Why Causal Mechanisms and Process Tracing Should Alter Case Selection Guidance

Case Studies and Causal Inference

The mainstream approach to case study research conceives of case studies as tools of causal inference. Social scientists make inferences by taking a theoretical premise and using data to scrutinize it (Waldner 2007:150). King, Keohane, and Verba (1994:46) define inference as “the process of using facts we know to learn about facts we do not know” and that “the best scientific way to organize facts is as observable implications of some theory or hypothesis.” Gerring (2012:423) characterizes inference as “the process of reaching conclusions as an extension of known facts or stated premises.” Seawright and Collier (2004:291) define it as “the process of using data to draw broader conclusions about concepts and hypotheses that are the focus of research.” Inference is a means to connect theory with data and bolster confidence that a theorized relationship holds generally (Kratochwil 2007:32).

The notion of inference has a particular philosophical genealogy. It is rooted in two major approaches to social science: the hypothetico-deductive (H-D) method and Carl Hempel’s logical empiricism. In the H-D method, one states a hypothesis and then sees if an empirical observation coheres with it. If it does, the hypothesis has been inductively confirmed (though this confirmation is tentative and subject to future scrutiny). Alternatively, Hempel’s logical empiricism is epitomized by the deductive nomological (DN) model. The DN model substitutes a covering law for the H-D method’s inductive premise. In the DN model, the covering law is presumed to be true. When one finds observational data consistent with the general law’s predictions, one confirms the prediction. Although these approaches vary in their emphasis on induction versus deduction, they are more similar than different. They both analyze the relationship between a theoretical premise (the explanans) and the thing to be explained (the explanandum; Waldner 2007:150-52; see also Rosenberg 2000; Salmon 1990:7, 46-50). Ultimately, an empirical regularity between an explanans and the explananda serves as the grounds upon which to confirm a predictive explanation (Jackson 2011:63-71, 2017). ¹

In contemporary social science, these philosophical underpinnings manifest themselves in the pursuit of “causal inference” and the estimation of causal effects. King et al. (1994:81-82) state that a “causal effect is the difference between the systematic component of observations made when the explanatory variable takes one value and the systematic component of comparable observations when the explanatory variable takes on another value.” Gerring (2012:219-24) likens causal effects to experimental treatment effects; they are what happens to an outcome variable Y when a causal factor X changes, ceteris paribus. The inferences that one makes as a result of these X:Y relationships reflect what Abbott (2001) calls general linear reality: the idea that causality in the social world conforms to the rules of linear transformations. This worldview is epitomized by statistical studies and also reflected in lots of case study research inspired by Lijphart’s (1971) comparative method. The approach is neopositivist, and its accompanying notion of causality is covariational. For now, the key point is that the cornerstone of causal inference in social science is that one generates knowledge about causal effects by examining empirical regularities (e.g., Freedman 1997; Jackson 2017).

In States and Social Revolutions, Skocpol expresses an affinity for what scholars today call causal inference. She writes that “Any valid explanation of revolution depends upon…[finding] important regularities across given historical instances” (p. 18). She likens her comparative historical analysis to “the mode of multivariate analysis to which one resorts when there are too many variables and not enough cases” (p. 36). Skocpol later reflected:

I remember being very taken by the analogy Lijphart drew between the statistical and the comparative methods. Without making controlled comparisons, I did not think I could establish whether a hypothesis could actually explain why an outcome did and did not happen. I picked up this idea in my basic statistical methods class. (quoted in Munck and Snyder 2007:663)

Principles for Case Selection

The pursuit of causal inference permeates mainstream advice on case selection. For example, Elman, Gerring, and Mahoney (2016:377) conceive of “case studies as tools of causal inference…[in contrast to] case studies whose goal is primarily descriptive or where there is no explicit and sustained causal argument.” Researchers are advised to select cases that control for confounding variables and thereby offer inferential leverage in the estimation of causal effects. The gold standard in this regard is Mill’s method of difference (aka most similar systems design), which pairs cases that are similar in many ways but differ on an explanatory variable. This design essentially employs an experimental logic to isolate the key difference among multiple cases (Gerring 2007:131-39; Lijphart 1971; Przeworski and Tenue 1970:31-34). Such controlled comparisons are both “ubiquitous” in and “indispensable” to comparative social research (Slater and Ziblatt 2013; see also Møller 2016). Landmark studies in this mold include Mahoney’s (2001:41-43) analysis of Central American regime dynamics, Smith’s (2007:55-60) seminal work on the resource curse, and Lieberman’s (2009:110-11) research on AIDS policy in Brazil and South Africa. One inflection of this case selection strategy uses statistical matching techniques (Nielsen 2016).

Most other strategies of case selection report their virtues in terms of how well they assist causal inference. They do so by describing how the cases chosen fit into a broader population of interest and are therefore representative of it. Among the strategies featured in Gerring’s (2007:86-105, 115-50) authoritative book, this reasoning applies to the typical, diverse, extreme, crucial, pathway, most similar, and most different techniques. ² In appealing to representativeness, practitioners seek to neutralize worries over selection bias, a perennial critique levied by skeptics of case study research (Geddes 1990). Representativeness is considered vital to achieving causal inference because a case study is ultimately a test of a general hypothesized relationship among a population of interest ³ ; it is therefore imperative to evaluate what one expects to be a representative instantiation of that relationship. ⁴ Case study researchers are also encouraged to “increase the N” because it expands the scope of the empirical test and bolsters confidence in the hypothesized relationship (Geddes 1990:132-41; King et al. 1994:213-17).

An alternative yet complementary perspective on case selection comes from qualitative comparative analysis (QCA). Ragin (2000:53-63, 120-45) defines populations of cases by identifying the factors associated with one’s outcome of interest. If an outcome seems to be influenced by three (dichotomous) variables, then one confronts eight potential subgroups within the universe of cases (because 2³ = 8). These eight hypothetical combinations of variables comprise a “truth table,” which sorts cases based on different covariational patterns. Case studies can then survey those patterns. For example, imagine that you conducted a case study of one case from a subgroup of six cases. The subgroup is defined by the conjunctural combination of three variables (in this example). Those six cases are united by an empirical regularity between an explanans and the explanandum. Any insights that you glean from your single case study are understood to apply to the five other cases, given their shared covariation (Schneider and Rohlfing 2016:554-57). Hence, a case study is necessarily representative of its subgroup. Overall, the understanding of case studies advanced in QCA is consonant with the worldview of causal inference.

