History-Philosophy Relations, Pt. 3: Empirical History, Transcendental Standards, and the Unity of Science March 28, 2013Posted by Will Thomas in Commentary Track.
Tags: Allan Franklin, Carl Anderson, Charles Weiner, Daniela Monaldi, Hans Reichenbach, Hilary Putnam, Imre Lakatos, Kent Staley, Paul Oppenheim, Peter Galison, R. A. Fisher
In my previous post in this series, I noted that the program of “historical epistemology” rejects conceptions of science informed by traditional philosophy of science in favor of seeking portraits that are both historicized, and that follow the historical record more directly. In general, I agree that historicity and fidelity to the historical record are both principles that must inform historians’ work. At the same time, I am not convinced that it is either necessary or wise to abandon traditional philosophy of science to realize those principles. To investigate this issue, I would like to turn to what I believe may be its high-water mark: the Kent Staley-Peter Galison dispute,1 which has been summarized by Allan Franklin in his 2002 book Selectivity and Discord. To conclude the post, I will develop my own opinion on the issue, elaborating on points I made in my recent article, “Strategies of Detection: Interpretive Strategies in Experimental Particle Physics, 1930-1950”.
In the view of Galison, science is fundamentally disunified, being divided into groups who adhere to irreconcilable ideals concerning what constitutes proper scientific practice and knowledge. According to him, this disunity is a crucial source of strength in science. First, scientists’ ability to establish points of agreement in spite of their differences testifies to the legitimacy of their knowledge. Second, disunity generates dynamism as tensions between ideals lead to the emergence of new ideals. Thus, in his 1997 book Image and Logic—one of my favorite history books—he argues that for much of the twentieth century, physics experimentation was divided into two epistemically divergent traditions of “image”-based detection and “logic”-based detection. Physicists in the former camp sought definitive images of phenomena (“golden events”), while those in the latter camp sought statistically rigorous proofs.
There is no dispute that “image” and “logic” traditions of instrumentation existed. One of Galison’s finest points in Image and Logic is his argument concerning how seldomly physicists moved from one tradition to the other. What is at issue is the question of epistemic divergence, which ultimately bears upon what historians take to constitute satisfactory portrayals of scientific thought.
In his 1999 article, “Golden Events and Statistics: What’s Wrong with Galison’s Image/Logic Distinction,” Kent Staley argues that even arguments in the image tradition adhered to a statistical structure, even though “such arguments might not always wear their statistical nature on their sleeves.” Arguments employing this structure “mark a unity between the two traditions at precisely the point where Galison sees an epistemic disunity” (202-203). In fact, Staley argues, “The epistemic divide between these two traditions was not so great as to make an interlanguage necessary for them to communicate, cooperate, and, eventually, unite in a single experimental pursuit” (224)—one of Galison’s central arguments.
Noting, “The trend in science studies is towards identifying disunities in the sciences” (226), Staley goes on to press a contrary programmatic argument (227):
We might entertain the following version of the ‘unity of methods’ thesis: there are a small number of forms of argument that are shared among otherwise diverse areas of investigation, or that are employed in common during otherwise distinct historical periods of scientific endeavor.
He swiftly qualifies: “I consider it to be an empirical question whether, and to what extent, this kind of unity exists within the sciences.” He allows, for instance, that he is examining only the case of experimental particle physics, where the “particular statistical form of argument makes use of an ontology of ‘events,’ which will not be shared by every field of empirical inquiry. (Although one might articulate a more general form that might be found among a yet wider variety of scientific disciplines)” (227). What Staley is advocating is a preference for the assumption of unity of argumentative form—or, following the language (if not the exact ideas) of Paul Oppenheim and Hilary Putnam,2 for him unity constitutes a “working hypothesis”.
