Discussions in the social sciences about the relative merits of qualitative and quantitative methods have acquired a mellower tone over the last decade or so. Researchers working within each methodological tradition, when critiquing methods from the other, have increasingly emphasized that both qualitative and quantitative methods are epistemologically sound and play important roles. Despite this welcome consensus, however, disagreements remain over fundamental issues. One recent volume by leading scholars from different subfields of political science, Robert Keohane, Gary King, and Sidney Verba (hereafter KKV), argues that there is only "one logic of inference" for both qualitative and quantitative research methods, and that this logic "tends to be explicated and formalized clearly in discussions of quantitative research methods." (KKV, 1994:3) In contrast, the eminent sociologists Charles Ragin and David Zaret have maintained that case-based methods and variable-based (statistical) methods "are neither congruent nor convergent in their (1) units of analysis, (2) conception of causality, (3) conception of adequate explanation, or (4) logic of analysis." (Ragin and Zaret, 1983:731)

Which view is correct? The answer depends on the definition of the "logic" of inference or analysis. If the logic of inference refers to the epistemological logic of positivist empiricism, broadly defined, then these two sets of scholars, as well as the present paper, can agree that there is a single logic of inference even though they might not agree on all of its particulars. On this level, most case study researchers would agree with KKV's emphasis on empirically testing theories and their suggestions, for example, to generate an inclusive list of alternative theories' observable implications and specify what evidence might infirm or affirm a theory. (KKV, 1994) However, if the logic of inference refers to specific methodological injunctions on the selection, study, and drawing of inferences from cases, then there are indeed two very different logics of inference.

This semantic and conceptual dichotomy illustrates the problem that is the focus of the present paper. Precisely because the methodological logic of statistical inferences has been articulated more systematically than the analogous but quite different methodological logic of case studies, researchers have often viewed case study methods through the prism of statistical terms and concepts. This has resulted in recurrent and basic misinterpretations of case study methods. In particular, this paper addresses eight misinterpretations of key methodological issues that have arisen from the application of statistical concepts to case study methods: 1) "degrees of freedom," 2) cases' "representativeness" of wider populations, 3) cases' independence from one another, 4) case studies' use of John Stuart Mill's methods of comparison, 5) the roles of "causal effects" and "causal mechanisms" as bases for causal inferences, 6) case selection and "selection bias," 7) "cell reduction," and, 8) left-out variables.

After reviewing each of these issues, this paper concludes that case study methods are on the whole stronger than the critics of these methods have argued. However, variants of many of the eight methodological problems elaborated below do apply to case study research. In some respects these variants are more constraining than the analogous limits on statistical methods, and in others they are less constraining; above all, they are simply different. It is also important to distinguish between the inherent limits of case study methods and the limits that can arise when researchers use these methods imperfectly, or when the phenomena to be researched are by their very nature challenging for any methods of inference. Often, the researchers who are most aware of the constraints and flaws of particular methods have been those who actively practice them, as has been true of recent critiques of statistical methods. (McKim and Turner, 1997). In this spirit, this paper aims to identify accurately the limitations of case study methods so that they can be used more effectively and judged more appropriately.

1. Case Studies and the "Degrees of Freedom Problem"

The first and perhaps most widespread misinterpretation of case studies is that they inherently suffer from what statisticians call a "degrees of freedom problem." (Achen and Snidal, 1989:156-7) In statistical terms, the number of degrees of freedom is defined as "the number of quantities that are unknown minus the number of independent equations linking these unknowns." (Blalock, 1979:205) The degrees of freedom problem arises because in order to obtain a unique solution for simultaneous equations, it is necessary to have the same number of unknowns (or cases) as equations. Thus, when a researcher has many independent variables but only one or a few observations on the dependent variable, the research design is indeterminate, and there is a very limited basis for causal inferences apart from simple tests of necessity or sufficiency.

Stated in these generic terms, there is indeed a degrees of freedom problem in any case study research design in which there are few observations but many independent variables. An important misinterpretation arises on this issue, however, from using definitions of "case," "variable," and "observation" that are excessively narrow. One common but potentially misleading definition describes a case a "phenomenon for which we report and interpret only a single measure on any pertinent variable." (Eckstein, 1975:85, KKV, 1994:52) This definition would lead naturally to the conclusion that any case study research design with fewer cases than independent variables would have a degrees of freedom problem. In fact, however, each qualitative variable has many different dimensions rather than providing a "single observation." Statistical researchers tend to aggregate variables together into single indices to get fewer independent variables and more degrees of freedom, but case study researchers do the reverse: they treat variables qualitatively, in all of their relevant dimensions, and they try to distinguish qualitatively different types of each independent and dependent variable. For example, rather than constructing a single index of "Soviet military interventionism," a case study researcher might look at the number of Soviet troops deployed, the kinds of weapons used, the rules of engagement, the amount of military aid, and so on. (Bennett, 1992) An independent variable affecting the level of Soviet interventionism, rather than the "Soviet economic situation" or "Soviet GNP," might include production in specific sectors, such as production of Soviet forces for power projection, production of weapons available for export, and so on. A case study researcher seeking to explain Soviet retrenchment in Afghanistan in the late 1980s, to continue the example, could test whether the many dimensions of independent variable(s) are congruent with those of the dependent variables. In this instance, Soviet military aid to Afghanistan increased even as Soviet troops withdrew, and the Soviet economy and particularly Soviet military production did not decline sharply until after the Soviet withdrawal, casting doubt on whether economic constraints were a major factor in causing this withdrawal.