In important ways, Skocpol’s (1979:35-42) case selection strategy suggests a pursuit of causal inference. First and foremost, she uses Mill’s method of agreement as justification for her unconventional comparison of France, Russia, and China and invokes the method of difference when examining her negative cases of England, Germany, Japan, Prussia, and Russia in 1905 (see also Mahoney 1999:1156-64). To execute her comparative historical analysis, Skocpol says that “Basically one tries to establish valid associations of potential causes with the given phenomenon one is trying to explain” and notes that her “overriding intent is to develop, test, and refine causal, explanatory hypotheses” (p. 36, my italics). Her affinities with what scholars today call causal inference are plain. ⁵

Attitudes About Cases

The pursuit of causal inference and the desire for representativeness dovetail with two attitudes in the conventional wisdom on case selection. The first standpoint is unit (or causal) homogeneity: The idea that when an explanatory variable takes on the same value, it will produce the same effect, at least within a defined population of cases (Seawright and Collier 2004:276). Unit homogeneity is what renders cases analytically equivalent for comparison (Falleti and Lynch 2009:1145). King et al. (1994:93) say it is “the assumption underlying the method of comparative case studies.” ⁶ Crucially, the “assumption” of unit homogeneity requires an X:Y empirical regularity (see King et al. 1994:91-93). This requisite indicates the evaluative purpose of case studies. Gerring (2007:138-39, 141) argues that cases selected via Mill’s methods can corroborate a known empirical regularity; but without an established association, case studies are merely exploratory (see also Beach and Pedersen 2013:89; Weller and Barnes 2016:432-33). Consequently, case studies are considered subordinate to their related empirical regularity.

The second viewpoint is that cases are conditionally independent, meaning that “the assignment of cases to the treatment and control groups is…unrelated to other characteristics…that may influence the dependent variable” (Seawright and Collier 2004:280). But if there is some variable, Z, that affects the segregation of cases into “control” and “treatment” groups, researchers can still undertake case study analysis so long as they identify Z’s influence and thereby “control” for it (Collier, Seawright, and Munck 2004:33; King et al. 1994:94-95). The notion of conditional independence is a key reason why researchers worry so much about representativeness and selection bias when choosing cases (Gerring 2007:91-97, 216).

By contrast, QCA does not worry about unit homogeneity or conditional independence per se, due to the understanding of what truth tables accomplish. Truth tables sort cases according to configurations of relevant causal conditions. These conjunctural combinations mean that subgroups are deemed causally homogenous by definition (Ragin 2000:51-61; see also Munck 2004:110; Paine 2016). ⁷ And because truth tables are understood to include all pertinent causal conditions, they do not suffer from omitted variable bias or other problems that could undermine conditional independence and corrupt causal inference (Ragin 2000:72n6, 289-90). ⁸ The spirit of QCA shares much in common with standard case study prescription, which obliges researchers to neutralize potential confounding variables when selecting cases. In QCA, deciding which cases to plumb comes after configurational sorting—a process that voids concerns surrounding unit homogeneity and conditional independence.

These attitudes toward case selection reveal that case studies are regarded as tests of a hypothesized relationship, which is denoted by an empirical regularity. The relevant covariations may be conceived of as being deterministic or probabilistic; what matters is that an empirical regularity provides the basis upon which to substantiate an inference (Jackson 2011:63-71). Mill’s methods epitomize this worldview because Millian case selection criteria serve as the basis for confirmation. Gerring (2007:131, 138) argues that cases selected with Mill’s method of difference can be confirmatory, but only if “a researcher begins with a strong hypothesis”—meaning an established cross-case pattern. An ensuing case study attempts to verify the broader inference by ascertaining if the observable implications of the empirical regularity are present, often by detailing the pathway between X and Y. Later, I argue that even if a case study illuminates such a “causal pathway,” this achievement still falls short of explaining of how and why X caused Y. Overall, leading advice on case selection is attuned to making causal inferences, and one confirms those inferences through demonstrated empirical regularities (Beach and Pedersen 2013:27-28).

Geddes’s (1990) well-known critique of Skocpol’s case selection reflects these tenets. Geddes rebukes Skocpol for using Mill’s method of agreement because “one should not make inferences based on samples selected on the dependent variable” (p. 138). In particular, Geddes criticizes Skocpol for not assessing the impact of international pressures in her contrasting cases because “many countries in the world have suffered foreign pressures as great as those suffered by France and yet revolutions occur infrequently” (p. 143). To expand the test, Geddes (1990:141-46) identifies eight instances across four Latin American countries that featured Skocpol’s structural conditions—intense geopolitical competition and conditions conducive for peasant uprisings—but counts just one revolution (Bolivia 1935–1952). ⁹ Geddes’s (1990) critique pivots on unit homogeneity; she believes Skocpol’s theory should operate in Latin America. To Geddes, the conclusion is straightforward: “if Skocpol had selected a broader range of cases to examine, rather than selecting three cases because of their placement on the dependent variable, she would have come to different conclusions” (p. 140). Geddes believes Skocpol’s findings are dubious because she failed to fulfill the imperatives for making valid causal inferences.

Critiques of the Conventional Wisdom on Case Selection

Geddes’s criticisms indicate wider misgivings about case study research and whether it can satisfy the requirements of unit homogeneity, conditional independence, and representativeness. For example, the viewpoint of unit homogeneity supposes that causation is recursive and symmetrical. Recursive causation refers to linkages flowing in one direction (X → Y). But causal relationships are often nonrecursive because there is feedback from Y to X. The notion of unit homogeneity also supposes causal symmetry: That the direction of change in X has the same predictive effect on Y. Yet causal relationships are often asymmetric. As the value of an explanatory factor X increases, it may have an effect on Y different from when X decreases. And sometimes a cause is irreversible, so the notion of causal symmetry is inapplicable (Lieberson 1985:63-87).

