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date: 09 December 2019

Introduction: Doing Philosophy of Social Science

Abstract and Keywords

This article reviews the changes in the philosophy of the social sciences, arguing that there have been significant advances in the thinking about the social world. In addition, it defines the frameworks and issues that motivate the kind of philosophy of social science and social science. The developments in the philosophy of science are introduced. The interest in causality was directly parallel to the interest in complex causality, which is used in various ways, but some standard notions are thresholds, conjunctive causes, and necessary causes. The directed acyclic graph (DAG) framework suffers in situations where the causal effect of one factor depends on the value of another. The formalism of DAG models can be a hindrance to recognizing causal complexities.

Keywords: philosophy, social science, causality, directed acyclic graph, causal complexities

This volume is shaped by important developments in both the social sciences and the philosophy of the social sciences over the last several decades. In this chapter I outline these changes and argue that they have indeed been significant advances in our thinking about the social world. Rather than providing linear summaries of twenty-plus chapters, I delineate the frameworks and issues that motivate the kind of philosophy of social science and social science that is represented in this volume. Both philosophy of social science and social science itself are intermixed in the following chapters. That is because the volume is built around a guiding naturalism that denies that there is something special about the social world that makes it unamenable to scientific investigation, and also denies that there is something special about philosophy that makes it independent or prior to the sciences in general and the social sciences in particular. In the process of outlining recent developments the chapters of the handbook are related and motivated, and open unresolved issues are discussed.

1.1. Developments in Philosophy of Science

I start with developments in the philosophy of science. Though the monikers are not entirely historically accurate, I want to contrast previous positivist philosophy of science with postpositivist views which I believe provide a much more useful (p. 4) framework for thinking about science and social science. Some of the key tenets of positivist philosophy of science are as follows.1

Theories are the central content of science. A mature science ideally produces one clearly identifiable theory that explains all the phenomena in its domain. In practice, a science may produce different theories for different subdomains, but the overarching scientific goal is to unify those theories by subsuming them under one encompassing account. Theories are composed of universal laws relating and ascribing properties to natural kinds and are best understood when they are described as formalized systems. Philosophy of science can aid in producing such formalizations by the application of formal logic.

The fundamental concepts of science should have clear definitions in terms of necessary and sufficient conditions. General philosophy of science is in large part about clarifying general scientific concepts, especially explanation and confirmation. The goal is to produce a set of necessary and sufficient conditions for application of these concepts. These definitions are largely tested against linguistic intuitions about what we would and would not count as cases of explanation and confirmation.

Explanation and confirmation have a logic—they conform to universal general principles that apply to all domains and do not rest on contingent empirical knowledge. A central goal of philosophy of science is to describe the logic of science. Explanation involves (in some sense still to be clarified) deductions from laws of the phenomena to be explained. Whether a science is well supported by evidence can be determined by asking whether the theory bears the right logical relationship to the data cited in support of it.

Independence of philosophy from science: Identifying the logic of inference and explanation and the proper definition of concepts are philosophical activities. Scientists certainly can act as philosophers, but the philosophy and the science are different enterprises with different standards. The collorary is that philosophy of science is largely done after the science is finished.

Social institutions are irrelevant. The social organization of science may be an interesting topic for sociologists, but it has little direct bearing on philosophy of science’s tasks.

The criteria for explanation and confirmation allow us to properly demarcate scientific theories from pseudoscientific accounts. Pseudoscientific accounts tend to sacrifice due attention to confirmation in favor of apparent explanation, and in so doing fail to be genuinely explanatory.

It is a serious open question to what extent any of the social sciences are real sciences. This question is best explored by comparing their logical structures with those characteristic of physics and, to a lesser extent chemistry, geology, and biology. All the key characteristics described above should characterize any scientific social science and its related philosophy of science.

These positivist ideas have been replaced with a considerably more subtle and empirically motivated view of the philosophy of science in the following ways.

