Abstract
Most social scientists agree that case studies are useful for “theory building,” but ethnographic methods papers often look to survey research for case selection strategies. This is due to a common but untenable distinction between theoretical and empirical generalization, which obscures how theoretically inclined ethnographers make implicit external validity claims. I analyze several exemplary ethnographies to show that (a) the distinction between theoretically and empirically oriented ethnography revolves around competing conventions for making claims that others accept as provisionally externally valid, (b) comparative-historical sociology provides a framework for evaluating how theoretically oriented ethnographies make such claims, and (c) each approach to making validity claims is optimized by different kinds of cases. Empirically oriented ethnographies make inductive claims via “pointy” cases wherein a phenomenon is pronounced or bifurcated. Theoretically oriented ethnographers are like post–Millian historical sociologist who triangulate past studies with resolutive or negative cases to make constitutive arguments.
Keywords
Molly is a medical student who routinely dissects cadavers as part of her training. On her way home one day, she waits for the bus near a young man who is sweating profusely and begins complaining of nausea and chest pain—classic symptoms of a heart attack. Molly calls 911, but the man’s condition deteriorates: He collapses, exhibiting first an irregular heartbeat then no heartbeat at all. He is dead before the paramedics arrive.
“Why?” Molly wonders once finally seated on the bus. Suddenly aware of her own mortality, she considers that the young do not usually suffer heart attacks and wonders about causes: Did the man eat too much bacon, smoke, or use illicit drugs? Molly’s medical training, including dissection of numerous cadavers who did and did not die of heart attacks, is of little use in confirming or ruling out such causes. Still, Molly, ever analytically minded, likes to take comfort in the certainty of science at times like these: whatever the man’s habits, genes, or vices, she is pretty sure that he died due to a clot in one of several coronary arteries.
What can one conclude about the world based on in-depth analysis of a few cases—or even a single case? Among ethnographers, there is surprisingly little consensus on this question, largely because scholars address the question in two different ways. Some ethnographers, especially those who work in subfields populated by survey methodologists, see case selection as primarily relevant for establishing external validity or one’s ability to “speak to empirical conditions in other cases (not observed)” (Small 2009:5; see also Elman, Gerring, and Mahoney 2016; King, Keohan, and Verba 1994). Other ethnographers focus on one’s ability to generate theory based on cases, which scholars often present as different from external validity—for instance, as an effort to formulate “theoretical generalizations” as opposed to “empirical generalizations” (Small 2009; Spillman 2014). And accounts of theory building usually take for granted that one has already selected a case and focus on how to mine it for theoretical insights (Becker 2008; Katz 2001; Tavory and Timmermans 2012), especially insights that allow one to formulate causal claims (e.g., Beach and Pedersen 2018; Blee 2013; Gross 2009; Katz 2001, 2002; Lichterman and Reed 2015; Ragin and Becker 1992).
Taken together, this methodological literature communicates three misleading impressions about theoretically oriented ethnographic research, which muddle prescriptions about case selection. First, it implies that theoretically oriented ethnographers cannot or should not try to make claims about empirical conditions in unobserved cases. Second, it suggests that theorization depends primarily on a “theoretical sensitivity” that allows one to appreciate anomalous findings rather than the characteristics of a given case (Tavory and Timmermans 2012:170). And finally, it suggests that theory is primarily about identifying causal mechanisms rather than “mere description.”
In what follows, I take a conventionalist approach to the question of ethnographic case selection: I analyze recent ethnographies that successfully make claims that others interpret as informative about empirical conditions in other cases—as provisionally externally valid. 1 American sociologists associate causality with the discipline’s most scientific aspects (Abbott 1992; Becker 2008:17), and in this respect ethnographers are “more royalist than the king”: even more likely than other social scientists to emphasize causal claims, especially when publishing in general sociology journals (Abend, Petre, and Sauder 2013:615). But the ethnographic claims that most inform others’ understanding of the world are rarely causal. Rather, I argue that ethnographers’ externally informative claims typically fall into a gray area between causal claims and context-dependent description, which I identify as constitutive arguments. Constitutive arguments are context-independent analytical descriptions about the makeup and useful categorization of social phenomenon, which commonly focus on existence (i.e., “X exists”), casing (i.e., “X is a case of Y”), or categorization (i.e., “X consists of subcomponents A and B”).
Consider Molly who is analogous to an ethnographer. Molly has conducted case studies of other bodies (i.e., dissections) and wants to use her expertise to say something valid about the empirical reality lying dead at her feet—though, naturally, without conducting a new dissection. In this respect, she is like an ethnographer who has studied a handful of suburban neighborhoods, elementary schools, or hospital waiting rooms in detail and wants to say something about other, unobserved neighborhoods, classrooms, or waiting rooms. Note that Molly’s knowledge of physiology gives her no special insight into the cause of the man’s heart attack. Following Small (2009), only samples—not cases—can be statistically representative. Molly may have dissected cadavers that suffered heart attacks due to smoking or poor dietary habits, but she knows nothing about the relationship between her cadavers and the population of all heart attack victims. She cannot draw inferences about the likelihood of different causes in this case. 2
But Molly can say with high certainty that the man’s heart attack was due to blockage of a coronary artery—a different sort of empirical claim. 3 We say in everyday speech that blockage of the coronary arteries “causes” a heart attack, but this is a misrecognition of a constitutive claim as causal. The statement is actually a useful analytical description, which pinpoints the features of the current situation that are equivalent to a heart attack taking place (Dasgupta 2017)—or, in this case, the physiological basis of the heart attack (myocardial infraction), which medical professionals identify as blockage of the coronary arteries. 4 It is more correct to say that, physiologically speaking, a clot in the coronary arteries is the heart attack or that a heart attack consists of such blockages. 5
If the point seems pedantic, consider that proponents and critics of qualitative methods routinely make characterizations that suggest a similar confusion between causal and constitutive arguments. For instance, many methodologists categorize qualitative sociologists as interested in deterministic rather than probabilistic causes or in variables that are “bigger,” “more complex,” or more likely to cluster into “combinations” than the sorts of variables that interest survey researchers (see, e.g., Lieberson 1994; Mahoney 2000; Sewell 2005; Skocpol and Somers 1980). But constitutive and causal arguments are simply different kinds of knowledge claims. Many scholars argue that claims about the constitution of social phenomena are necessary for fully satisfactory causal accounts (Abbott 1992; Gorski 2009; Hirschman and Reed 2014; Lichterman and Reed 2015; Martin 2011; Reed 2011; Steinmetz 1998), which is consistent with recent debates among philosophers of science (e.g., Hall 2004). 6 By analogy, Molly’s knowledge about the physiological basis of heart attacks can help her explain why, for example, eating badly or smoking increases the likelihood of having one. Following Gross (2009), constitutive arguments help one to identify the “gears” that form the links of mechanistic explanations. 7 Yet it does not follow from this that constitutive arguments are only informative in the service of particular causal accounts. For one thing, the same constitutive claim can inform multiple causal explanations. And constitutive claims also inform the audience’s understanding of empirical reality absent any causal account.