Case study researchers know of these issues. They appreciate the importance of causal complexity and feedback loops. So even if they use Mill’s methods, they recognize that his basic case selection techniques are oriented to uncovering monocausal relationships and cannot grapple with interaction effects or complex causal sequences (George and Bennett 2005:153-60). But rather than question the pertinence of unit homogeneity to case study research, practitioners often strive to demonstrate it. Munck (2004:110, italics original) maintains that researchers can “achieve causal homogeneity” by considering the relative influence of a variety of factors when conducting case study analysis or QCA. Falleti and Lynch (2009:1144) believe that delineating contextual differences can do the same: “One way to appreciate the importance of context for causal arguments is to think about context as a problem of unit homogeneity” (see also Munck 2004:107-10). Researchers try to fulfill the expectation of unit homogeneity instead of deeming it a conception inapplicable to their work.

Many case study researchers act similarly toward conditional independence. Social scientists analyze phenomena that have likely been influenced by unmeasured selectivity, which may affect what types of things are available to study (Lieberson 1985:14-43). Any study of contemporary European states examines a handful of countries that survived a long-term, nonrandom selection process that winnowed away about 200 polities over the past 500 years. Or, if ideational diffusion shapes lawmakers’ perceived policy options, conditional independence has been corrupted (Collier, Seawright, et al. 2004:31). Skocpol (1979:39) notes that conditional independence does not hold for her case studies because most strikingly “Russian revolutionaries actually played a role in the Chinese Revolution.” Because the notion of conditional independence is usually untenable, many researchers instead embrace the specification assumption, which demands that one’s explanatory variable is not correlated with the error term. ¹⁰ Collier, Brady, and Seawright (2004:244) consider the specification assumption useful for case study research. My point is not whether case study researchers have devised strategies to meet the specification assumption. Rather, the point is that they regard it as relevant because it “specifies the criteria that must be met to move in the direction of causal inference” (Collier, Brady, et al. 2004:243).

The emphases on unit homogeneity and conditional independence incline researchers to analyze representative cases. The prevailing belief is that a case study that typifies an X:Y pattern may illuminate connections between X and Y that are common to the population, more so than a case with extreme values on either variable. Typical cases are understood to have small residuals, rendering them more likely to meet the specification assumption (Geddes 2003:123-29; Gerring 2007:91-97, 2012:87). Likewise, researchers working in areas with well-established typologies are encouraged to examine cases that are “typologically representative” (Slater and Ziblatt 2013:1312). ¹¹ In practice, however, there are powerful disciplinary incentives for researchers to press along untrodden terrain. Researchers may not know what is representative of a population when selecting cases (Collier, Mahoney, et al. 2004:88). Their research will proceed as “inductive iteration,” which contravenes key principles underpinning case selection advice (Yom 2015). Thus, representativeness may often be impracticable as a guide for choosing cases. More important, by accentuating representativeness, practitioners signal that case studies are tools of causal inference.

Yet, while many case study researchers strive to fulfill the imperatives of unit homogeneity, conditional independence, and representativeness, other scholars have championed the unique ability of case studies to illuminate causal mechanisms. In the Skocpol–Geddes debate, Little (1995) ruminated on extending Skocpol’s theory to other cases, but his conclusions differ starkly from Geddes’s. Like Geddes, Little codes Skocpol’s variables for France, Russia, China, and England as well as for additional cases of Cuba, Italy, and Sweden. But he recognizes that his Millian table provides an incomplete accounting of the variables’ possible permutations. So Little makes a large QCA truth table, entailing 64 logically possible combinations. After eliminating combinations that are socially impossible, Little remains unsatisfied. Many plausible combinations lack empirical instantiations, so the truth table “will not be able to provide an exhaustive statement of the causal regularities” of interest (p. 50). He concludes that “it appears dubious that there are analytical techniques that permit us to infer the underlying causal relations without putting forward hypotheses about possible mechanisms” (p. 53). To Little, expanding an empirical test of Skocpol’s thesis is an ill-fated way to scrutinize it. Instead, one ought to probe the causal mechanisms undergirding her argument in order to judge its usefulness.

Little’s contribution to the Skocpol–Geddes debate indicates a tension within the practice of case study research. On the one hand, numerous case study researchers question the applicability of key attitudes of causal inference—unit homogeneity, conditional independence, and representativeness—to case study research. But in general, they have not rejected these standpoints; rather, they strive to conform to them. In addition, many practitioners stress that they can illuminate causal mechanisms via process tracing and thereby differentiate empirical regularities with real causal connections from spurious correlations. They have conceived of causal mechanisms mainly as causal pathways, which I describe below. Later, I argue that this approach cannot mitigate the discordance present in much case study research.

One Solution: Causal Mechanisms as Causal Pathways

Early methodological attention to causal mechanisms and process tracing came as a response to King et al. (1994), who subordinate case study research to large-N statistical analysis. This burgeoning literature, epitomized by Brady and Collier (2004), argued that causal mechanisms and process tracing (aka. causal process observations) could help case study researchers fulfill the imperatives of causal inference. ¹² For example, Munck (2004:110) maintains that when one finds a causal mechanism producing similar outcomes in multiple cases, one finds proof of unit homogeneity. Collier, Brady, et al. (2004:244) contend that King et al.’s (1994) emphasis on conditional independence places “too much attention on control variables as a solution to problems of causal inference.” They believe that process tracing can assuage these worries. And Collier, Mahoney, et al. (2004:92-101, quotation from p. 97) argue that purposive case selection—which KKV malign as selection bias—does not imperil validity because process tracing can “distinguish between the effect of the independent variable and the error within each case, [so] comparisons of effects across cases are not confounded with those errors.” They believe that process tracing can help meet the specification assumption. Overall, these contributions defend case studies as inferential tests.

Seminal statements on causal mechanisms usually likened them to intervening variables, and this perspective endures. Gerring’s (2008:163) minimal definition of a causal mechanism is that it “is the causal pathway, process or intermediate variable by which a causal factor of theoretical interest is thought to affect an outcome. Thus: X₁ → X₂ → Y” (where X₂ is the causal mechanism; see also Collier 2011:823; Weller and Barnes 2016:428-29). George and Bennett (2005:206, 141, respectively) characterize process tracing as the identification of “the intervening causal process—the causal chain and causal mechanism—between an independent variable (or variables) and the outcome of the dependent variable.” Causal mechanisms supply “a ‘process’ (X leads to Y through steps A, B, C).” ¹³ Beach and Pedersen (2013:29-30) regard a causal mechanism as “a theory of a system of interlocking parts that transmits causal forces from X to Y.” Specifically, X channels “causal energy through the mechanism to produce an outcome,” such that X → [(n_n →)] Y, where n refers to a mechanism of n parts. Falleti and Lynch (2009) build on this perspective and argue that causal mechanisms (M) can have different effects in different contexts. In context A, X → M → Y_A, whereas in context B, X → M → Y_B. To them, context and causal mechanisms can account for cross-case variation. These scholars contend that causal mechanisms specify the pathway between a cause and its effect.

