Abstract and Keywords
There is a historical trajectory in methods discourse that is worth uncovering, encompassing changes in content, in the ways in which methods discourse is incorporated in experimental reports to establish proper procedure and changes in the ways in which the experimenters utilized statements and reflections about methods to confer epistemic force on the results presented. It is this trajectory that the book captures, and the distinctions among layers of methods discourse and among descriptive and critical perspectives on methodological issues are means to this end. Methodological advancement means increasing awareness of the obstacles and limitations of experimentation: the unknown but suspected contingencies, the countless circumstances, the variations among living beings, the complexity of organic bodies, and the uncertainties related to techniques and instruments for the study of subvisible phenomena. Methodological advancement means increasing efforts to develop strategies for managing and perhaps overcoming these challenges. Methodological advancement also includes the realization that the means through which we make sense of the world might forever remain precarious.
Keywords: layers of methods discourse, history of methodology, experimentation
This book began as an extended comment on Fontana’s careful descriptions and justification of his methods, his approach, and his strategies for making experimental findings more secure. Thinking about Fontana’s work has brought into focus an aspect of science that has often been neglected in history as well as in philosophy of science: working scientists’ methods discourse, its meanings, the roles it plays in reports of experiments, the textual forms in which it is presented, the link to contemporaneous philosophy of science (or lack thereof), and the historical development of it all.
Methods discourse comes in layers. There are the protocols—scientists’ (or experimental philosophers’) accounts of the steps of an experiment or observation, as well as of the materials, equipment, and techniques that were used. Methods discourse also encompasses methodological views—scientists’ (or experimental philosophers’) conceptualization of procedures to assess and secure empirical results. In addition, methods discourse involves broader commitments to experimentalism—specifically to the imperative that scientific ideas must be confronted with, or based on, empirical findings.
Protocols, methodological criteria for successful experimentation, and even the commitment to experimentalism have histories. The procedures and techniques for experimentation changed, different methodological criteria were privileged at different times, entirely new criteria for securing and validating experimental results emerged, and what it meant to be committed to experimentation changed, too. Because these changes did not always occur at the same time—nor did they happen at the same pace—the distinction among the layers is a convenient analytic tool for the history of methods discourse.
(p.214) Scientists may take descriptive or critical perspectives on methods discourse. Experimenters’ pronouncements and commitments relating to methods are sometimes, but not always, accompanied by explicit reflections on, and justifications and defenses of, methods, techniques, and methodologies. Broader commitments to experimentalism are at times explicitly defended, specific methodological strategies are singled out and bolstered with supportive arguments, and even the proper ways of writing about methods-related issues might become a theme for critical reflection.
Fontana’s treatise is such a remarkable document because it exemplifies so well both the layering of methods discourse and the distinction between descriptive and critical perspectives on methodological issues. Fontana described at length the plan, experimental setup, and procedure for each of his numerous experimental projects. In his narrative, he expounded again and again the criteria for successful experimentation, and he included in his book a methodological essay in which he described, explained, and defended his methodological principles and his experimentalism. Fontana’s work exemplifies how methods discourse is shaped and influenced by a range of factors. Not only the social organization of the scientific community and its place in society but also prevalent conceptions of nature, of proper reasoning, and of scientific writing affect the content and presentation of methods discourse. The organization of the community of naturalists, the recalcitrance of experimental objects, conventions for writing analytically, and conceptions of nature and body impinged on the content of his methodological views, as well as on the ways in which methods discourse was integrated in his writings.
The distinctions among the different layers of and perspectives on methods discourse are not always perfectly clear-cut, neither in Fontana’s treatise nor in other experimenters’ reports of their activities and endeavors. Nevertheless, these distinctions are helpful tools for a fine-grained analysis of methods discourse in different fields and historical periods as well as for comparisons across fields and periods. Protocols are often bound to specific investigative contexts. Methodological views are typically transcontextual, spanning longer periods and more fields of investigation. Broader commitments—in particular the general commitment to experimentalism—are often of long duration, although, as we have seen, there were a number of different reasons why and various audiences to whom such a commitment was expressed.