Theories as central: “The” theory in a given discipline is typically not a single determinate set of propositions. What we find instead are common elements that (p. 5) are given different interpretations according to context. For example, genes play a central role in biological explanation, but what exactly a gene is taken to be varies considerably depending on the biological phenomena being explained (Moss 2004). Often we find no one uniform theory in a research domain, but rather a variety of models that overlap in various ways but that are not fully intertranslatable. Cartwright (1980) gives us the example of models of quantum damping, in which physicists maintain a toolkit of six different mathematical theories. Because these aren’t strictly compatible with one another, a traditional perspective in the philosophy of science would predict that physicists should be trying to eliminate all but one. However, because each theory is better than the others for governing some contexts of experimental design and interpretation, but all are reasonable in light of physicists’ consensual informal conception of the basic cause of the phenomenon, they enjoy their embarrassment of riches as a practical boon. There is much more to science than theories: experimental setup and instrument calibration skills, modeling ingenuity to facilitate statistical testing, mathematical insight, experimental and data analysis paradigms and traditions, social norms and social organization, and much else—and these other elements are important to understanding the content of theories.

Theories, laws, and formalization: Laws in some sense play a crucial role in scientific theories. Absent any trace of what philosophers call modal structure, it is impossible to see how scientists can be said to rationally learn from induction. However, some of our best science does not emphasize laws in the philosopher’s sense as elegant, context-free, universal generalizations, but instead provides accounts of temporally and spatially restricted context-sensitive causal processes as its end product. Molecular biology is a prime example in this regard, with its emphasis on the causal mechanisms behind cell functioning that form a complex patchwork of relations that cannot be aggregated into an elegant framework. Expression in a clear language—quantitative where possible—is crucial to good science, but the ideal of a full deductive system of axioms and theorems is often unattainable and not, as far as one can see, actually sought by many scientific subcommunities that are nevertheless thriving.

Conceptual analysis: Some important scientific concepts are not definable in terms of necessary and sufficient conditions but are instead much closer to the prototypes that, according to cognitive science, form the basis for our everyday concepts of kinds of entities and processes. The concept of the gene is again a good example. There is no definition of gene in terms of its essential characteristics that covers every important scientific use of the concept. Cartwright (2007) has argued recently that the same holds even for so general and philosophical an idea as cause: There are different senses of cause with different relevant formalizations and evidence conditions. Equally important, the traditional philosophical project of testing definitions against what we find it appropriate to say is of doubtful significance. Who is the relevant reference group? The intuitive judgments of philosophers, whose grasp of science is often out of date and who are frequently captured by highly specific metaphysical presuppositions, do not and should not govern (p. 6) scientific usage at all (Ladyman and Ross 2007, chapter 1). Questions about the usage of scientists is certainly more relevant, but this also may not be the best guide to the content of scientific results.

The logic of confirmation and explanation: Confirmation and explanation are complex practices that do not admit of a uniform, purely logical analysis. Explanations often have a contextual component set by the background knowledge of the field in question that determines the question to be answered and the kind of answer that is appropriate. Sometimes that context may invoke laws, but often it does not, at least not in any explicit way. Confirmation likewise depends strongly on domain-specific background knowledge in ways that make a purely logical and quantitatively specifiable assessment of the degree to which specified evidence supports a hypothesis unlikely. The few general things that can be said about confirmation are sufficiently abstract that they are unhelpful on their own. The statements “a hypothesis is well supported if all sources of error have been ruled out” or “a hypothesis is well supported by the evidence if it is more consistent with the evidence than any other existing hypothesis” are hard to argue with. Yet to make any use of these standards in practice requires fleshing out how error is ruled out in the specific instance or what consistency with the evidence comes to in that case. Other all-purpose criteria such as “X is confirmed if and only if X predicts novel evidence” or “X is confirmed if and only if X is the only hypothesis that has not been falsified” are subject to well-known counter examples and difficulties of interpretation.

Holism: It is a fallacy to infer from the fact that every hypothesis is tested in conjunction with background theory that evidence only bears on theories as wholes (Glymour 1980). By embedding hypotheses in differing background theoretical and experimental setups, it is possible to attribute blame and credit to individual hypotheses. Indeed, this is how the overwhelming majority of scientists view the overwhelming majority of their own research results. Judged on the basis of considerations that scientists typically introduce into actual debates about what to regard as accepted results, the relationships between theories, applications, and tests propagated by Quine, Kuhn, and Lakatos look like philosophers’ fantasies. While these three philosophers were instrumental in the transition from positivist philosophy of science, their arguments and views have been superceded: Data may be theory-laden, but theory-laden comes to many things and does not mean that every piece of data is laden with whole theories, and does not prevent the kind of triangulation and piecemeal testing of specific hypotheses characteristic of good science.

