3.5.2 Rule 2: Build Theories That Are Internally Consistent.

A theory which is internally inconsistent is not only falsifiable-it is false. Indeed, this is the only situation where the veracity of a theory is known without any empirical evidence: if two or more parts of a theory generate hypotheses that contradict one another, then no evidence from the empirical world can uphold the theory. Ensuring that theories are internally consistent should be entirely uncontroversial, but consistency is frequently difficult to achieve. One method of producing internally consistent theories is with formal, mathematical modeling. Formal modeling is a practice most developed in economics but increasingly common in sociology, psychology, political science, anthropology, and elsewhere (see Ordeshook 1986). In political science, scholars have built numerous substantive theories from mathematical models in rational choice, social choice, spatial models of elections, public economics, and game theory. This research has produced many important results, and large numbers of plausible hypotheses. One of the most important contributions of formal modeling is revealing the internal inconsistency in verbally stated theories.

However, as with other hypotheses, formal models do not const.i.tute verified explanations without empirical evaluation of their predictions.Formality does help us reason more clearly, and it certainly ensures that our ideas are internally consistent, but it does not resolve issues of empirical evaluation of social science theories. An a.s.sumption in a formal model in the social sciences is generally a convenience for mathematical simplicity or for ensuring that an equilibrium can be found. Few believe that the political world is mathematical in the same way that some physicists believe the physical world is. Thus, formal models are merely models-abstractions that should be distinguished from the world we study. Indeed, some formal theories make predictions that depend on a.s.sumptions that are vastly oversimplified, and these theories are sometimes not of much empirical value. They are only more precise in the abstract than are informal social science theories: they do not make more specific predictions about the real world, since the conditions they specify do not correspond, even approximately, to actual conditions.

Simplifications are essential in formal modeling, as they are in all research, but we need to be cautious about the inferences we can draw about reality from the models. For example, a.s.suming that all omitted variables have no effect on the results can be very useful in modeling. In many of the formal models of qualitative research that we present throughout this book, we do precisely this. a.s.sumptions like this are not usually justified as a feature of the world; they are only offered as a convenient feature of our model of the world. The results, then, apply exactly to the situation in which these omitted variables are irrelevant and may or may not be similar to results in the real world. We do not have to check the a.s.sumption to work out the model and its implications, but it is essential that we check the a.s.sumption during empirical evaluation. The a.s.sumption need not be correct for the formal model to be useful. But we cannot take untested or unjustified theoretical a.s.sumptions and use them in constructing empirical research designs. Instead, we must generally supplement a formal theory with additional features to make it useful for empirical study.

A good formal model should be abstract so that the key features of the problem can be apparent and mathematical reasoning can be easily applied. Consider, then, a formal model of the effect of proportional representation on political party systems, which implies that proportional representation fragments party systems. The key causal variable is the type of electoral system-whether it is a proportional representation system with seats allocated to parties on the basis of their proportion of the vote or a single-member district system in which a single winner is elected in each district. The dependent variable is the number of political parties, often referred to as the degree of party-system fragmentation. The leading hypothesis is that electoral systems based on proportional representation generate more political parties than do district-based electoral systems. For the sake of simplicity, such a model might well include only variables measuring some essential features of the electoral system and the degree of party-system fragmentation. Such a model would generate only a hypothesis, not a conclusion, about the relationship between proportional representation and party-system fragmentation in the real world. Such a hypothesis would have to be tested through the use of qualitative or quant.i.tative empirical methods.

However, even though an implication of this model is that proportional representation fragments political parties, and even though no other variables were used in the model, using only two variables in an empirical a.n.a.lysis would be foolish. A study that indicates that countries with proportional representation have more fragmented party systems would ignore the problem of endogeneity (section 5.4), since countries which establish electoral systems based on a proportional allocation of seats to the parties may well have done so because of their already existent fragmented party systems. Omitted variable bias would also be a problem since countries with deep racial, ethnic, or religious divisions are probably also likely to have fragmented party systems, and countries with divisions of these kinds are more likely to have proportional representation.