Case studies afford unparalleled opportunities to examine such causal pathways. Mahoney (1999:1168) stresses that narrative analysis (i.e., process tracing) “makes an independent contribution” beyond what nominal or ordinal comparisons can accomplish. In terms of the Skocpol–Geddes debate, he implies that Geddes’s critiques were misguided because they focused on Skocpol’s nominal Millian comparisons, when Skocpol also used narrative analysis. Mahoney (1999:1168) lauds Skocpol’s process tracing because it “meaningfully assemble[d] specific information concerning the histories of cases into coherent processes” and bolsters confidence in her argument (see also George and Bennett 2005:158-59; Skocpol 1979:320n16). He magnificently diagrams the 37-step pathway between the ancien régime and state breakdown in France. Mahoney suggests that Skocpol’s narrative analysis blunts Geddes’s critiques and concludes that process tracing is a key way that case study researchers make and affirm causal inferences. ¹⁴

Yet, when causal mechanisms are conceived of as causal pathways, they do not resolve the discordance that I noted above. Recall that causal mechanisms appeal to researchers because they can supposedly differentiate between spurious correlations and empirical regularities with real causal connections. Put differently, causal mechanisms allow one to move beyond an X:Y regularity and toward an explanation of how X → Y. But if, in the X₁ → X₂ → Y formulation, X₂ is a causal pathway, then it just tells us that X₁ and Y are conditionally independent and that their connection hinges on the presence of X₂. So X₂ is akin to an intervening variable. And the case study itself remains a test of a broader cross-case pattern because X₂ is simply a step between the X:Y regularity that prompted the case study. The observation of X₂ does not explain how, why, or if X₁ causes Y. Although one may make a causal inference based on this regularity, one has not constructed a causal explanation (Jackson 2011:67-68, 108-10). ¹⁵ Hence, invoking a causal mechanism conceived of as a causal pathway does not help researchers close the “epistemological gap [that] separates observed regularities from causal explanation” (Dessler 1991:339).

In practice, however, many researchers want to construct explanations. Reconsider the exemplars mentioned earlier. Mahoney (2001: xii, 264) considers his book to be “a full-blown…explanation of Central American political development.” Although Mill’s methods helped him reappraise conventional wisdoms, Mahoney contends that process tracing is what ultimately makes his arguments convincing. Smith (2007:202) concludes that process tracing confirms his theory because “comparative historical analysis provides causal leverage over questions for which statistical inquiry can provide only inferential conclusions.” And Lieberman (2009:22) judges that his statistical analyses of AIDS policy are worthwhile but that “the real test was to trace causal processes and to see if I could find compelling evidence linking the hypothesized cause to effect.” Explanation is their goal, but it is a goal that cannot be achieved by conceiving of causal mechanisms as pathways.

Explanations Are Distinct From Inferences

Although the notions of inference and explanation are often conflated in our discourse, they are distinct. Whereas an inference connects a hypothesis with data, an explanation is a “statement about why an outcome has occurred” (Seawright and Collier 2004:288). A causal explanation describes what happened and what caused that thing to happen. It is also a statement about why one thing, and not another, happened (Jackson 2017). Thus, explanations go further than inferences. Inferences marshal data to demonstrate conformity to a hypothesis; they indicate the strength of a theoretical statement via reference to an empirical regularity. But of course, this pattern may be spurious to the actual process producing the observed outcomes. Hence, many scholars believe that “an epistemological gap separates observed regularities from causal explanation” (Dessler 1991:339). Waldner (2007:151) states that “Explanations are inferential, but not all inferences explain.” ¹⁶

This approach to social science is present in some alternatives to neopositivism, especially causal realism and analyticism (see Miller 1987; Jackson 2011, respectively). A shared feature of these approaches is their interest in entities with capacities to bring about change. A good explanation must reference those entities and describe how they exacted change in a particular instance. A key part of an explanation therefore relates to a statement about manipulability: specifically, an understanding of how a purported cause changed something and thereby produced its alleged effect (Jackson 2017; Little 1998:205-7; Woodward 2003:9-12). In doing so, researchers strive to go beyond the X:Y relationships that constitute causal inferences and detail the factors that were present and jointly sufficient for a particular outcome (Little 1998:207-8; Miller 1987:86-87). Consequently, one can build a compelling explanation without reference to an empirical regularity (Jackson 2017).

In contemporary social science, these philosophical and epistemic concerns have prompted attention to causal mechanisms as ingredients of adequate explanations. Causal mechanisms allow scholars to better understand a relationship between two factors by peering inside the “black box” of causality. Mechanisms help researchers move beyond an X:Y correlation and toward a causal understanding of how and why X → Y (Elster 1989:3-10; Gerring 2007:161-64; Hedström and Ylikoski 2010). Researchers explicate how causal mechanisms link a cause to its effect through process tracing, which illuminates how variables generated particular events and produced what researchers sometimes refer to as a causal chain (e.g., Bennett and Checkel 2015:6; Waldner 2012:69). Causal mechanisms and process tracing can facilitate explanation (Dessler 1991; Waldner 2007, 2012).

In practice, however, the notions of explanation and inference are often conflated. As I noted above, Skocpol, in States and Social Revolutions, expresses an affinity for what scholars today call causal inference, particularly when she endorses Lijphart’s comparative method. Yet Skocpol (1979) simultaneously maintains that she is producing an explanation. She argues that the similarities in France, Russia, and China are “more than sufficient to warrant their treatment together as one pattern calling for a coherent causal explanation” (p. 41; see also pp. xi, 234-35). Skocpol says she used her case studies “to see whether a particular causal argument or process actually illuminates patterns found in the data” (quoted in Munck and Snyder 2007:666). In contemporary parlance, she wanted to show how certain variables and causal mechanisms generated the outcomes in her cases.