This is why causal and constitutive claims, which ethnographers sometimes make jointly within a particular work, often become decoupled in the course of disciplinary debate and inquiry—and, in such cases, it is the latter claims that tend to carry. One can easily list ethnographies that reshaped the field with constitutive arguments. Household gender relations are built on an implicit economy of exchange (Hochschild 1989). Becoming a habitual user of some intoxicants involves redefining their physiologically ambiguous effects as pleasurable (Becker 1953). Financial markets contain subcultures consisting of traders who adhere to common norms of opportunism (Abolafia 2001). The presentation of lessons in schools is shaped by a hidden curriculum that presupposes different personality traits in students (Anyon 1980).
But why do constitutive claims carry so effectively, and how should one select cases to formulate those that do? I argue that ethnographers can align their prescriptions about case selections with the reality of how successful ethnographers actually select cases by borrowing strategies from comparative-historical sociology. For ethnographers and historical sociologists alike, the lived experience of case selection usually falls between the extremes of a priori selection and skillful theorization of existing cases (see, respectively, King et al. 1994; Tavory and Timmermans 2012). Most ethnographers begin by focusing their attention broadly on a handful of sites or dynamics within a site and “select cases” by devoting greater time or analytical energy to a subset of observations. Therefore, the key to case selection is better intuition about characteristics of cases that others will find surprising or informative. In this respect, ethnographers can learn practical insights from historical sociology, wherein methods debates focus centrally on case selection, studies of single cases are now common (Clemens 2007), and scholars routinely use cases to make constitutive arguments. Two historical approaches offer particularly useful models for ethnography: the formation story approach (Hirschman and Reed 2014) and negative case analysis (Emigh 1997).
The article proceeds in three parts. The first section reviews debate over comparison in historical sociology, which many scholars now see as primarily useful for identifying the complex formations that constitute historical processes. The second section shows how such attention to the constitution of social phenomena disambiguates ethnographic debates about case selection—especially the common distinction between case studies that allow for empirical and theoretical generalization, which I show to be logically and practically untenable.
The third and final section examines recent exemplars to determine how ethnographers actually use cases to make claims that others accept as externally valid. Ethnographers do so by establishing a warrant for thinking that similar social formations are consequential elsewhere. The common distinction between empirically and theoretically oriented ethnography is actually about different conventions for how one makes such claims. Empirically oriented ethnographers follow the prescriptions of Small (2009) and make external validity claims inductively via “pointy” cases, wherein phenomenon of interest is large, bifurcated, or otherwise suggest causal or logical relations to other variables of interest. Theoretically oriented ethnographers make constitutive claims abductively vis-à-vis existing theory (Tavory and Timmermans 2012). They are best served by resolutive cases, wherein analysis resolves a contradiction in the literature, or negative cases (Emigh 1997), wherein empirical regularities predicted by theory do not occur.
Historical Comparison: From Causal to Constitutive Argument
Historical sociologists evolving understanding of case selection is informative for methodological debates among ethnographers. The subfield emerged during the methods wars of the late twentieth century, when many scholars seemed ready to jettison case study research altogether. Campbell and Stanley (1966:6-7), for example, famously argued that encouraging students to conduct case studies is “unethical” since they have “such a total absence of control as to be of almost no scientific value.”
In this context, historical sociologists initially argued that case studies allow one to make causal claims comparable to those of survey research. 8 Most notably, Skocpol (1979; Skocpol and Somers 1980) argued that Mill’s method of similarity and difference should be central to historical sociology due to its capacity to generate causal inference. When using the method of similarity, one looks for a common causal factor in maximally different cases that evince a common outcome. To use the method of difference, one looks for differences in similar cases with divergent outcomes. Skocpol argued that scholars can reliably identify necessary and sufficient causes by using both methods—for instance, of social revolutions (Skocpol 1979).
Many critics have argued, convincingly, that Mill’s method of agreement and difference is inappropriate for analysis of social phenomena. The method assumes a deterministic causality based in necessary and sufficient causes, whereas causal relationships between social phenomena are typically probabilistic. For instance, (Lieberson 1991) showed that Mill’s method can rule out drunk driving and running a red light as causes of car accidents: Drunk and unsafe driving increase the odds of an accident but are neither necessary nor sufficient to causes one. By the same token, Molly could use Mill’s method to rule out smoking and poor diet as causes of a heart attack. Such critiques put historical sociologists into a quandary, because although most observers agree that Mill’s method is inappropriate for analysis of social phenomena, it appears to somehow work in practice. As in Skocpol’s (1979) original analysis, the method often produces creative causal accounts that are at least rhetorically convincing (Mahoney 2000; Sewell 2005; Steinmetz 2004).
