Scientific rationality and anomaly

Some discussion of the empirical status of social science theories and hypotheses in the past has revolved around Karl Popper's formulation of the doctrine of falsifiability. However, this criticism is almost always misplaced in the context of the social sciences. This is true for several reasons: sociologists rarely offer unified deductive theories of social phenomena; the heterogeneity of the social world implies that explanations of social outcomes almost always need to be multi-causal; and as a result of these two features, social explanations and theories can usually be supported through piecemeal empirical investigation -- not through their distant global deductive consequences (link). Sociology is not physics.

Popper's requirement is that all scientific hypotheses must in principle be falsifiable: that is, it must be possible to specify in advance a set of empirical circumstances which would demonstrate the falsity of the hypothesis. Popper writes, "A theory which is not refutable by any conceivable event is non-scientific. Irrefutability is not a virtue of a theory (as people often think) but a vice" (Conjectures and Refutations: The Growth of Scientific Knowledge, p. 36). This criterion is often used to fault social science research on the ground that social scientists are often prepared to adjust their hypotheses in such a way as to render them compatible with unexpected empirical results (anomalies).

Popper's falsifiability thesis arose in response to the ubiquitous problem of anomaly in science. Anomalies -- facts or discoveries that appear inconsistent with a given theory -- are found everywhere in the history of science, since scientific inquiry is inherently fallible. If a theory implies some sentence S and S is false, it follows that the theory must be false as well. In such a case the scientist is faced with a range of choices -- reject the theory as a whole; reject some portion of the theory in order to avoid the conclusion S; modify the theory to avoid the conclusion S; or introduce additional assumptions to show how the theory is consistent with "not S." A strict falsificationist requires that we disavow the theory, but this response is both insensitive to actual scientific practice and implausible as a principle of methodology.

When faced with anomaly, then, the scientist must choose whether to abandon the theory altogether or modify it to make it consistent with the contrary observations. If the theory has a wide range of supporting evidence, there is a strong incentive for salvaging the theory, that is, of supplementing it with some further assumption restricting the application of its laws, or modifying the laws themselves, to reconcile theory with experience. Ideally the scientist ought to proceed by attempting to locate the source of error in the original theory. Theory modification in the face of contrary evidence should result in a more realistic description of the world, either through the correction of false theoretical principles or through the description of further factors at work that were previously unrecognized.

It is possible, of course, to modify a theory in ways that do not reflect any additional insight into the real nature of the phenomena in question, but are rather merely mechanical modifications of the theory made to bring it into line with the contrary evidence. The problem of avoiding adhocness is a substantive one. Does the modification contribute to a theory that affords simple explanations of a wide range of phenomena? Does it appear to represent an increased knowledge of the real mechanisms that underlie observable phenomena? Post-positivist philosophy of science substantially extended these ideas by introducing the notion of a research program.

Post-positivist philosophy of science attempted to formulate more adequate standards for modifying theory in the light of anomaly. Important insights resulted from a shift of attention from the level of finished theories to the level of the research program, that is, from the formal laws and principles of a theory to the more encompassing set of presuppositions, methodological commitments, and research interests that guide scientists in the conduct of research and theory formation. The philosophy of science of the 1970s and 1980s offered greater focus on the "context of discovery"--the assumptions and research goals that guide scientists in their research. Philosophers of science in this tradition rejected the idea that the conduct of research is an unstructured, nonrational process, and they tried to formulate a theory of the standards that distinguish good scientific research from bad. From this starting point, the "research program" becomes the central interest. (Larry Laudan's Progress and Its Problems (1977) provided a good critical summary of the views of philosophers of science who give attention to the idea of a research program or research tradition.)

