Paradigms, conceptual frameworks, and denkkollektive

Image: Ludwik Fleck as prisoner / scientist in Buchenwald

An earlier post opened a discussion of the "historical turn" in the philosophy of science in the early 1960s (link). This innovation involved two large and chiefly independent features: deep attention to the social and institutional context of scientific research, and the intriguing idea that research communities give rise to specific "mentalities" or conceptual schemes that are distinctive to that community. The previous post focused on the social and institutional contexts of science. Here I am interested in unpacking the second point about the specialized conceptual schemes and mental frameworks of scientific research communities.

This dimension of the sociological approach to the history of science has primarily to do with the mental frameworks of the practitioners. Here I am referring to the thinking, concepts, and practices of the practitioners within a give area of scientific research. This is the idea that participants in a research community develop shared mental or cognitive frameworks and conceptual schemes on the basis of which to organize their research and theories about the domains they study. It is sometimes argued that these schemes are to some extent incommensurable across research communities (as Kuhn sometimes maintained), leading to the difficulty or impossibility of genuine communication across research traditions. The guiding intuition is that the scientists' conceptual schemes are embedded in an extended social discourse within the research community, and the meanings (and even references) associated with key scientific terms differ systematically from one research community to the other. Important examples include Thomas Kuhn's conception of a paradigm (link), Imre Lakatos's conception of a research programme, or Ludwik Fleck's conception of a "thought collective" (link).

Let's first consider Kuhn's claims about incommensurability across scientific paradigms. (Oberheim and Hoyningen-Huene's article on incommensurability in the Stanford Encyclopedia of Philosophy is very helpful; link.) The idea of a paradigm is somewhat unclear in the original version of Structure of Scientific Revolutions. In its narrow meaning a paradigm is simply a clear example or illustration of something -- for example, a well-designed chemistry experiment. ("This is how you separate heavy water from common H20.") But more commonly Kuhn uses the concept of paradigm more broadly, intending to refer to the heterogeneous mix of material and cognitive practices shared by a scientific research tradition -- laboratory procedures, theoretical concepts, methodological principles, dissemination practices, ideas about the use of evidence and experimental data, and so on. In the 1969 postscript to SSR Kuhn refines his language of paradigm to refer to a "disciplinary matrix". A disciplinary matrix is "an entire theoretical, methodological, and evaluative framework within which scientists conduct their research" (174). The implication is that if one has acquired his or her intellectual reflexes within a discipline, each statement within the science will have a meaning that is affected by other elements of the framework.

(It is worth noting that this point about the dependency of the meaning of a theoretical sentence on a myriad of other commitments and concepts is similar to Quine's explanation in Word and Object of the underdetermination of theory and the indeterminacy of translation: the "meanings" of individual sentences can be adjusted according to the status of other assertions in the web of belief. In Quine's example: in the presence of a certain common small animal, I refer to "rabbit", you refer to "gavagai", and we cannot determine whether gavagai refers to the "individual whole animal" that I have in mind, or your own conceptual scheme of "undetached rabbit parts".)

Here is the first place that Kuhn refers to incommensurability in SSR. The concept arises in discussing successive schools of scientific thought such as Ptolemy and Copernicus:

What differentiated these various schools was not one or another failure of method—they were all “scientific”—but what we shall come to call their incommensurable ways of seeing the world and of practicing science in it. Observation and experience can and must drastically restrict the range of admissible scientific belief, else there would be no science. But they cannot alone determine a particular body of such belief. An apparently arbitrary element, compounded of personal and historical accident, is always a formative ingredient of the beliefs espoused by a given scientific community at a given time. (3)

A hundred pages later he returns to the topic of paradigm incommensurability:

As a result, the reception of a new paradigm often necessitates a redefinition of the corresponding science. Some old problems may be relegated to another science or declared entirely “unscientific.” Others that were previously nonexistent or trivial may, with a new paradigm, become the very archetypes of significant scientific achievement. And as the problems change, so, often, does the standard that distinguishes a real scientific solution from a mere metaphysical speculation, word game, or mathematical play. The normal-scientific tradition that emerges from a scientific revolution is not only incompatible but often actually incommensurable with that which has gone before. (103)

It should be noted that Kuhn's claims of incommensurability generally comes with qualifications. It is not a general claim of radical mutual unintelligibility across scientific research communities, but rather a claim about the impossibility of perfect and exact translation: "After he has done so [stepped from the old paradigm to the new] the world of his research will seem, here and there, incommensurable with the one he had inhabited before. This is another reason why schools guided by different paradigms are always slightly at cross-purposes" (111). The highlighted phrases demonstrate the intended softening of the claim.

The claim of incommensurability certainly seems to be a view about the mental constructs -- ideas, concepts, ways of evaluating claims -- that scientists use in their theories and their empirical and experimental practices. Kuhn, and later Feyerabend, seem to assert that participants in competing paradigms of the "same" subject matter see the world differently, and cannot fully agree or disagree with each other about apparently fundamental statements about the world. The classical physicist "parses" the physical world differently than does the relativistic physicist. And these mental schemes are conveyed to the young physicist through his or her training in the discipline; they are only partially formalized in the apparatus of scientific knowledge. In Michael Polanyi's formulation, they are a form of "tacit knowledge": “the aim of a skillful performance is achieved by the observance of a set of rules which are not known as such to the person following them”; Polanyi, Personal Knowledge: 49. Ways of viewing a laboratory across paradigms are sufficiently different that it requires a "gestalt shift" for a scientist to view the world through the alternative theoretical constructs. All of this sounds "mental".

(Here again Quine's views of semantics in Word and Object and "Ontological Relativity" are relevant. Quine seeks to undermine the "museum myth" of sentence meanings. "Uncritical semantics is the myth of a museum in which the exhibits are meanings and the words are labels. To switch languages is to change the labels" (186).)

Now let's turn to a scientist-philosopher whose work influenced Kuhn's, Ludwik Fleck. (A prior discussion of Fleck's work can be found here.) Fleck was a Polish scientist who offered a similar view of scientific conceptual spaces in 1935 in Genesis and Development of a Scientific Fact (1979/1935). Fleck was a medical researcher, and he developed his view of scientific concepts and research communities in Genesis around the example of the development of the concept of syphilis over several centuries.

Fleck was an important innovator in both aspects of the "historical turn" in science studies. Fleck's approach to the history and philosophy of science championed both aspects of the founding ideas of historicized science studies -- the importance of the specific social settings of the scientists, and the cognitive features of scientific work within a community of researchers. He emphasized the importance of the specific social arrangements within which scientific knowledge is produced:

When we look at the formal aspect of scientific activities, we cannot fail to recognize their social structure. We see organized effort of the collective involving a division of labor, cooperation, preparatory work, technical assistance, mutual exchange of ideas, and controversy. Many publications bear the names of collaborating authors. Scientific papers almost invariably indicate both the establishment and its director by name. There are groups and a hierarchy within the scientific community: followers and antagonists. societies and congresses, periodicals, and arrangements for exchange. A well-organized collective harbors a quantity of knowledge far exceeding the capacity of any one individual. (42)

Fleck also emphasized the conceptual dependency or incommensurability that became important in Kuhn's thought. In particular, Fleck offered a highly original idea about the social or "collective" nature of scientific concepts with his idea of a "thought collective" (denkkollektiv). (Thaddeus Trenn, the translator of Genesis and Development, notes that this term is a neologism introduced by Fleck, and it has no natural counterpart in English.) Here is how Fleck defines denkkollektiv:

If we define "thought collective" [denkkollektiv] as a community of persons mutually exchanging ideas or maintaining intellectual interaction, we will find by implication that it also provides the special "carrier" for the historical development of any field of thought, as well as for the given stock o f knowledge and level of culture. This we have designated thought style. The thought collective thus supplies the missing component. (39)

Fleck illustrates the dependence of scientific theory on the specific denkkollektiv with the example of the development of the modern concept of the agent of syphilis:

Siegel also recognized, in his own way, protozoa-like structures as the causative agent of syphilis. If his findings had had the appropriate influence and received a proper measure of publicity throughout the thought collective, the concept of syphilis would be different today. Some syphilis cases according to present-day nomenclature would then perhaps be regarded as related to variola and other diseases caused by inclusion bodies. Some other cases would be considered indicative of a constitutional disease in the strict sense of the term. Following the train of thought characterized by the "carnal scourge" idea, still another, completely different set of concepts concerning infectious disease and disease entities would have arisen. Ultimately we would still have reached a harmonious system of knowledge even along this line, but it would differ radically from the current one. (39)

The point here is important and plausible. Assumptions about biological structures, causation, and disease accreted within one research tradition -- one denkkollektiv -- constituted an extended and growing system of statements, investigative procedures, and research groups as scientific understanding of syphilis developed, and the theories and findings of the science must be interpreted in terms of that system of beliefs and assumptions. But the development of such a system is a highly contingent process, and a different ensemble of assumptions was possible. On that alternative ensemble, the eventual scientific product would have been quite different. This suggests the idea of "brachiation" in evolutionary theory, where the founder finch has one set of properties, and the daughter variants continue to diverge until there is little similarity with the founder or among the daughter sub-species.