In his response, Galison did not prove amenable to this suggestion, insisting that such presumptions were contrary to the plain evidence of the historical record. To be valid, any underlying statistical unity would have either to structure scientists’ psychology unconsciously, or it would have to structure the progress of science by some means that transcended the efforts of the individual scientist. Galison rejected both possibilities, noting that the latter replicated philosopher Imre Lakatos’s call for the “rational reconstruction” of science, which Galison regarded as anathema to proper historiography. In making this argument, Galison specifically, if tacitly, supposed that valid epistemological theories must replicate what philosophers have referred to as a “logic of discovery”, that is, a historically coherent account of the process of knowledge construction.
However, it has been a long time since philosophers believed that the philosophy of science describes a logic of discovery. Unhaunted by Kuhn’s Demon, Lakatos himself argued in his famous 1970 paper, “History of Science and Its Rational Reconstructions” (92):
There are several methodologies afloat in contemporary philosophy of science; but they are all very different from what used to be understood by ‘methodology’ in the seventeenth or even eighteenth century. Then it was hoped that methodology would provide scientists with a mechanical book of rules for solving problems. This hope has now been given up: modern methodologies or ‘logics of discovery’ consist merely of a set of (possibly not even tightly knit, let alone mechanical) rules for the appraisal of ready, articulated theories. Often these rules, or systems of appraisal, also serve as ‘theories of scientific rationality’, ‘demarcation criteria’ or ‘definitions of science’. Outside the legislative domain of these normative rules there is, of course, an empirical psychology and sociology of discovery.
Now, Lakatos went on to argue that science could be rationally reconstructed according to the rules of appraisal dictated by whatever philosophical methodology one happened to adhere to, that this “internal history” should be treated as “primary” in the construction of historical accounts of scientific progress, and that such reconstructions would then be “supplemented by an empirical (socio-psychological) ‘external history'” (91). This, of course, was the point of view (even more so than Mertonian sociology) to which sociologists of scientific knowledge so strenuously objected. I agree that Lakatos’s primary/secondary ordering of internal and external history is overly constraining. But Lakatos’s emphasis on appraisal—what Hans Reichenbach referred to as the “context of justification”—should be taken into account in understanding the history-philosophy relationship (whatever the ultimate philosophical validity of the discovery-justification distinction).
Let us take as a case in point Carl Anderson’s discovery of the positron, which Galison considers to be exemplary of the image tradition, and which Staley argues is really statistical (if something of a slam-dunk case). It so happens we have two separate accounts of Anderson concerning his confidence in the discovery, based on the photograph to the right. The first is from his 1999 autobiography, The Discovery of Anti-Matter:
An experienced scientist, just by looking at the photograph, can readily come to the conclusion that the ‘thin curved line’ represents the path of a new, hitherto unknown type of subatomic particle. Although only a twenty-seven year old post doctoral research fellow, I actually reached that conclusion as I looked at the still wet film just after it had been put on the drying rack.
This sort of instantaneous recognition (and, indeed, the materiality of the story, “wet film” and all that) is very amenable to Galison’s point of view, and his concept of “trained judgment,” but it is not the end of the story. In a 1966 interview with historian Charles Weiner, Anderson recalled (my emphases):
I worried a great deal about the simultaneous occurrence of independent tracks [above and below the plate], which is always a possibility—two different electrons which happen to have this orientation—and felt that it was so extremely unlikely because we have stereoscopic cameras and could make fairly precise measurements of the position in the chamber in all three dimensions, and the lining up was just fantastically accurate. So that caused the publication.
The two remarks can be reconciled by supposing that, between Anderson’s discovery and his publication of that discovery, a further, more rigorous process of justification had to occur. Whatever personalized predilection Anderson might have had for this or that kind of evidence, that had to be put aside to accommodate possible objections. This point is very much in line with Alfred Nordmann’s response to Image and Logic, “Establishing Commensurability: Intercalation, Global Meaning and the Unity of Science,” where he claims that, even if science is not manifestly unified, for scientific figures the “idea of a unified science” (my emphasis) functions as a “regulative ideal,” which compels them to argue from other scientists’ points of view, and so to demonstrate how different points of view can be reconciled. This contrasts with Galison’s perspective, where agreement seems to be a phenomenon that emerges in spite of figures’ dogged adherence to disparate evidentiary ideals.