In addition, within a single case there are many possible process tracing observations along the hypothesized causal paths between independent and dependent variables. A causal path may include many necessary steps, and they may have to occur in a particular order. At each step, the researcher may measure the magnitudes and signs of intervening variables to see if they are as the hypothesis predicts. These many predicted observations may provide sufficient "degrees of freedom," or many more observations than variables, even when the researcher is studying a single case and using several independent variables. KKV, for example, note that "defining and then searching for these different causal mechanisms may lead us to find a plethora of new observable implications for a theory." (KKV, 1994: 225)

This is why the accomplished methodologist Donald Campbell recanted his criticism that an inherent degrees of freedom problem plagued case study methods. Admirably setting out to "correct some of my own prior excesses in describing the case study approach," Campbell noted that:

I have overlooked a major source of discipline (i.e., degrees of freedom if I persist in using this statistical concept for the analogous problem in nonstatistical settings). In a case study done by an alert social scientist who has thorough local acquaintance, the theory he uses to explain the focal difference also generates predictions or expectations on dozens of other aspects of the culture, and he does not retain the theory unless most of these are also confirmed. In some sense, he has tested the theory with degrees of freedom coming from the multiple implications of any one theory. (Campbell, 1975: 179, 181-2)

As Campbell describes this process, which he terms "pattern matching," it involves elements of two modes of within-case analysis, the "congruence method" and "process tracing." The congruence method (addressed in detail in a related conference paper by Alexander L. George) involves testing for whether the outcome of a case, in its various dimensions, is congruent with the various dimensions of the independent variable(s) and the expectations of the underlying theory linking the two. Process tracing involves testing whether all of the intervening variables were consistent with the expectations of the causal theory under consideration and the causal mechanisms that it posits. Thus, as long as sufficient evidence is accessible for congruence tests and process tracing, case study researchers have the means to resolve the degrees of freedom problem. (KKV, 1994:119-120) Instead of arguing over whether there is an inherent degrees of freedom problem in case study methods, methodological critiques can focus on whether in a particular study a researcher has generated enough process-tracing and congruence predictions and tested them against sufficient data to make valid inferences.

At the same time that they have allayed the standard degrees of freedom criticism of case studies, however, KKV have suggested that case studies suffer from the exact opposite of the degrees of freedom problem. In this view, "there always exists in the social sciences an infinity of causal steps between any two links in the chain of causal mechanisms," raising the danger of an "infinite regress" in process tracing. (KKV 1994:86) Thus, ironically, case studies have been criticized for drawing on data that some see as too scarce and others wrry is potentially infinite. In fact, however, the resolution of the "infinite regress" problem is no more difficult than the problem of selecting from among the infinite possible hypotheses and observations to be used in studies of covariance. The domains of hypotheses to be traced and observations to be used are restricted by the definition of research objectives, the selection of the levels of analysis that are of interest, the relevant body of alternative hypotheses on the relationship under study, and the distinction between enabling variables and immediate causes. Thus, it is not necessary to examine all links between links. (Sayer, 1992: 120, Yee, 1996:84)

There are two other constraints on process tracing that pose more telling limits on its actual practice. Process tracing provides a strong basis for causal inference only if it can be established whether an uninterrupted causal path existed linking the putative causes to the observed effects, at the appropriate level(s) of analysis as specified by the theory being tested. Evidence that a single necessary intervening variable along this path was contrary to expectations strongly impugns any hypothesis whose causal affects rely on that causal path alone. The inferential and explanatory value of a causal path is weakened, though not negated, if the evidence on whether a certain step in the putative causal path conformed to expectations is simply unobtainable. Also, theories frequently do not make specific predictions on all of the steps in a causal process, particularly for complex phenomena. When data is unavailable or theories are indeterminate, process verification can reach only provisional conclusions.

Another potential problem for process tracing is that there may be more than one hypothesized causal mechanism consistent with any given set of process tracing evidence. When this problem of indeterminacy arises, there is no absolute standard for excluding alternative hypotheses that may be spurious. (Njolstad, 1990; Achen and Snidal 1989:156-157)) There are only empirical, methodological (Lakatos, 1976), aesthetic, analytical (Ikenberry, 1989: 10), and sociological (Kuhn, 1970) criteria for selecting hypotheses, testing them, strengthening or infirming them on the basis of the evidence, and modifying them. There are no absolute means of proving or disproving theories or establishing that changes in these theories are progressive rather than regressive. Still, even if it is not possible to exclude all but one hypothesis as a potential explanation for a particular case, it may possible to exclude at least some hypotheses and draw inferences that are useful for theory-building and/or policymaking.

2. Cases "Representativeness" of Wider Populations

Statistical methods require a large sample of cases that is representative of and allows inferences about an even wider population of cases. To get such a representative sample, statistical studies often rely on random selection of cases. While useful and necessary in statistical studies, these requirements and practices are inappropriate and counterproductive when extended to case study methods or used to judge these methods, as some methodologists have urged (Lieberson, 1992:108-9, 113, 116; Achen and Snidal, 1989:160-1)

Case study researchers do not aspire to select cases that are "representative" of diverse populations and they do not make claims that their findings are applicable to such populations. Instead, these researchers seek only contingent generalizations that apply to cases that are similar in the values of their variables to the types of cases under study. (George and Smoke, 1989: 171; Bennett and George, 1997:12). Ideally, these contingent generalizations will cumulate into typological theories which address the causal dynamics of many different types of a phenomenon or different causal paths to the outcomes of interest, but each generalization is by itself still contingent. Case study researchers are more interested in finding out the conditions under which specified outcomes occur than the frequency with which those conditions and their outcomes arise. (Bennett and George, 1997:13)

In fact, case study researchers may sometimes deliberately select cases that are infrequent and unrepresentative, particularly "deviant" cases, or those cases whose outcomes do not match the expectations of established theories. Such cases may embody previously unexplored causal paths, and they may call attention to variables that are left out by the leading theories.(Bennett and George, 1997:12) Thus, statistical researchers sometimes tend to view "outlier" data points as problematic because they do not fit the model or theory in question but are too few in number to be analyzed by statistical techniques, but case study researchers see such outliers (so long as they are not caused by simple measurement error) as potential opportunities for theory building.