Thus, both of the requirements for omitted variable bias (section 5.2) seem to be met: the omitted variable is correlated both with the explanatory and the dependent variable, and any a.n.a.lysis ignoring the variable of social division would therefore produce biased inferences.

The point should be clear: formal models are extremely useful for clarifying our thinking and developing internally consistent theories. For many theories, especially complex, verbally stated theories, it may be that only a formal model is capable of revealing and correcting internal inconsistencies. At the same time, formal models are unlikely to provide the correct empirical model for empirical testing. They certainly do not enable us to avoid any of the empirical problems of scientific inference.

3.5.3 Rule 3: Select Dependent Variables Carefully.

Of course, we should do everything in research carefully, but choosing variables, especially dependent variables, is a particularly important decision. We offer the following three suggestions (based on mistakes that occur all too frequently in the quant.i.tative and qualitative literatures): First, dependent variables should be dependent. A very common mistake is to choose a dependent variable which in fact causes changes in our explanatory variables. We a.n.a.lyze the specific consequences of endogeneity and some ways to circ.u.mvent the problem in section 5.4, but we emphasize it here because the easiest way to avoid it is to choose explanatory variables that are clearly exogenous and dependent variables that are endogenous.

Second, do not select observations based on the dependent variable so that the dependent variable is constant. This, too, may seem a bit obvious, but scholars often choose observations in which the dependent variable does not vary at all (such as in the example discussed in section 4.3.1). Even if we do not deliberately design research so that the dependent variable is constant, it may turn out that way. But, as long as we have not predetermined that fact by our selection criteria, there is no problem. For example, suppose we select observations in two categories of an explanatory variable, and the dependent variable turns out to be constant across the two groups. This is merely a case where the estimated causal effect is zero.

Finally we should choose a dependent variable that represents the variation we wish to explain. Although this point seems obvious, it is actually quite subtle, as ill.u.s.trated by Stanley Lieberson (1985:100):A simple gravitational exhibit at the Ontario Science Centre in Toronto inspires a heuristic example. In the exhibit, a coin and a feather are both released from the top of a vacuum tube and reach the bottom at virtually the same time. Since the vacuum is not a total one, presumably the coin reaches the bottom slightly ahead of the feather. At any rate, suppose we visualize a study in which a variety of objects is dropped without the benefit of such a strong control as a vacuum-just as would occur in nonexperimental social research. If social researchers find that the objects differ in the time that they take to reach the ground, typically they will want to know what characteristics determine these differences. Probably such characteristics of the objects as their density and shape will affect speed of the fall in a nonvacuum situation. If the social researcher is fortunate, such factors together will fully account for all of the differences among the objects in the velocity of their fall. If so, the social researcher will be very happy because all of the variation between objects will be accounted for. The investigator, applying standard social research-thinking will conclude that there is a complete understanding of the phenomenon because all differences among the objects under study have been accounted for. Surely there must be something faulty with our procedures if we can approach such a problem without even considering gravity itself.

The investigator's procedures in this example would be faulty only if the variable of interest were gravity. If gravity were the explanatory variable we cared about, our experiment does not vary it (since the experiment takes place in only one location) and therefore tells us nothing about it. However, the experiment Lieberson describes would be of great interest if we sought to understand variations in the time it will take for different types of objects to hit the ground when they are dropped from the same height under different conditions of air pressure. Indeed, even if we knew all about gravity, this experiment would still yield valuable information. But if, as Lieberson a.s.sumes, we were really interested in an inference about the causal effect of gravity, we would need a dependent variable which varied over observations with differing degrees of gravitational attraction. Likewise, in social science, we must be careful to ensure that we are really interested in understanding our dependent variable, rather than the background factors that our research design holds constant.

Thus, we need the entire range of variation in the dependent variable to be a possible outcome of the experiment in order to obtain an unbiased estimate of the impact of the explanatory variables. Artificial limits on the range or values of the dependent variable produce what we define (in section 4.3) as selection bias. For instance, if we are interested in the conditions under which armed conflict breaks out, we cannot choose as observations only those instances where the result is armed conflict. Such a study might tell us a great deal about variations among observations of armed conflict (as the gravity experiment tells us about variations in speed of fall of various objects) but will not enable us to explore the sources of armed conflict. A better design if we want to understand the sources of armed conflict would be one that selected observations according to our explanatory variables and allowed the dependent variable the possibility of covering the full range from there being little or no threat of a conflict through threat situations to actual conflict.