Paying attention to the different layers methods discourse shows that protocols, descriptions and justifications of methodological criteria, and (p.215) commitments to experimentation are incorporated in different portions of experimental reports, whether in introductions, in methodological essays, as integral parts of descriptions of experimental projects, or in highly technical “methods sections.” Not only the content but also the stylistic features and organization of methods discourse change over time. Methods discourse does not constitute a specific genre of text. In fact, experimental reports themselves already come as different textual genres—letters, book-length narratives of experimental projects, journal articles, articles in peer-reviewed professional journals, and articles in popular magazines. The organization of such texts is historically variable, too. Modular scientific articles with distinct methods sections became common only from the 1930s onward. Today, new communication tools, especially electronic publication, even allow outsourcing methods sections to separate files.
Of course, little insight would be gained if we simply compared seventeenth-century and present-day methods discourse—say, the seventeenth-century treatment of repetitions and the twentieth-century notion of independent support or the plan of an early modern animal experiment with the design of biochemical analyses of protein molecules, or else the seventeenth-century narrative of an experimental project with the twentieth-century modular article. These things are simply too different for comparisons to be very illuminating. But there is a historical trajectory in methods discourse that is worth uncovering—namely, changes in content, in the ways in which methods discourse is incorporated in experimental reports to establish proper procedure, and in the ways in which the experimenters used statements and reflections about methods to confer epistemic force on the results presented. It is this trajectory that this book has sought to capture, and the distinctions among layers of methods discourse and among descriptive and critical perspectives on methodological issues are means to this end.
Protocols comprise the description of the experimental design and setup, procedures, and interventions to obtain an effect. Protocols encapsulate the correct way of doing things within and even beyond a particular laboratory context. The protocol is the most variable ingredient in methods discourse because it is often (but by no means always) closely tied to concrete experimental projects. The life span of experimental designs might (p.216) be comparatively short; protocols might be adapted quickly or might be replaced as new or improved instruments, research techniques, and materials become available. Nevertheless, writing the history of methods discourse with an eye to protocols can lead to unexpected insights about the constitution and situation of scientific disciplines when it turns out that researchers working in quite different fields adopted quite similar protocols. The migration of protocols across different fields is especially noticeable in the second half of the nineteenth century, and it binds fields together in ways that the mapping of personal interactions among researchers or the tracking of explicit citations might not capture. For the history of venom research, paying attention to protocols is particularly enlightening. One of the key features of venom research is that it intersects with so many different fields in the life sciences, and this is reflected in venom researchers’ incorporation of protocols from medical chemistry, physiology, pathology, bacteriology, immunology, and so forth.1
Writing the history of methods discourse with an eye to protocols can be informative also because it can tell us how much certain techniques and procedures were standardized, how technologies became established and eventually black-boxed, how resources were exchanged among research groups, and so on.2 For instance, especially from the nineteenth century onward, we find names attached to procedures, techniques, and tools (the Sternberg bulb, the Tiselius apparatus), and we have seen how Slotta’s ample resources and generous gifts of venom made an entire generation of venom researchers focus on the Brazilian rattlesnake.
Typically, experimental reports contain at least some descriptions of procedures. We know from older histories of experimentation that the style of presentation of protocols might vary dramatically—between the seventeenth and the early twentieth century, it changed from prolix and vivid narrations and depictions of all the conditions and procedures involved in the experiment to terse, parsimonious descriptions, increasingly reduced to mere lists of instruments, processes, and acronyms that only the expert reader can understand. Perhaps the most detailed descriptions of instruments, techniques, equipment, and so on were published in the early modern period, but even in the seventeenth century, by no means were all descriptions prolix. In the second half of the nineteenth century, as experimental reports proliferated, easy access to information became a prime concern, and prolixity turned from a virtue to a vice.
Explicit reflections on protocols are rare, however, except in periods of controversy about appropriate procedures or as part of a retrospective in (p.217) a review article. As we have seen, authors of reviews sometimes discuss in hindsight procedural errors that were deemed particularly damaging to an unfolding field.