The incommensurability to which Fleck refers seems to be of a fairly ordinary kind: if the scientist in the B-denkkollektiv of syphilis science frames his or her thinking in terms of dramatically different ways from scientists in the A-denkkollektiv -- different ways of defining the problem, different views of biological causation, and different assumptions about "causative agents", then their apparently simple statements about the disease will be difficult to inter-translate. This implies that apparently similar statements in A-language and B-language will have significantly different meanings, implications, and avenues of investigation for the two communities. The scientists in the two denkkollektive in the same domain will often talk past each other -- just as Kuhn asserts 25 years later in SSR.

To some extent a close reading of both Kuhn and Fleck serves to de-dramatize the implications of "incommensurability" that each asserts. Neither of these theorists puts forward a radical view of mutual unintelligibility across research communities, or a radical relativism of the findings of science in a particular field of research. Both reject the simple reductionist semantics of positivism (verificationism, instrumentalism) according to which the meaning of a scientific concept can be fully articulated as a set of procedures for verification. But they do not seem to think that conversation with comprehension is impossible between classical physicists and relativity or quantum physicists, or between wave theorists and particle theorists in subatomic physics, or between gradualists and punctuated-equilibrium theorists in evolutionary theory. Substantive disagreements about the domain of investigation and conflicting predictions about outcomes are possible, and that is enough to allow for meaningful scientific discourse to proceed across paradigms or "thought collectives". In this respect both Kuhn and Fleck are less radical than Berger and Luckmann (link), who make a case for an extreme version of conceptual relativism across cultures in The Social Construction of Reality: A Treatise in the Sociology of Knowledge.

(Polish researcher Paweł Jarnicki has written extensively on Fleck and on the relationship between Fleck's ideas and those of Kuhn. His article "On the shoulders of Ludwik Fleck? On the bilingual philosophical legacy of Ludwik Fleck and its Polish, German and English translations" provides a fascinating philological study of the difficulties of translation raised by Fleck's multilingual writings (link).)

(Here is a discussion of "conceptual frameworks" that is relevant to this discussion of incommensurability of scientific concepts and statements (link).)

Social embeddedness of scientific and intellectual work

How do complex, socially embodied processes of cultural and scientific creation work? (I'm thinking of artistic traditions, scientific research communities, literary criticism schools, high-end culinary experts, and mental health professionals, for example.) This is a complex question, by design. It is a question about how a field of "cumulative" symbolic production moves forward and develops; so it is related to intellectual history, art history, and the philosophy of science. But it is also a question about the social embeddedness of creative work -- the idea that the practitioners of literary theory, political science, high-energy physics, biology, or international relations theory proceed within material and social conditions, institutions, and incentives and constraints that train, guide, and valorize practitioners.

One of the important developments in the philosophy of science since 1970 was the development of large concepts designed to capture the social and institutional context of science, and to discover how the details of these social arrangements influence the content and value of the resulting scientific research. Thomas Kuhn's framing of the history of science around paradigms, normal science, and anomaly was one of the early contributions to this perspective, as was Imre Lakatos's focus on research programmes. There has emerged a strong interest in studying the sociological context of scientific and cultural work, and the institutions that facilitate and regulate publication and validation in various fields. These contextual arrangements define the systems of valuation that distinguish "good" products from "bad" products (good pieces of scientific discovery, good works of literary criticism). And they determine the prestige and career prospects of the researchers.

The "historical turn" in the study of science resulted in two large and independent innovations in how to think about "science in context". The first is the recognition that scientific work (or cultural work) takes place within specific social and material conditions, and it is important to study those environments. The second is that research communities develop forms of "social cognition" that are specialized to their community, and that strongly influence the ways that they conceive of the world and design their research efforts. Both aspects are important insights, but they derive from separate insights into scientific work. I will address the social cognition feature in a later post.

The "new sociology of knowledge" (link) represents a fresh start on the "social embeddedness" orientation towards culture and knowledge, building on interdisciplinary fields like Science and Technology Studies (STS) and Sociology of Scientific Knowledge (SSK) (link). Charles Camic, Neil Gross, and Michele Lamont offer examples of some very interesting recent work in this field in Social Knowledge in the Making. Here is one of the core observations that the editors draw from the research contributions to the volume:

One of these themes is that social knowledge practices are multiplex, composed of many different aspects, elements, and features, which may or may not work in concert. Surveying the broad terrain mapped across the different chapters, we see, for example, the transitory practices of a short-lived research consortium as well as knowledge practices that endure for generations across many disciplines and institutions... (kl 338)

At site after site, heterogeneous social knowledge practices occur in tandem, layered upon one another, looping around and through each another, interweaving and branching, sometimes pulling in the same directions, sometimes in contrary directions. (kl 353)

The social-embeddedness approach to thinking about science and culture is intended to situate a cultural or scientific activity within a set of social/intellectual relationships, with the background hypothesis that the activity develops as a result of the cognitive, symbolic, and material relationships that exist among its practitioners. These may include graduate curricula, laboratory procedures, journal publication policies, funding agencies, and the other social, political, and intellectual/institutional resources that exist within that community of practitioners.

Detailed studies in the sociology of science shed light on how this conception of scientific research and valuation takes place. Norwood Hanson's Patterns of Discovery (1958) was one of the earliest careful studies of a physics laboratory that demonstrated the impossibility of maintaining a rigid separation between observation and theory -- a key tenet of logical positivism. As such, Hanson's work represented one of the earliest contributions to post-positivist philosophy of science. Since then a large field of study has emerged that focuses on the details of research communities and laboratories. Paul Rabinow's Making PCR is a fascinating account of a biotech laboratory in which he documents the extensive interdependency that exists among research scientists, laboratory technicians, managers, research assistants, and others. Bruno Latour and Steve Woolgar's Laboratory Life provides an ethnographic study of a biological research lab.

Pierre Bourdieu's concept of a "field" of cultural and intellectual activity (link) in The Field of Cultural Production falls in the broad category of the social-embeddedness approach to cultural and intellectual activities described here. The heart of Bourdieu's concept of "field" is "relationality" -- the idea that the participants in cultural production and their products are situated and constituted in terms of a number of processes and social realities. Cultural products and producers are located within "a space of positions and position-takings" (30) that constitute a set of objective relations.

The space of literary or artistic position-takings, i.e. the structured set of the manifestations of the social agents involved in' the field -- literary or artistic works, of course, but also political acts or pronouncements, manifestos or polemics, etc. -- is inseparable from the space of literary or artistic positions defined by possession of a determinate quantity of specific capital (recognition) and, at the same time, by occupation of a determinate position in the structure of the distribution of this specific capital. The literary or artistic field is a field of forces, but it is also a field of struggles tending to transform or conserve this field of forces. (30)

This text give us a better idea of what a "field" encompasses for Bourdieu. It is a connected network of social activity in which there are "creators" who are intent on creating a certain kind of cultural product. The product is defined, in part, by the expectations and values of the audience -- not simply the creator. The audience is multiple, from specialist connoisseurs to the mass public. And the product is supported and filtered by a range of overlapping social institutions -- galleries, academies, journals, reviews, newspapers, universities, patrons, sources of funding, and the market for works of "culture."