3.5.4 Rule 4: Maximize Concreteness.

Our fourth rule, which follows from our emphasis on falsifiability, consistency, and variation in the dependent variable is to maximize concreteness. We should choose observable, rather than un.o.bservable, concepts wherever possible. Abstract, un.o.bserved concepts such as utility, culture, intentions, motivations, identification, intelligence, or the national interest are often used in social science theories. They can play a useful role in theory formulation; but they can be a hindrance to empirical evaluation of theories and hypotheses unless they can be defined in a way such that they, or at least their implications, can be observed and measured. Explanations involving concepts such as culture or national interest or utility or motivation are suspect unless we can measure the concept independently of the dependent variable that we are explaining. When such terms are used in explanations, it is too easy to use them in ways that are tautological or have no differentiating, observable implications. An act of an individual or a nation may be explained as resulting from a desire to maximize utility, to fulfill intentions, or to achieve the national interest. But the evidence that the act maximized utility or fulfilled intentions or achieved the national interest is the fact that the actor or the nation engaged in it. It is inc.u.mbent upon the researcher formulating the theory to specify clearly and precisely what observable implications of the theory would indicate its veracity and distinguish it from logical alternatives.

In no way do we mean to imply by this rule that concepts like intentions and motivations are unimportant. We only wish to recognize that the standard for explanation in any empirical science like ours must be empirical verification or falsification. Attempting to find empirical evidence of abstract, unmeasurable, and un.o.bservable concepts will necessarily prove more difficult and less successful than for many imperfectly conceived specific and concrete concepts. The more abstract our concepts, the less clear will be the observable consequences and the less amenable the theory will be to falsification.

Researchers often use the following strategy. They begin with an abstract concept of the sort listed above. They agree that it cannot be measured directly; therefore, they suggest specific indicators of the abstract concept that can be measured and use them in their explanations. The choice of the specific indicator of the more abstract concept is justified on the grounds that it is observable. Sometimes it is the only thing that is observable (for instance, it is the only phenomenon for which data are available or the only type of historical event for which records have been kept). This is a perfectly respectable, indeed usually necessary, aspect of empirical investigation.

Sometimes, however, it has an unfortunate side. Often the specific indicator is far from the original concept and has only an indirect and uncertain relationship to it. It may not be a valid indicator of the abstract concept at all. But, after a quick apology for the gap between the abstract concept and the specific indicator, the researcher labels the indicator with the abstract concept and proceeds onward as if he were measuring that concept directly. Unfortunately, such reification is common in social science work, perhaps more frequently in quant.i.tative than in qualitative research, but all too common in both. For example, the researcher has figures on mail, trade, tourism and student exchanges and uses these to compile an index of "societal integration" in Europe. Or the researcher asks some survey questions as to whether respondents are more concerned with the environment or making money and labels different respondents as "materialists" and "post-materialists." Or the researcher observes that federal agencies differ in the average length of employment of their workers and converts this into a measure of the "inst.i.tutionalization" of the agencies.

We should be clear about what we mean here. The gap between concept and indicator is inevitable in much social science work. And we use general terms rather than specific ones for good reasons: they allow us to expand our frame of reference and the applicability of our theories. Thus we may talk of legislatures rather than of more narrowly defined legislative categories such as parliaments or specific inst.i.tutions such as the German Bundestag. Or we may talk of "decision-making bodies" rather than legislatures when we want our theory to apply to an even wider range of inst.i.tutions. (In the next section we, in fact, recommend this.) Science depends on such abstract cla.s.sifications-or else we revert to summarizing historical detail. But our abstract and general terms must be connected to specific measureable concepts at some point to allow empirical testing. The fact of that connection-and the distance that must be traversed to make it-must always be kept in mind and made explicit. Furthermore, the choice of a high level of abstraction must have a real justification in terms of the theoretical problem at hand. It must help make the connection between the specific research at hand-in which the particular indicator is the main actor-and the more general problem. And it puts a burden on us to see that additional research using other specific indicators is carried on to bolster the a.s.sumption that our specific indicators really relate to some broader concept. The abstract terms used in the examples above-"societal integration," "post-materialism," and "inst.i.tutionalization" -may be measured reasonably by the specific indicators cited. We do not deny that the leap from specific indicator to general abstract concept must be made-we have to make such a leap to carry on social science research. The leap must, however, be made with care, with justification, and with a constant "memory" of where the leap began.