Imre Lakatos was one of the philosophers who explored the idea of a scientific research program in the 1960s and 1970s. (The Stanford Encyclopedia of Philosophy entry on Lakatos by Musgrave and Pigden is very good; link.) A research program is the framework of assumptions, experimental procedures, explanatory paradigms, and theoretical principles that guide the conduct of research. With this different starting point concerning the locus of scientific knowledge, post-positivist philosophers of science have posed a different question for themselves. Rather than the positivists' question--What is the criterion of an empirically adequate theory?--they have asked, What are the features that distinguish a rational and progressive program of research from its contrary? The problem of theory adequacy does not disappear, but it becomes a subordinate concern. This broader approach to empirical rationality lays emphasis on the degree to which the commitments of the research program successfully direct research productively and suggest empirically adequate theories--rather than on the narrower question of the criterion of empirical adequacy of theories. On this view, empirical rationality is chiefly a feature of the program of research rather than the finished theory; theories are tools for understanding empirical phenomena created by the scientist within the context of a framework of methodological and substantive assumptions. And from this research-oriented point of view, falsificationism is an unsound principle of theory choice, since it is an extreme principle that requires the rejection of any theory with false consequences.

It is also worth noting that social explanations often depend on discovery of a number of separate and independent causal mechanisms leading to a certain kind of outcome. Sociological explanations do not usually reflect unified, abstract theories that are thought to apply uniformly across a whole society. It is entirely commonplace to discover that a simple monocausal theory of a sociological pattern -- for example, patterns of high infant mortality in low income zip codes -- may begin with a causal theory that turns out to be overly simple. In the infant mortality case, it might first be hypothesized that "infant mortality is increased in a zip code with low average family income because poor families have poor nutrition". But then it turns out that there are glaring exceptions -- zip codes with low income, poor nutrition, and low infant mortality. Further research may discover that the causes of population infant mortality are more complex and numerous. The "poor-nutrition" theory is not abandoned, but is supplemented by the "low level of available and affordable pre-natal care" hypothesis, the "religious composition of the population" hypothesis, and the "environmental justice" hypothesis. These additional mechanisms do not invalidate the original simple theory (poor nutrition), but they demonstrate that a more adequate theory must refer to other mechanisms as well. (This pluralistic view of sociological theory is explored in an earlier post; link.)

These considerations show that the core values of empirical assessment, shared by all scientists, do not entail commitment to the doctrine of falsifiability. Against Popper, it is not scientifically irrational to continue to adjust and modify theoretical hypotheses so as to make sense of anomalous empirical observations. The crucial question is not falsifiability, but rather whether the research program continues to broaden its empirical scope. It is reasonable for scientists to modify their hypotheses and theories in light of anomalous findings; the crucial empirical constraint is that the modified theory ought to have additional empirical scope. The standard of strict falsifiability, then, is not a reasonable constraint on hypothesis formation in social scientific research. (Here is an earlier treatment of Popper's philosophical ideas about history and the social sciences; link.)

(The shape and function of the puffin's beak is sometimes regarded as an anomaly in Darwinian evolutionary theory, since it seems to differ from the case of the finch beak that Darwin analyzes: "beak shape is determined by food source availability in habitat". But in fact, the puffin is not an exception or anomaly to the principle of natural selection; rather, the influences on "reproductive fitness" conferred by beak shape are more complex and multiple than Darwin's analysis of the finch would indicate.)

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.

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

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. 

A big-data contribution to the history of philosophy

The history of philosophy is generally written by subject experts who explore and follow a tradition of thought about which figures and topics were "pivotal" and thereby created an ongoing research field. This is illustrated, for example, in Stephen Schwartz's A Brief History of Analytic Philosophy: From Russell to Rawls. Consider the history of Anglophone philosophy since 1880 as told by a standard narrative in the history of philosophy of this period. One important component was "logicism" -- the idea that the truths of mathematics can be derived from purely logical axioms using symbolic logic. Peano and Frege formulated questions about the foundations of arithmetic; Russell and Whitehead sought to carry out this program of "logicism"; and Gödel proved the impossibility of carrying out this program: any set of axioms rich enough to derive theorems of arithmetic is either incomplete or inconsistent. This narrative serves to connect the dots in this particular map of philosophical development. We might want to add details like the impact of logicism on Wittgenstein and the impact of Tractatus Logico-Philosophicus, but the map is developed by tracing contacts from one philosopher to another, identifying influences, and aggregating groups of topics and philosophers into "schools".