There is one sense, however, in which case studies may occasionally lead to inferences on the likelihood or frequency of possible cases, as opposed to that of actual cases. When case studies lead to fully developed and empirically supported typological theories, they may provide a sense of what types of cases are possible even though they have not yet occurred, and what types of cases are unlikely even though they have taken place. Particularly for low probability causal mechanisms that result in a small number of historical cases, the frequency distribution of actual cases may be very different from that of the possible or likely cases. Process tracing and typological theories built upon an understanding of the underlying causal mechanisms can provide information on the extent to which the outcome of a case depended on an unlikely combination of variables. For example, one could construct a "representative" sample of different kinds of hands in five card draw poker, as a statistical researcher might. However, this could greatly overstate the likelihood of the rare hands, like straight flushes, if someone got lucky, or it would more likely understate their probability, unless a huge number of games were sampled. Alternatively, a researcher aware of the probabilities of drawing certain kinds of cards, and the strategies of the players, could construct a typological theory that estimates the probability of straight flushes even if one has not yet occurred. Of course, social theories are almost never as reliable or precise as our knowledge of card games, but good typological theories, like more purely deductive theories such as game theory, may point out that cases that have not yet occurred are socially possible and perhaps equally likely as those that have taken place.

The issue of "representativeness" is closely related to that of "selection bias." The problem of "representativeness" relates to making claims that cases represent wider or different populations than they actually do, while selection bias relates to unwittingly choosing for study cases whose outcomes are biased or "represent" a skewed population. The issue of selection bias is taken up in detail below in section 6.

3. Cases "Independence" of One Another

A third issue, related to that of degrees of freedom, concerns whether cases are "independent" of one another. If an empirical relationship observed in several cases is the result not of the hypotheses under consideration but of learning or diffusion from one case to the others, then the additional cases do not provide new information, there are fewer degrees of freedom, and there is a danger of spurious correlation. (George, 1982: 19-23; KKV, 1994:222) This problem of the independence of cases is sometimes referred to as "Galton's problem." There is indeed a danger of this problem in case study research, but it is not inherent in case studies and it is not necessarily amplified by the intentional selection of cases based on a preliminary knowledge of their variables (indeed, such intentional selection may be designed specifically to address the issue of the independence of cases). As Alexander George has argued, the question of whether the independence of cases is a relevant consideration is not a question that can be answered "on a priori grounds; the answer surely depends on the research objectives of a particular study, what theory or hypothesis is being developed, and how the comparison of cases is structured." (George, 1982:21) As George notes, methods of within-case analysis, particularly process tracing, reduce the dangers of any unanticipated lack of independence of cases. When learning or diffusion processes are anticipated, studied empirically, and accounted for, they need not invalidate cases that are to some extent dependent. Indeed, only cases that are perfectly dependent provide no additional information. (KKV, 1994:222) Moreover, as George notes, case study methods can be particularly effective at examining precisely the kinds of learning and diffusion processes that give rise to Galton's problem, which can allow researchers to gauge more accurately how much of the variance in outcomes is explained by learning or diffusion and how much is explained by other variables. (George, 1982: 21).

4. Case Studies' Use of Mill's Methods

Case study methods have frequently been criticized for their use of John Stuart Mill's "method of agreement" and his "method of difference." (Lieberson, 1992, 1994, Little, 1995; Nichols, 1996) However, Mill's methods of comparison are only one source of inference in case studies and are almost never used alone, yet commentators have attributed to case studies all of the well-known limits that Mill and others have identified regarding his methods. In fact, the use of typological theories (Bennett and George, 1997), together with methods of within-case analysis such as congruence testing and process tracing, can compensate for many of the limits of Mill's methods, even though it cannot eliminate them entirely.

In general, this is because case study methods are theory-driven rather than blindly empirical. Without prior theories, or at least proto-theories, it is impossible to select which of the thousands of facts about cases should be analyzed for purposes of comparison or within-case analysis. Case comparisons, congruence testing, and process tracing are all set up by prior theories, and their results should be weighted or discounted by our existing level of confidence in these theories. This, together with methodological standards for progressive theorizing (Lakatos, 1976), provides safeguards against the potential pitfalls of Mill's methods.

The key limitation of Mill's methods, which Mill himself identified, is that they cannot work well in the presence of equifinality. Put another way, Mill's methods can work well at identifying underlying causal relations only under three very strong conditions. First, the causal relations being investigated must be deterministic regularities involving conditions that are either necessary or sufficient for a specified outcome. Second, all causally-relevant variables must be identified prior to the analysis. Third, there must be available for study cases that represent the full range of all logically and socially possible causal paths. (Little, 1996; Lieberson 1994, George and McKeown, 1985)

Clearly, these strong assumptions seldom hold true. However, typological theorizing and case study methods do not require such stringent conditions. Let us consider each condition in turn. First, typological theories address the problem of equifinality directly, acknowledging and even taking advantage of the fact that there may be different causal paths to similar outcomes. The inductive development of typological theory attempts to map out the different causal paths, while the deductive development of typological theory attempts to provide theoretical reasons why particular conjunctions of variables lead to particular outcomes. Case study methods do not require causal relations of necessity and sufficiency, although case study methods -- like all methods -- offer stronger inferences on the existence of such relations than on that of equifinality or probabilistic causality. (Dion, 1997)