Ingredients of Causal Explanation

Earlier in the article, I note that making a causal inference entails estimating causal effects, ideally in a controlled, quasi-experimental way. Case studies used to corroborate an inference are therefore tests of a cross-case covariational pattern. By contrast, case studies that are understood to be explanatory are not tests per se. Rather, they are constructions of an explanation of an individual case. Researchers who want to explain a case strive to demonstrate how a purported cause manipulated or changed something and produced its alleged effect (Jackson 2017; Woodward 2003).

To construct an explanation, researchers use process tracing to illuminate the concatenation between a cause and its effect. Yet process tracing is often presented as means of theory testing; Bennett and Checkel’s (2015:20-31) best practices for process tracing suggest as much. But process tracing is not necessarily a testing device. Consider this definition: “In process tracing, one concatenates causally relevant events by enumerating the events constituting a process, identifying the underlying causal mechanisms generating those events, and hence linking constituent events into a robust causal chain that connects one or more independent variables to the outcome in question” (Waldner 2012:68-69; Bennett and Checkel [2015:6] have a similar definition). Nothing in this definition automatically disposes process tracing to being a test of a cross-case pattern. Process tracing is better thought of as a means to formulate an explanation.

An adequate explanation depends on three things: good description, causal depth, and competition among rival hypotheses. First, good explanations require that researchers describe the factors that were present and together responsible for bringing about a specific outcome (Little 1998:198-201; Miller 1987:86-98; Ylikoski 2012:23-24). Process tracing embodies this pursuit to show how X₁ → X₂ → Y. It invokes a counterfactual notion of explanatory dependence: Had X₁ not occurred, then neither would have X₂ (at least due to X₁). Or, even if X₁ had occurred, some countervailing force Z may have thwarted the realization of X₂ and Y (Hedström and Swedberg 1998; Ylikoski 2012:33-39; see also Woodward 2003:70-74). When researchers detail the factors jointly responsible for an outcome in a given case, they are not testing an empirical regularity; they are constructing an explanation of a case (Jackson 2011:149).

Second, good explanations must provide adequate causal depth. This imperative requires that one try to trace causes back to their roots to avoid wrongfully attributing causality to a factor that is epiphenomenal of another factor (Miller 1987:98-105). Although the burgeoning literature on process tracing lacks a shared definition of what it is, the spirit of much of this scholarship suggests that good process tracing should not merely describe a sequence of seemingly causally related events. Rather, it should marshal evidence to demonstrate the generative links within a causal chain. Bennett and Checkel (2015:6) state that the “essential meaning” of process tracing “refers to the examination of…how that process took place and whether and how it generated the outcome of interest.” Waldner (2012:69) argues that concatenation “places a very heavy emphasis on claims of necessity” in order to show that the generative links identified through process tracing explain how and why an outcome was bound to occur (cf. Miller 1987:98-102). Waldner (2015:132) refers to the resulting delineation of a causal process in a particular case as an event-history map. The pursuit of causal depth is demanding and necessitates that researchers make prudent choices about where to begin and end process tracing (Bennett and Checkel 2015:26-29).

Third, an adequate explanation also hinges on competition with its rivals; judgments about the fitness of an explanation are always tentative and subject to change (Miller 1987; see also Hall 2003:381-95, 2013). This comparative assessment centers on a given case-specific explanation, unlike judgments of competing cross-case causal inferences, which may be made on the basis of R² or predicted marginal effects. Indeed, Skocpol recounts that some of the most fervent critics of States and Social Revolutions were historians who disputed her case-specific explanations (Munck and Snyder 2007:670-71). Overall, adequate explanations entail good description, causal depth, and competition among rival hypotheses. These requirements underscore that an explanation of a case is not simultaneously an inferential test of a cross-case pattern, let alone an “explanation” of such covariation (cf. Jackson 2011:152-55).

Another View of Causal Mechanisms: Entities With Invariant Properties

The difference between an inference and an explanation, as well as the requisites for adequate explanations, further reveals the discordance in much case study research. Invoking causal mechanisms that are conceived of as causal pathways cannot harmonize this discordance. Fortunately, an alternative view of causal mechanisms—as entities with invariant properties—can help researchers construct explanations. As I describe in this subsection, invariant causal mechanisms assist explanation because they are understood to be unchanging and can therefore explicate how certain factors altered things and generated an outcome (Waldner 2016). Then, in the next subsection, I argue that this view of causal mechanisms warrants rethinking what case studies are and what principles ought to guide their selection.

This conception of causal mechanisms focuses on invariance as their vital property. Waldner (2012:75) defines a causal mechanism as “an agent or entity that has the capacity to alter its environment because it possesses an invariant property that, in specific contexts, transmits either a physical force or information that influences the behavior of other agents or entities.” This view is distinct from the notion of causal mechanisms as pathways or intervening variables. ¹⁷ Variables can be manipulated or altered. Invariant causal mechanisms cannot be: They constitute “the fundamental nature of a phenomenon” and remain “unchanged under some transformation” (Waldner 2016:30, 29, respectively). For example, Waldner describes how combustion is an invariant mechanism that helps to explain how automobiles work. One can prevent a car from working through a variety of manipulations (e.g., taking gasoline out of it); but given the proper conditions for combustion, it will occur.

Defining causal mechanisms as possessing invariant properties enables researchers to move beyond inference and toward explanation. Recall that if one conceives of a causal mechanism as a pathway, and one observes that X₁ → X₂ → Y, one has learned that X₁ and Y are conditionally independent on the presence of X₂. But one does not know how, why, or if X₁ causes Y. Ultimately, “theories that attempt to define causality in terms of regularities…are not compatible with mechanism-based theories” (Hedström and Ylikoski 2010:53; see also Tilly 2001:24-25). By contrast, one can invoke an invariant causal mechanism to explain how and why X₁ activates X₂, which manipulates or alters things and generates Y. Process tracing often focuses on microfoundations to explicate how macrolevel factors affected individuals’ decision-making about a particular course of action and yielded a specific outcome (Beach and Pedersen 2013; Bennett and Checkel 2015; Waldner 2015). For example, the desire to obtain distributive political advantage—a ubiquitous feature of politics—may help explain why changing social structural conditions regularly result in new political coalitions. Both social structure and political coalitions are alterable; they are variables. But the quest for distributive advantage is an invariant mechanism; one cannot alter its constitutive features without connoting something altogether different. ¹⁸ Thus, the mechanisms that link X₁ to X₂ and X₂ to Y explain those connections because the mechanisms are unalterable and thereby provide a compelling theoretical account of how one variable manipulated things and changed the other. ¹⁹