Brian Weatherson, a philosopher at the University of Michigan, has a different idea about how we might proceed in mapping the development of philosophy over the past century (link) (Brian Weatherson, A History of Philosophy Journals: Volume 1: Evidence from Topic Modeling, 1876-2013. Vol. 1. Published by author on Github, 2020; link). Professional philosophy in the past century has been primarily expressed in the pages of academic journals. So perhaps we can use a "big data" approach to the problem of discovering and tracking the emergence of topics and fields within philosophy by analyzing the frequency and timing of topics and concepts as they appear in academic philosophy journals.

Weatherson pursues this idea systematically. He has downloaded from JSTOR the full contents of twelve leading journals in anglophone philosophy for the period 1876-2013, producing a database of some 32,000 articles and lists of all words appearing in each article (as well as their frequencies). Using the big data technique called "topic modeling" he has arrived at 90 subjects (clusters of terms) that recur in these articles. Here is a quick description of topic modeling.

Topic modeling is a type of statistical modeling for discovering the abstract “topics” that occur in a collection of documents. Latent Dirichlet Allocation (LDA) is an example of topic model and is used to classify text in a document to a particular topic. It builds a topic per document model and words per topic model, modeled as Dirichlet distributions. (link)

Here is Weatherson's description of topic modeling:

An LDA model takes the distribution of words in articles and comes up with a probabilistic assignment of each paper to one of a number of topics. The number of topics has to be set manually, and after some experimentation it seemed that the best results came from dividing the articles up into 90 topics. And a lot of this book discusses the characteristics of these 90 topics. But to give you a more accessible sense of what the data looks like, I’ll start with a graph that groups those topics together into familiar contemporary philosophical subdisciplines, and displays their distributions in the 20th and 21st century journals. (Weatherson, introduction)

Now we are ready to do some history. Weatherson applies the algorithms of LDA topic modeling to this database of journal articles and examines the results. It is important to emphasize that this method is not guided by the intuitions or background knowledge of the researcher; rather, it algorithmically groups documents into clusters based on the frequencies of various words appearing in the documents. Weatherson also generates a short list of keywords for each topic: words of a reasonable frequency in which the probability of the word appearing in articles in the topic is significantly greater than the probability of it occurring in a random article. And he further groups the 90 subjects into a dozen familiar "categories" of philosophy (History of Philosophy, Idealism, Ethics, Philosophy of Science, etc.). This exercise of assigning topics to categories requires judgment and expertise on Weatherson's part; it is not algorithmic. Likewise, the assignment of names to the 90 topics requires expertise and judgment. From the point of view of the LDA model, the topics could be given entirely meaningless names: T1, T2, ..., T90.

Now every article has been assigned to a topic and a category, and every topic has a set of keywords that are algorithmically determined. Weatherson then goes back and examines the frequency of each topic and category over time, presented as graphs of the frequencies of each category in the aggregate (including all twelve journals) and singly (for each journal). The graphs look like this:

We can look at these graphs as measures of the rise and fall of prevalence of various fields of philosophy research in the Anglophone academic world over the past century. Most striking is the contrast between idealism (precipitous decline since 1925) and ethics (steady increase in frequency since about the same time), but each category shows some interesting characteristics.

Now consider the disaggregation of one topic over the twelve journals. Weatherson presents the results of this question for all ninety topics. Here is the set of graphs for the topic "Methodology of Science":

All the journals -- including Ethics and Mind -- have articles classified under the topic of "Methodology of Science". For most journals the topic declines in frequency from roughly the 1950s to 2013. Specialty journals in the philosophy of science -- BJPS and Philosophy of Science -- show a generally higher frequency of "Methodology of Science" articles, but they too reveal a decline in frequency over that period. Does this suggest that the discipline of the philosophy of science declined in the second half of the twentieth century (not the impression most philosophers would have)? Or does it rather reflect the fact that the abstract level of analysis identified by the topic of "Methodology of Science" was replaced with more specific and concrete studies of certain areas of the sciences (biology, psychology, neuroscience, social science, chemistry)?