Methodological strategies or criteria typically transcend local contexts and remain in effect for extended periods. Repetitions or repeatability are obvious examples for strategies or criteria that have long governed experimental practice. Early modern experimenters insisted that experiments must be repeated several times; to this day, repeatability remains one of the hallmarks of successful experimentation. But even though certain methodological concerns have long remained in place, they have not continuously been foregrounded in scientific discourse. Early modern experimenters were concerned about repetitions; some explicitly required multiple trials. Fontana took this requirement to the extreme. He stated that thousands of repetitions might be necessary to gain confidence in a result, and again and again he pointed out that he had repeated a trial numerous times. Even today, a singular experimental trial that cannot be performed again would not count for much, but this condition is just too basic, too taken for granted, to be discussed in a research article. The Stanford Encyclopedia of Philosophy entry on experiments in biology does not mention repetitions. The list of key epistemic strategies for validating experimental outcomes in the entry on experiments in physics also does not include repetitions. In the text, authors Allan Franklin and Slobodan Perovic do briefly discuss repetitions, but only in connection with a specific controversy in high-energy physics—namely, the debates about the “Fifth Force.”3 (High-energy physics is a special case, because repetitions of experiments pose particular challenges.) Replication (in the sense of repeating other people’s results) is a different issue. The question of whether it is possible to replicate particular research outcomes is often intensely debated, but predominantly in contexts where certain findings are challenged.
Fontana put repetition first on his list of principles for successful experimentation, and he took his preoccupation with repetitions to the extreme. Still, he and other late eighteenth-century investigators placed the emphasis on variations: through countless “diversifications” of setups, initial conditions, tools, and experimental objects, they tried to establish cause–effect relations and to identify potentially confounding factors.
(p.218) Charting the history of scientists’ methods discourse has led to a better understanding of the changing relations between the experimenters’ own methodological reflections and the history of professional philosophy of science. In the course of the nineteenth century, systematic analyses of scientific methods and logic and working scientists’ reflections on their practices gradually diverged, and more formal treatments of methods were presented in books on the logic of science (or natural philosophy). In the mid-nineteenth century, the systematic search for and identification of causes through variations and comparative experimentation were explicitly conceptualized in works such as Herschel’s Preliminary Discourse of the Study of Natural Philosophy, Mill’s System of Logic, and Comte’s Cours de philosophie positive. These systematic analyses of the structure of methodological issues were often in tension with the more pragmatic concerns and approaches of working scientists. It is in this context that working experimenters explicitly rejected the idea that many earlier experimenters took for granted—namely, that medical experimentation could profit from an orientation toward the physical sciences. Mead and other early eighteenth-century medical men wanted “Newtonian medicine”—the medicine of numbers, math, and geometry. By contrast, many (but not all!) mid-to late nineteenth-century experimenters emphasized that biomedical experimentation was profoundly different from physical experimentation, that methodological ideas from physics could not be transferred to the life sciences, and that the ideal experimental situation could never be obtained in biomedical investigations. They assumed that life, living organisms, and those organisms’ environments were too complex to be fully understood by the experimenter and that rigorous experimentation as required by Mill’s methods of experimental reasoning was impossible.
Mill himself acknowledged that his method was idealized and must be amended for practical purposes even in the physical and chemical sciences, as experimental conditions could not always be completely specified in actual experimental situations. Mill was most concerned with the ideal experimental situation and the inferences that could be drawn from such ideal experiments, as well as the epistemic force of these inferences. Many practitioners of experimentation in the second half of the nineteenth century were more concerned with the actual challenges they encountered every day in the laboratory. Some even introduced terminological distinctions to mark the difference—Bernard’s notion of comparative experimentation, for instance, encapsulates a retreat from Mill’s ideal experimental situation and an explicit acknowledgement that in practice, the (p.219) experimental conditions for determining truly causal relations could only be approximated.