The social embeddedness of intellectual and scientific research is important and worth careful study. We learn a great deal about the course of development of fields such as "high-energy physics in the United States", "neo-liberal economic development theory", or "post-modern literary studies" by discovering the ways in which researchers in these fields are trained (graduate programs), how they are funded, how their results are evaluated for publication, how the national laboratories work, what the peer networks are, how the researchers are awarded the signs of success within the discipline, and so on. We can perhaps trace the spread of new ideas over a period of time -- for example, computable general equilibrium models in development economics -- based on an understanding of the institutional settings of the relevant discipline. And this "embeddedness" feature is quite general across fields of intellectual, cultural, and scientific work.

An important question arises within this framework: why should we expect these kinds of sociological institutions to lead to "better science", more insightful literary criticism, or better ethnography? We can certainly point to what Lakatos referred to as "degenerating research programmes", and the case of Soviet biology under the iron hand of Trofim Lysenko provides a clear example of "bad science resulting from a disciplined research community". Examples like these confirm that a "disciplinary matrix" is no guarantee of scientific progress or eventual discovery of the truth about a domain.

This is a question that philosophers of science have confronted, and there are substantive efforts to provide answers to the question, revolving around the fact that the empirical world provides its own feedback to bad science (through observation, experiment, and independent critical thinking). There is also a "bootstrapping" mechanism at work in the peer-review process for evaluating scientific work for publication, though it is also clear that a peer-review process may also have perverse results. Dogma is a risk within a scientific research community no less than in a culinary community (never, never, never use dried basil for pesto!). This is the point of the critique involved in the Perestroika debate in political science (link), where the critics maintain that orthodox journal editors and power holders show a dogmatic adherence to rational-choice theory over other possible approaches, and there is an equally deep divide within sociology over the validity of non-quantitative methods for sociological research (link). The fissure in literary studies between post-modern criticism and what Satya Mohanty calls "realist literary theory" represents a disciplinary divide in the humanities. All of that accepted -- it is seems clear that scientific understanding of the world proceeds best when scientists criticize each others' research on the basis of evidence and theoretical coherence. Fallible, yes; but a better bet than any other approach humanity has considered. We might go further and postulate that some institutional arrangements work better than others for promoting the truth-enhancing goals of science -- for example, institutions that encourage independent thinking across ranks within the discipline.

The open texture of the social world

What is involved in arriving at scientific knowledge about the social world? The position I have consistently taken emphasizes contingency and heterogeneity of the social: the social world is a mixture of diverse processes and structures; it is constituted by socially constituted and socially situated actors, leading to ineliminable features of contingency and heterogeneity; and there are no unified "grand theories" that permit us to capture "the way the social world works". Social phenomena are multi-threaded, multi-causal, and multi-semiotic. So the most we can hope for in the social sciences is to identify some of the threads of change and stability, some of the distinct causes at work, and some of the systems of meaning through which actors frame the world in which they live and act.

So the social sciences can only consist of a large number of separate and largely independent lines of investigation into different strands of social life. And these diverse lines of investigation also correspond to a plurality of methodologies for research. These limited forms of knowledge are enormously valuable, both intellectually and practically -- even though they do not add up to a unified and comprehensive representation of the social world as a whole. Social knowledge is inherently incomplete and incompletable. Weber points to this idea in his essay, "'Objectivity' in Social Science and Social Policy" in The Methodology of The Social Sciences (link):

There is no absolutely "objective" scientific analysis of culture -- or put perhaps more narrowly but certainly not essentially differently for our purposes -- of "social phenomena" independent of special and "one-sided" viewpoints according to which -- expressly or tacitly, consciously or unconsciously -- they are selected, analyzed and organized for expository purposes. (72)

I do not construe this passage as an early version of "post-modernist relativism", but rather Weber's recognition of the inherently open texture of social phenomena. There is no limit to the empirical, theoretical, causal, cultural, and historical research questions that can be formulated with regard to almost any ensemble of social phenomena over time.

Consider a particular sociological topic: the nature and dynamics of the 20th-century urban place -- the city. Acquaintance with a range of cities allows us to note that there are aspects of similarity and difference across "cities". This suggests a range of kinds of investigation of urban life. We can study the particulars of specific cities (Mumbai, Bonn, Mexico City, Chicago) through careful case studies. Second, it is promising to engage in comparative studies of aspects of a range of cities that seem to work out differently. How do the public transit systems of Mexico City, Mumbai, and Chicago compare to each other? How does corruption affect the municipal governments of several cities differently? And finally, it is intriguing to consider whether there are some processes and mechanisms that are recur across cities in the modern world, leading to limited but genuine generalizations that can be discovered through quantitative comparisons. Epidemiological findings about the transmission of infectious diseases might be one such area where generalizations across many or all cities can be discovered.

But consider the enormous range of questions that can be asked about cities:

• Why is Chicago located where it is?
• Why are cities located where they are?
• What are the patterns of residence in cities, and what factors explain these patterns?
• How are features of health status distributed across place and population in cities?
• What kinds of transportation exist in the urban environment, and why?
• How are the necessities of life -- food, water, clothing, ... -- provided in adequate quantities to the population of a city?
• How do people in the city make their livings?
• How are urban services provided, funded, and managed?
• How is the urban population governed?
• How is civil peace maintained in the urban population?
• Why did Detroit, Newark, and Cleveland experience uprisings/race riots in 1967 and 1968?
• What meanings are associated with the design and architecture of a given city by its residents?
• What kinds and frequencies of crimes occur in the city?
• What factors enhance or inhibit crime in cities?
• ...

It is evident that this list can be extended indefinitely. There are always new and interesting questions that can be posed and investigated about an individual city or a group of cities. And any one of these questions can be the basis of an entire research program in the social and human sciences, involving theory, observation, archival research, discovery of institutional arrangements, cultural interpretation, historical research, and so on, for a densely developed set of research ideas and initiatives. So, QED: there can never be a "finished and comprehensive sociology of the city".

This discussion supports the conclusion that the open-endedness of the social world is quite different from the natural world. Once scientific attention turned to the question of the behavior and properties of gases, there were a number of different avenues that could be pursued; but ultimately, we can understand the behavior of gases in terms of a few simple laws and mechanisms: molecules, elastic collisions, intermolecular forces, kinetic energy, entropy, laws of thermodynamics, and perhaps a bit of the mathematics of complex systems to explain local patterns of turbulence. But there is no hidden mystery in the behavior of a gas. The behavior of a population in a city over the stretch of a century is entirely different from this simple story about gases. The mechanisms, meanings, and dynamics of a social population can be investigated along countless different dimensions, and there are no fixed and final "laws of social interaction" that ultimately allow the explanation of the social ensemble -- the city. And this open texture of sociological investigation of the city seems to be true for virtually every aspect of social life.

(Here are some additional posts on cities illustrating the range of social-science studies of urban life that is possible; link, link, link, link, link.)

Ludwik Fleck and "thought styles" in science

Let's think about the intellectual influences that have shaped philosophers of science over the past one hundred years or so: Vienna Circle empiricism, logical positivism, the deductive-nomological method, the Kuhn-Lakatos revolution, incorporation of the sociology of science into philosophy of science, a surge of interest in scientific realism, and an increasing focus on specific areas of science as objects of philosophy of science investigations. And along these waypoints it would be fairly easy to place a few road signs indicating the major philosophers associated with each phase in the story -- Ayer, Carnap, Reichenbach, Hempel, Nagel, Hanson, Hesse, Kuhn, Lakatos, Putnam, Boyd, Quine, Sellars, Bhaskar, Sober, Rosenberg, Hausman, Epstein ...

So we might get the idea that we've got a pretty good idea of the "space" in which philosophy of science questions should be posed, along with a sense of the direction of change and progress that has occurred in the field since 1930. The philosophy of science is a "tradition" within philosophy, and we who practice in the field have a sense of understanding its geography.