These results permit many other kinds of questions and discoveries. For example, in chapter 7 Weatherson distills the progression of topics across decades by listing the most popular five topics in each decade:

This table too presents intriguing patterns and interesting questions for further research. For example, from the 1930s through the 1980s a topic within the general field of the philosophy of science is in the list of the top five topics: methodology of science, verification, theories and realism. These topics fall off the list in the 1990s and 2000s. What does this imply -- if anything -- about the prominence or importance of the philosophy of science within Anglophone philosophy in the last several decades? Or as another example -- idealism is the top-ranked topic from the 1890s through the 1940s, only disappearing from the list in the 1960s. This is surprising because the standard narrative would say that idealism was vanquished within philosophy in the 1930s. And another interesting example -- ordinary language. Ordinary language is a topic on the top five list for every decade, and is the most popular topic from the 1950s through the present. And yet "ordinary language philosophy" would generally be thought to have arisen in the 1940s and declined permanently in the 1960s. Finally, topics in the field of ethics are scarce in these lists; "promises and imperatives" is the only clear example from the topics listed here, and this topic appears only in the 1960s and 1970s. That seems to imply that the fields of ethics and social-political philosophy were unimportant throughout this long sweep of time -- hard to reconcile with the impetus given to substantive ethical theory and theory of justice in the 1960s and 1970s. For that matter, the original list of 90 topics identified by the topic-modeling algorithm is surprisingly sparse when it comes to topics in ethics and political philosophy: 2.16 Value, 2.25 Moral Conscience, 2.31 Social Contract Theory, 2.33 Promises and Imperatives, 2.41 War, 2.49 Virtues, 2.53 Liberal Democracy, 2.53 Duties, 2.65 Egalitarianism, 2.70 Medical Ethics and Freud, 2.83 Population Ethics, 2.90 Norms. Where is "Justice" in the corpus?

Above I described this project as a new approach to the history of philosophy (surely applicable as well to other fields such as art history, sociology, or literary criticism). But it seems clear that the modeling approach Weatherson pursues is not a replacement for other conceptions of intellectual history, but rather a highly valuable new source of data and questions that historians of philosophy will want to address. And in fact, this is how Weatherson treats the results of this work: not as replacement but rather as a supplement and a source of new puzzles for expert historians of philosophy.

(There is an interesting parallel between this use of big data and the use of Ngrams, the tool Google created to map the frequency of the occurrences of various words in books over the course of several centuries. Here are several earlier posts on the use of Ngrams: link, link. Gabriel Abend made use of this tool in his research on the history of business ethics in The Moral Background: An Inquiry into the History of Business Ethics. Here is a discussion of Abend's work; link. The topic-modeling approach is substantially more sophisticated because it does not reduce to simple word frequencies over time. As such it is a very significant and innovative contribution to the emerging field of "digital humanities" (link).)

The Malthusian problem for scientific research

It seems that there is a kind of inverse Malthusian structure to scientific research and knowledge. Topics for research and investigation multiply geometrically, while actual research and the creation of knowledge can only proceed in a selective and linear way. This is true in every field -- natural science, biology, social science, poetry. Take Darwin. He specialized in finches for a good while. But he could easily have taken up worms, beetles, or lizards, or he could have turned to conifers, oak trees, or cactuses. The evidence of speciation lies everywhere in the living world, and it is literally impossible for a generation of scientists of natural history to study them all.

Or consider a topic of current interest to me, the features that lead to dysfunctional performance in organizations large and small. Once we notice that the specific workings of an organization lead to harmful patterns that we care about a great deal, it makes sense to consider case studies of an unbounded number of organizations in every sector. How did the UAW work such that rampant corruption emerged? What features of the Chinese Communist Party led it to the profound secrecy tactics routinely practiced by its officials? What features of the Xerox Corporation made it unable to turn the mouse-based computer interface system into a commercial blockbuster? Each of these questions suggests the value of an organized case study, and surely we would learn a lot from each study. But each such study takes a person-year to complete, and a given scholar is unlikely to want to spend the rest of her career doing case studies like these. So the vast majority of such studies will never be undertaken. 