In addition, as long as all relevant variables are included in a typology, that typology inherently reflects interactions effects, even when those effects are not fully identified or understood by the researcher. Some critics of case study methods have suggested otherwise, arguing that these methods cannot incorporate interactions effects. (Lieberson, 1992:109-113) In fact, the logic of case study methods and the notions of causality associated with them have made case study researchers very attentive to interactions effects. (Ragin, 1987). If there are no measurement errors and there are deterministic or very high probability processes involved, admittedly two big assumptions, then two typologically similar cases, or cases with highly similar values on their independent variables, will have the same outcome, even if the interactions among the variables are caused that outcome are not fully understood or specified. Thus, we can have accurate predictions without accurate explanations, or the problem of spuriousness. For some research objectives, such as policy-makers' use of typologies, this may be acceptable, while for others, such as explanation by reference to causal mechanisms, it is not. Typological theorizing, as opposed to the simple use of typologies, pushes theorists to try to anticipate and explain interactions effects, although there is no guarantee that they will do so adequately. Process tracing and cross-case comparisons, though still fallible, may help identify which interactions are causal and which are spurious.

The second limitation of Mill's methods, the problem of left-out variables, is discussed in detail in section 8 below and need not be presented fully here. Briefly, the cases study researchers' approach is to identify possible left-out variables through process tracing. This reduces the likelihood of left-out variables, even though it does not reduce their consequences if they are not discovered through process tracing.

The third limitation on Mill's methods, the requirement of having available for study cases representing all logically and socially possible causal paths, is a more binding constraint on case study methods. Causal inferences are indeed stronger when extant cases cover more of the typological space. Even so, having all possible types of cases available for study, while desirable, is not necessary. Not all research designs or research objectives require a diverse range of cases. Single cases, if they are most-likely, least-likely, or especially crucial cases, can be quite revealing about the strength of a theory. Comparisons of a few cases, if they are most similar or least similar, can also be revealing. Some cases provide more information than others on the theoretical issues of interest to a particular researcher. Moreover, for some research objectives, there may be cases for study representing most or even all of the possible types. The extant cases may also provide diverse causal paths even if the cases for any one causal path are not numerous enough for statistical methods.

Perhaps the most important difference between Mill's methods and case study methods in all three of the areas discussed immediately above is that case study methods can use within-case analyses, particularly process tracing, to ameliorate the limits of Mill's methods. Process tracing can identify different causal paths to an outcome, point out variables that otherwise might be left out, check for spuriousness, and allow causal inferences on the basis of a few cases or even a single case. These potential contributions of process tracing make case studies worthwhile even when sufficient cases exist for the use of statistical methods. Sophisticated critiques of case study methods acknowledge the value of process tracing. For example, Daniel Little, while more pessimistic than we are on the possibilities for typological theorizing, notes that such theorizing can be strengthened by the use of empirically supported social theories to establish hypothesized causal linkages that can then be tested through process tracing. As an example, Little notes that Theda Skocpol's work on social revolutions, in addition to traditional comparative analysis based on Mill's methods, uses established social theories in this manner. (Little, 1995:54)

5. Causal Effects and Causal Mechanisms as Bases for Causal Inferences

Tests of covariations between observed outcome variables and their hypothesized causal variables, whether they take the form of case study congruence tests or statistical correlations among many cases, involve efforts to estimate the causal effects of variables. The causal effect of an explanatory variable is defined here as the change in the probability and/or value of the dependent variable that would have occurred if the explanatory variable had assumed a different value. Because this is a counterfactual definition -- regarding what would have happened if one variable had been different and all others had been held the same -- it raises what has been termed the "fundamental problem of causal inference." (KKV p. 79, following Holland, 1986) This problem derives from that fact that we cannot re-run history and change only one variable in a perfect experiment that would allow us to observe the actual causal effect of that variable. Tests of covariation are an avowedly imperfect alternative to perfect experiments. These tests try to measure causal effects by controlling for the effects of variables other than the variable of interest. In correlational studies, this control is attempted through statistical methods that use large numbers of observations to estimate the partial correlations between each independent variable and the dependent variable. In case studies, the method of congruence testing attempts to control for all but one independent variable at a time by using theories to create expectations about the dependent variable that can be compared to its actual value. (George, 1997) These methods of estimating covariations are limited in ways both similar and different.

Congruence testing and statistical correlations are useful components of broader means of making causal inferences, but because covariations have important and well-known limitations as sources of causal inference, philosophers of science and social science methodologists have given increasing emphasis in the last two decades to causal mechanisms as a second basis for causal inferences. (Sayer, 1992: 104-105; Dessler, 1991: 343; Miller, 1987: 139; Yee, 1996; Salmon, 1989; Marini and Singer, 1988) Causal mechanisms are defined here as the causal processes and intervening variables through which causal or explanatory variables produce causal effects. While the notion of causal mechanisms is often explicated in terms of physical causal processes, it is applicable as well to social processes, including intentions, expectations, information, small group and bureaucratic decisionmaking dynamics, coalition dynamics, strategic interaction, and so on. (Little, 1995)

It is interesting to note that of the three sources of causal inferences recognized by the philosopher David Hume, covariance, which Hume termed "constant conjunction," was only one. The other two, temporal succession and contiguity, relate to what modern philosophers of science consider to be causal mechanisms. One school of thought in particular, self-designated among philosophers of science and methodologists as the "scientific realist" school, has defined itself in part by the view that covariation has been over-emphasized relative to causal mechanisms as a source of causal inferences. David Dessler, for example, has argued that (1991:345):

the "why?" question is construed as meaning, "By the workings of what structures is the phenomenon produced?" Here events are distinct from the structures that produce them, so causation cannot be dismissed or reduced to behavioral regularity. . . Recall that at the correlational level we cannot differentiate between causal and accidental sequences, nor can we conceptually distinguish the correlates of an event that are its causes (say, a cold front and a thunderstorm) from those that are not (say, a falling barometer and a thunderstorm).