Independence of philosophy from science: Philosophy of science and science are continuous in several senses. As we saw, the traditional conceptual analysis of analytic philosophy is a nonstarter and philosophical claims are subject to broad empirical standards of science. Of course, getting clear on concepts has real value. However, it is something scientists do all the time, but in ways far more sophisticated and empirically disciplined than the traditional philosophical practice of testing proposed definitions against what we would say or against intuitions (Wilson 2007). Philosophy of science is also continuous with science in that philosophy (p. 7) of science is not entirely or mostly something that is done after the science is settled. Instead, philosophy of science issues arise in ongoing scientific controversies and part of the process of settling those issues. Again, philosophy of science is something that scientists themselves do, and in a sense science is something that philosophers of science do. Contemporary philosophy of biology is a paradigm case in this regard. Philosophers of science publish in biology journals and biologists publish in philosophy of biology venues. The problems tackled are as much biological as philosophical or conceptual: The questions are such things as how is genetic drift to be understood or what is the evidence for group selection.

Science and pseudoscience: Several of the insights about science already discussed suggest that judging theories to be scientific or pseudoscientific is a misplaced enterprise. Scientific theories and their evidence form complexes of claims that involve diverse relations of dependence and independence and, as a result, are not subject to uniform or generic assessment. Any general criteria of scientific adequacy that might be used to distinguish science from pseudoscience are either too abstract on their own to decide what is scientific or not, or they are contentious. This is not to deny that astrology, so-called creation science, and explicitly racialist sociobiology are clearly quackery or disguised ideology; it is merely to point out that these judgments must be supported case by case, based on specific empirical knowledge.

Institutions can matter: Science has to be studied as it actually works and that requires investigating much more than a rarified logic of explanation and confirmation. Science is surely a social enterprise. It does not follow from this claim that science is a mere social construction, that evidence plays no role in science, or that science has no better epistemic status than any other institution. It is an empirical question whether the institutions, culture, power relationships, and so on of science promote or hinder the pursuit of scientific knowledge (Kitcher 1993). Social scientists, historians, and philosophers of science have indeed produced many illuminating studies of science in practice and treating science scientifically requires asking what role social processes play, but they do not support the more extreme, all-encompassing claims about mere social construction.

Scientific social science: The above discussion of science and pseudoscience should make it obvious that questions about the genuine scientific status of all—or some particular—social science are sensible only if (1) they are posed as questions about specific bodies of social research and (2) they are approached as concrete inquiries into the evidential and explanatory success of that body of work. Assessing scientific standing is continuous with the practice of science itself.

This means that providing all-purpose arguments about what the social sciences can or cannot do on broad conceptual grounds is misguided. The same holds for judging the social sciences by comparison with positivist misunderstandings of physics.

A fair amount of past philosophy of social science was this kind of unfortunate project. For example, Charles Taylor (1971) argued in a widely cited article that the “human” sciences were fundamentally different from the other sciences because (p. 8) explaining human behavior requires understanding meanings and therefore the human sciences cannot provide the kind of “brute” data (Taylor’s word) that the natural sciences provide.

There are two clear problems with arguments like this. First, they make blanket claims about the social sciences that are implausible. Lots of social research is not about individual beliefs, interpretations, symbols, and so on. Instead it is about macrolevel or institutional processes. So organizational ecology studies the competitive environment determining the differential survival of organizations (Hannan and Freeman 1989). Individual beliefs and interpretations are not part of the story. There is an implicit individualism in arguments like Taylor’s.

Secondly, Taylor’s argument has an implict positivist understanding of the natural sciences, which is ironic given that Taylor would certainly not think of himself as holding such views. Data in the natural sciences are acquired and interpreted based on a host of background assumptions and are not “brute.” Understanding meanings—and this term hides a host of different things—certainly requires background knowledge, but the question for the social sciences is the same as for the natural sciences: What knowledge is assumed and what is its quality? This general point has been argued by Follesdol (1979), Kincaid (1996), and Mantzavinos (2005). In a way Daniel Dennett’s entire project argues something similar. Good social science is aware of the problem that meanings bring and tries to deal with them. For example, careful experimental work in the social sciences goes to great pains to control for subjects’ understanding. There are many ways such problems show up in the social sciences and no doubt some social science handles them badly. But it is a case-by-case empirical issue, not a deep conceptual truth about the nature of the human.