This observation has very intriguing implications for the nature of our knowledge about the world -- natural, biological, and social. It seems to imply that our knowledge of the world will always be radically incomplete, with vast volumes of research questions unaddressed and sources of empirical phenomena unexamined. We might take it as a premise that there is nothing in the world that cannot be understood if investigated scientifically; but these reflections suggest that we are still forced to conclude that there is a limitless range of phenomena that have not been investigated, and will never be.

It is possible that philosophers of physics would argue that this "incompleteness" result does not apply to the realm of physical phenomena, because physics is concerned to discover a small number of fundamental principles and laws about how the micro- and macro-worlds of physical phenomena work. The diversity of the physical world is then untroubling, because every domain of physics can be subsumed under these basic principles and theories. Theories of gravitation, subatomic particles and forces, space-time relativity, and the quantum nature of the world are obscure but general and simple, and there is at least the hope that we might arrive at a comprehensive physics with the resources needed to explain all physical phenomena, from black-hole pairs to the nature of dark matter.

Whatever the case with physics, the phenomena of the social world are plainly not regulated by a simple set of fundamental principles and laws. Rather, heterogeneity, exception, diversity, and human creativity are fundamental characteristics of the social world. And this implies the inherent incompleteness of social knowledge. Variation and heterogeneity are the rule; so novel cases are always available, and studying them always leads to new insights and knowledge. Therefore there are always domains of phenomena that have not yet been examined, understood, or explained. This conclusion is a bit like the diagonal proof of the existence of irrational numbers that drove Cantor mad: every number can be represented as an infinite decimal, and yet for every list of infinite decimals it is simple to generate another infinite decimal that is not on the list.

Further, in this respect it may seem that the biological realm resembles the social realm in these respects, so that biological science is inherently incomplete as well. Even granting that the theories of evolution and natural selection are fundamental and universal in biological systems, the principles specified in these theories guarantee diversification and variation in biological outcomes. As a result we might argue that the science of living systems too is inherently incomplete, with new areas of inquiry outstripping the ability of the scientific enterprise to investigate them. In a surprising way the uncertainties we confront in the Covid-19 crisis seem to illustrate this situation. We don't know whether this particular virus will stimulate an enduring immunity in individuals who have experienced the infection, and "first principles" in virology do not seem to afford a determinate answer to the question.

Consider these two patterns. The first is woven linen; the second is the pattern of habitat for invasive species across the United States. The weave of the linen is mechanical and regular; it covers all parts of the space with a grid of fiber. The second is the path-dependent result of invasion of habitat by multiple invasive species. Certain areas are intensively inhabited, while other areas are essentially free of invasive species. The regularity of the first image is a design feature of the process that created the fabric; the irregularity and variation of the second image is the consequence of multiple independent and somewhat stochastic yet opportunistic exploratory movements of the various species. Is scientific research more similar to the first pattern or the second?

I would suggest that scientific research more resembles the second process than the first. Researchers are guided by their scientific curiosity, the availability of research funding, and the assumptions about the importance of various topics embodied in their professions; and the result is a set of investigations and findings that are very intensive in some areas, while completely absent in other areas of the potential "knowledge space".

Is this a troubling finding? Only if one thought that the goal of science is to eventually provide an answer to every possible empirical question, and to provide a general basis for explaining everything. If, on the other hand, we believe that science is an open-ended process, and that the selection of research topics is subject to a great deal of social and personal contingency, then the incompleteness of science comes as no surprise. Science is always exploratory, and there is much to explore in human experience.

(Several earlier posts have addressed the question of defining the scope of the social sciences; link, link, link, link, link.)

Asian Conference on the Philosophy of the Social Sciences

photo: Tianjin, China

A group of philosophers of social science convened in Tianjin, China, at Nankai University in June to consider some of the ways that the social sciences can move forward in the twenty-first century. This was the Asian Conference on the Philosophy of the Social Sciences, and there were participants from Asia, Europe, Australia, and the United States. (It was timely for Nankai University to host such a meeting, since it is celebrating the centennial of its founding in 1919 this year.) The conference was highly productive for all participants, and it seems to have the potential of contributing to fruitful future thinking about philosophy and the social sciences in Chinese universities as well.