Similarly, the philosopher of science Andrew Sayer has stated that "what we would like . . . is a knowledge of how the process works. Merely knowing that 'C' has generally been followed by 'E' is not enough; we want to understand the continuous process by which 'C' produced 'E,' if it did." (Sayer, 1992: 106-107) Sayer adds that whether the causal powers inherent in a variable are activiated in a particular case depends on the presence of contingent conditions. Because such contingent conditions and counteracting forces can ennable, conceal, or override the causal powers of a variable, he argues, "the discovery of what a given mechanism can and cannot do requires considerable effort and ingenuity and . . . the search for regularities is inadequate." (Sayer, 1992: 110) In short, an adequate scientific explanation must include both arguments and measures on the causal effect of an independent variable and the hypothesized and observed causal mechanisms through which it achieves this effect.

In this view, new and more sophisticated statistical methods, and the philosophy of science notions of probabilistic causality that underly them, are not by themselves sufficient for defining causal explanations, nor can they rectify the inherent limits of covariation as the observational basis for causal inference. Wesley Salmon, a philosopher of science who has played an important role in the development of notions of probabilistic causality, came to this conclusion after surveying three prominent theories of probabilistic causality in the mid-1980s. He later noted that "the primary moral I drew was that causal concepts cannot be fully explicated in terms of statistical relationships; in addition, I concluded, we need to appeal to causal processes and causal interactions." (Salmon, 1989: 168, citing Suppes, 1970, Reichenbach 1956, and Good, 1961-2) New statistical methods have allowed more sophisticated modelling of non-linear processes and interaction effects, and some computer methods even suggest possible model specifications. However, none of these methods, which generally allow for tighter correlations between data and theoretical models, shows promise of addressing the version of the fundamental problem of inference that applies to statistical and other methods of assessing covariations: observed correlations do not provide a solid basis for inferring underlying causality.

For scientific realists, the disjuncture between correlation and causality is related to but not synonomous with that between "explanation" and "prediction." Because the ability to predict does not necessarily provide a satisfactory explanation to the causal "Why?" question, it is possible to have non-predictive explanations (as in the theory of evolution) and non-explanatory predictions (such as the use of barometer readings to predict the weather). (Sayer, 1992: 131-132; Salmon, 1989: 129-130) Causal mechanisms are also relevant to policy interventions because the ability to predict outcomes may not confer the ability to affect them through manipulable variables. For example, even if it continues to hold up to empirical scrutiny, the observed correlation that democracies do not engage in wars with one another even though they have frequently fought wars against non-democratic states is only a starting point for policy prescriptions. It would be best to understand both the causal mechanisms behind the apparent democratic peace and those behind the emergence of democracy, and to identify those mechanisms that policy interventions can affect. Indeed, some studies suggest that transitional democracies are quite war-prone and may fight other democracies (Snyder and Mansfield, 1995) Similarly, microbiologists devote great attention to understanding the causal mechanisms behind cancer, AIDs, and other diseases so that they can establish more options for appropriate interventions at various points in the causal process. In these instances, it should be noted, knowledge of causal mechanisms can be of practical use even when the entire causal process or path is not fully understood.

None of the above should be taken as suggesting in any way that causal effects are not relevant to definitions of causality, or that attempts to observe covariations are not relevant to making causal inferences. Causal effects and causal mechanisms are both essential to the definition of causality and attempts to make causal inferences. A subtle but important debate has emerged on this issue that obscures this central point. On one side, some have attempted to address causality and explanation primarily in terms of causal effects, while downplaying the status of causal mechanisms. For example, KKV argue that their definition of causal effect, similar to that adopted here,

is logically prior to the identification of causal mechanisms . . .we can define a causal effect without understanding all of the causal mechanisms involved, but we cannot identify causal mechanisms without defining the concept of causal effect .. . Identifying causal mechanisms can sometimes give us more leverage over a theory by making observations at a different level of analysis into implications of the theory. The concept can also create new causal hypotheses to investigate. However, we should not confuse a definition of causality with the nondefinitional, albeit often useful, operational procedure of identifying causal mechanisms. (1994: 86)

While this view recognizes that identification of causal mechanisms can play a role in both testing theories and developing hypotheses, it risks conflating the definition of "causality" with the definition of "causal effect" and relegating the identification of causal mechanisms to an inferior, "operational" status. The observation of putative causal mechanisms, through process tracing, is indeed an operational procedure, just as methods of examining covariations are operational procedures for assessing the observable analogues of causal effect. The final sentence in the passage quoted above could be easily transposed to read, with equal authority, "we should not confuse a definition of causality with the nondefinitional, albeit often useful, operational procedure of estimating observed covariations." Methodological procedures and ontological definitions should indeed not be conflated. Both causal mechanisms and causal effects are theoretical entities that are central to notions of causality and explanation. A variable cannot have a causal effect on an outcome unless there is an underlying causal mechanism, and it makes no sense to define any entity as a causal mechanism if it has no causal effect.

An opposite and equally misleading practice is to accord causal mechanisms a status that is somehow superior to that of causal affects. Albert Yee risks adopting this approach when, in citing and responding to the passage from KKV quoted above, he states that "causal mechanisms and capacities are ontologically prior to, and account for, both statistical associations and controlled experimental results." (Yee, 1996:84) This sentence, while defensible, does not improve upon the passage that it seeks to refute. The debate over whether causal effects are "definitionally" prior to causal mechanisms, as KKV argue, or causal mechanisms are "ontologically" prior to causal effects, as Yee maintains, misses the more fundamental point that both are essential to causality, explantion, and the building and testing of explanatory social theories.