Views like Taylor’s are a denial of an important—and correct, in my view—doctrine about the social sciences that is a form of naturalism (Kincaid 1996). Human social organization and behavior is part of the natural order and thus amenable to scientific study. No doubt human social behavior raises its own set of difficulties calling for methods not found in physics, for example. But the methods of the natural sciences differ greatly across the sciences as well. Geology, cosmology, and evolutionary biology are much less experimental than other natural sciences, but basic scientific virtues such as ruling out competing explanations are embodied in their practices. Naturalism says that those virtues are possible and necessary in the social sciences as well.

These are the guiding philosophical ideas behind the chapters in this volume. The goal has been to promote work in philosophy of social science that parallels the good work our colleagues in philosophy of biology have produced—work that engages with the science and its ongoing controversies. Plenty of philosophical issues arise but largely in the context of problems in contemporary social research. Given the latter interest, it is not surprising that contemporary developments in social science also strongly influence the chapters included. I want to next discuss some of those developments and in the process survey the issues raised by the various chapters.

(p. 9) 1.2. Overview of the Issues

There has been a renewed interest in causality and causal complexity among social scientists that has interacted with other developments in methodology. It is arguable that much social science from the 1950s through the 1970s was suspicious of making causal claims about the social world (Hoover 2004). This suspicion goes back to Hume through Pearson, whose causal skepticism was part of the trimmings of the new statistical methods he helped develop that have been central to much social science. However, social scientists have deep interests in policy and political issues, and thinking about those things requires causal notions. So causal interest never really went away. Some social scientists—primarily economists—started trying to determine the conditions under which regressions could be interpreted causally in the 1950s, and there were further forays later. However, in the last fifteen years the tools for explicit causal modeling have expanded and increased in rigor with groundbreaking contributions from computer science (Pearl 2000) and philosophers of science (Glymour et. al 1987). Explicit causal models are now much more common in the social sciences in part due to these developments. At the same time, philosophers of science took increasing interest in nonreductive accounts of causation and the methods they entail (Cartwright 1989, 2009 and Woodward 2005).

Several other factors also contributed to renewed interest in and confidence about making causal judgments. Movements in sociology have emphasized the importance of mechanisms (Hedström and Swedberg 1998) and mechanisms are naturally explicated by causal notions. A need for such mechanisms was also motivated by the widespread expansion of rational choice game theory and then evolutionary game theory (and related modeling techniques) in social sciences outside economics. Applied game theory provides possible mechanisms for stable macropatterns, raising suspicions of macropatterns without a mechanism.

A third trend that has moved causal thinking to the fore is increasing statistical sophistication in the social sciences, made possible in part by increased computing power. Part of that sophistication appeared in the explicit causal modeling mentioned above, which moved in tandem with application of Bayesian notions in the social sciences. Another source of sophistication that led to more explicit causal thinking was the introduction of large-scale randomized trials into the social sciences and the development of statistical methods such as instrumental variables and potential outcomes analysis (Dufflo, Glennerster, and Kremer 2008, Angrist and Pischke 2008). These methods hope to indentify causes explicitly.

Parallel to increased interest in causality was an increased interest in complex causality. Complex causality is used in various ways, but some standard notions are threshholds, conjuctive causes, and necessary causes. The basic claim is that in the social world, the causes are not thought of as a set of independently acting sufficient causes that operate everywhere and are everywhere the same. These recognitions were embodied in innovative and nontraditional methods for dealing with constellations (p. 10) of causes, using Boolean algebra and fuzzy set theory (Ragin 1987), for example. Anthroplogists had always argued that social causality was complex and contextual, but now sociologists and political scientists were saying the same thing, using new tools to look at their subject matters.