But now I suggest that readers examine Wojciech Sady's excellent article on Ludwik Fleck in the Stanford Encyclopedia of Philosophy (link). Fleck (1896-1961) was a Polish-Jewish scientist and medical researcher who wrote extensively in the 1930s about "social cognition" and what we would now call the sociology of science. His biography is fascinating and harrowing; he and his family survived life in Lvov under the Soviet Union (1939-1941) after the simultaneous invasion of Poland by Germany and the USSR; occupation, pogroms, and capture by the Germans in Lvov; resettlement in the Lvov ghetto; transport to Auschwitz and later Buchenwald; and survival throughout, largely because of his scientific expertise on typhus vaccination. Fleck survived to serve as a senior academic scientist in Lublin. In 1957 Fleck and his wife emigrated to Israel, where their son had settled.

Fleck is not entirely unknown to philosophers today, but it's a close call. A search for articles on Fleck in a research university search engine produces about 2,500 academic articles; by comparison, the same search results in 183,000 articles on Thomas Kuhn. And I suspect that virtually no philosopher with a PhD from a US department of philosophy since 1970 and with a concentration in the philosophy of science has ever heard of Fleck. 100% of those philosophers, of course, will have a pretty good idea of Kuhn's central ideas. And yet Fleck has a great deal in common with Kuhn -- some three decades earlier. More importantly, many of Fleck's lines of thought about the history of concepts of disease in medicine are still enormously stimulating, and they represent potential sources of innovation in the field today. Fleck asked very original and challenging questions about the nature of scientific concepts and knowledge. Thomas Kuhn was one of the few historians of science who were aware of Fleck's work, and he wrote a very generous introduction to the English translation of Fleck's major book in the sociology and history of science, Genesis and Development of a Scientific Fact (1979/1935).

Here are Fleck's central ideas, as summarized by Sady. Understanding the world around us (cognition) is a collective project. Individuals interacting with each other about some aspect of the world constitute a "thought collective" -- "a community of persons mutually exchanging ideas or maintaining intellectual interaction" (Sady, sect. 3). A thought collective forms a vocabulary and crafts a set of concepts that are mutually understood within the group, but misunderstood by persons outside the group. A "thought collective" forms a "collective bond" -- a set of emotions of loyalty and solidarity which Fleck describes as a "collective mood". There are no "objective facts"; rather, facts are defined by the terms and constructs of the "thought collective". And the perceptions, beliefs, and representations of different "thought collectives" concerned with ostensibly the same subject matter are incommensurable.

So it is not possible to compare a theory with “reality in itself”. It is true that those who use a thought style give arguments for their views, but those arguments are of restricted value. Any attempt to legitimize a particular view is inextricably bound to standards developed within a given style, and those who accept those standards accept also the style. (Sady, sect. 7)

And scientific knowledge is entirely conditional upon the background structure of the "thought collective" or conceptual framework of the research community:

As Fleck states in the last sentence of (1935b), “'To see’ means: to recreate, at a suitable moment, a picture created by the mental collective to which one belongs”. (Sady, sect. 5)

Thus, it is impossible to see something radically new “simply and immediately”: first the constrains of an old thought style must be removed and a new style must emerge, a collective's thought mood must change— and this takes time and work with others. (Sady, sect. 5)

These ideas plainly correspond closely to Imre Lakatos's idea of a research community and Thomas Kuhn's idea of a paradigm. They stand in striking contrast to the logical positivism of the Vienna Circle being developed at roughly the same time. (And yet Sady notes that Moritz Schlick offered to recommend publication of Genesis and Development of a Scientific Fact in 1934.)

Upon first exposure to Fleck's ideas from the Sady article I initially assumed that Fleck was influenced by Communist ideas about science and knowledge (as were Polish sociologists and philosophers in the 1950s). The "collective thoughts" that are central to Fleck's account of the history of science sound a lot like Engels or Lenin. And yet this turns out not to be the case. Nothing in Sady's article suggests that Fleck was influenced by Polish Communist theory in the 1920s and 1930s. Instead, his ideas about social cognition seem to develop out of a largely central European tradition of thinking about thinking. According to Sady, Fleck's own "thought collectives" (research traditions) included: (1) medical research; (2) the emerging field in Poland of history of medicine (Władysław Szumowski, Włodzimierz Sieradzki, and Witold Ziembicki); (3) the Polish "philosophical branch" of mathematical-philosophical school (minor); (4) sociology of knowledge (Levy-Bruhl, Wilhelm Jerusalem; but not Max Scheler or Karl Mannheim; also minor). Sady also emphasizes Fleck's interest in the debates that were arising in physics around the puzzles of quantum mechanics and relativity theory.

So there is a major irony here: one of Fleck's central ideas is that individual thinkers can achieve nothing by themselves as individuals. And yet Fleck's ideas as developed in his history of the medical concept of syphilis appear to be largely self-generated -- the results of his own knowledge and reflection. The advocate of the necessity of "thought collectives" was himself not deeply integrated into any coherent thought collective.

This story has an important moral. Most importantly, it confirms to me that there are always important perspectives on a given philosophical topic that have fallen outside the mainstream and may be forever forgotten. This suggests the value, for philosophers and other scholars interested in arriving at valuable insights into difficult problems, of paying attention to the paths not taken in previous generations. There is nothing in the nature of academic research that guarantees that "the best ideas of a generation will become part of the canon for the next generation"; instead, many good and original ideas have been lost to the disciplines through bad luck. This is largely true of Fleck.

But here is another, more singular fact that is of interest. How did Sady's article, and therefore Fleck himself, come to my attention? The answer is that in the past year I've been reading a lot about Polish and Jewish intellectuals from the 1930s with growing fascination because of a growing interest in the Holocaust and the Holodomor. That means a lot of searches on people like Janina Bauman, Leszek Kołakowski, and Vasily Grossman. I've searched for the histories of places like Lvov, Galicia, and Berdichev. And in the serendipity of casting a wide net, I've arrived at the happy experience of reading Sady's fascinating article, along with some of Fleck's important work.

Here is the prologue to Fleck's Genesis and Development of a Scientific Fact. It expresses very concisely Fleck's perspective on science, concepts, and facts.

What is a fact?

A fact is supposed to be distinguished from transient theories as something definite, permanent, and independent of any subjective interpretation by the scientist. It is that which the various scientific disciplines aim at. The critique of the methods used to establish it constitutes the subject matter of epistemology.

Epistemology often commits a fundamental error: almost exclusively it regards well-established facts of everyday life, or those of classical physics, as the only ones that are reliable and worthy of investigation. Valuation based upon such an investigation is inherently naive, with the result that only superficial data are obtained.

Moreover, we have even lost any critical insight we may once have had into the organic basis of perception, taking for granted the basic fact that a normal person has two eyes. We have nearly ceased to consider this as even knowledge at all and are no longer conscious of our own participation in perception. Instead, we feel a complete passivity in the face of a power that is independent of us; a power we call “existence” or “reality.” In this respect we behave like someone who daily performs ritual or habitual actions mechanically. These are no longer voluntary activities, but ones which we feel compelled to perform to the exclusion of others. A better analogy perhaps is the behavior of a person taking part in a mass movement. Consider, for instance, a casual visitor to the Stock Exchange, who feels the panic selling in a bear market as only an external force existing in reality. He is completely unaware of his own excitement in the throng and hence does not realize how much he may be contributing to the general state. Long-established facts of everyday life, then, do not lend themselves to epistemological investigation.

As for the facts of classical physics, here too we are handicapped by being accustomed to them in practice and by the facts themselves being well worn theoretically. I therefore believe that a “more recent fact,” discovered not in the remote past and not yet exhausted for epistemological purposes, will conform best to the principles of unbiased investigation. A medical fact, the importance and applicability of which cannot be denied, is particularly suitable, because it also appears to be very rewarding historically and phenomenologically. I have therefore selected one of the best established medical facts: the fact that the so-called Wassermann reaction is related to syphilis.

HOW, THEN, DID THIS EMPIRICAL FACT ORIGINATE AND IN WHAT DOES IT CONSIST?

Lvov, Poland, summer 1934

Decision-making for big physics

Big science is largely dominant in many areas of science -- for example, high-energy physics, medical research, the human genome project, and pandemic research. Other areas of science still function well in a "small science" framework -- mathematics, evolutionary biology, or social psychology, for example, with a high degree of decentralized decision-making by individual researchers, universities, and laboratories. But in areas where scientific research requires vast investments of public funds over decades, we are forced to ask a hugely important question: Can governmental agencies act rationally and intelligently in planning for investments in "big science"?