This would be a harmless debate of the chicken and egg variety were it not for the fact that it entails, on each side, the inclination to priviledge the particular methodology that is best suited to addressing the element of causality that each side favors. Large N statistical studies are strongest at documenting partial correlations that attempt to measure causal effects as one basis for causal inference. Yee argues that the analysis of symbolic discourse is useful for identifying causal mechanisms related to the causal role of ideas. Similarly, in case study methods, the identification of causal mechanisms through process tracing is a stronger methodological basis for causal inferences than the estimation of covariation through congruence tests. Different methods do indeed present different strengths and weaknesses in attempting to measure either causal effects or causal mechanisms. But this does not suggest that definitions of causality should be driven by researchers' choice of methods. Rather, causality involves both causal effects and causal mechanisms and its study requires a diversity of methods, of which some are better adapted to the former and some to the latter. The search for causal explanations in any given research project can focus on either causal effects or causal mechanisms alone or on both together, but research programs as a whole, if they aspire to be progressive, should include efforts to link the two.

A related problem has arisen in the context of deductive theories, particularly rational choice theories. Some rational choice theorists have argued that their theories can be treated as causal explanations for particular cases even if the causal mechanisms that these theories posit were not observably present in these cases. Christopher Achen and Duncan Snidal, for example, have argued that "rational deterrence [theory] is agnostic about the actual calculations that decision makers undertake. It holds that they will act as if they solved certain mathematical problems, whether or not they actually solve them." (Achen and Snidal, 1989: 164) Similarly, John Ferejohn and Debra Satz have argued that "a successful social-science explanation presupposes that the behavior in question be describable as being intentionally brought about by human agents seeking goals and holding beliefs," but they add in a footnote that "this constraint does not require that the behavior in question was actually brought about intentionally, and certainly not that it was done consciously; it requires only that it could be described as having been done in that way." (Ferejohn and Satz, 1995:74, and footnote 3, p.83, their emphasis). Such formulations fail to recognize the distinction between prediction and explanation: even if rational choice theories do achieve impressive predictive performance, this does not inherently mean that they are useful causal explanations. Well-defined causal mechanisms that are consistent with the available process-tracing evidence are essential for explanations of individual behavior, just as theories of weather formation are necessary to explain why the barometer is a good predictor of weather. Rational choice theories, like other deductive theories, cannot be exempted from empirical tests against observed causal mechansims, particularly since alternative psychological theories of individual behavior make profoundly different assumptions and do hold themselves up to the empirical standard of consistency with observed decision-making processes and outcomes.

6. "Selection Bias"

One of the most common critiques of case study methods is that they are particularly or even inherently prone to the versions of "selection bias" discussed by statistical researchers. KKV warn categorically against the "dangers" of selection bias in research design, and Achen and Snidal term selection bias an "inferential felony" in case study research. (KKV, 1994: 116, 128-149; Achen and Snidal, 1989: 160; see also Geddes, 1990) Selection bias, in statistical parlance, " is commonly understood as occuring when some form of selection process in either the design of the study or the real-world phenomena under investigation results in inferences that suffer from systematic error." (Collier and Mahoney, 1996: 59) Such biases can occur when cases or subjects are self-selected, or when the researcher unwittingly selects cases that represent a truncated sample along the dependent variable of the relevant universe of cases. (Collier and Mahoney, 1996:60; KKV 128-132)

A simple graph helps illustrate the problem of selection bias as commonly understood by statistical researchers. In Figure 1, the x-axis measures values on the independent variable, the y-axis measures values on the dependent variable, and the letters A, B, D, L, and M represent the total population of cases for the phenomenon under study. If for some reason the researcher has unwittingly truncated the sample of cases to be studied to include only those whose dependent variable is above or below an extreme value (in this illustration, equal to or greater than Y', the dotted line), then an estimate of the regression slope for this truncated sample (represented here by the line Z to Z'') will be biased toward zero. In other words, in this view selection bias always understates the strength of the relationship between the independent and dependent variables. The source of the bias is the selection of cases based on the value of the dependent variable; selection based on some truncated sample by values of the independent variable would not result in systematic bias of the estimated regression slope. (Collier and Mahoney, 1996:60)

Figure 1

This is the reasoning behind the categorical injunctions issued to case study researchers against various forms of selection on the dependent variable. Some critics have even argued that single case studies, even crucial ones, cannot test theories (KKV, 1994: 209-211) However, numerous practitioners and analysts of case study methods have argued that selection on the dependent variable and single-case research designs should not be rejected out of hand. Cases selected on the dependent variable, including single case studies, can serve to identify which variables are not necessary or sufficient conditions for the selected outcome (Dion, 1997; Collier, 1995:464)

In addition, most of the value of single case studies comes from their juxtaposition against existing theories. When a single case study goes against an accepted theory and indicates that a supposedly "necessary" condition is not necessary, this is significant. Single cases that are most-likely, least-likely, or deviant can provide greater feedback on theories than large numbers of cases that do not fit any of these criteria. Graphically, in Figure 1, the researcher might focus on the deviant case D, or the most similar cases M, or least similar cases L. In all these research designs, identifying left-out variables is an important objective. Why is there the same outcome in the cases L, despite different values of X? Why are the outcomes in cases M different, despite the same values of X? Why is case D so far from the rest of the population? Many of the most influential research findings in political science have come from single case studies that raised such questions and presented anomalies for accepted theories (Rogowski, 1995).

Of course, ideally, researchers would have the functional equivalent of a controlled experiment, with controlled variation in independent variables and resulting variation in dependent variables. One such case study research design would involve two cases that are perfectly similar in all but one independent variable and the dependent variable. Another, less pure example would be a typological theory for which suitable cases exist in every relevant and socially possible type. However, the requisite cases for such research designs seldom exist (although researchers may try to approximate them while acknowledging the remaining imperfections). This is why case study researchers turn to single or multiple case study designs that may or may not have variation on the independent or dependent variables.