In these discussions, the difference between the practice of identifying causes in complex, complicated real-life experimentation and the structure of causal reasoning from ideal experimental situations came to the fore. It is, above all, a question of emphasis. The experimenters in the life sciences sought to develop strategies for dealing with complexity—and yet they did try their best to constrain and determine the experimental situation so as to approximate ideal of a completely determined physical experiment. The authors of methods treatises, by contrast, concentrated on the structure and epistemic force of experimental strategies—and yet they did acknowledge that in actual investigations, the ideal was unattainable.
In current historiography and philosophy of science, this tension between systematic, idealized philosophical reconstructions and real-life methodologies has turned into a tug-of-war between different brands of historically informed philosophy. The emergence of the concept of control is a wonderful (and to the analytically inclined philosopher quite maddening) illustration of this tension. In hindsight, it appears plausible to interpret the structure of control experiments with the conceptual tools of Mill’s methods of inquiry. But the actual scientific discussions around 1900 about controls, controlling experiments, and control-experiments are so multifaceted and conceptually elusive that they escape easy categorization along these lines. Careful analysis of the different uses of control concepts shows, moreover, that the various terms related to experimental control capture quite different practical concerns—including concerns with the stabilization of experimental conditions, with causality, and with uniformity and comparability across local contexts.
Equally striking are the endeavors to establish the existence and agency of things and processes that were not directly observable. The investigators had to find ways of identifying substances and of assessing their agency, all while trying to stabilize very complex experimental environments. The factors assumed to be relevant for the formation and development of embryos or the pathogens bringing about diseases could only be inferred; intermediary bodies, complement, and even the products of their agency were assumed to be present or absent in experimentally generated and manipulated fluids. These challenges linked the work of investigators in seemingly remote fields, such as experimental embryology, pathology, physiology, and immunology, and they continued to occupy researchers in early twentieth-century life sciences.
(p.220) The very fact that experiments and observations dealt with unobservables—that is, with entities that could not be directly manipulated and with processes that could not be seen to happen—was not considered problematic in itself. But for many investigators, the problem of how to connect theoretical assumptions to observable phenomena was a point of concern. How could these assumptions be assessed? How could hypotheses about hidden entities and processes be validated? The question of the role of hypotheses in scientific research had been a part of methodological debates at least since the days of Newton. The exchanges between Mill and Whewell about induction brought the issue to the fore. Again, the most systematic treatments of the problem at the time can be found in books of the logic of science. For us, what is at stake in these discussions is the underdetermination of theories and hypotheses about unobservables. Past experimenters themselves were less explicit in their reflections, although we do find occasional suggestions along the line of Whewell’s ideas about the testing of hypotheses—namely, that the degrees of predictive success and simplicity of the hypothesis be considered in hypothesis evaluation. Other than that, the responses remained practical and pragmatic: As long as the evidence fit with the hypothesis or theory, as long as the hypothesis explained the phenomena, it was considered acceptable.
For late nineteenth- and early twentieth-century investigators, the question of how to deal with theoretical and instrumental uncertainties became the most pressing methodological issue. Of course, repetitions, variations of experimental conditions, and systematic comparisons were still a relevant part of experimental practice, but the emphasis in methods discourse had shifted. The investigators were confronted with two problems: First, the elaborate techniques and instruments for investigating subvisible phenomena that had become available were not completely understood. Second, the results obtained with those techniques and instruments were too narrow and piecemeal to yield comprehensive understanding of a phenomenon of interest. Again, we find in the strategies of the experimenters a pragmatic, “real-life” counterpart to philosophical discussions about underdetermination—namely, the integration of multiple research techniques and approaches.
Protocols are described at least briefly in virtually every experimental report. Methodological views, by contrast, are not always explicitly stated. If they are mentioned, they are often not discussed in detail. Explicit methodological discussions might indicate novelty. Fontana’s methodology of experiment, for instance, reflects not only his attempts to disarm his opponents (p.221) but also the emergence of a new conception of circumstances of experimentation that demanded a novel approach to experimentation. Most of the time, however, methodological views and strategies come to the fore in controversies and critical debates. Such controversies might concern concrete empirical results or entire approaches, such as the best way to pursue developmental embryology or the soundness of the metaphysical principles underlying experimental medicine. Researchers who had an axe to grind might even include a methodological essay in their work, as Fontana did. Or, like Roux, researchers might frame an entire discipline-specific journal to good effect with a long programmatic introduction saturated with methodological pronouncements. Yet others might publish whole books on the methodology of experiment, as Bernard did in his attempt to intervene in contemporaneous debates about the usefulness of statistics and about the plausibility of vitalism vis-à-vis determinism in physiology.