Organized by Francesco Di Iorio and the School of Philosophy at Nankai University, the meeting was a highly productive international gathering of scholars with interests in all aspects of the philosophy of the social sciences. Topics that came in for discussion included the nature of individual agency, the status of "social kinds", the ways in which organizations "think", current thinking about methodological individualism, and the status of idealizations in the social sciences, among many other topics. It was apparent that participants from many countries gained insights from their colleagues from other countries and other regions when discussing social science theory and specific social challenges.

Along with many others, I believe that the philosophy of social science has the potential for being a high-impact discipline in philosophy. The contemporary world poses complex, messy problems with huge import for the whole of the global population, and virtually all of those challenges involve difficult situations of social and behavioral interaction (link). Migration, poverty, youth disaffection, the cost of higher education, the importance of rising economic and social inequalities, the rise of extremism, and the creation of vast urban centers like Shanghai and Rio de Janeiro all involve a mix of behavior, technology, and environment that will require the very best social-science research to navigate successfully. And if anyone ever thought that the social sciences were simpler or easier than the natural sciences, the perplexities we currently face of nationalism, racism, and rising inequalities should certainly set that thought to rest for good.

Philosophy can help social scientists gain better theoretical and analytical understanding of the social world in which we live. Philosophers can do this by thinking carefully about the nature of causal relationships in the social world (link); by considering the limitations of social-science inquiry that are inherent in the nature of the social world (link); and by assessing the implications of various discoveries in the logic of collective action for social life (link).

When we undertake large technology projects we make use of the theories and methods of analysis about forces and materials that are provided by the natural sciences. This is what gives us confidence that buildings will stand up to earthquakes and bridges will be able to sustain the stresses associated with traffic and wind. We turn to policy and legislation in an effort to solve social problems. Public policy is the counterpart to technology. However, it is clear that public policy is far less amenable to precise scientific and analytical guidance. Cause and effect relationships are more difficult to discern in the social world, contingency and conjunction are vastly more important, and the ability of social-science theories to measure and predict is substantially more limited than the natural sciences. So it is all the more important to have a clear and dynamic understanding of the challenges and resources that confront social scientists as they attempt to understand social processes and behavior.

These kinds of "wicked" social problems occur in every country, but they are especially pressing in Asia at present (link, link). As citizens and academics consider their roles in the future of their countries in Japan, Thailand, China, or Russia, Serbia, or France, they will be empowered in their efforts by the best possible thinking about the scope and limits of various disciplines of the social sciences.

This kind of international meeting organized around topics in the philosophy of the social sciences has the potential of stimulating new thinking and substantial progress in our understanding of society. The fact that philosophers in China, Thailand, Finland, Japan, France, and the United States bring very different national and cultural experiences to their philosophical theories creates the possibility of synergy and the challenging of presuppositions. One such example came up in a discussion with Finnish philosopher Uskali Maki over my use of principal-agent problems as a general source of organizational dysfunction. Maki argued that this claim reflects a specific cultural context, and that this kind of dysfunction is substantially less prevalent in Finnish organizations and government agencies. (Maki also argued that my philosophy of social science over-emphasizes plasticity and change, whereas Maki holds that the fact of social order must be explained.) It was also interesting to consider with a Chinese philosopher whether there are aspects of traditional Chinese philosophy that might shed light on current social processes. Does Mencius provide a different way of thinking about the role and legitimacy of government than the social contract tradition in which European philosophers generally operate (link)?

So along with all the other participants, I would like to offer sincere appreciation to Francesco Di Iorio and his colleagues at the School of Philosophy for the superlative inspiration and coordination they provided for this international conference of philosophers.

A plan for philosophy of social science circa 1976

image: Imre Lakatos

My Ph.D. dissertation in philosophy was written between 1974 and 1977 and was accepted in 1977. The topic was Marx's theory of science as embodied in Capital, and it was one of the early attempts to join an analytical philosophical perspective with careful study of Marx's ideas. The title of the dissertation was Marx's Capital: A Study in the Philosophy of Social Science. The dissertation proposed a different way of attempting to understand Marx, and it also proposed a different approach to developing the philosophy of social science -- an approach that gives greater attention to the details and history of social-science research. This part of the introduction to the dissertation describes the view I then had of the purposes and current deficiencies of the philosophy of science.