Scholars commonly account for the surprising utility of Mill’s method by arguing that it allows for a form of analogical reasoning that facilitates causal inference but does not produce reliable causal inference on its own (Mayrl 2018; Sewell 2005; Vaughan 2004). Instead, causal inference requires intra-case methods like pattern matching and process tracing (Goertz and Mahoney 2012). In one revisionist reading of States and Social Revolutions, for example, Sewell (2005:199-200) argues that comparison actually allowed Skocpol to identify “conditions of state breakdown” as a key feature of social revolutions, which facilitated a parallel intra-case sequence analysis that ultimately does the volume’s causal work. An important corollary of this argument is that comparison is inessential to historical sociology or at least performs a different function than comparison in survey methods. And indeed, historical sociology has grown to look less like quantitative analysis as scholars more regularly analyze processes within a single historical case (Clemens 2007). This has led many scholars to ask whether historical sociology and survey methods are scientific in the same way, or even scientific at all—for instance, whether the two rely on the same logic of causality (Abbott 1988; Mahoney 2000) and are interested in the same sorts of variables (Lieberson 1994; Mahoney 2000; Sewell 2005; Steinmetz 2004).
A closer look at recent methods papers suggests that the defining feature of post–Millian historical sociology is neither a different causal logic nor interest in different kinds of variables, but rather a superordinate concern with the constitutive properties of social phenomena. This is not to say that post–Millian historical sociologists do not make causal claims nor even emphasize causal claims as their main contribution. But the logic of historical case analysis commonly focuses centrally on the constitution of social phenomena. This focus is evident in two common types of contemporary historical argument: formation stories and negative case analysis.
Following Hirschman and Reed (2014), many contemporary historical sociologists produce formation stories, which provide narrative accounts of the emergence of a new social types—actors, organizational forms, concepts, and the like. For example, scholars explain how think tanks became separate from lobby firms and universities (Medvetz 2012), autism became a common diagnosis (Eyal 2013), nonprofits became a stable organizational form (Barman 2013), or impersonal political authority emerged from cliental relations (Padgett and Ansell 1993). Hirschman and Reed (2014) argue that formation stories are a useful corrective to “forcing-cause accounts,” which include variable based, experimental accounts, and historically invariant mechanistic explanations. Following Abbott (1988), such forcing-cause accounts presuppose that the world consists of fixed entities with historically and contextually independent causal powers, which—like machines—reliably turn X’s into Y’s. But, in fact, history shows that the causal powers of X’s change. For example, the effects of a nobility title are different in feudal and contemporary times (Gorski 2009:162). Hirschman and Reed (2014:259-60) therefore see formation stories as a necessary component of satisfactory causal accounts because they “provide the historical and empirical boundaries for the functioning of forcing-cause accounts” that explain how a phenomenon became “stable enough to force or be forced.”
Hirschman and Reed (2014:260) insist that formation stories are “fundamentally causal,” though perhaps this is because they worry that others have traditionally “written [them] off as merely descriptive rather than explanatory claims.” But, in fact, it is more correct to classify formation stories as incidentally causal since their capacity to inform new scholarship is often unrelated to their causal claims. That is, formation stories actually consist of two separate arguments. First, they are rooted in what might be termed an account of a formation, which is a constitutive argument about the nature of a newly emergent phenomenon. Second, these constitutive accounts are couched in an origin story about the formation or a causal narrative about how the new phenomenon emerged. Hirschman and Reed (2014:274) argue, rightly, that accounts of social formations are often analytically inseparable from their historical origin story because phenomena acquire characteristics and qualities due to the way that they are formed. But many examples show that the two types of claims can become decoupled in the course of disciplinary debate, and moreover that other social scientists are frequently more informed by accounts of social formations than by their origin stories.
Consider one influential formation story: Krippner’s account of financialization. In Capitalizing on Crisis, Krippner (2011) provides a causal argument about the origins of financialization, but my guess is that readers with no particular interest in late twentieth-century American political development will have forgotten it. 9 But in fact, Krippner popularized the financialization concept in an earlier article, which contains no causal argument (and remains more cited than her book). The article aims to determine “how to conceptualize most usefully long term structural changes in the US economy” (Krippner 2005:174). The argument is definitional or constitutive: Krippner argues that financialization is best understood as corporations’ growing dependence on profits derived via financial mechanisms and defends this claim by considering and rejecting alternate ways of defining financialization. For example, she rejects measuring the growing importance of finance via employment numbers because financial firms employ few workers but impact the behavior of nonfinancial firms. Indeed, it says much about sociologists’ tendency to overhype causality that Krippner (2005:174) sounds almost apologetic about her agenda-setting contribution: “the objectives of this paper are primarily descriptive and conceptual in nature—a full causal analysis is left to other writings.”
Accounts of formation like Krippner’s are useful for the reasons identified by Hirschman and Reed (2014): They describe the characteristics and properties of a newly emergent phenomenon. In simple terms, the claim is “X is a thing with the following properties.” This kind of claim improves others’ intuitions about the phenomenon, including but not exclusively others’ causal intuitions about appropriate casing, relevance criteria, and the range of plausible mechanistic accounts (Lichterman and Reed 2015). For instance, Krippner’s account suggests that financialization impacts inequality by changing workplace management in firms with financial investments—a causal argument substantiated by Lin and Tomaskovic-Devey (2013), who find that financialization may account for half of labor’s declining share of income since the 1970s. Absent the causal corollary, constitutive arguments can appear as poor causal arguments to those accustomed to thinking in terms of variable causality—as tautological “analysis of the dependent variable” (Becker 1992; Lieberson 1994). But this reaction stems from an inability to recognize constitutive arguments as distinct from causal ones. By the same token, the claim that a myocardial infraction result from blockages in coronary arteries is equally tautological, but it is certainly no less scientific than the claim that eating a high-fat diet increases the probability of a heart attack. Indeed, following Lichterman and Reed (2015), one cannot really interpret the latter claim scientifically absent the former.
Constitutive arguments are likewise central to analysis of exceptional or negative cases, another common research strategy in historical sociology. Scholars have traditionally identified deviant cases as useful for generating or extending theory (Burawoy 1998; Emigh 1997; Ermakoff 2014), and contemporary historical sociologists frequently identify negative case analysis as consonant with Kuhn (1962) and Lakatos (1970) theories of science. These theories hold that knowledge does not advance through falsification since all theories cannot account for some anomalies (Emigh 1997; Ermakoff 2014). In this light, Emigh (1997) argues that scientists’ approach to anomalous cases is key to progressive science: Scholars in a regressive regime simply ignore anomalies, whereas scholars in a progressive ones incorporate them into existing theory by creating subtheories, identifying previously unnoticed counterveiling mechanisms, and specifying scope conditions. Emigh (1997) therefore suggests that historical sociologists study negative cases, wherein an outcome predicted by theory should have occurred but did not. Although negative case analysis focuses attention on a surprisingly inactive causal mechanism, Emigh (1997:649) argues that the aim is primarily to “expand a theory’s range of explanation” by clarifying the conceptual model of a phenomenon.
