an understanding of scientific work.

A collection of papers originating in a conference of 1985 on ‘The Uses of Experiment’ (Gooding et al. 1989, see also Le Grand 1990 for a similar collection) attempted to shed light on experiment as a category used by scientists rather than as an epistemologically significant item singled out by philosophers. The contributors made use of the new work in science studies to lay out, chiefly by means of empirical studies of contemporary and past science, the multifarious ways in which experiment has been used as a rhetorical and practical tool in the establishment of knowledge- claims and in the consolidation of scientific communities of practice. One especially notable concept deployed in this volume, centrally in the contribution by Simon Schaffer (Schaffer 1989), was that of experimental ‘transparency.’ This concept designated situations in which an experimental apparatus becomes so unproblematic and theoretically unquestioned that the phenomena to which it affords access are seen directly, as it were, as if no theoretically justified experimental device intervened between observer and phenomena. In such cases, in effect, the apparatus has changed from being an experimental set-up to being a scientific instrument. For example, such, was the fate of the mercury barometer in the seventeenth century, which began life as an experiment intended to examine the pressure of the air and the possibility of a vacuum but which, by the end of the century, had become an instrument for measuring atmospheric pressure as an aid to understanding the weather. These kinds of conceptualization also hark back to the much earlier work of the French philosopher Gaston Bachelard, who spoke of the artificial creation of phenomena by apparatus, using the term phenomeno-technique (e.g., Bachelard 1938, see Gaukroger 1976 for a lucid introduction).

The second half of the 1980s also saw the appearance of empirical studies of modern physical experimentation that adopted attitudes quite different from those of the advocates of SSK. Peter Galison, in his book How Experiments End (Galison 1987), examined several episodes in post-WWII high-energy physics in the United States. The book’s intention was to describe the ways in which experimental closure was brought about in the episodes discussed, but in a way explicitly opposed to that of such as Collins; that is, Galison’s aim was to show that social mechanisms were insufficient to explain the outcome of the experimental work. Allan Franklin also published work on modern experimental physics with broadly the same aim (Franklin 1986, 1990). In both cases, the role of an independent physical world in creating sometimes-unexpected outcomes to experiments was emphasized, to reduce the role of social actions and social structures in determining outcomes: in Franklin’s case, at least. It was argued that social considerations become irrelevant in light of the overwhelming influence of objective experimental outcomes and their correct rational assessment. Franklin’s position, however, appears largely to ignore the epistemological problems that fueled SSK.

Discussions of experiments and the best ways of understanding their role in science also went well beyond issues of their direct epistemological function. Historical studies, pre-eminently Shapin and Schaffer’s Leviathan and the Air-Pump, were by now having an impact on wider conceptions of the ideological structure and social meaning of science. The most important example of that impact was Yaron Ezrahi’s The Descent of Icarus (Ezrahi 1990). This took Shapin and Schaffer’s presentation of Robert Boyle’s kind of experimental science as the model for science ever since the seventeenth century, and adapted their view of its political meaning to an account of the development of modern liberal ideology and, subsequently, modern liberal states from the eighteenth to the twentieth centuries. In Ezrahi’s view, the legitimacy of experimental knowledge claims in science became the accepted norm for knowledge claims in the political arena as well. Shapin and Schaffer had stressed the role of ‘witnessing’ in Boyle’s kind of experimental science, whereby many people, either directly or through the reading of detailed reports (‘virtual witnessing’), came to attest the truth of an asserted experimental outcome and thereby its associated factual knowledge claim. Ezrahi suggested that a similar visibility, or transparency, of political actions and the reasons for them became the political ideal, along with the notion of the accountability of political leaders. Ezrahi’s ideal-type of such a polity, the United States in the twentieth century, thus placed great stress on the possibility of citizens seeing what their government was doing and in assessing the grounds for and wisdom of those actions (see also Latour 1993 for different political extrapolations).

4. Latour On Experiments And Their Mobility

Other aspects of experimentation were also investigated in the 1980s and early 1990s, most notably in the work of Bruno Latour. Latour’s naturalistic approach to scientific practice, which had been explicitly anthropological in inspiration in Laboratory Life, extended his representation there of laboratory science as an enterprise centrally concerned with the production of ‘literary inscriptions’ (any kind of trace inscribed on paper). This extension took the form, in his Science in Action (Latour 1987), of an analysis of the structure of experimental papers. That structure, he argued, reveals the agonistic logic of experimental procedures through a kind of shadowboxing, whereby the paper’s authors attempt to anticipate and head off skeptical criticisms of their claims, such as might be put forward by a determined opponent. Thus, the experimental paper (and, by implication, the experimental protocol itself ) takes the form of one side of a dialogue aimed at silencing the critic through anticipation of all plausible objections. Part of the power of this analytical approach supposedly resides in Latour’s stress on semiotic analysis (Latour and Bastide 1986), which connects with his emphasis on taking into account ‘natural actants’ in accounts of scientific activity (cf. also Latour 1988). Thus semiotic actors in the experimental account which are normally taken to refer to things in the natural world (such entities as subatomic particles, or microbes, etc.) are treated on a par with those semiotic actors normally taken to refer to things in the social world (preeminently, the scientists performing the experiment). Thus, they are understood in exactly the same way. Latour therefore claims that there is no justification for treating social actors as real while treating ‘natural actors’ as simply social constructs, which is what the SSK approach advocates. Problems seem to arise in Latour’s approach, however, when the question of shifting between the analytical level of the semiotic and the analytical level of the putatively ‘real’ is considered; Latour is obscure on the point.