Consider the following example, cast in the X₁ → X₂ → Y mold. Spruyt (1994) examines how expanding trade around 1100 spurred varying institutional arrangements in Europe. A key consequence of rising trade was the growth of merchant power in towns (X₁). In turn, new political coalitions formed (X₂), leading to institutional variation (Y). The first causal mechanism, which links X₁ to X₂, is the desire for distributive political advantage. When merchants’ economic power increased, they sought commensurate gain in the political arena and forged new coalitions to that end. Spruyt employs another invariant causal mechanism, coalitional bargaining, to explain why new political coalitions (X₂) resulted in institutional change (Y). In France, merchants traded in low value-added goods, such as grain, which had small profit margins. They wanted rulers to reduce transaction costs and facilitate profit-making by establishing centralized rule. Once merchants formed new political coalitions, they bargained for institutional change. ²⁰

In Spruyt’s account, the appeal to an invariant causal mechanism enables one to ascertain why the manipulation of one variable, relative merchant power, resulted in new political coalitions. And one can imagine a counterfactual state of affairs, in which the French economy stagnated, political coalitions remained unchanged, and there was institutional stasis (Jackson 2017; Waldner 2007, 2016; Woodward 2003:9-12). ²¹ Making reference to invariant causal mechanisms helps researchers construct a fully specified accounting of a particular case, even though they cannot observe its counterfactual state (Waldner 2016:31). This emphasis on manipulability “provides a useful way to distinguish between mere correlational association (even sequential association) and a causal connection” (Jackson 2017:703).

I conclude this subsection by returning to the Skocpol–Geddes debate. Recall that Skocpol (1979:xi, 41, 234-35) says that she is producing an explanation. Part of her argument is that rising geopolitical pressures promoted state breakdowns, which can be represented in X₁ → X₂ → Y form. Skocpol describes how international pressures (X₁) demanded greater resource extraction by the state (X₂), which spawned severe state–elite conflict and state breakdown (Y). The invariant causal mechanism linking X₁ to X₂ is the revenue imperative, the necessity that government fund its operations. The mechanism connecting X₂ to Y is a decision-making framework informing rulers’ revenue extraction policies (e.g., Levi 1988). Skocpol (1979:49) notes that, in her cases, “states and the landed classes were…competitors in controlling the manpower of the peasantry and in appropriating surpluses from the agrarian-commercial economies.” In France, dire fiscal needs provoked state leaders to introduce “sweeping proposals for legal and tax reforms,” which would have displaced landed elites’ hegemony in local resource extraction. A variety of case-specific factors induced these astounding proposals (Skocpol 1979:63-64). ²² These actions unleashed acute state–elite conflict and led to social revolution.

Geddes does not consider such mechanismic implications when stretching Skocpol’s arguments to Latin America. Geddes (1990:141-46) identifies eight cases that featured intense geopolitical competition and conditions conducive for peasant uprisings but counts just one revolution. In terms of variables, things seem similar: There was geopolitical competition (X₁) and growing revenue needs (X₂). But unlike in France, Latin American governments did not try to fund war-making by wresting economic surplus directly from local agrarian economies. Instead, they relied on trade duties, foreign loans, and the printing press (Centeno 2002:108-37). These fiscal strategies were used in Geddes’s counterexamples. ²³ States could expand revenue without confronting landed elites. ²⁴ Latin American policy makers probably used a decision-making framework analogous to their French counterparts; but because of contextual differences, they could adopt fiscal policies that avoided state–elite conflict. Once one considers the causal mechanism linking X₂ and Y, and examines the contexts of these cases, one recognizes why revenue demands in Latin America would be unlikely to spawn state breakdown and social revolution.

The difference between Skocpol’s and Geddes’s perspectives boils down to the distinction between an inference and an explanation. Geddes interprets Skocpol as merely making a broad covariational claim and wants to expand a test of it. Ultimately, however, Skocpol is constructing case-specific explanations of the French, Chinese, and Russian Revolutions. So even though Skocpol invokes Mill’s methods in case selection, insofar as she is not claiming to have discovered a wide empirical regularity, neither her case selection nor her argument should be assessed according to the rules of causal inference. Skocpol should be scrutinized according to principles of causal explanation. Yet just because Skocpol constructs explanations of three cases, instead of theorizing a wide empirical regularity, it does not mean that her endeavor (or case study research in general) is parochial, idiographic, or detached from broader theoretical concerns. But it does demand that one rethink how case studies relate to these larger concerns.

Case Studies Engage Analytical Ideal Types

An alternative way to think about case studies is in relation to an analytical ideal type. Researchers can use theory to develop ideal types that offer “idealizations or oversimplifications” of empirical reality. And they can then harness ideal types to help construct explanations of particular cases. One can build an explanation by considering to what extent an analytical ideal type renders a case intelligible and how case-specific factors affected the outcome as well (Jackson 2011:113, 152). ²⁵

Weber (1949:90, italics original) conceived of an ideal type as a “synthesis of a great many diffuse, discrete, more or less present and occasionally absent concrete individual phenomena, which are arranged…into a unified analytical construct” that is conceptually pure and “cannot be found empirically anywhere in reality.” Ideal types are “instrumental…deliberate oversimplifications” that can be employed in case study research to help build explanations (Jackson 2011:142). Weber (1949:90) believed that ideal types could facilitate explanation because “historical research faces the task of determining in each individual case, the extent to which [an] ideal-construct approximates to or diverges from reality.” Thus, the “construction of abstract ideal-types recommends itself not as an end but as a means” to better understand the social world (Weber 1949:92, italics original).

In practice, case study researchers can use ideal types as something to which the empirical facts of a case can be juxtaposed. But ideal types do not offer falsifiable claims that case studies test (see Weber 1949:90). Rather, ideal types are more like “specialized conceptual filters that focus our scholarly attention on particular aspects of actually existing things.” They help researchers “to organize empirical observations into systematic facts” by directing their attention in certain ways. Ideal types are not intended as true representations of empirical reality; they are models that can be used to help construct explanations (Jackson 2011:144-53, quotations from pp. 145, 151).