It is true that single-case or no-variance research designs give up an important source of inferences by foregoing the opportunity to analyze covariance of the dependent variable. However, the logic of inferences made from such cases intentionally relies on sources of inference other than covariation, such as within-case analysis. As one review of the selection bias issue in qualitative research concluded, the forfeiture of analysis of covariance "is hardly an appropriate basis for the kind of emphatic rejection of no-variance designs offered by King, Keohane, and Verba. We are convinced that these designs are better evaluated from alternative viewpoints offered in the literature on comparative method and small-N analysis." (Collier and Mahoney, 1996:73).

A related issue is whether foreknowledge of the values of variables in cases, and perhaps researchers' cognitive biases in favor of particular hypotheses, necessarily bias the selection of case studies. The standard protection against this bias in statistical studies is random selection, but as KKV note, in studies of a small number of cases, random selection can result in even worse biases than intentional selection. (KKV, 1994:124-7) More generally, selection with some preliminary knowledge of cases allows much stronger research designs, as cases can be selected with a view toward whether they are most likely, least likely, or crucial, and whether they are suited for plausibility probes, theory testing, or other purposes. In addition, intentional selection of cases can benefit from knowledge of the findings of exisiting studies, and it can be guided by estimations of whether the theories of interest are strong and previously-tested or new and relatively weak. (Laitin, 1995:456) There are also methodological safeguards against investigator-induced bias in case studies, as careful congruence testing and process tracing often result in the finding that the researcher's (or the literature's) preliminary knowlege of the values of certain variables was incomplete or simply wrong, and case study researchers sometimes conclude that none of the proposed theories are adequate explanations of a case. (Campbell, 1975)

A different kind of problem, related to the discussion above of cases' representativeness of wider populations, can arise if case study researchers overstate the generality of their theories. Case study researchers must be careful to limit their claims to contingent generalizations and to limit or identify as speculative any generalizations beyond the typological categories of the cases they have studied. Contingent generalizations extend only among cases that are typologically similar, that is, that have the same or roughly the same values on the specified variables. In some instances, however, critiques of particular case studies have overstated the problems of representativeness and selection bias by assuming that these studies have purported to offer generalizations that cover broad populations, whereas in fact these studies carefully circumscribed their claims to apply them only to cases similar to those studied. (Collier and Mahoney, 1996: 80-87 make this critique of Barbara Geddes's (1990) review of case studies and selection bias)

It is true that even if they are seeking only contingent generalizations, case study researchers in many instances should make comparisons between the subset of cases or types studied and the larger population, where there is more variance on the dependent variable. (Collier and Mahoney, 1996:63) Sometimes, such comparisons can be made to existing case studies in the literature, or the researcher might include "mini-case" studies, or less in-depth studies, of a wide number of cases in addition to full studies of the caes of greatest interest. A key requirement of the relevance of such comparisons, however, is that there be a theoretical basis for assuming that there is causal homogeneity across the groups of cases being compared. As Collier and Mahoney note,

It is unrealistic to expect qualitative researchers, in their effort to avoid selection bias, to make comparisons across contexts that may reasonably be thought to encompass heterogeneous causal relations. Given the tools that they have for causal inference, it may be more appropriate for them to focus on a more homogenous set of cases, even at the cost of narrowing the comparison in a way that may introduce problems of selection bias. (1996: 68-69)

Perhaps the greatest shortcoming of the application of statistical views of selection bias to case studies, however, is that they understate both the most severe and the most common kinds of selection biases in qualitative research. The potential case study selection bias with the most damaging consequences arises from selecting only those cases whose independent and dependent variables vary as the favored hypothesis suggests, ignoring cases that appear to contradict the theory, and overgeneralizing from the cases selected to wider populations. This type of selection bias can occur even when the traditional warnings against selection bias have not been violated; that is, even when there is variation on both independent and dependent variables, and even when this variation covers the full range of values that these variables can assume. Rather than understating the relationship between independent and dependen variables, as in the traditional statistical view of selection bias, this selection bias can understate or overstate the relationship. (Collier and Mahoney, 1996:71-72) The graphical example in Figure 1 makes this obvious: selecting the "A" cases results in bias in one direction, the "B" cases in another.

This error of selecting cases where both independent and dependent variables just happen to fit the hypothesis seems almost too obvious to mention, but case researchers may fail to realize that by implicitly or explicitly limiting their universe of cases (say, to history that is contemporary, Western, specific to one country, or easily-researchable), they have biased their sample.

While this is the most dangerous kind of selection bias, it is far more common in political argumentation than in social science case studies. Several other biases, however, are quite common in case study selection, but they have not been an important focus of statistical researchers' critiques of case studies. These include selection of cases based on extreme values (in a different sense from that used above), on the availability of evidence, and on the cases' "intrinsic" historical importance. Stephen Van Evera has raised each of these as criteria for the selection of particular cases, and each does have value. (Van Evera, 1996: 42-49) However, there is also a risk in emphasizing these criteria to the exclusion of other standards. Selection of cases based on extreme values may allow researchers to isolate the effects of particular variables or to identify unique causal paths, but if researchers are not vigilant in reminding others (and themselves) that they are working on an extremely truncated sample, their results may be over-generalized. (Collier and Mahoney, 71) Selection on the basis of easily obtainable evidence is useful if all other factors are equal. However, if it is allowed to override other criteria, it risks repeating the fallacy of the drunk who looks for his car keys by the light post not because he dropped them there, but because that is where the light is. Finally, selection of intrinsically important cases should not be allowed to supercede criteria on which cases are likely to be the most theoretically informative. Research programs as a whole often reflect a combination of all three biases. For example, there are far more studies of the great powers' military strategies in major wars than of small powers' strategies in minor wars, even though the latter may be equally informative on such issues as the role of technology or organizational culture in military strategy. Van Evera in fact offers many criteria for selecting the most theoretically informative cases, including cases with large within-case variance, cases about which competing theories make opposite and unique predictions, cases that are well-matched for controlled comparisons, outlier cases, and cases whose results can be replicated. These criteria present fewer complications than those of extreme values, data availability, and intrinsic importance.