One especially influential idea in Latour (Latour 1983, 1988) concerns a way of understanding how experimental outcomes can be mobile; that is, how a successful experiment conducted in a specific laboratory is made to be successful at other locations. This issue has been referred to as the ‘problem of constructivism’ in Golinski (1998); although Latour would not count himself as a ‘constructivist’ in the SSK sense, his similar stress on the work that goes into creating an experimental ‘fact’ leaves him with the same problem. The difficulty that Latour purports to solve is to explain how, if experimental facts are made in situations whose specificity and locality (‘natural’ and ‘social’) are taken as crucial to explaining the particular outcome, that outcome is seen to be reproduced in significantly different settings. The traditional (‘received view’) answer is that the experimental outcome is simply a reflection of the way that nature works, and an implicit principle of the uniformity of nature therefore implies that the same experiment, in the sense of the same material set-up and procedure, will yield the same result wherever it is conducted. The constructivist, however, because of a conviction that ‘social’ elements (however defined in detail) are essential to producing the outcome, appears to have difficulty in explaining this mobility of experiment (cf. Collins 1985 on the TEA-laser). Specifically, Latour explains the apparent paradox of experimental success outside the laboratory setting, using Louis Pasteur’s field trials of his anthrax vaccine as an example, by denying that the laboratory has ever really been abandoned. Instead, when, for instance, Pasteur managed to create a vaccine found to work on animals in carefully controlled laboratory conditions, his demonstration of its effectiveness on actual farm animals involved, according to Latour, transferring his laboratory to the farm. It was not that Pasteur’s vaccine worked in the laboratory and on the farm; the vaccine only ever worked in the context of the laboratory trial. Pasteur’s trick was in turning the farm into a laboratory while maintaining the illusion that it was still a farm. Hence, experiments can be spread, on this view, only via networks of laboratories or laboratory-equivalents; they do not in fact work everywhere.

5. Experimental Systems

In the 1990s, there appeared a number of new conceptualizations of experiment, including an important collection of essays concerning the life sciences, The Right Tools for the Job (Clarke and Fujimura 1992), and significant discussions of various experimental practices and regimes in Peter Galison’s Image and Logic (Galison 1997). These new conceptualizations had in common a more expansive and complex view of the ways in which experiment forms a part of elaborate systems of scientific practice. Andrew Pickering’s The Mangle of Practice (Pickering 1995) developed from and built upon his earlier SSK- influenced work by attempting to understand scientific practice as a pragmatic interaction between experimental procedures, theoretical models, and physical reality. The constraints on scientific ideas resulting from the interaction between these theoretical and material practices had become in Pickering’s work an important and central feature that rejected any attempt at pure sociological reductionism (although whether this has ever truly existed in STS is a debated point). Pickering saw scientific work as an ongoing enterprise aimed at stabilization: theory and experiment cooperate, at least for a time, in producing mutually consistent, intelligible interactions between human beings and the world. By placing experiment within this more complex structure of scientific practice, Pickering thus endeavored to move beyond the sociological insights of science studies and to regain a connection with the natural reality with which science has always claimed to deal.

Similar pragmatic moves had also appeared in an important study by the historian Robert Kohler. In his Lords of the Fly (Kohler 1994), Kohler studied the early decades of drosophila (fruit-fly) research in the United States, centered on the laboratory of Thomas Hunt Morgan at Columbia University and subsequently at the California Institute of Technology. Kohler described the operations of Morgan’s fly lab in terms of the exploitation of the capabilities of the materials, centrally including the flies, with their particular breeding and variation characteristics. The whole taken together, and crucially including material practices (given some precedence in this study over intellectual practices), was characterized by Kohler variously in terms of ‘experimental practice,’ ‘experimental production,’ or as a ‘system of experimental mass production.’ The term ‘experimental system’ was also used by Hans-Jorg Rheinberger in an ambitious study, Toward a History of Epistemic Things (Rheinberger 1997). Rheinberger, following the same general tendencies as Kohler and others, and with an important nod to Fleck, represented his project as being directed against the old philosophical tendency to view experiments as isolated epistemological elements, instead focusing his attention on the integration of experiment within a multifaceted system of practices which together constitute the modern scientific enterprise (cf. also Knorr-Cetina 1999, especially pp. 39–43). Consequently, experiment has lost much of its former philosophical mystique.

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