Using an ideal type to form a case-specific explanation resembles what many researchers already do. One applies an ideal type to an individual case in order to understand the extent to which the ideal type can account for the permutation of that case. Some of what explains the outcome may be factors described in the ideal type; other factors may be idiosyncratic. Together, these factors are what Weber refers to as the “adequate causes” of an outcome (Jackson 2011:145-49; see also Weber 1949:174-77). This list is not unlike Miller’s (1987:86-98) emphasis on detailing the factors that were present and jointly responsible for an outcome. Throughout the dialogue between an ideal type and a case, researchers employ counterfactual reasoning, by imagining if the observed outcome could have occurred in the absence of the adequate causes. Jackson (2011:152-54) stresses that the analytically general claims encapsulated in an ideal type are not empirical generalizations but are means to facilitate a singular explanation.

Hence, one necessarily analyzes context when constructing an explanation. Context refers to a wide range of things—including culture, ideas, time and place, population and demography, and prevailing technology—that may influence the process and outcome in which one is interested (e.g., Goodin and Tilly 2006). Context is important to case studies that engage analytical ideal types in two ways. First, context can be understood as the variety of factors that are not part of the general claims of an ideal type but which contribute to the case-specific outcome. Tilly and Goodin (2006:25) characterize such considerations as “correcting for context.” These “contextual milieux” are partly why one should never expect an empirical situation to be identical to an ideal type (see also Tilly 2001).

Second, context can also be thought of as the aspects of a case that make it relatable to an ideal type. Imagine some ideal typical claim that X₁ → X₂ → Y. Researchers hold expectations about the circumstances under which X₁ often triggers X₂. This context may be described as part of the ideal type and thereby offers clues as to the cases that may relate to the ideal type (see Berger 1987:158-59). The contextual features suggested by an ideal type may lead one to suspect that a given case is relatable to it. By relatable, I mean that the known features of a case make it seem pertinent and applicable to the ideal type. But one cannot be certain beforehand whether the ideal type is useful for explaining the case because it is through constructing the explanation that one learns the extent to which an ideal type renders a case intelligible.

I emphasize this inherent uncertainty to distinguish my approach from the prevailing worldview on case selection. The contextual features suggested by an ideal type are not a delimitation of scope conditions within which an empirical regularity holds (see Berger 1987:159). Neither are they an attempt to “control” for context so that one can isolate potential confounding variables (cf. Tilly and Goodin 2006:23-24; Franzese 2007). Delimiting scope conditions and attempting to control for context are strategies bound together with an approach that regards case studies as tools of causal inference. Consider Nielsen’s (2016) excellent primer on using statistical algorithms to match cases for a method of difference comparison. He plainly describes how matching is oriented to facilitating causal inferences. An ideal type cannot be harnessed for matching because an ideal type is not intended to be a plain representation of empirical reality but rather an avowed oversimplification of it. Individual cases will never mirror an ideal type, which means that they cannot be selected according to their scores on key variables, as with Mill’s methods. An ideal type simply indicates contextual features that can guide researchers toward cases that seem applicable to the general claims of the ideal type.

This understanding of context supports an alternative outlook on case selection. If a case has contextual features that make it relatable to an ideal type, then one can viably study that case in relation to the ideal type, regardless of the case’s other characteristics. For instance, Jackson (2011:148) uses an example from international relations: That states situated in anarchy will try to balance power. So in deciding which state to study vis-à-vis this general analytic claim, one should examine a state that seems to be situated in anarchy. This criterion is obvious. Yet its simplicity overturns much of the conventional wisdom on case selection. First, the case is selected without certainty that it is indeed situated in anarchy (i.e., its status is suspected, not confirmed). Second, a researcher need not profess that her case is representative of some larger class of units, that her case selection strategy has controlled for confounding variables, or that her case conforms to an empirical regularity. These things are inessential to whether a case relates to a particular ideal type and whether a case study may produce an adequate explanation. Instead, basic contextual similarity can serve as a robust basis for case selection.

The same logic applies to researchers who want to study multiple cases. The conventional wisdom on case selection maintains that studying multiple cases is desirable because it increases the N and performs a larger test of a covariational pattern. Mainstream advice encourages researchers to choose cases that differ on key variables to offer inferential leverage for the test (e.g., Weller and Barnes 2016). By contrast, examining multiple cases in relation to an ideal type does not serve this end because each explanation is case specific. That does not mean, however, that studying multiple cases is useless. Knowledge of multiple cases could assist the development and refinement of an analytical ideal type and enhance understanding of a social phenomenon (Berger 1987:175-79; Jackson 2011:152-53). For researchers who want to study multiple cases, one should select them in reference to the contextual features that make them relevant to an ideal type. In my approach, contextual similarity alone justifies case selection. This principle for case selection can embolden unconventional comparisons that are currently deemed untenable.

Dueling Perspectives on Context and Case Selection

This final subsection contrasts my perspective with the conventional wisdom on context and case selection. I juxtapose my approach to Falleti and Lynch (2009) and continue the examples from Spruyt and Skocpol–Geddes. Falleti and Lynch are interested “in how context affects…mechanismic [arguments]” and how contextual “surroundings…allow the mechanism to produce the outcome” of interest (pp. 1144, 1152, respectively). They define context “broadly, as the relevant aspects of a setting (analytical, temporal, spatial, or institutional) in which a set of initial conditions leads (probabilistically) to an outcome” (p. 1152). They state that “the interaction between mechanism and context is what determines the outcome.” In context A, X → M → Y_A. In context B, X → M → Y_B (p. 1151). Detailing contexts A and B shows how “[f]ormally similar inputs, mediated by the same mechanisms, can lead to different outcomes if the contexts are not analytically equivalent” (p. 1160). Contextual delineation establishes unit homogeneity and identifies the different empirical regularities within distinct contexts. They conclude that “the indeterminacy of the outcome resides not in the mechanism but in the context” (p. 1151).