For instance, Emigh (1997) illustrates negative case analysis via investigation of early modern Tuscany, which did not transition to capitalism despite having characteristics commonly associated with capitalist development—an efficient agricultural sector, declining feudal ties, a large urban economy, and a commercial manufacturing sector. Emigh (1997:669) finds that this was due to preunification Italy’s political geography. Cities were tied to their immediate countryside, which first stimulated development but later retarded it as markets had limited ties to other regions. Thus formulated, the account sounds as though it is motivated by a deterministic logic akin to Mill’s method of difference, but Emigh argues otherwise. As others have argued, mechanisms are contextually and historically embedded (Hirschman and Reed 2014), and many incidental events or typically inconsequential mechanisms could prevent transition to capitalism, even if all theoretically consequential factors are present (Gorski 2009; Steinmetz 1998). For instance, one can easily imagine a state that has its transition to capitalism arrested by a plague or conquest. Rather, Emigh’s account extends the range of theory by altering understanding of what capitalist transition consists of both in the case of Tuscany and in previously examined historical cases. The analysis shows that political arrangements that allow for geographically extensive markets are a component of capitalist development, even in larger European states, wherein this went unnoticed by virtue of many states having similar political geographies in common. Here again, the constitutive argument facilitates causal analysis but is separate from it.
Empirical versus Theoretical Generalization in Ethnographic Research: An Untenable Distinction
Historical sociologists’ approaches to formulating constitutive arguments can disambiguate debates among ethnographers for how to select cases and utilize them to make claims. Generally, the issue of casing is not as central to debates about ethnographic methods, and there is hardly consensus among ethnographers about appropriate strategies of case selection. Nevertheless, one can identify two general approaches. Ethnographers discuss case selection, first, in the context of establishing external validity. Small (2009) offers one widely applied set of guidelines, which is standard reading in graduate courses and offers advice that is consistent with the guidelines of funding entities like the National Science Foundation (NSF) (Lamont and White 2009). But other ethnographers select and mobilize cases to “build theory,” an ill-defined enterprise that ethnographers nevertheless widely take to be different from efforts to establish external validity.
In what follows, I argue that the distinction between empirically and theoretically oriented ethnography does reflect a different approach to case selection, but not for the reasons commonly provided in the literature. That is, ethnographic methods articles portray ethnographers in the two camps as interested in making different kinds of claims—most commonly, (externally valid) empirical generalizations versus theoretical generalizations of questionable or unclear external validity (Small 2009; Spillman 2014). Below, I first show that the distinction between empirical and theoretical generalization is logically and practically untenable. Then, via engagement with exemplars, I illustrate that empirically and theoretically oriented ethnographers routinely make similar types of context-independent constitutive claims, but according to different conventions for what makes such claims provisionally externally valid.
The distinction between empirical and theoretical generalization was popularized by Small’s (2009) influential article, which is centrally concerned with how to make ethnographic findings legible to survey researchers. Small (2009:10) presents the problem as one of external validity: Scholars in many subfields look to ethnographers to produce “case studies that somehow…‘speak’ to empirical conditions in other cases (not observed).” But case selection strategies like random sampling, selection of “average” cases, and others that bear superficial resemblance to survey methodology fail. Just as one cannot draw valid inferences about a population by interviewing one person—even an entirely average person chosen at random—no selection criteria for field sites will get ethnographers any closer to statistical generalizability.
Given the nonexistence of “representative cases,” Small argues that ethnographers should instead select cases deliberately to maximize their ability to make two types of inductive arguments: Existence proofs and logical hypotheses that are compelling by virtue of direct observation of a causal mechanism. 10 I will argue that Small’s formulation nicely spells out how some ethnographers make external validity claims—particularly those working in subfields populated by survey methodologists. But Small also falls short of universal rules for ethnographic casing, because many ethnographers are interested in theory building instead, which does not fit easily into the existence proof or compelling hypothesis categories. Timmerman and Tavory (2012:168), for instance, identify the core aim of their method as “construction of theoretical ideas on the basis of data…creative attempts to generalize mechanisms, particular cases, or links between causal statements.”
Small allows that ethnographies can produce theory but argues that this is distinct from empirical generalizations—a distinction borne partially of his critical engagement with Burawoy (1998), which Small illustrates via a reexamination of Geertz’s (1973) account of the Balinese cockfight. Small’s (2009:9) key claim is that Geertz was unconcerned with the empirical features of cockfights outside of his field site: Geertz expected his theory of games to “be applicable to other sites, [but not] the empirical findings to be so applicable—that is, for cockfights to look similar or to follow the same rules in other villages throughout or outside of Indonesia.” 11 For Small (2009:9), building theory is fine, but it is distinct from “some logical justification, some basis for feeling confident” that one has attained “empirical knowledge about how other cases work.” Many sociologists ultimately want ethnographers to produce the latter sort of knowledge. For instance, Small (2009:9) argues that ethnographers should study “one St. Louis neighborhood” that speaks to “conditions in black neighborhoods in general—in Boston, Los Angeles, New York, and perhaps even London and Rio de Janeiro.”
There are two problems with Small’s formulation. First, Small sets an impossibly high standard for social science—not just ethnography, but survey methods too. No social scientific method provides insight into empirical reality in general if by this we mean something that allows one to make deterministic statements about unobserved cases. Presumably, the formulation unwittingly conflates reality “in general” with a representative sample. But representative samples—or, for that matter, knowledge about averages within an entire population—only allow one to make probabilistic statements about unobserved cases, not acquire “empirical knowledge” about them. The only way to know what Rio de Janeiro is really like is to go to Rio.