Thus the chapters in part I take up a variety of issues about causality in the social sciences. Petri Ylikoski and I are both concerned with unpacking the claims that social science needs causal mechanisms. Ylikoski argues that on one of the best conceived pictures of mechanisms—that outlined by philosophers of biology—mechanisms in the social sciences argue against various forms of individualism. Mechanisms may certainly make heavy use of agents’ perceptions, intentions, and actions. Yet nothing about a proper understanding of mechanisms makes explanations in terms of individuals the full story or the fundamental story. Rather, mechanism-based explanation is largely achieved through interfield accounts from multiple disciplines linking macro and micro in reciprocal ways. It is individual behavior acting in the preexisting institutional and social context that is important. This theme is repeated in part III, Norms, Culture, and the Social-Psychological, in the chapter by David Henderson on norms and by Don Ross on the origins of social intelligence. Both argue that such context is essential for successful explanations to take into account the institutional and cultural factors.

David Waldner continues the discussion of mechanisms by looking at the currently popular idea in the social sciences that process tracing is an important evidential and explanatory strategy, and ties it to a particular understanding of mechanisms. He notes that there is a clear distinction between wanting mechanisms for explanation as opposed to wanting them to provide evidence. Waldner argues that the most interesting understanding of process tracing comes from identifying the mechanisms that underlie established causal relations (what I call vertical mechanisms). Identifying intervening causes between established causal relations (horizontal mechanisms) has value, but it does not explain why causal relations hold. Mechanisms that do so provide explanatory added value and they are not variables as traditionally conceived (they cannot be manipulated independently of the causal relations they bring about), but are invariants—they generate the correlations and causal relations that are observed. Mechanisms in this sense can be individual actions, institutional constraints, and so on and combinations thereof.

On the evidential side, the methods associated with process tracing claim to be different than standard statistical methods. Waldner agrees. Yet he argues persuasively that these alternative methods at present are quite informal and in need of further clarification to establish their reliability. In terms of the philosophies of science sketched earlier, advocates of process tracing realize that social science evidence is not reducible to simple, more or less a priori rules. Yet that does not mean that anything goes, and defending and articulating the reasoning behind process tracing is an important and underdeveloped project essential to advancement in the social sciences.

Julian Reiss ties into Waldner’s discussion of process tracing by giving clear conditions and usages for counterfactual claims in the social sciences. He points out (p. 11) that process tracing does not give us information about the actual difference a potential cause makes (which is Robert Northcott’s main concern). Counterfactuals can help tell us about such differences. Furthermore, analyzing counterfactuals requires explicit causal models, and developing these can help avoid various biases that often operate when no such model is present (I make a parallel point).

I also point out that the notion of a mechanism can mean multiple different things, that mechanisms can be wanted for different things—for example, for confirmation of causal claims versus for providing causal claims of sufficient explanatory depth—and that the resulting variety of different claims about mechanism need not all fall or stand together. Using the directed acyclic graph (DAG) framework, I argue that there are some specific situations where mechanisms are needed to avoid bias and confounding. Standard regression analysis in the social sciences often misses these problems because they work without explicit causal models. These arguments are about mechanisms in general and give no support to the idea that the mechanisms must be given in terms of individuals.

The DAG framework suffers in situations where the causal effect of one factor depends on the value of another. I argue that the DAG formalism has no natural way to represent this and other complex causes such as necessary causes. In part II, Evidence, Stephen Morgan and Christopher Winship present an interesting, novel, and empirically well motivated route for handling a specific subset of interactions in DAGs motivated by the literature on education and outcomes that will be an important contribution to the literature and builds on their previous substantial work on causal modeling in the social sciences (obviously, the evidence and causation chapters overlap). Their results certainly provide another concrete sense of needing mechanisms.

The causal complexity discussed in my chapter and by Morgan and Winship refers to situations where it is unrealistic to think that a particular type of effect is caused by a list of individual causes, each having an independent measurable sufficient partial effect on the outcome. Further complications involved in this picture of social causation are investigated by Northcott and by David Byrne and Emma Uprichard. Northcott’s concern is finding coherent accounts of causal effect size in the existing (mostly regression based) literature. To put the moral in brief, regression coefficients are not generally good measures of effect size or causal strength and even when they are, they depend strongly upon already having good evidence about the causal relations or structure in play, a point emphasized by Northcott as well as myself. Byrne and Uprichard discuss varieties of causal complexity—in cases where it is not realistic to think that the string of independent causes model applies—and methods for dealing with them. In particular, they focus on the qualitative comparative analysis framework of Ragin using Boolean logic and fuzzy set theory that promises to go beyond standard correlation statistics when dealing with complex causes. That framework deserves more discussion than space allowed for in this volume—it deals with complex causation in a way that philosophers would naturally understand and it has novel methodological tools that are becoming increasingly popular.