Today, we often find that the more concrete methodological debates about proper procedure migrate to outlets other than the experimental report. On the one hand, professional philosophers of science discuss in more or less abstract terms the structure and epistemic force of specific experimental strategies and proper reasoning processes—measurement robustness, severe testing, the argument from coincidence, and so forth. On the other hand, scientists themselves might be driven to discuss methodological problems in general science journals or even in popular media—because established professional practices are under scrutiny or because they are held accountable for spending taxpayers’ monies, or both.
Commitments to Experimentalism
General commitments to the view that experimentation is the hallmark of science transcend even long-term methodological commitments such as the commitment to repetitions, to the variation of experimental conditions, or to “causal research.” Commitments to experimentalism have been expressed ever since the rise of the “new” experimental method in the seventeenth century. In the broadest sense, “proper procedure” for the study of nature just means “experimental inquiry” per se. With the possible exception of Redi’s and Charas’s contemporary Bourdelot, all investigators who populate this book endorsed experimentation and were experimentalists in this broad sense, and many of them explicitly committed themselves to experimentalism.
(p.222) Even the very commitment to experimentalism has a history, however: It meant different things and served different purposes for different people. Sometimes it evoked Bacon’s Novum Organum, sometimes Newtonianism (which also comes in different flavors). Experimentation was favorably contrasted with the practice of following or trusting ancient authorities; at other times experimentation was favorably contrasted with “mere” (e.g., noninterventive) observation of events and processes in nature. The commitment to experimentation could also be made to align oneself with a particular professional community—such as, for instance, those medical men who endorsed scientific medicine.
The audiences for the commitment to experimentalism and the ways in which this commitment was expressed changed accordingly. In the early modern period, scholars who endorsed experimentalism addressed other scholars who engaged in the study of nature, religious authorities, or aristocratic patrons. It thus made sense for them to treat the broader commitment to experimentalism as an integral part of the letters they wrote to their sponsors and patrons. In the nineteenth century, experimenters such as Mitchell addressed their arguments for experimentalism to university trustees, perhaps also to antivivisectionism advocates, or else to fellow members of the medical community who doubted that experimental methods could ever advance therapeutics. Here the commitment to experimentalism became a battle cry in disputes among different professional groups and between professional scientists and the larger public. At this time, commitments to experimentalism had become largely separated from experimental reports. They had drifted to introductory sections, and sometimes they were entirely removed from scientific articles and appeared in public addresses and commencement speeches. Only rarely do we find commitments to experimentalism within experimental reports in publications after 1850. If we do, we can be sure that specific battles were fought within the relevant community of experimenters. Explicit discussions of and apologies for experimentalism migrated from experimental reports, textbooks, and programmatic writings for scientists to public addresses for broader, often nonscientist audiences.
Writings on scientific writing are valuable resources for tracing the dynamics of methods discourse, because they tell us what was deemed to (p.223) be an effective means of presentation and persuasion at a certain time. Of course, we cannot assume that experimenters actually read all these books about writing scientifically and followed the guidelines. Some of the medical students at Oxford might well have glanced at Allbutt’s treatise on the composition of scientific papers if they had any time to spare before submitting their theses, but they probably generally didn’t. If at all, past experimenters will have followed editorial and journal guidelines when they were submitting their texts for publication. But for the historian of methods discourse, the manuals and guidelines on writing scientifically are valuable sources of information because they reflect the different conceptions of good argumentation and effective organization of a scientific text that were held at specific points in time.