And, second, if external validity means simply “some logical justification [or] basis for feeling confident” about probabilistic empirical statements, then Geertz’s theory of games certainly does that. For one, Geertz (1973) states his aim as developing “a less purely economic idea of what ‘depth’ in gaming amounts to” (p. 432)—that is, to develop a theory of “deep gaming” or deep games in general. Geertz also develops the theory by engaging with Bentham’s account of deep play, which was presumably formulated based on observations in Britain, and this engagement concerns empirically observable features of games and is therefore not “purely theoretical.” Geertz’s analysis even facilitates prediction. For example, deep play often involves betting, but there are reasons to think that betting in deep games—wherever they occur—is not about the money but about public participation in a form of collective storytelling (Geetrz 1973:432-36). In sum, Geertz’s “theory building” is just a vague label for an essentially constitutive argument: An analytical description of deep games, which identifies their key features and how they fit together. All this given one a logical justification for believing that certain empirical features of deep games probably cluster together in other unobserved cases.
Small’s (2009) position on Geertz is commonly interpreted ecumenically to imply a division of labor between ethnographers who make “empirical generalizations” and those who make “theoretical generalizations.” Spillman (2014), for example, revisits the Balinese cockfight example and argues that some ethnographers are interested in gaining empirical knowledge about other cockfights, just as a survey methodologist would, whereas theoretically inclined ethnographers are interested in general insights that apply to other situations of gaming, but not necessarily other cockfights. That distinction also suffers under closer scrutiny. First, one can easily imagine a survey that samples cockfights as cases drawn from different kinds of populations—of deep games, holiday rituals, or masculine displays—and speaks to empirical regularities in the latter rather than cockfights as such (conversely, nothing prevents one from developing a theory that applies only to cockfights). Second, and more to the point, both the survey method and Geertz’s approach employ theoretical constructs to explain empirical regularities—if by theoretical construct we mean an abstract entity that may be unobservable (Steinmetz 2004). Survey methodologists explain regularities by treating cases as members of a population in the statistical sense, an abstraction that cannot be empirically observed. Theoretically inclined ethnographers explain regularities via recourse to constitutive properties and mechanisms, which can similarly defy empirical observation and are sometimes only inferable from empirical patterns (Gorski 2009; Steinmetz 2004). Both explain empirical reality with theory, albeit in different ways. 12
As final illustration of this point, consider a scenario in which a survey methodologist and historical sociologist are invited to make a prediction: about whether Donald Trump is a harbinger of authoritarianism in the United States. The survey methodologist might collect a data set of stable and failed democracies, however defined, code their characteristics into variables, and run a regression. The historical sociologist might construct a theory of democratic failure by analyzing a few cases to identify the typical path that nations follow as they acquire the characteristics of authoritarianism, then assess the degree to which the United States has or likely will take each step. It should be evident that both arguments are about external validity, but neither guarantees empirical certainty about an unobserved and uncertain future. One can argue that one approach is preferable to the other in various ways—for instance, in the precision of uncertainty about predictions. But the approaches are, at base, similar. Both rely on different theoretical conventions for explaining and anticipating the same empirical regularities. By the same token, empirically and theoretically oriented ethnographers make similar types of external validity claims, but according to different conventions.
How to Think About Ethnographic Case Selection Like a Historical Sociologist
In this section, I argue that the primary difference between empirically and theoretically oriented ethnographies revolves around different conventions for making constitutive claims that others treat as provisionally externally valid. The claim that ethnographies produce analytically useful constitutive arguments is not new; many identify arguments like Geertz’s as central to ethnography. Becker (2008:10), for example, argues that ethnographers contribute to knowledge by supplying underlying images of the world, which impact “selection and formulation of problems, the determination of what data are, the means to be used in getting the data, and the forms in which propositions are cast.” Vaughan (2004) argues that historical ethnography facilitates “analogical theorizing…a method that compares similar events or activities across different social settings and leads to more refined and generalizable theoretical expectations.” Such aims are also implicit in pragmatic methods (Gross 2009) and those that emphasize abduction, wherein the goal is analysis that “abstracts…the phenomenon…turning it into a generalization than can be linked to other fields” (Timmermans and Tavory 2012:177).
But prescriptions on how to select cases that facilitate such analogical reasoning are thin, and many unhelpfully recommend looking for theoretically generative cases (Burawoy 1998) or focus on the subjective experience of surprise (Tavory and Timmermans 2012). There are practical reasons why ethnographic methods papers are equivocal on case selection: Ethnographers’ context of discovery and justification are intertwined and one is often unsure what the field site is a “case of” until late in the process (Ragin 1992). Therefore, an element of surprise probably is common to cases of successful fieldwork. Vaughan (2004), for example, reports staring research on the challenger disaster and expecting another case of organizational misconduct, being surprised by the absence of rule violations, and only then developing a new theory of production cultures. But my guess is that cases of very late casing like Vaughan’s are relatively rare. Like historical sociologists, most ethnographers begin by conducting preliminary research in several sites, reflect on what sort of cases they might have on their hands, and then invest their energies and adjust their research practices accordingly (see, e.g., Mayrl 2018). A clearer account of what makes cases theoretically generative can facilitate this winnowing process by helping one to identify which of numerous potential cases are likely to prove informative for others. To this end, analogies to comparative-historical sociology are useful.
Following Hirschman and Reed (2014), constitutive arguments are accounts of formation, which concern both the building blocks of the social and how best to categorize them. As such, constitutive arguments take one of the two general forms. The simpler form is an existence proof, which simply asserts that “X exists.” More complex constitutive arguments concern the correct casing or categorization of social phenomena or relationships between their properties—commonly, arguments take the form “X is really a case of Y” or “A, B, and C are key features of X” (or incidental to X). But a constitutive argument about one case is typically not enough. Successful ethnographies require some warrant for convincing the audience that the constitutive properties of observed cases somehow inform accounts of other unobserved cases, and the conventional distinction between empirically and theoretically oriented ethnography is rooted in different conventions for making such provisional validity claims. In the two sections that follow, I illustrate differences in how empirically and theoretically oriented ethnographers make such claims via engagement with recent ethnographies that exemplify the strategy.