(p. 12) Gary Goertz picks up on the limitations of standard statistical methods for confirming causal claims. His chapter is full of rich, interesting examples of social science causal-descriptive generalizations that are well established, despite the common mantra that none such exist. He makes an important point that seems obvious once it is understood but is not widely grasped: A set-theoretical claim of all As are Bs can be consistent with zero correlation in statistical senses. In terms of the philosophy of science sketched at the beginning, statistical reasoning relies on a formal logic of inference that does not handle all relevant complexities.

A deeper, more philosophical issue lying behind work on causality in the social sciences concerns understanding the probabilities they support. While it is possible to interpret probabilities in social research as resulting from measurement imprecision or from unmeasured variables, these are not entirely satisfactory accounts. It seems that we end up with probabilistic causes even when our measurements are quite reliable. Second, why should unmeasured causes produce the kinds of stable frequencies that we see in the social realm? Marshall Abrams provided a sophisticated answer in terms of a novel account of what he calls mechanistic probability—stable frequencies produced from underlying causal processes with specific structure. Such structures exist in nature—a roulette wheel is a paradigm instance—and there is good reason to think that in the social realm there are social equivalents of roulette wheels.

Part II of the volume contains chapters about evidence. Of course, chapters in part I are also concerned with evidence, and explanation issues show up in part II. However, there is a decisive shift in emphasis in the chapters of the two parts.

Fred Chernoff surveys the history up to the present of the Duhem’s underdetermination thesis. He notes that it is not nearly as radical as Quine’s, which I argued earlier was excessive and ignored the variety of techniques that scientists can use to triangulate on where to place blame when hypotheses do not match the data. Duhem’s concern was to deny that simply by the use of formal deductive logic, one could determine with certainty whether a hypothesis was confirmed or not. In short, he was a precursor of the postpositivist philosophy of science sketched earlier that rejects the logic of science model. Assessing the evidence depended upon the good common sense of the relevant scientific community.

Chernoff also discusses the relevance of Duhem’s view that there may be multiple ways to measure or operationalize aspects of theories, and in that sense which measure is used is conventional. Duhem did not think that this made the choice arbitrary—the good common sense of the scientific community was again needed—but that adopting a common measuring procedure was crucial for scientific progress. Chernoff provides a detailed case study of two important areas in international relations—the democratic peace hypothesis and balance of power theories—showing how in the former common measures promoted significant scientific progress, and the lack of them in the latter undermines its empirical qualifications.

Andrew Gelman and Cosma Rohilla Shalizi discuss the use of Bayesian methods in social science testing based on their considerable combined experience. However, their take on Bayesian methods is quite different than the usual subjective Bayesians (p. 13) versus objective frequentist debate. That debate is often framed as being about which of these views is the true logic of science, and thus based on a false presupposition from the postpositivist point of view. Gelman and Shalizi don’t see much value in the exercise of starting with subjective priors and updating them to a new posterior distribution. However, they argue that Bayesian methods are quite useful when it comes to model checking in the social sciences. Model checking as they mean it is a paradigm instance of the kind of piecemeal triangulation that radical holists miss.

Aviezer Tucker also uses Bayesian ideas in his discussion of the relation between the social sciences and history. He argues that history is not applied social science, and social science is generally not history. History is about inferring to common cause token events in the past using background theories of information transfer applied to currently available traces in the form of such evidence as documents. Social science is about relating types—variables—by quite different, often statistical, methods. Bayesian ideas come into play in two ways. He argues that inferring to a past token event as a common cause of multiple present information traces is a matter of the likelihood of the common cause hypothesis versus its competitor. That is not a fully Bayesian framework, because it does not involve priors. However, Tucker argues that social science results can tell historians what possible past tokens are initially plausible as common causes. Inferring who wrote the Bible can be informed by the finding that writing only arises in the presence of a centralized bureaucratic state, and thus that books of the Old Testament cannot be contemporary to the events they described. In that sense the social sciences can provide priors. However, priors in this sense are just relevant background information—in other words, good scientific common sense.