The preceding chapters have shown not only that there are different genres of experimental reports but also that there are different genres of “writing on scientific writing”—the eighteenth-century books on scientific methods, the manuals on professional writing that developed out of books on classical rhetoric in the second half of the nineteenth century, and the specific guidelines for writing professionally that appeared around 1900.
These differences are significant, and they point to a transformation in methods discourse that has not attracted much attention. Until the mid-nineteenth century, writings on writing scientifically invoke contemporaneous ideas about both proper experimental procedure and proper reasoning practices. The very first chapter of this book showed that for Boyle, the distinction between experience and speculation was the complement of the distinction between narrative and argument in an experimental report. Late eighteenth-century guidelines bring theoretical notions and empirical facts closer together, but the organization of the account is still expected to elucidate experimental procedures—the guidelines call for the demonstration of the discoverability of a theoretical idea. The organization of Fontana’s bulky tome exemplifies this approach.
In contrast, from the late nineteenth century onward, the sequence of experimental steps and the steps of the argument were separated, and argument and methods discourse no longer had to correspond to the actual practices of experimentation. One of the main driving forces for the turn to so-called deductive composition was the notion that “composing deductively” could facilitate the researcher’s understanding of the main points of a scientific paper.
Paying attention to the history of methods discourse also sheds new light on Charles Bazerman’s suggestion that scientific writing underwent a (p.224) transformation from “establishing credibility of the author” to “establishing credibility of the procedure.” In his account, seventeenth- and early eighteenth-century experimenter–authors aimed to establish their own credibility when they were presenting their results. They did so by citing illustrious witnesses or by assuring their readers that they had performed experiments with care and caution. Starting in the late eighteenth century, scientist–authors began to offer detailed reports of each individual experiment to support their views. In such reports, the burden of persuasion falls on “the representation: to establish proper procedure (that is, the experiment is done as any scientist might have done it), to specify all the conditions and procedures (that is, replication instructions), and to indicate how the experimental procedure answers potential objections.”4
The distinction between establishing the credibility of authors and establishing the credibility of procedures is a helpful analytic tool for examining experimental reports, but my study has shown that the notion of an overall transformation from author-centered to procedure-centered writing is misleading. Early modern authors, too, made efforts to establish the credibility of procedures when they wrote about experiments. Redi did try to establish his trustworthiness by referring to witnesses, as did several of his critics, but he also presented, and to some extent discussed and defended, “proper procedure” to establish credibility of his experiments and results. He admonished one of his adversaries who had not performed enough repetitions of experimental trials, for example—not to question his opponent’s credibility, however, but to question the reliability of the trial outcome. If we compare Redi’s letters with late eighteenth-century writings on experiments, what we find is not so much a transformation but rather a shift of emphasis from person to procedure in the sense that later writings contain a much larger proportion of methods discourse and only a few references to witnesses and their social positions. Establishing the credibility of the experimental procedure was always a prime concern.5
Transformations of Methods Discourse
We are left with the question of how the dynamics of methods discourse can be explained. Why were some aspects of methods discourse preserved over longer time periods but others not? What forces drove the shifts, the innovations, and the transformations? Historians and sociologists of experimental science have shown that the social organization of the scientific (p.225) community shapes certain features of methods discourse (such as eponymy and the modularity of scientific papers). But the social does not fully explain the content of the methodological reflections that are incorporated in scientific texts. Other factors that constitute methods discourse are metaphysical conceptions of nature, life, disease, and causality, new theoretical ideas and investigative techniques, and the very practice of experimentation itself.
Early modern experimenters required that experiments be repeated because they were concerned with the possible effects of accidental events and contingencies that, unknown to the experimenter, might interfere with the experiment. Fontana, by contrast, assumed that the circumstances surrounding the experiment could be identified, and he required all experimenters to identify them—and thus must have assumed that circumstances were not random occurrences but rather regular phenomena amenable to systematic study and general characterization.