The Existence Proof
Many scholars argue that the simplest ethnographic finding is often the most theoretically generative: that a phenomenon exists. Following Small (2009), arguing that a phenomenon exists is also the only empirical claim that one can make with absolute certainty based on analysis of a single case. But in practice, existence proofs require more than simple observation of a phenomenon because social scientists chose to focus on only a small subset of all phenomena (Abbott 2014). To convince the audience that the phenomenon “matters,” ethnographers must provide some warrant for thinking that it is consequential in other cases. In sum, a successful existence proof is simultaneously an importance proof. Successful ethnographies establish this warrant in one of two ways: following Small (2009), some do so inductively, whereas theoretically oriented ethnographies do so abductively.
One exemplar of the inductive strategy is Harris, Evans, and Beckett’s (2010) account of legal monetary sanctions. The authors engage primarily with criminologists in an effort to convince them that legal fees and fines are an important component of the criminal justice system. They do so via an analysis of such sanctions in Washington state, and the central claim is, effectively, “legal monetary sanctions are a thing that you should pay attention to.” The article is noteworthy for its’ relative lack of theory building in the conventional sense. For instance, the authors treat what monetary sanctions are a “case of” as self-evident (Ragin 1992) and present their argument as consistent with existing disciplinary narratives: Research shows that people who are convicted of crimes are…highly disadvantaged [and] criminal justice involvement…is both consequence and cause of poverty. [Because] the prevalence and consequences of monetary sanctions have not been systematically explored, the extent to which penal expansion contributes to inequality, and the full array of mechanisms by which it does so, has not been fully recognized. (Harris et al. 2010:1756)
In contrast to this inductive strategy, other ethnographers rely on what might be termed resolutive cases, which resolve a contradiction or tension within the literature. A similar strategy is common in historical formation stories, wherein the usually result is reformulation of taken for granted historical categories. For example, Prasad’s (2012) The Land of Too Much begins by highlighting a contradiction within welfare state scholarship. Most scholars identify the American welfare state as extremely liberal in its deference to the market (Esping-Anderson 1991), but the American state was once also surprisingly interventionist. Until the 1970s, American income taxes were the most progressive in the world and federal agencies were unusually aggressive in policing monopolies. Prasad resolves this contradiction by showing that architects of the American state were uniquely focused on stimulating consumer demand to combat the Great Depression’s deflationary spiral. This leads Prasad to a new theoretical distinction. European governments, which fixated on catching up to a wildly productive United States, developed “supply-side” states that won over workers with government benefits in exchange for policies that dampened consumption (e.g., wage controls, consumption taxes). American policy makers developed a “demand side” state focused on substituting consumption and privatized welfare for state programs (i.e., traditionally via cheap credit, progressive income taxes, policies that encourage home ownership, and by regulating and breaking up monopolies). The argument works because the American welfare state is something scholars care about on its own terms, but note that Prasad (2012) also resolves a theoretical contradiction and thereby provides insight into unobserved cases. By observing European welfare states alone, as Esping-Anderson (1991) did, one might conclude that they fall into liberal, conservative, and social democratic categories. But Prasad shows that they are also all supply-side welfare states.
One ethnographic example of a similarly resolutive case is Desmond’s (2012) analysis of “disposable ties” in Milwaukee—or, strictly speaking, among residents of a trailer park and black neighborhood therein. Desmond’s argument is superficially similar to Harris et al.’s (2010): “Disposable ties exist and matter for accounts of urban poverty.” But unlike Harris et al. (2010), Desmond spends little time on inductive arguments. For example, he makes no effort to contextualize the size or scope of wealth transfers via disposable ties, document how disposable ties impact poverty, and so on. Instead, the article goes straight to theory, shows that it is already muddled, and argues that the existence of disposable ties un-muddles it. Desmond’s primary point of engagement is Stack’s (1975) All Our Kin, which argues that minority populations, although impoverished, rely on extensive kin networks for economic and social support. Desmond then marshals findings from other studies, survey measures, and logical extrapolation to convince the reader that Stack’s narrative no longer fits the facts. The General Social Survey (GSS) shows that African Americans do not have more extensive social networks than whites and—even if they did—welfare state retrenchment makes the needs of impoverished blacks larger than what kin networks could plausibly handle. The warrant, then, is a logical contradiction in the literature: If conditions have become decidedly worse for the urban poor since midcentury, how do they endure conditions of severe economic deprivation if doing so single-handedly is virtually impossible and if their kin are no longer a sufficient source of support? (Desmond 2012:1299)
Complex Constitutive Arguments: Casing and Categorization
Ethnographers also use competing conventions to facilitate complex constitutive arguments. Here again, one strategy is inductive and mirrors Small’s (2009) advice for formulating plausible hypotheses. The other is more common among theoretically oriented ethnographers and mirrors negative case analysis in historical sociology.
Following Small (2009), case studies are useful for direct observation of causal mechanisms, which can give readers a plausible or logically compelling reason for thinking that causal relationships operate similarly in other cases. 14 To this end, Small (2009:18) recommends looking to what might be described as “pointy” cases that are extreme in ways that point to causal mechanisms. For instance, he suggests studying marriage among the poor via analysis of an impoverished city, wherein the mayor gives rent subsidies to unwed mothers who marry before birth of their second child. Note that the logic is similar to that of instrumental variables in quantitative analysis. Presumably, marriage rates in impoverished cities are correlated with many factors that impact life outcomes (e.g., employment status, criminal justice involvement, and household wealth). But in Small’s imaginary city, the mayor’s program creates single mothers who marry just for the incentive, a scenario that allows one to formulate an extremely plausible hypothesis about how marriage status alone impacts other life outcomes (or not). The extent to which this procedure truly concerns causal or constitutive relationships is debatable—Small (2009) argues that it concerns the former. But in fact, plausible hypotheses also inform scholars’ implicit understanding of the “contrast space” for a causal argument, or the universe of relevant variables, which may or may not bear out in variable analyses (Lichterman and Reed 2015). It is plausible, for example, for marriage to impact poverty in Small’s imaginary case but to be so interrelated with other variables in other cases as to produce no independent causal effect. But even then, Small’s hypothetical findings are noteworthy because they inform others’ understanding of marriage as a phenomenon and its causal powers (whether realized or not).