Consider the outcome we would like to see: adoption of a well-funded and well-coordinated multi-investigator, multi-institutional, multi-year research effort well designed to achieve important scientific results. This is the ideal result. What is required in order to make it a reality? Here are the key activities of information-gathering and decision-making that are needed in order to arrive at a successful national agenda for an area of big-science research.

1. selection of one or more research strategies that have the best likelihood of bringing about important scientific results
2. a budgeting process and series of decisions that make these strategies feasible
3. implementation of a multi-year plan (often over multiple research sites) implementing the chosen strategy
4. oversight and management of the scientific research sites and expenditures to ensure that the strategy is faithfully carried out by talented scientists, researchers, and directors

In A New Social Ontology of Government: Consent, Coordination, and Authority I argue that governments, agencies, and large private organizations have a great deal of difficulty in carrying out large, extended plans. There I highlight principal-agent problems, conflicting priorities across sub-groups, faulty information sharing, and loose coupling within a large organization as some of the primary sources of dysfunction within a large organization (including a national government or large governmental agency). And it is apparent that all of these sources of dysfunction are present in the process of designing, funding, and managing a national science agenda.

Consider item 1 above: selection of a research strategy for scientific research. At any given time in the development of a field of research there is a body of theory and experimental findings that constitute what is currently known; there are experts (scientists) who have considered judgments about what the most important unanswered questions are, and what technologies or experimental investments would be most productive in illuminating those questions; and there are influential figures within government and industry who have preferences and beliefs about the direction that future research ought to take. 

Suppose government has created an agency -- call it the Office of High Energy Physics -- which is charged to arrive at a plan for future directions and funding for research in the field of high energy physics. (There is in fact the Office of High Energy Physics located within the Department of Energy which has approximately this responsibility. But here I am considering a hypothetical agency.) How should the director and senior staff of OHEP proceed? 

They will recognize that they need rigorous and developed analysis from a group of senior physicists. The judgments of the best physicists in the national research and university community are surely the best (though fallible) source of guidance about the direction that future physics research should take. So OHEP constitutes a permanent committee of advisors who are tasked to assess the current state of the field and arrive at a consensus view of the most productive direction for future investments in high-energy physics research.

The Standing Scientific Committee is not a decision-making committee, however; rather, it prepares reports and advice for the senior staff and director of OHEP. And the individuals who make up the senior staff themselves have been selected for having a reasonable level of scientific expertise; further, they have their own "pet" projects and ideas about what topics are likely to be the most important. So the senior staff and the Standing Committee are in a complex relationship with each other. The Standing Scientific Committee collectively has greater intellectual authority in the scientific field; many are Nobel-quality physicists. But the senior staff have greater influence on the decisions that the Office makes about strategies and future plans. The staff are always there, whereas the Standing Committee does its work episodically. Moreover, the senior staff has an ability to influence the deliberations of the Standing Committee in a variety of ways, including setting the agenda of the Standing Committee, giving advice about the likelihood of funding of various possible strategies, and so forth. Finally, it is worth noting that a group of twenty senior physicists from a range of institutions throughout the country are likely to have interests of their own that will find their way into the deliberations, leading to disagreements about priorities. In short, the process of designing a plan for the next ten years of investments in high-energy physics research is not a purely rational and scientific exercise; it is also a process in which interests, influence, and bureaucratic manipulation play crucial roles.

Now turn to item 2 above, the budgeting issue. Decisions about funding of fundamental scientific research result from a political, legislative, and bureaucratic process. Congressional committees will be involved in the decision whether to allocate $5 billion, $10 billion, or $15 billion in high-energy physics research in the coming decade. And Congressional committees have their own sources of bias and dysfunction: legislators' political interests in their districts, relationships with powerful industries and lobbyists, and ideological beliefs that legislators bring to their work. These political and economic interests may influence the legislative funding process to favor one strategy over another -- irrespective of the scientific merits of the alternatives. (If one strategy brings more investment to the home state of a powerful Senator, this may tilt the funding decision accordingly.) Further, the system of Congressional staff work can be further analyzed in terms of the interests and priorities of the senior staffers doing the work -- leading once again to the likelihood that funding decisions will be based on considerations other than the scientific merits of various strategies for research. (Recall the debacle of Congressional influence on the Osprey VTOL aircraft development process.) 

Items 3 and 4 introduce a new set of possible dysfunctions into the process, through the likelihood of principal-agent problems across research sites. Directors of the National Laboratories (like Fermilab or Lawrence Berkeley National Laboratory, for example) have their own interests and priorities, and they have a fairly wide range of discretion in decisions about implementation of national research priorities. So securing coordination of research efforts across laboratories and research sites introduces another source of uncertainty in the implementation and execution of a national strategy for physics research. This is an instance of "loose coupling", a factor that has led organizational theorists to come to expect a fair degree of divergence across the large network of sub-organizations that make up the national research system. Thomas Hughes considers these kinds of problems in Rescuing Prometheus: Four Monumental Projects That Changed the Modern World; link. 

These observations do not imply that rational science policy is impossible; but they do underline the difficulties that arise within normal governmental and private institutions that interfere with the idealized process of selection and implementation of an optimal strategy of scientific research. The colossal failure of the Superconducting Super Collider -- a multi-billion dollar project in high-energy physics that was abandoned in 1993 after many years of development and expenditure -- illustrates the challenges that national science planning encounters (link). Arguably, one might hold that the focus at Fermilab on neutrino detection is another failure (DUNE) -- not because it was not implemented, but because it fails the test of making possible fundamental new discoveries in physics.

Several interdisciplinary fields take up questions like these, including Science and Technology Studies and Social Construction of Technology studies. Hackett, Amsterdamska, Lynch, and Wajcman's Handbook of Science and Technology Studies provides a good exposure to the field. Here is a prior post that attempts to locate big science within an STS framework. And here is a post on STS insights into science policy during the Cold War (link).

Vienna Circle in Emerson Hall

image: University of Vienna, 2016

I am enjoying reading David Edmonds' The Murder of Professor Schlick: The Rise and Fall of the Vienna Circle, which is interesting in equal measures in its treatment of the rise of fascism in Austria and Germany, the development of the Vienna Circle, and -- of course -- the murder of Schlick. Edmonds' presentation of the philosophical issues that drove the Vienna Circle is especially good. (Here is a link to an earlier discussion of Schlick's murder; link.) 

In addition to the narrative, the book contains some very interesting photographs of most of the participants in the Vienna Circle. One of those is this image, captioned "Otto Neurath chatting to Alfred Tarski". The caption does not include information about date or location.

1939

The photo immediately struck me as familiar. It seemed to be the side entrance to Emerson Hall, home of the philosophy department at Harvard. So I did some searching on the web and found that there was a meeting of the International Congress for the Unity of Science (the descendent of the Vienna Circle), which took place at Harvard September 3-9, 1939. This was the fifth and final congress. And both Neurath and Tarski were in attendance. It seems likely enough, then, that this photo is from the 1939 gathering at Harvard. Here is Gerald Holton's list of the attendees and presenters at the Congress (Science and Anti-Science):

I located a photo taken of that entrance to Emerson Hall just a few years ago:

2017

Here is a version of that image, cropped to roughly the proportions of the 1939 photo. 

2017

I'm convinced -- this certainly looks like the same location to me. Harvard has made some improvements on the entrance since 1939 -- the door is modernized, the lamps have been added, the vines have been pruned, and the handrails have been provided. The shape of the brick columns to the sides of the entrance is visible through the vines in the 1939 photo. I seem to remember luxuriant vines from the 1970s on that face of the building. And indeed, that is true. Other photos of the same entrance from 1973 show the vines are more extensive. (Also there are no handrails.)

But one challenge remains: is it possible to identify other people in the 1939 photo? Here is a possibility: I think Quine is one of the people in the photo. Here is Quine as I remember him from 1973:

But his looks changed dramatically from his 30s to his sixties and seventies. Here is Quine as photographed in the Edmonds book from the 1930s:

Finally here is Quine in a book cover photo, evidently taken in the 1940s:

This looks a lot like the man standing directly behind Tarski in the first photo (above Tarski's head). The giveaway is the pattern baldness visible in the 1939 photo and the book jacket photo. It is hard to be sure, of course, but the similarity is striking.