Nancy Cartwright’s chapter on randomized controlled trials (RCTs) as evidence for potential policy effectiveness echoes the general theme of part II that evaluating evidence in practice is a complex and fallible affair that rules of scientific logic do not capture. RCTs are treated by the medical profession and increasingly by social scientists—they are all the rage in development economics, for example—as the gold standard. That phrase is widely used without clear explanation, but it generally means either that RCTs are thought to be near conclusive proof, the only real proof, or by far and away the best proof. In short, their logic guarantees reliable outcomes, another of the hopes for a logic of science. Cartwright argues convincingly and in detail that RCTs can be quite unreliable as guides to policy effectiveness.

Morgan and Winship take up in much greater detail the issues raised by interaction effects and heterogeneity for DAG analyses that I raise in my chapter. They provide an explicit framework for incorporating such complications into DAGs. Their basic approach to the possible errors caused by interaction and heterogeneity is to model them. Like Gelman and Shalizi, their concerns are driven by the kinds of problems they see in existing research, which in their case are the causes of educational attainment. Formal methods like DAGs are useful, but their usefulness has to be evaluated according to the kinds of causal complexity faced by practicing researchers and adapted accordingly. They note that the formalism of DAG models can be a hindrance to recognizing causal complexities.

(p. 14) Ken Kollman’s chapter continues the emphasis on the complexities of evidence, focusing on the burgeoning field of computational models of social phenomena. In one way his topic is a classical one, especially in philosophy of economics, about the status of abstract and idealized models. Kollman notes what modelers often say in their defense—namely, that models provide insight. However, he goes a step further and realizes that appeals to insight are not enough (it could be a warm and fuzzy feeling only, though this is my formulation, not his). Kollman gives several other, more concrete reasons such models may be reasonable. It is possible to generate simulated data with computational models and then compare the patterns in the data with real empirical patterns in analogous social data. So empirical testing is possible, though Kollman cautiously notes that there are still issues about how strong the analogy is. Computational models also have explanatory virtues: They instantiate the causal mechanical ideals advocated in the chapters in part I. This means they can represent dynamics, something that rational choice game theory, for example, cannot. He also argues that they provide ways to model micro and macro social phenomena, in line with Ylikoski and Waldner’s idea that mechanism-based explanation defuses individualism/holism debates.

The chapters in part III deal with an intersecting set of topics concerning culture, norms, and the explanation of sociality. Here issues of explanation (macro and micro, for example), evidence, and more philosophical issues concerning how to understand key concepts are intertwined. Most chapters ask the question: How do explanations in terms of norms, culture, and related concepts relate to psychological explanations? To what extent are the latter sufficient? Necessary? What is the basis of human sociality? Human nature or social organization or some mix of the two? And if the latter, how does that work?

Mark Risjord provides a history up to the present of the concept of culture in anthropology, where the concept is most used. That history has been a running conflict between treating culture as a trait of individuals—a form of methodological individualism—and as something superseding individuals and sometimes indeed as controlling them. The most plausible view, according to Risjord (echoing the approach emphasized by Ylikoski) is to see that debate as dissipated by a more interactive view where neither the individualist or holist view is on the table. Though that is a common theme throughout the volume, there is obviously more work to do in fleshing out that claim. My guess is that there are multiple, domain-specific ways of doing so, and I would not claim that this volume is anything like the final word on the issue.

Henderson takes on clarifying norms, a concept widespread throughout the social sciences, though it is generally not carefully explicated. Sometimes norms are only behavioral regularities. Henderson argues convincingly that in this guise they are not particularly explanatory. His main focus is on norms as knowing (and having attitudes about) a rule, following some of the most sophisticated recent analyses. Henderson argues that rules cannot be seen as entirely a psychological phenomenon, because payoffs and differences in social status and power are part of the explanation. However, there are important questions, largely unexplored in the (p. 15) literature, about the psychological basis and explanation of knowing rules. To what extent can cognitive science accounts be integrated with sociological, economic, and anthropological accounts? Like Ylikoski in chapter 2, Henderson thinks that an interfield account is called for.