One actual example of the plausible hypothesis approach is Vargas’s (2016) Wounded City, which focuses on the relationship between political efficacy and neighborhood violence in Chicago’s Little Village. In some respects, Wounded City is more than an effort to formulate a plausible hypothesis. For example, Vargas combines aspects of neighborhood ecology and political economy into a new theory of political fields. Nevertheless, the work is centrally motivated by a desire to convince criminologists to include political variables in future analyses. 15 To this end, Vargas mobilizes the peculiarities of Little Village, which consists of two gerrymandered areas with different relationships to Chicago’s political structure. The west side is in a single alderman’s district, who views it as an important constituency. It witnessed a decline of violent crime, much like other American neighborhoods in recent decades. The east side is gerrymandered into three aldermanic districts, none of which are important to their alderman. It witnessed an anomalous rise of violent hot spots. The case is “pointy,” because the Little Village’s two halves are similar in all the ways that matter, except for their gerrymandering. This contrast allows Vargas to pinpoint and enumerate how political efficacy matters by allowing residents to get violence prevention, job, and surveillance programs via relations with ward officials and nonprofits. Here again, the analysis does not prove that political efficacy matters in other neighborhoods but shows how it is a central constituent of crime prevention strategies in Little Village, thereby giving the reader a logical reason to expect a causal effect elsewhere.
By contrast, other ethnographers formulate complex constitutive arguments via strategies that mirror negative case analysis in historical sociology. Following Emigh (1997), negative case analysis is useful when (a) the gap between empirical reality and a theoretically expected outcome is large and (b) examination of the case leads to a theoretical reformulation of the phenomenon. Ethnographers make such arguments in two ways, which might be further subdivided as negative outcome and negative cause analysis. In negative outcome analysis, a cause is present but its theoretically expected outcome is absent. In negative cause analysis, a common outcome is present but the cause usually associated with the outcome is absent.
One example of negative outcome analysis is Brown’s (2011) study of immigrant Liberians’ relationship with the American state. Brown engages with theories of immigrant incorporation, which identify labor market participation as key to political incorporation: The documented and undocumented alike equate good citizenship with individual work and responsibility, which leads undocumented immigrants to question their own political legitimacy (Menjívar 2006). One would therefore expect the Liberians in Brown’s study to question their own political legitimacy, because most are displaced, illiterate refugees from the countryside, who are unemployed and likely unemployable (e.g., grandparents raising grandchildren). But Brown finds a negative outcome: Liberians feel entitled to a nurturing and personal relationship with the state. Brown shows that Liberians’ disposition is due to their particular relationship with United States, which they see as complicit in Liberia’s civil war. Because many lost family in the war, they feel entitled to replacement personal-like ties with the state, a disposition reinforced by frequent and positive interaction with resettlement services.
As prescribed by Emigh (1997), Brown’s analysis both explains the anomalous case and offers general insight into the constitutive properties of immigrant incorporation. Brown (2011:161) argues that the immigrant incorporation is not purely about labor markets and the documented–undocumented distinction, as prior studies have assumed, but can also occur through political channels. This conclusion gives one a reason to expect refugee’s political positionality vis-à-vis the United States to matter causally for experiences of immigration. It also expands understanding of what political incorporation is about, which points to counterfactuals that are informative even if not currently reflected in actually existing causal relationships. For instance, Liberians’ relationship with the American state appears relatively unique, but one imagines that if other immigrants expected personalized ties to the state, their experience of incorporation would be comparable to those of Liberians. In sum, the analysis changes one’s underlying image of what immigrant incorporation is in practice, which leads one to expect empirical regularities in other cases, including actual and hypothetical causal relations.
One example of negative cause analysis is Pacewicz’s (2015) study of partisan politics in a Rust Belt city. Pacewicz engages with accounts of grassroots party politics, which identify community leaders and other local elites’ exit from local party-building efforts as a key turning point in American politics (McAdam and Kloos 2014; Skocpol 2003). Scholars argue that community elites’ exit allowed ideologically motivated activists to take over local branches of the two parties and—via control over primaries and other aspects of grassroots politicking—shift party priorities toward the extreme and reactionary, especially on the Republican side. Skocpol (2003) argues that this shift in grassroots politics occurred due to changes in the field of national political advocacy, which cut institutional ties between Washington, DC, and grassroots community institutions, leaving community elites and other locals parochial in outlook. Pacewicz (2015) finds that the outcome predicted by this theory is present, but the cause absent. Since the 1970s, community elites in the city he studied did withdraw from Democratic and especially Republican politics, leaving party affairs in the hands of ideologically polarized activists. But the theoretically expected cause was missing: Community leaders were not more parochial in outlook. Pacewicz’s utilization of the case is partially resolutive in that he shows that community elite’s orientation is more consistent with scholarship on urban governance. Contrary to accounts of grassroots party politics, American urban elites have generally become more outward looking and entrepreneurial since the 1970s (Harvey 1989; Molotch 1976). Thus, the puzzle is why community elites—who became generally more interested and engaged in the world outside of city limits—withdrew from party politics in particular.
Pacewicz (2015) resolves this puzzle by showing how changes in urban governance led community leaders to avoid party politics. In the late 1970s and 1980s, financial deregulation sets off the twentieth century’s largest corporate merger wave, during which corporations headquartered elsewhere acquired most of the Rust Belt’s previously locally owned industries. Local elites became increasingly focused on economic development efforts centered on wooing outside employers, which they organize around broad-based partnerships that flexibly market the city to outsiders. In this context, engagement in party politics polarizes community initiatives, practically complicating both collective efforts to market the city and individual leaders’ ability to rise within the local pecking order. In this respect, Pacewicz’s (2015) argument is constitutive: He argues that party polarization at the grassroots is not just a case of rising extremism within political party networks, but rather a “disembedding of party politics from community governance,” which allows for and encourages polarization among party activists. As such, the argument gives one a logical reason to expect both constitutive and causal regularities in other unobserved cases. One expects that in cities with similar economic histories, grassroots political parties now operate relatively independently of local elite networks—a significant shift from when the Democratic Party and Grand Old Party (GOP) were effectively an organizational extension of, respectively, the local labor movement and chamber of commerce. One also expects that in communities wherein local elites are more fixated on economic development, they are extra avoidant of party politics—a scenario that promotes extremism among party activists who are maximally disembedded from moderating community institutions.