Are there any other familiar faces in the photo? Carnap was present at the Congress and was close to Quine, but none of the faces I see in the photo look much like Carnap. I am especially curious about the man standing behind Neurath and talking with the person I take to be Quine.

This is all very interesting to me, for a number of reasons. I was a graduate assistant to Quine in his undergraduate course on "Methods of Logic," and I took his course on Word and Object in 1973 or so. It is striking today to realize that Quine in 1973 was closer in time to the Vienna Circle in the 1930s (35-40 years) than we are today to Quine and Goodman in the 1970s in Emerson Hall (45-50 years). In a small way this illustrates a meaningful point that Marc Bloch makes about the philosophy of history: we are connected to events in the past through meaningful chains of relationships with other human beings. 

Experimental methods in sociology

An earlier post noted the increasing importance of experimentation in some areas of economics (link), and posed the question of whether there is a place for experimentation in sociology as well. Here I'd like to examine that question a bit further.

Let's begin by asking the simple question: what is an experiment? An experiment is an intervention through which a scientist seeks to identify the possible effects of a given factor or “treatment”. The effect may be thought to be deterministic (whenever X occurs, Y occurs); or it may be probabilistic (the occurrence of X influences the probability of the occurrence of Y). Plainly, the experimental evaluation of probabilistic causal hypotheses requires repeating the experiment a number of times and evaluating the results statistically; whereas a deterministic causal hypothesis can in principle be refuted by a single trial.

In "The Principles of Experimental Design and Their Application in Sociology" (link) Michelle Jackson and D.R. Cox provide a simple and logical specification of experimentation:

We deal here with investigations in which the effects of a number of alternative conditions or treatments are to be compared. Broadly, the investigation is an experiment if the investigator controls the allocation of treatments to the individuals in the study and the other main features of the work, whereas it is observational if, in particular, the allocation of treatments has already been determined by some process outside the investigator’s control and detailed knowledge. The allocation of treatments to individuals is commonly labeled manipulation in the social science context. (Jackson and Cox 2013: 28)

There are several relevant kinds of causal claims in sociology that might admit of experimental investigation, corresponding to all four causal linkages implied by the model of Coleman’s boat (Foundations of Social Theory)—micro-macro, macro-micro, micro-micro, and macro-macro (link). Sociologists generally pay close attention to the relationships that exist between structures and social actors, extending in both directions. Hypotheses about causation in the social world require testing or other forms of empirical evaluation through the collection of evidence. It is plausible to ask whether the methods associated with experimentation are available to sociology. In many instances, the answer is, yes.

There appear to be three different kinds of experiments that would possibly make sense in sociology.

1. Experiments evaluating hypotheses about features of human motivation and behavior
2. Experiments evaluating hypotheses about the effects of features of the social environment on social behavior
3. Experiments evaluating hypotheses about the effects of “interventions” on the characteristics of an organization or local institution

First, sociological theories generally make use of more or less explicit theories of agents and their behavior. These theories could be evaluated using laboratory-based design for experimental subjects in specified social arrangements, parallel to existing methods in experimental economics. For example, Durkheim, Goffman, Coleman, and Hedström all provide different accounts of the actors who constitute social phenomena. It is feasible to design experiments along the lines of experimental economics to evaluate the behavioral hypotheses advanced by various sociologists.

Second, sociology is often concerned with the effects of social relationships on social behavior—for example, friendships, authority relations, or social networks. It would appear that these effects can be probed through direct experimentation, where the researcher creates artificial social relationships and observes behavior. Matthew Salganik et al’s internet-based experiments (2006, 2009) on “culture markets” fall in this category (Hedström 2006). Hedström describes the research by Salganik, Dodds, and Watts (2006) in these terms:

Salganik et al. (2) circumvent many of these problems [of survey-based methodology] by using experimental rather than observational data. They created a Web-based world where more than 14,000 individuals listened to previously unknown songs, rated them, and freely downloaded them if they so desired. Subjects were randomly assigned to different groups. Individuals in only some groups were informed about how many times others in their group had downloaded each song. The experiment assessed whether this social influence had any effects on the songs the individuals seemed to prefer. 

As expected, the authors found that individuals’ music preferences were altered when they were exposed to information about the preferences of others. Furthermore, and more importantly, they found that the extent of social influence had important consequences for the collective outcomes that emerged. The greater the social influence, the more unequal and unpredictable the collective outcomes became. Popular songs became more popular and unpopular songs became less popular when individuals influenced one another, and it became more difficult to predict which songs were to emerge as the most popular ones the more the individuals influenced one another. (787)

Third, some sociologists are especially interested in the effects of micro-context on individual actors and their behavior. Erving Goffman and Harold Garfinkel offer detailed interpretations of the causal dynamics of social interactions at the micro level, and their work appears to be amenable to experimental treatment. Garfinkel (Studies in Ethnomethodology), in particular, made use of research methods that are especially suggestive of controlled experimental designs.

Fourth, sociologists are interested in macro-causes of individual social action. For example, sociologists would like to understand the effects of ideologies and normative systems on individual actors, and others would like to understand the effects of differences in large social structures on individual social actors. Weber hypothesized that the Protestant ethic caused a certain kind of behavior. Theoretically it should be possible to establish hypotheses about the kind of influence a broad cultural factor is thought to exercise over individual actors, and then design experiments to evaluate those hypotheses. Given the scope and pervasiveness of these kinds of macro-social factors, it is difficult to see how their effects could be assessed within a laboratory context. However, there are a range of other experimental designs that could be used, including quasi-experiments (link) and field experiments and natural experiments (link),  in which the investigator designs appropriate comparative groups of individuals in observably different ideological, normative, or social-structural arrangements and observes the differences that can be discerned at the level of social behavior. Does one set of normative arrangements result in greater altruism? Does a culture of nationalism promote citizens’ propensity for aggression against outsiders? Does greater ethnic homogeneity result in higher willingness to comply with taxation, conscription, and other collective duties?

Finally, sociologists are often interested in macro- to macro-causation. For example, consider the claims that “defeat in war leads to weak state capacity in the subsequent peace” or “economic depression leads to xenophobia”. Of course it is not possible to design an experiment in which “defeat in war” is a treatment; but it is possible to develop quasi-experiments or natural experiments that are designed to evaluate this hypothesis. (This is essentially the logic of Theda Skocpol’s (1979) analysis of the causes of social revolution in States and Social Revolutions: A Comparative Analysis of France, Russia, and China.) Or consider a research question in contentious politics, does widespread crop failure give rise to rebellions? Here again, the direct logic of experimentation is generally not available; but the methods articulated in the fields of quasi-experimentation, natural experiments, and field experiments offer an avenue for research designs that have a great deal in common with experimentation. A researcher could compile a dataset for historical China that records weather, crop failure, crop prices, and incidents of rebellion and protest. This dataset could support a “natural experiment” in which each year is assigned to either “control group” or “intervention group”; the control group consists of years in which crop harvests were normal, while the intervention group would consist of years in which crop harvests are below normal (or below subsistence). The experiment is then a simple one: what is the average incidence of rebellious incident in control years and intervention years?

So it is clear that causal reasoning that is very similar to the logic of experimentation is common throughout many areas of sociology. That said, the zone of sociological theorizing that is amenable to laboratory experimentation under random selection and a controlled environment is largely in the area of theories of social action and behavior: the reasons actor behave as they do, hypotheses about how their choices would differ under varying circumstances, and (with some ingenuity) how changing background social conditions might alter the behavior of actors. Here there are very direct parallels between sociological investigation and the research done by experimental and behavioral economists like Richard Thaler (Misbehaving: The Making of Behavioral Economics). And in this way, sociological experiments have much in common with experimental research in social psychology and other areas of the behavioral sciences.

STS and big science

A previous post noted the rapid transition in the twentieth century from small physics (Niels Bohr) to large physics (Ernest Lawrence). How should we understand the development of scientific knowledge in physics during this period of rapid growth and discovery?