Even the diligent application of methodological principles in experimentation might in turn lead to methodological innovation. In the late seventeenth century, the identity of experimental outcomes was the ideal that guided methodological reflections and the evaluation of experimental trials. In the course of the eighteenth century, the commitment to numerous repetitions combined with the increased emphasis on measurement became a driving force for the development of new methodological concepts. Many repetitions of measurements yielded discrepant data sets, which in turn motivated changes of protocols. Sometimes these changes led to more uniform results. At other times, however, greater uniformity of the results could not be achieved. Around 1800, we notice an erosion of the ideal of uniformity as an unintended consequence of the methodological goal of numerous repetitions, and new approaches to data management emerged as well.
Rapid development of new theories and instruments could also drive methodological innovation. Around 1900, the problem of uncertain theories and techniques justified the strategy to seek independent confirmation for one’s findings through a different experimental approach. Experimenters remarked that some of the newly emerging and intricate technologies were not yet completely understood and that others were too specialized and too narrow in scope to provide comprehensive information about a particular subject.
Methodological discussions and reflections might get to a point where stock-taking appears necessary. Experimental strategies and methods (p.226) are explicitly justified and formalized in systematic treatises on logic and method. Sometimes, such books were written by authors who were well read in the sciences (and their history) but who were not (at least not predominantly) experimental researchers themselves—authors such as Bacon, Mill, Whewell, or Comte. These treatises were often the culmination of a period of methodological innovation; they were produced in hindsight, intended as an intervention to advance a certain position or to offer a synopsis and achieve closure in a period of intense debate. Those treatises might in turn become sources of reference for experimental researchers. These researchers might present themselves as Baconians or Newtonians, like Mead and Fontana, or they might engage critically with the programmatic texts, as the nineteenth-century critics of Mill did.
Critics and analysts of science like Mill developed their philosophical views through an engagement with scientific debates and practices, as have many philosophers of science in the late twentieth and early twenty-first centuries. At the same time, working scientists engage with and scrutinize philosophical thought. Mill’s explication of the methods of experimental inquiry, for instance, drew on early nineteenth-century science, as did Comte’s discussion of experiments in physics and biology. Bernard’s methodological conception of “comparative experimentation” emerged from a reflection on his own earlier experiments as well as from a critique of Comte and Mill. Roux’s discussion of the causal method of research and of hypotheses combined a critique of Mill with an invocation of Whewell.
In the preface to the third edition of Against Method, Paul Feyerabend reassured his most zealous critics that “‘anything goes’ is not a ‘principle’ I hold—I do not think that ‘principles’ can be used and fruitfully discussed outside the concrete research situation they are supposed to affect—but the terrified exclamation of a rationalist who takes a closer look at history.”6 An even closer look at history shows that there is a sense in which strategies and tools of experimentation transcend the concrete research situation. There were trends and strands, shifts and innovations on all levels of methods discourse—even advancement of sorts. Many strategies and tools of experimentation became more refined, results became more quantitative and precise, and experiments became more informative about subvisible worlds. Overall, however, the long-term history of methods discourse as it emerges from this book’s analysis is not simply a steady progression toward more sophisticated or more improved methodologies of experimentation. Methodological advancement means increasing awareness of the obstacles and limitations of experimentation: (p.227) the unknown but suspected contingencies, the countless circumstances, the variations among living beings, the complexity of organic bodies, and the uncertainties related to techniques and instruments for the study of subvisible phenomena. Methodological advancement means increasing efforts to develop strategies for managing and perhaps overcoming these challenges. Methodological advancement also includes the realization that the means through which we make sense of the world might forever remain precarious. (p.228)
(1.) Such migration of protocols is also visible in other fields. Late nineteenth-century histologists, for instance, used experimental designs from experimental physiology in their studies of fluids and tissues; see Schickore, “‘… as Many and as Diverse Methods as Possible Ought to Be Employed. …’”
(2.) Hannah Landecker, Culturing Life: How Cells Became Technologies (Cambridge, MA: Harvard University Press, 2007).
(5.) Steven Shapin, The Scientific Life: A Moral History of a Late Modern Vocation (Chicago: University of Chicago Press, 2008).
(6.) Paul Feyerabend, Against Method: Outline of an Anarchistic Theory of Knowledge, 3rd ed. (London: Verso, 1993), vii.