The evolutionary program in social science is the subject of Francesco Guala’s and Tim Lewens’s chapters. Guala focuses particularly on the debate over whether cooperation and sociality in humans requires strong reciprocity—roughly, the willingness to perform costly sanctions to enforce norms—or can be simply explained in terms of self-interest. This empirical issue is important for policy decisions, since if humans are not generally capable of strong reciprocity, policies that assume they are will lead to bad outcomes. Lewens provides an overview of objections to theories of cultural evolution. He delineates the relation between sociobiology and other kinds of evolutionary accounts and between meme-based versions and population level learning accounts. Levens give us a balanced account that argues that not all problems raised in the literature against evolutionary models are decisive, and yet is wary of attempts to push further than we can go.

Ross looks at the interactive origins of human intelligence and sociality, specifically at the thesis that human intelligence in evolutionary history resulted from the need to meet the needs of social interactions. He surveys neurobiological and other evidence that suggests primates in general have natural dispositions to cooperate. So human intelligence seems unlikely to be the result simply of the need for social coordination. Instead, Ross suggests that that when hominid groups developed specialization and trading, greater demands arose to deal with these new forms coordination. Complex socialized selves were needed to play the more complex games that exchange and specialization involves.

Ron Mallon and Daniel Kelly examine the status of race as a social science concept. The biological notion of race seems quite unfounded, so how has it been a useful concept in the social sciences—or has it been? They deny that race is fully explained as a social role and argue that there is important empirical evidence suggesting that there are strong psychological underpinnings behind our tendencies to categorize people in terms of race. This is in keeping with the theme of many chapters that macro and micro accounts need to be involved and integrated.

The chapters in part IV focus on issues in the sociology of knowledge. Earlier chapters had already informally considered some sociological and rhetorical aspects of social science research. As argued earlier in the chapter, information about the sociological factors driving research can be useful information in assessing the scientific standing of various lines of research.

Amy Mazur discusses feminist social science research, especially feminist comparative politics (FCP), her prime area of interest. The feminist research she advocates and discusses aims to contribute to accumulation of knowledge through empirical research, and she carefully distinguishes this from extreme constructivist views about science that some feminists have espoused. The feminist research she advocates does proceed, however, with an awareness of and interest in gender issues and a recognition of how gender biases can infect standard social science research. (p. 16) She details the empirical success of feminist comparative politics. Mazur describes the social organization of the FCP community and its interaction with elements of national governments that have made it a success. However, she notes that mainstream comparative politics has largely ignored these achievements and argues that gender biases continue to plague the mainstream, which is still largely comprised of male researchers.

Allan Horwitz applies the sociology of knowledge approach to mental illness. He rejects the idea that the sociology of mental illness classification and organizational embeddedness shows that mental illness is a pure social construct (just as Mazur rejects radical constructivist feminist views about science). He also thinks that saying that all mental illness is a matter of looping kinds—interaction between individual traits and the effect on the individual classified as having some mental disorder—as Hacking sometimes suggests is too crude a formulation that glosses important differences. Looping seemingly plays a much bigger role in ADHD than it does in schizophrenia. Horwitz believes that there can be neurobiologically based mental malfunctions that constitute mental illness. Looking at the social and institutional processes involved in the classification and treatment of behavior of mental disorders can be quite helpful in assessing which current practices have a grounded basis and which ones exist largely due to the sociology of the psychiatric profession and the classification process.

The final chapters of the volume comprising part V focus on normative issues that have important ties to social science research and philosophy of science issues. James Woodward uses the kind of work on reciprocity in cooperative behavior discussed by Guala and Ross to ask what implications it may have for political philosophy. Daniel Hausman discusses the difficulties in evaluating health outcomes in terms of the preferences of patients and concludes that evaluation often relies on messy ad hoc processes. Anna Alexandrova asks if social science research on well-being actually gets at well-being (something its critics wonder about). She argues that philosophical accounts of well-being are of minimal help, and in practice the different sciences that study well-being use different, local notions relevant to the context without compromising their results. This is in keeping with the postpositivist moral drawn at the beginning that science often does not work with concepts definable in terms of necessary and sufficient conditions.

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Notes:

(1) . Another distinct difference is over the role of values. Since I have pursued this at length elsewhere (Kincaid 2007), I am not going to do so systematically here. There are many different ways values can be involved with different consequences. The short answer is that science is a complex set of practice and that values can cause bias in some cases but not in others. For example, Mazur’s chapter shows how values can both lead to better science and to bad science as does Horwitz’s chapter on mental illness.