One approach is through the familiar methods and narratives of the history of science -- what might be called "internal history of science". Researchers in the history of science generally approach the discipline from the point of view of discovery, intellectual debate, and the progress of scientific knowledge. David Cassidy's book  Beyond Uncertainty: Heisenberg, Quantum Physics, and The Bomb is sharply focused on the scientific and intellectual debates in which Heisenberg was immersed during the development of quantum theory. His book is fundamentally a narrative of intellectual discovery. Cassidy also takes on the moral-political issue of serving a genocidal state as a scientist; but this discussion has little to do with the history of science that he offers. Peter Galison is a talented and imaginative historian of science, and he asks penetrating questions about how to explain the advent of important new scientific ideas. His treatment of Einstein's theory of relativity in Einstein's Clocks and Poincare's Maps: Empires of Time, for example, draws out the importance of the material technology of clocks and the intellectual influences that flowed through the social networks in which Einstein was engaged for Einstein's basic intuitions about space and time. But Galison too is primarily interested in telling a story about the origins of intellectual innovation.

It is of course valuable to have careful research studies of the development of science from the point of view of the intellectual context and concepts that influenced discovery. But fundamentally this approach leaves largely unexamined the difficult challenge: how do social, economic, and political institutions shape the direction of science?

The interdisciplinary field of science, technology, and society studies (STS) emerged in the 1970s as a sociological discipline that looked at laboratories, journals, and universities as social institutions, with their own interests, conflicts, and priorities. Hackett, Amsterdamska, Lynch, and Wajcman's Handbook of Science and Technology Studies provides a good exposure to the field. The editors explain that they consulted widely across researchers in the field, and instead of a unified and orderly "discipline" they found many cross-cutting connections and concerns.

What emerged instead is a multifaceted interest in the changing practices of knowledge production, concern with connections among science, technology, and various social institutions (the state, medicine, law, industry, and economics more generally), and urgent attention to issues of public participation, power, democracy, governance, and the evaluation of scientific knowledge, technology, and expertise. (kl 98)

The guiding idea of STS is that science is a socially situated human activity, embedded within sets of social and political relations and driven by a variety of actors with diverse interests and purposes. Rather than imagining that scientific knowledge is the pristine product of an impersonal and objective "scientific method" pursued by selfless individuals motivated solely by the search for truth, the STS field works on the premise that the institutions and actors within the modern scientific and technological system are unavoidably influenced by non-scientific interests. These include commercial interests (corporate-funded research in the pharmaceutical industry), political interests (funding agencies that embody the political agendas of the governing party), military interests (research on fields of knowledge and technological development that may have military applications), and even ideological interests (Lysenko's genetics and Soviet ideology). All of these different kinds of influence are evident in Hiltzik's account in Big Science: Ernest Lawrence and the Invention that Launched the Military-Industrial Complex of the evolution of the Berkeley Rad Lab, described in the earlier post.

In particular, individual scientists must find ways of fitting their talents, imagination, and insight into the institutions through which scientific research proceeds: universities, research laboratories, publication outlets, and sources of funding. And Hiltzik's book makes it very clear that a laboratory like the Radiation Lab that Lawrence created at the University of California-Berkeley must be crafted and designed in a way that allows it to secure the funds, equipment, and staff that it needs to carry forward the process of fundamental research, discovery, and experimentation that the researchers and the field of high-energy physics wished to conduct.

STS scholars sometimes sum up these complex social processes of institutions, organizations, interests, and powers leading to scientific and technological discovery as the "social construction of technology" (SCOT). And, indeed, both the course of physics and the development of the technologies associated with advanced physics research were socially constructed -- or guided, or influenced -- throughout this extended period of rapid advancement of knowledge. The investments that went into the Rad Lab did not go into other areas of potential research in physics or chemistry or biology; and of course this means that there were discoveries and advances that were delayed or denied as a result. (Here is a recent post on the topic of social influences on the development of technology; link.)

The question of how decisions are made about major investments in scientific research programs (including laboratories, training, and cultivation of new generations of science) is a critically important one. In an idealized way one would hope for a process in which major multi-billion dollar and multi-decade investments in specific research programs would be made in a rational way, incorporating the best judgments and advice of experts in the relevant fields of science. One of the institutional mechanisms through which national science policy is evaluated and set is the activity of the National Academy of Science, Engineering, and Medicine (NASEM) and similar expert bodies (link). In physics the committees of the American Physical Society are actively engaged in assessing the present and future needs of the fundamental science of the discipline (link). And the National Science Foundation and National Institutes of Health have well-defined protocols for peer assessment of research proposals. So we might say that science investment and policy in the US have a reasonable level of expert governance. (Here is an interesting status report on declining support for young scientists in the life sciences in the 1990s from an expert committee commissioned by NASEM (link). This study illustrates the efforts made by learned societies to assess the progress of research and to recommend policies that will be needed for future scientific progress.)

But what if the institutions through which these decisions are made are decidedly non-expert and bureaucratized -- Congress or the Department of Energy, for example, in the case of high-energy physics? What if the considerations that influence decisions about future investments are importantly directed by political or economic interests (say, the economic impact of future expansion of the Fermilab on the Chicago region)? What if companies that provide the technologies underlying super-conductor electromagnets needed for one strategy but not another are able to influence the decision in their favor? What are the implications for the future development of physics and other areas of science of these forms of non-scientific influence? (The decades-long case of the development of the V-22 Osprey aircraft is a case in point, where pressures on members of Congress from corporations in their districts led to the continuation of the costly project long after the service branches concluded it no longer served the needs of the services; link.)

Research within the STS field often addresses these kinds of issues. But so do researchers in organizational studies who would perhaps not identify themselves as part of the STS field. There is a robust tradition within sociology itself on the sociology of science. Robert Merton was a primary contributor with his book The Sociology of Science: Theoretical and Empirical Investigations (link). In organizational sociology Jason Owen-Smith's recent book Research Universities and the Public Good: Discovery for an Uncertain Future provides an insightful analysis of how research universities function as environments for scientific and technological research (link). And many other areas of research within contemporary organizational studies are relevant as well to the study of science as a socially constituted process. A good example of recent approaches in this field is Richard Scott and Gerald Davis, Organizations and Organizing: Rational, Natural and Open Systems Perspectives.

The big news for big science this week is the decision by CERN's governing body to take the first steps towards establishment of the successor to the Large Hadron Collider, at an anticipated cost of 21 billion euros (link). The new device would be an electron-positron collider, with a plan to replace it later in the century with a proton-proton collider. Perhaps naively, I am predisposed to think that CERN's decision-making and priority-setting processes are more fully guided by scientific consensus than is the Department of Energy's decision-making process. However, it would be very helpful to have in-depth analysis of the workings of CERN, given the key role that it plays in the development of high-energy physics today. Here is an article in Nature reporting efforts by social-science observers like Arpita Roy, Knorr Cetina, and John Krige to arrive at a more nuanced understanding of the decision-making processes at work within CERN (link).

Big physics and small physics

When Niels Bohr traveled to Britain in 1911 to study at the Cavendish Laboratory at Cambridge, the director was J.J. Thompson and the annual budget was minimal. In 1892 the entire budget for supplies, equipment, and laboratory assistants was a little over about £1400 (Dong-Won Kim, Leadership and Creativity: A History of the Cavendish Laboratory, 1871-1919 (Archimedes), p. 81). Funding derived almost entirely from a small allocation from the University (about £250) and student fees deriving from lectures and laboratory use at the Cavendish (about £1179). Kim describes the finances of the laboratory in these terms:

Lack of funds had been a chronic problem of the Cavendish Laboratory ever since its foundation. Although Rayleigh had established a fund for the purchase of necessary apparatus, the Cavendish desperately lacked resources. In the first years of J.J.’s directorship, the University’s annual grant to the laboratory of about £250 did not increase, and it was used mainly to pay the wages of the Laboratory assistants (£214 of this amount, for example, went to salaries in 1892). To pay for the apparatus needed for demonstration classes and research, J.J. relied on student fees. 