Remarkably, we find ourselves back at R. A. Fisher’s Tower of Babel analogy, where scientific figures become so wrapped up in their own area of work that they begin to have difficulty communicating with each other, which is more or less Galison’s message. But, according to Fisher, statistics and mathematics promised the only plausible means of reconciling disparate perspectives back into a unified science, which is more or less Staley’s message.
I propose that to reconcile these points of view—and I suspect this is fairly close to Staley’s perspective—we should think of logic, statistics, and probability as describing a transcendental standard, to which arguments should conform, but which need only be explicitly invoked in difficult cases. As is always the case with supposing the existence of anything transcendental in history, its existence should be considered a social construction in the strictest sense of the term. That is, it can only be considered to exist insofar as historical actors agree to its meaning, and agree that that meaning should structure their actions, including defending and reconsidering their points of view and resisting or admitting defeat in intellectual disputes.
Importantly, a transcendental standard (not unlike an “epistemic virtue”) can suffer an implicit existence, evident in its effect on actors’ actions, even if not fully articulated in a rigorous form by them or even the R. A. Fishers of the world. I allow it is, therefore, permissible for philosophers to articulate these standards on their own in any language they see fit, including formalistic ones. These articulations constitute not a description of history, but a lexicon that historians can use to describe patterns in historical actors’ actions and reasoning. Naturally, some elements of this lexicon will be useless for studying some corners of history, particularly the older ones, where more refined forms of argument had not yet been established or were not used (i.e., epistemology is indeed historicizable). At any point in history, only sociological factors can be responsible for raising or lowering the bar of argumentation. What our lexicon does is permit us to describe the intricacies of actors’ actions more accurately in those scenarios where they choose to raise the bar, as Anderson did in presenting his positron discovery. The alternative is to ignore the importance, or even the existence of those intricacies.
As I argue in “Strategies of Detection,” as unprecedentedly rich as Galison’s portrait of particle physics experimentation is, his historical portrait does, in fact, fail to satisfactorily describe the standards that many experimenters used to interpret their experiments and others’ experiments. In my article, I suppose that experimenters using different instruments had access to overlapping “strategies” that they could use selectively to design and interpret experiments in ways that varied in their conclusiveness: they could interpret individual events, they could aggregate evidence, they could use physical knowledge to narrow a range of possible interpretations, etc. Thus, for example, in some circumstances, image-tradition experimenters certainly sought golden events, but they also undertook many types of experiments (such as measuring the properties of cosmic rays) in which golden events would not have constituted a valid form of evidence. I do not suppose that these strategies were necessarily statistical, probabilistic, or logical, but I would allow—and this claim does not appear in my paper—that both these strategies, and the logic governing experimenters’ choice of strategies, could be legitimately rendered in such a language, and that, further, the depth of such a language would be necessary for capturing actors’ patterns of accepting and rejecting interpretations in their own, or in neighboring, traditions, even beyond the degree to which they articulated their rationales privately or in their publications.
If fully articulated, would such a language be unified? As even Lakatos noted, such a language might well not be “tightly knit”. However, it is abundantly clear that historians cannot simply say that science is disunified by reference to the obvious distinctions between, say, botany and physics, which, in turn, suggests that Staley’s suggestion for presuming unity is salubrious. As most actors would only use a slice of this language in their work, it may ultimately be immaterial whether the language is unified or not. What is clear, though, is that while such a language can never explain the history of science, historians require access to it in order to explain history in increasingly satisfactory ways, and we should pay attention to what it has to offer.3
1 I originally addressed this dispute in this post. The present post represents an update on my thinking.
2 Paul Oppenheim and Hilary Putnam, “Unity of Science as a Working Hypothesis,” (pdf) in Minnesota Studies in the Philosophy of Science, Vol. 2 (1958)
3 The historiography of particle physics is slow at the moment, but some other historians are also developing deeper descriptive vocabularies; see especially Daniela Monaldi, “The Indirect Observation of the Decay of Mesotrons: Italian Experiments on Cosmic Radiation, 1937-1943,” Historical Studies in the Natural Sciences 38 (2008): 353-404.