Discussion and Conclusions: Learning to Ask “What” Before “Why”
What can one conclude about the world based on ethnographic study of a single case? I have argued that ethnographic methods papers often answer this question in ways that are disconnected from how social scientists actually interpret and utilize ethnographic research.
At one extreme, a genre of methods papers, often written by those who do not themselves conduct case studies, offer blueprints for ethnographic “airplanes that will never fly” (Small 2009:28): Studies that copy the form but not function of survey methods research (e.g., Elman et al. 2016; King et al. 1994). Although of questionable practical utility for ethnographers, such articles do focus attention on ethnographers’ capacity for making claims that speak to empirical reality outside their cases. Ethnographers themselves are partly to blame for mudding the water on this issue, especially by positing a distinction between empirically and theoretically oriented research (e.g., Small 2009; Spillman 2014). This distinction is perhaps functional in protecting a sanctum of theoretical ethnography from the usual disciplinary critiques, but it is logically and practically untenable. I have argued that disambiguating how ethnographers make external validity claims requires attention to noncausal arguments. But contemporary social scientists fixate on causal inference and tend to “leave aside…[research] whose primary goal is mainly descriptive” when evaluating case studies (Elman et al. 2016). And many ethnographers have engaged such debates by pointing out, rightly, that ethnography can improve causal inference. Therefore, the overall impression left by contemporary methods statements is one of ambivalence about the capacity of ethnographers to inform others’ understanding of the empirical world and the strong presumption that truly scientific ethnography is about causal argument rather than description.
Meanwhile, outside the world of methods debates, the role that ethnographers play in knowledge production appears different. Ethnographic arguments carry and routinely inform others’ understanding of the larger world. The arguments that do are neither causal arguments nor context-dependent “pure description.” Rather, they fall into a third category that I identified as constitutive arguments: Context-independent claims about the makeup and correct categorization of social phenomena, which inform others’ understanding of empirical reality in unobserved cases. Constitutive arguments commonly take the forms, “X exists,” “X is a case of Y,” or “X has the properties A and B.” Contrary to the conventional division between empirical and theoretical ethnography, constitutive arguments usually combine empirical claims about unobserved cases with novel theoretical insights: Poor urbanites’ survival strategies consist of forming and breaking disposable ties (Desmond 2012), local GOP chapters have become disembedded from networks of corporate and urban governance (Pacewicz 2015), positive interactions with the state are a form of immigrant incorporation (Brown 2011).
My aim in this article has been to determine how ethnographers actually formulate constitutive claims that other social scientists accept as provisionally externally valid. Knowing this will not generally allow one to select a case a priori because ethnographers trade on insight into the internal conditions of cases and there is often no way to know about such conditions without preliminary investigation. But greater clarity about the conventions that scholars use to make claims can help one better identify generative cases within the messy and open-ended stage of initial fieldwork—to see which among many possible cases is usefully “surprising” (Tavory and Timmermans 2012) or otherwise informative for others.
I identified two such conventions, which revolve around different warrant for establishing that a phenomenon is relevant to other unobserved cases. Those ethnographies conventionally understood as empirically oriented follow the advice of Small (2009) and establish this warrant inductively. Ethnographers in this tradition examine “pointy” cases, wherein the phenomenon of interest is unusually large, bifurcated, or causally related to other issues of disciplinary interest. Theoretically oriented ethnographers make claims of external validity similarly to historical sociologists who examine single cases (Emigh 1997; Hirschman and Reed 2014). They proceed abductively and use existing theory to suggest that observed phenomena are of wider significance. They commonly look to resolutive cases—wherein analysis resolves what is otherwise a contradiction in the literature—or negative cases, wherein prior theory leads one expect empirical regularities different from those that actually occur.
In sum, ethnographers confronted with the messy reality of early fieldwork are best served by asking how they can make a convincing argument about the makeup of the social world. And to this end, they can proceed most productively by plucking two types of cases from the many possibilities before them. They may proceed by looking for phenomena that are unusually large, bifurcated, or related to other phenomena of interest. Or they may proceed like historical sociologists by looking for cases that appear to resolve a preexisting debate with the literature or ones wherein a common causal sequence fails to manifest—either because a cause is present but result absent or because a cause is absent but result present.
By focusing on such cases, ethnographers increase the likelihood that they will be able to formulate novel constitutive arguments, a task to which ethnography is uniquely suited. Because conventions for making such arguments are fundamentally different from how survey methodologists make generalizability claims, some argue that social scientists are wrong to interpret ethnographers’ constitutive claims as provisionally externally valid (see, e.g., Small 2007). But because “representative” cases are a logical impossibility, one is hard pressed to identify an alternative. Social scientists think about data by implicitly utilizing complex images of the world (Becker 2008), and if these images do not come from ethnography, scholars will just take them from the popular media, fiction, or the stock of common stereotype. And it is especially important for social scientists to update their conceptual models because objects of social inquiry are notably changeable vis-à-vis phenomena in the natural sciences (Hirschman and Reed 2014). To return to Molly’s predicament, consider that the causes of heart attacks have probably changed plenty since 1700, but their physiological basis in blocked coronary arteries has not. The same cannot be said of what social scientists mean by terms like upward mobility, romantic relationships, and social movements. There is constant need for ethnographers and other qualitative scholars to remind us what it is that we are actually talking about.
Footnotes
Acknowledgments
This argument benefited from several rounds of feedback during meetings of the working group on post-positivist comparison, which included Nicholas Hoover Wilson, Damon Mayrl, Laura Ford, Phil Gorski, Stefan Bargheer, Xiaohong Xu, Dani Lainer-Vos, Simeon Newman, and Carly Knight. I am also grateful to Andrew Schrank, Dan Menchik, Lyn Spillman, Dan Hirschman, and Paki Reid-Brossard for feedback.
Declaration of Conflicting Interests
The author(s) declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.
Funding
The author(s) received no financial support for the research, authorship, and/or publication of this article.