Students ordinarily paid a fee of £1.1 to attend a lecture course and a fee of £3.3 to attend a demonstration course or to use space in the Laboratory. As the number of students taking Cavendish courses increased, so did the collected fees. In 1892, these fees totaled £1179; in 1893 the total rose a bit to £1240; and in 1894 rose again to £1409. Table 3.5 indicates that the Cavendish’s expenditures for “Apparatus, Stores, Printing, &c.” (£230 3s 6d in 1892) nearly equaled the University’s entire grant to the Cavendish (£254 7s 6d in 1892). (80)

The Cavendish Laboratory exerted great influence on the progress of physics in the early twentieth century; but it was distinctly organized around a "small science" model of research. (Here is an internal history of the Cavendish Lab; link.) The primary funding for research at the Cavendish came from the university itself, student fees, and occasional private gifts to support expansion of laboratory space, and these funds were very limited. And yet during those decades, there were plenty of brilliant physicists at work at the Cavendish Lab. Much of the future of twentieth century physics was still to be written, and Bohr and many other young physicists who made the same journey completely transformed the face of physics. And they did so in the context of "small science".

Abraham Pais's intellectual and scientific biography of Bohr, Niels Bohr's Times: In Physics, Philosophy, and Polity, provides a detailed account of Bohr's intellectual and personal development. Here is Pais's description of Bohr's arrival at the Cavendish Lab:

At the time of Bohr's arrival at the Cavendish, it was, along with the Physico-Technical Institute in Berlin, one of the world's two leading centers in experimental physics research. Thomson, its third illustrious director, successor to Maxwell and Rayleigh, had added to its distinction by his discovery of the electron, work for which he had received the Nobel Prize in 1906. (To date the Cavendish has produced 22 Nobel laureates.) In those days, 'students from all over the world looked to work with him... Though the master's suggestions were, of course, most anxiously sought and respected, it is no exaggeration to add that we were all rather afraid he might touch some of our apparatus.' Thomson himself was well aware that his interaction with experimental equipment was not always felicitous: 'I believe all the glass in the place is bewitched.' ... Bohr knew of Thomson's ideas on atomic structure, since these are mentioned in one of the latter's books which Bohr had quoted several times in his thesis. This problem was not yet uppermost in his mind, however, when he arrived in Cambridge. When asked later why he had gone there for postdoctoral research he replied: 'First of all I had made this great study of the electron theory. I considered... Cambridge as the center of physics and Thomson as a most wonderful man.' (117, 119)

On the origins of his theory of the atom:

Bohr's 1913 paper on α-particles, which he had begun in Manchester, and which had led him to the question of atomic structure, marks the transition to his great work, also of 1913, on that same problem. While still in Manchester, he had already begun an early sketch of these entirely new ideas. The first intimation of this comes from a letter, from Manchester, to Harald: 'Perhaps I have found out a little about the structure of atoms. Don't talk about it to anybody... It has grown out of a little information I got from the absorption of α-rays.' (128)

And his key theoretical innovation:

Bohr knew very well that his two quoted examples had called for the introduction of a new and as yet mysterious kind of physics, quantum physics. (It would become clear later that some oddities found in magnetic phenomena are also due to quantum effects.) Not for nothing had he written in the Rutherford memorandum that his new hypothesis 'is chosen as the only one which seems to offer a possibility of an explanation of the whole group of experimental results, which gather about and seems to confirm conceptions of the mechanismus [sic] of the radiation as the ones proposed by Planck and Einstein'. His reference in his thesis to the radiation law concerns of course Planck's law (5d). I have not yet mentioned the 'calculations of heat capacity' made by Einstein in 1906, the first occasion on which the quantum was brought to bear on matter rather than radiation. (138)

But here is the critical point: Bohr's pivotal contributions to physics derived from exposure to the literature in theoretical physics at the time, his own mathematical analysis of theoretical assumptions about the constituents of matter, and exposure to laboratories whose investment involved only a few thousand pounds.

Now move forward a few decades to 1929 when Ernest Lawrence conceived of the idea of the cyclical particle accelerator, the cyclotron, and soon after founded the Radiation Lab at Berkeley. Michael Hiltzik tells this story in Big Science: Ernest Lawrence and the Invention that Launched the Military-Industrial Complex, and it is a very good case study documenting the transition from small science to big science in the United States. The story demonstrates the vertiginous rise of large equipment, large labs, large funding, and big science. And it demonstrates the deeply interwoven careers of fundamental physics and military and security priorities. Here is a short description of Ernest Lawrence:

Ernest Lawrence’s character was a perfect match for the new era he brought into being. He was a scientific impresario of a type that had seldom been seen in the staid world of academic research, a man adept at prying patronage from millionaires, philanthropic foundations, and government agencies. His amiable Midwestern personality was as much a key to his success as his scientific genius, which married an intuitive talent for engineering to an instinctive grasp of physics. He was exceptionally good-natured, rarely given to outbursts of temper and never to expressions of profanity. (“ Oh, sugar!” was his harshest expletive.) Raising large sums of money often depended on positive publicity, which journalists were always happy to deliver, provided that their stories could feature fascinating personalities and intriguing scientific quests. Ernest fulfilled both requirements. By his mid-thirties, he reigned as America’s most famous native-born scientist, his celebrity validated in November 1937 by his appearance on the cover of Time over the cover line, “He creates and destroys.” Not long after that, in 1939, would come the supreme encomium for a living scientist: the Nobel Prize. (kl 118)

And here is Hiltzik's summary of the essential role that money played in the evolution of physics research in this period:

Money was abundant, but it came with strings. As the size of the grants grew, the strings tautened. During the war, the patronage of the US government naturally had been aimed toward military research and development. But even after the surrenders of Germany and Japan in 1945, the government maintained its rank as the largest single donor to American scientific institutions, and its military goals continued to dictate the efforts of academic scientists, especially in physics. World War II was followed by the Korean War, and then by the endless period of existential tension known as the Cold War. The armed services, moreover, had now become yoked to a powerful partner: industry. In the postwar period, Big Science and the “military-industrial complex” that would so unnerve President Dwight Eisenhower grew up together. The deepening incursion of industry into the academic laboratory brought pressure on scientists to be mindful of the commercial possibilities of their work. Instead of performing basic research, physicists began “spending their time searching for ways to pursue patentable ideas for economic rather than scientific reasons,” observed the historian of science Peter Galison. As a pioneer of Big Science, Ernest Lawrence would confront these pressures sooner than most of his peers, but battles over patents—not merely what was patentable but who on a Big Science team should share in the spoils—would soon become common in academia. So too would those passions that government and industry shared: for secrecy, for regimentation, for big investments to yield even bigger returnsParticle accelerators became the critical tool in experimental physics. A succession of ever-more-powerful accelerators became the laboratory apparatus through which questions and theories being developed in theoretical physics could be pursued by bombarding targets with ever-higher energy particles (protons, electrons, neutrons). Instead of looking for chance encounters with high-energy cosmic rays, it was possible to use controlled processes within particle accelerators to send ever-higher energy particles into collisions with a variety of elements. (kl 185)

What is intriguing about Hiltzik's story is the fascinating interplay of separate factors the narrative invokes: major developments in theoretical physics (primarily in Europe), Lawrence's accidental exposure to a relevant research article, the personal qualities and ambition of Lawrence himself, the imperatives and opportunities for big physics created by atomic bomb research in the 1940s, and the institutional constraints and interests of the University of California. This is a story of the advancement of physics that illustrates a huge amount of contingency and path dependency during the 1930s through 1950s. The engineering challenges of building and maintaining a particle accelerator were substantial as well, and if those challenges could not be surmounted the instrument would be impossible. (Maintaining a vacuum in a super-large canister itself proved to be a huge technical challenge.)

Physics changed dramatically between 1905 and 1945, and the balance between theoretical physics and experimental physics was one important indicator of this change. And the requirements of experimental physics went from the lab bench to the cyclotron -- from a few hundred dollars (pounds, marks, krone, euros) of investment to hundreds of millions of dollars (and now billions) in investment. This implied, fundamentally, that scientific research evolved from an individual activity taking place in university settings to an activity involving the interests of the state, big business, and the military -- in addition to the scientific expertise and imagination of the physicists.