7. Cell Reduction

Critiques of case study methods have often urged that researchers should wherever possible engage in cell reduction, or the inclusion of greater numbers of cases in fewer and more general cells. Such cell reduction may be driven by the desire for broader generalizations, but it is all too often motivated by a desire to achieve higher degrees of freedom so that statistical analysis is possible. (KKV, 1994: 217-228; Lijphart, 1971) This latter incentive for cell reduction is exactly counter to the purposes and logic of case study methods. Case study methods are designed in part to address the possibility that equifinality, or the presence of alternative causal paths to similar outcomes, may characterize many social phenomena. The goal of case study research, and particularly of the typological theories to which case studies contribute, is to map out the range of causal paths for a phenomenon and to identify their causal mechanisms and the conditions under which they occur. This often requires differentiating types of variables or paths, rather than aggregrating them together into larger and more general categories.

Moreover, as noted above, case study researchers often address the degrees of freedom problem not by studying more cases, but by generating more process tracing evidence on the observable implications of theories. Even though each new independent variable or theory requires additional evidence, it also generates more process-tracing predictions, so there is not necessarily a tight limit on the number of cells that can be considered. A more constraining tradeoff is that a greater number of variables or cells increases the complexity of typological theories. A typology with N dichotomous variables has two to the power of N possible types. As N gets larger than six or so, it quickly becomes difficult for researchers or their readers to research, understand, or remember the numerous types. Fortunately, not all types or cells are equally informative theoretically or possible socially, and in practice, researchers may be able to narrow the number of relevant types without resorting to cell reduction (Bennett and George, 1997) An additional practical bound on the number of cells or types is the theoretical or policy relevance of the phenomenon under study. The more important the phenomenon, the more cells researchers will be willing to define and explore.

8. Left-out Variables

Several critiques have argued that left-out variables can be particularly damaging to case study methods. (Lieberson, 1992, 1994, Little, 1995) Some kinds of case study methods, particularly cross-case comparisons related to Mill's methods, are indeed vulnerable to left-out variables, as are all methods. However, relevant independent variables are less likely to be left out of case study research designs than statistical designs for two reasons. First, the tension between degrees of freedom and left-out variable bias, acknowledged by statistical researchers (KKV, 1994, 123) is less of a Faustian bargain for case studies than for statistical studies. Because case study researchers do not face an unyielding constraint on degrees of freedom and can generate process tracing evidence, they face fewer incentives to leave out variables that might play a small but causal role. Second, because process tracing methods are partly inductive, case study researchers are more likely than statistical researchers to identify variables that have been left out of previous studies. One of the most important contributions of case studies over time, in fact, has been the identification of new variables, types, and levels of analysis relevant to specific research programs. In the deterrence literature, for example, case studies have added psychological dynamics and domestic politics to problems that had previously been viewed primarily through the prism of rational choice theories. (George and Smoke, 1989)

Conclusions

Critiques of case study methods through the prism of statistical concepts have often misconstrued the strengths and weaknesses of case studies. On the issues of degrees of freedom, "representativeness," independence of cases, uses of Mills' methods, the role of causal mechanisms, cell reduction, and left-out variables, case studies are generally stronger than their critics have suggested. On the question of case selection and selection bias, standard statistical critiques have overstated some methodological problems but understated others. The most constraining limits of case study methods -- the problem of getting a range of cases for study that covers many of the possible causal paths or types, the problem of addressing low-probability causal relations, and the problem of interpreting outcomes and processes that are consistent with more than one theory -- have received less attention because they do not fit as readily into statistical terms (exceptions are Little, 1995, Lieberson, 1992, 1994, Ragin, 1987, and Njolstad)

The choice of methods depends on many factors, not just the availability of evidence or cases. These factors include the research objective, the state of development of the research program, and the nature of the hypothesized causal processes at work. Differences in sample size -- the large N versus small n divide -- are only one of the many differences between quantitative and qualitative methods, and they are not necessarily the most salient or interesting difference. While it is true that case study methods are the only alternative when only a small number of cases exists, this is not the sole nor even the strongest justification for case study methods. The main advantage of case study methods is their superior ability to trace causal mechanisms and identify left-out variables. This makes case study methods valuable in the study of many phenomena for which the number of cases is also sufficient for statistical analysis, and it imparts to case studies a methodological logic of their own. The contributions and quality of case studies should be judged by this methodological logic, and not by those of other methods.

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Note *: This paper is a preliminary discussion of material that will appear in a book on the use of case studies for theory development, co-authored by Andrew Bennett, Georgetown University, and Alexander George, Stanford University. The book will also include material from two other papers being presented in Toronto: A. L. George, "The Role of the Congruence Method for Case Study Research," and A. Bennett and A. L. George, "Developing and Using Typological Theories in Case Study Research." Some of the discussions in the present paper, particularly on "representativeness," Mill's methods, left-out variables, and cell reduction, parallel sections of these related conference papers, and are included here in part for the convenience of addressing in one place the common critiques of case study methods. Additional material being prepared for the book addresses such topics as structured focused comparison, research design, criteria for selection of cases, lessons learned from past uses of case studies for theory development, and other issues. Back.

Note **: Andrew Bennett, Georgetown University Back.