Here is an interview published in 2008 in 5 Questions: Philosophy of the Social Sciences, edited by Diego Rios and Christoph Schmidt-Petri, that gives an indication of how this program has developed in my research and writing (link).

The image of Imre Lakatos is used above because his work from the early 1970s was part of the inspiration for the more contextualized and historical view of the philosophy of social science described in this introduction. I found Lakatos much more stimulating than Kuhn in the early 1970s.

The full introduction is posted here. The full dissertation is posted here.

The philosophy of social science

The philosophy of social science is not a particularly strong area within contemporary philosophy. To some degree it suffers from the division between continental and analytic philosophy. Analytic philosophers have stressed the positivist theory of science, and have consequently come to social sciences with some distrust, while continental philosophers have been preoccupied with the relation of social science to philosophy, rather than the more central question of the defining characteristics of social science. Neither approach has been conducive to the project of constructing a viable, systematic, and sympathetic theory of social science. More importantly, however, the philosophy of social science suffers from its proximity to the philosophy of natural science. The analytical theory of science took shape in the hands of philosophers whose primary training was in natural science, and consequently, whose chief examples were drawn from the natural sciences. Philosophers of social science have all too often shown a tendency to merely import into their field the categories and questions formulated with respect to natural science, rather than posing questions and categories more closely tailored to the real outlines of typical social sciences.{6} It may eventually turn out, of course, that all sciences have the same epistemological structure; but that issue ought not be prejudged. The philosophy of social science needs, therefore, to develop a theory of social science which is not parasitic upon theories of natural science.

Ideally, a philosophy of social science ought to contain an analytical theory of social science which directs attention at the particular trouble spots of social knowledge. It ought to include a discussion of the peculiar nature of the subject matter of social science, an account of the characteristics of social explanation, an account of the relation between empirical evidence and theory in social science, and so forth; and more generally, it ought to consist of a set of questions and categories specifically suited to the special problems confronting social explanation and social theory. Contemporary philosophy of social science fails to come forward with such a theory, in large part because it formulates its theory of science in terms of concepts suggested by the philosophy of natural science.

This diagnosis of the weakness of philosophy of social science indicates that the philosophy of natural science bears a large responsibility for that weakness; happily, however, it is now able to provide the beginnings of a method of philosophical inquiry which can begin to undo that damage. For in the past two decades the philosophy of natural science has witnessed an important transformation in its method of inquiry. It has been transformed from an attempt to provide high-level abstractions concerning the basic concepts of explanation, confirmation, empirical significance, theory choice, and the like, to an attempt to provide a more detailed theory of scientific practice through detailed studies of particular examples of scientific inquiry. Historians of science have argued that the philosophy of science will benefit from greater attention to particular scientific theories and programmes of research, and increasingly philosophers have accepted this judgment. And this shift of attention has already begun to pay off in the form of theories of science which correspond more closely to the actual nature of science, and which thereby come closer to explaining science as a form of human knowledge.

I suggest that the philosophy of social science can benefit from the application of this historical method: its theory of social science can be enriched and corrected through closer attention to actual case studies drawn from the history of social science. Such studies have the potential of suggesting new categories and new questions concerning the nature of knowledge about society and history, and they provide the means by which the analytical theory of science itself may be assessed.

We may get a better idea of the logical relations between case studies of that sort and the formulation of a more general theory of science by working out a rough taxonomy of the logical structure of the philosophy of science.{7} The philosophy of science is (at least in part) a meta-level theory of the epistemological, methodological, and structural characteristics of science. If all scientific theories share certain epistemological characteristics in common, these certainly ought to be part of that theory of science; and if there is diversity, the theory of science ought to indicate the dimensions around which such diversity occurs. The theory of science ought to answer questions like: What is scientific explanation? How are scientific theories organized? How are scientific hypotheses given empirical justification? The theory of science, in other words, attempts to codify the most general characteristics of scientific knowledge.