Falleti and Lynch’s (2009) perspective is consonant with the conventional wisdom on case study research. They want to achieve unit homogeneity and believe that delineating context can do so. They instruct researchers to use theory to identify “what aspects of a context are likely to be relevant to the process and outcome” (pp. 1151-53) being studied. But ultimately such relevance is marked by a probabilistic association with the outcomes of interest because different empirical regularities distinguish contexts A and B (see p. 1151). So context is akin to a bundle of potential confounding variables; indeed, they refer to context as “variables that reside ‘outside’ the theory but nevertheless affect the operation of the causal mechanism” (p. 1145). Case studies are therefore tests that seek to validate a causal inference (Falleti and Lynch 2009:1159, 1144-45; cf. Jackson 2011:109).

I do not contend that contextual delineation establishes unit homogeneity. Instead, contextual analysis can suggest whether a case is relatable to the general analytic claims encapsulated within an ideal type. Once again, imagine an ideal typical claim that X₁ → X₂ → Y. If one chooses to study multiple cases in relation to that ideal type, one merely declares that those cases possess attributes which seem to render them applicable to the ideal type. One is not maintaining that the cases are analytically equivalent because one’s judgment regarding a case’s relevance to an ideal type is tentative. Neither is one implying that an empirical regularity holds across multiple cases because one is seeking to construct case-specific explanations, not searching for probabilistic associations. And as I note above, during case selection, one remains agnostic as to whether the ideal type will help elucidate the observed outcome. But to Falleti and Lynch, ascertaining some context A implies that, within it, X₁ → X₂ → Y_A, at least probabilistically. By contrast, the contextual features suggested by an ideal type describe a constellation of factors that may be useful in explaining a number of cases, even if that constellation will never be fully present in any of them or shared across them (see Berger 1987:159).

Two final examples illustrate the difference between Falleti and Lynch’s perspective and the one I advance herein. Recall that Spruyt (1994) examines how rising trade led to increased merchant power (X₁), new political coalitions (X₂), and institutional variation (Y) in the High Middle Ages. He believes that the widespread economic expansion in eleventh-century Europe makes his argument widely applicable (Spruyt 1994:61). In France and “Germany,” merchants traded in low value-added goods and wanted to reduce transaction costs by establishing centralized rule. Spruyt (1994:61-67, 86-89, 112-14) provides general reasons to anticipate that X₁ → X₂ → Y_A, with Y_A being a centralized sovereign state. He describes that merchants in both cases sought this outcome. In addition, France and “Germany” had similar contexts: They were former parts of the Carolingian Empire; they developed feudalism; but by the High Middle Ages, it was in decline with little residual institutionalization.

As it happened, merchants received centralized rule in France but did not in Germany. Whereas the French monarch aligned with merchants and built a sovereign state, the German king allied with landed nobles, thwarting centralized rule. The German king’s geopolitical ambitions compelled him to ally with the nobles instead of merchants (Spruyt 1994:116-17). It is difficult to account for this varied outcome from Falleti and Lynch’s standpoint, given the similarities of context, merchants’ preferences, and merchants’ relative strength. One possibility is that Spruyt’s argument is undertheorized—he does not offer a theory of ruler preferences—and that a more intricate theory could account for the cross-case variation (Waldner 2015:143-47). But another possibility is that Spruyt’s claims are ideal typical. ²⁶ The French case largely accords with the ideal type, but the German case can be rendered intelligible only once one appreciates the German king’s geopolitical dilemma. Spruyt uses his ideal type and “corrects for context” to construct explanations of these particular outcomes; and currently, Spruyt’s explanations are considered more robust than alternative accountings (see Waldner 2015:147, on this latter point). Spruyt demonstrates the viability of the approach that I advocate.

Last, in terms of the Skocpol–Geddes debate, a final reason I find Geddes’s criticisms wanting is because she rejects the limits that Skocpol places on her own argument. Skocpol (1979:287-90) restricts her argument to relatively wealthy, agrarian countries that had not been subjected to colonial rule. Geddes (1990:143-44, especially 144n3) finds this delimitation unjustifiable because some Latin American countries score similarly on Skocpol’s variables and witnessed “widespread, sustained peasant revolutionary movements,” even if they did not experience full revolutions. The ensuing debate has surrounded whether Skocpol’s restriction is justified or arbitrary and unjustifiable. Sekhon (2004:290n63) agrees with Geddes: “it is not clear why the domain…should be so restricted.” Gerring (2007:81-82) distills the issue into one of unit homogeneity; he thinks Skocpol’s restriction is “plausible” but also maintains that “social science gives preference to broad inferences over narrow inferences.” Collier and Mahoney (1996:81-82) defend Skocpol because more recent revolutions have occurred in relatively poor ex-colonies, where the military apparatus was independent of the landed classes (see also George and Bennett 2005:119-20). But they too frame the issue in terms of unit homogeneity: Collier and Mahoney say Skocpol’s boundary conditions lead one to expect different “causal patterns” (empirical regularities) in her cases versus Latin America.

To be clear, Gerring’s and Collier and Mahoney’s assessments are consonant with Skocpol’s (1979:18) desire “to find important regularities across given historical instances.” But Skocpol also strives to produce case-specific explanations. Conceiving of her argument as an ideal type can help to shift the debate surrounding her scope restriction. An ideal type is not intended to discover empirical regularities; it is meant to be useful for constructing explanations (Jackson 2011:153). In Skocpol’s case, the contextual factors that render a country relatable to her claims—being relatively wealthy, agrarian, and a noncolony—might encourage one to examine France, China, or Russia, to see if her claims are useful for explaining those social revolutions. This contextual constellation would likewise discourage one from probing a Latin American case because the mechanismic links in Skocpol’s theory are unlikely to have developed in the Latin American context. But even if one studied Bolivia, one would quickly realize that Skocpol’s ideal type, especially its insights about revenue-raising strategies, is not useful for understanding why the Bolivian revolution occurred (cf. Gallo 1991). The usefulness of Skocpol’s delimitation makes her scope restriction justifiable. Moreover, if one considers Skocpol to be articulating an ideal typical claim, one would not have conducted a wide-ranging test of it in the first place.

Overall, this section articulates an approach to case study research that better coheres with the aim of researchers who want to construct explanations. Much of what is normally prescribed to case study researchers diverges consequentially from the epistemic project in which many of them are engaged. By focusing on how one builds explanations, I hope to alter the strictures that currently inform how one should select case studies and relate them to broader theoretical issues.