On this account the theory of science stands at the greatest degree of abstraction: it attempts to make assertions which are true of all or most sciences. At the opposite end of the spectrum stands the particular scientific hypothesis or system: Darwinian evolutionary theory, Newtonian mechanics, Piaget’s psychological theory, and so forth. Each such theory is an attempt to apply empirical rationality to the problem of explaining some complex domain of phenomena; and each advances a theory to the scientific community for some form of evaluation or acceptance. The crucial point to note, however, is that each such theory is an extended and complex argument, in which the principles of inference are almost always left unstated. The scientist engages in a complex form of empirical reasoning, but he does not codify that process of reasoning. For each such example of an empirical hypothesis and explanation, therefore, it is possible to attempt to unravel the implicit standards of empirical rationality, or the implicit conceptions of scientific explanation, inference, evidence, and so forth. This process is in large part the domain of the history of science; however, its results are of plain importance to the general theory of science described above. For if we suppose that any scientific theory rests upon a complex and unstated "grammar" of scientific inference and argument, we may sensibly ask whether there are any regularities among those implicit. theories of science. These particular theories of science embody the set of standards of empirical rationality which guide and regulate the particular scientist, and they constitute part of the raw material for the analytical theory of science. They are what the analytical theory of science is a theory of.

Using this basic taxonomy of the philosophy of science, it is possible to restate the innovation in the practice of the philosophy of science which was described above as having occurred of late: historically minded philosophers of science have argued that we ought to make more explicit the relationship between the two levels of theories of science, and ought to pay more attention to the concrete theories of science implicit in particular scientific systems when formulating and criticizing the analytical theory of science. We ought, that is, to formulate an analytical theory of science which is more sensitive to the particular details of the actual practice of scientific explanation and justification, rather than relying on a priori and unsystematic arguments about science in general.

Notes

1. Consider social theorists like Louis Althusser, Nicos Poulantzas, Lucio Coletti, and Maurice Godelier; empirical sociologists like Tom Bottomore, Ralph Miliband, and J. H. Westergaard; economists like Paul Sweezy, Maurice Dobb, and Ernest Mandel; and historians like E. P. Thompson, Eugene Genovese, Eric Hobsbawm, and Albert Soboul.

2. For a description of a similar project in the biological sciences, consult David Hull, Philosophy of Biological Science (Englewood Cliffs, N.J.: Prentice-Hall, 1974), pp. 5-7. Consider also Norwood Hanson, Patterns of Discovery, An Inquiry into the Conceptual Foundations of Science (Cambridge: Cambridge University Press, 1965, p. 2.

3. Louis Althusser and Etienne Balibar, Reading Capital, trans. Ben Brewster (London: New Left Books, 1970), pp. 30-1; Louis Althusser, For Marx, trans. Ben Brewster (London: New Left Books, 1969), pp. 34-5.

4. David McLellan, Karl Marx (New York: Viking Press, 1975), pp. 303-305; Albrecht Wellmer, Critical Theory of Society (New York: Herder & Herder, 1971), Chap. 2; Carl Boggs, Gramsci's Marxism (London: Pluto Press,·1976) Chap. 1.

5. Thomas Kuhn, The Structure of Scientific Revolutions, 2nd ed. ·(Chicago: University of Chicago Press, 1970); Norwood Hanson, Patterns of Discovery; Imre Lakatos, “Methodology of Scientific Research Programmes," Criticism and the Growth of Knowledge, ed. Imre Lakatos & Alan Musgrave (Cambridge: Cambridge University Press, 1970); David Hull, Philosophy of Biological Science. These works share a commitment to constructing a theory of science based on a close reading of some specific scientific theory.

6. Cf. Richard Rudner, Philosophy of Social Science (Englewood Cliffs., N.J.: Prentice-Hall, 1966). This is a good example of such studies.

7. Consider Israel Scheffler, The Anatomy of Inquiry (Indianapolis: Bobbs-Merrill, 1963), pp. 3-15, for a similar discussion and taxonomy of the philosophy of science.