Thus, we do not argue against abstractions. But we do argue for a language of social research that is as concrete and precise as possible. If we have no alternative to using un.o.bservable constructs, as is usually the case in the social sciences, then we should at least choose ideas with observable consequences. For example, "intelligence" has never been directly observed but it is nevertheless a very useful concept. We have numerous tests and other ways to evaluate the implications of intelligence. On the other hand, if we have the choice between "the inst.i.tutionalization of the presidency" and "size of the White House staff," it is usually better to choose the latter. We may argue that the size of the White House staff is related to the general concept of the inst.i.tutionalization of the presidency, but we ought not to reify the narrower concept as identical to the broader. And, if size of staff means inst.i.tutionalization, we should be able to find other measures of inst.i.tutionalization that respond to the same explanatory variables as does size of staff. Below, we shall discuss "maximizing leverage" by expanding our dependent variables.

Our call for concreteness extends, in general, to the words we use to describe our theory. If a reader has to spend a lot of time extracting the precise meanings of the theory, the theory is of less use. There should be as little controversy as possible over what we mean when we describe a theory. To help in this goal of specificity, even if we are not conducting empirical research ourselves, we should spend time explicitly considering the observable implications of the theory and even possible research projects we could conduct. The vaguer our language, the less chance we will be wrong-but the less chance our work will be at all useful. It is better to be wrong than vague.

In our view, eloquent writing-a scarce commodity in social science-should be encouraged (and savored) in presenting the rationale for a research project, arguing for its significance, and providing rich descriptions of events. Tedium never advanced any science. However, as soon as the subject becomes causal or descriptive inference, where we are interested in observations and generalizations that are expected to persist, we require concreteness and specificity in language and thought.43

3.5.5 Rule 5: State Theories in as Encompa.s.sing Ways as Feasible.

Within the constraints of guaranteeing that the theory will be falsifiable and that we maximize concreteness, the theory should be formulated so that it explains as much of the world as possible. We realize that there is some tension between this fifth rule and our earlier injunction to be concrete. We can only say that both goals are important, though in many cases they may conflict, and we need to be sensitive to both in order to draw a balance.

For example, we must not present our theory as if it only applies to the German Bundestag when there is reason to believe that it might apply to all independent legislatures. We need not provide evidence for all implications of the theory in order to state it, so long as we provide a reasonable estimate of uncertainty that goes along with it. It may be that we have provided strong evidence in favor of the theory in the German Bundestag. Although we have no evidence that it works elsewhere, we have no evidence against it either. The broader reference is useful if we remain aware of the need to evaluate its applicability. Indeed, expressing it as a hypothetically broader reference may force us to think about the structural features of the theory that would make it apply or not to other independent legislatures. For example, would it apply to the U.S. Senate, where terms are staggered, to the New Hampshire a.s.sembly, which is much larger relative to the number of const.i.tuents, or to the British House of Commons, in which party voting is much stronger? An important exercise is stating what we think are systematic features of the theory that make it applicable in different areas. We may learn that we were wrong, but that is considerably better than not having stated the theory with sufficient precision in the first place.

This rule might seem to conflict with Robert Merton's ([1949] 1968) preference for "theories of the middle-range," but even a cursory reading of Merton should indicate that this is not so. Merton was reacting to a tradition in sociology where "theories" such as Parson's "theory of action" were stated so broadly that they could not be falsified. In political science, Easton's "systems theory" (1965) is in this same tradition (see Eckstein 1975:90). As one example of the sort of criticism he was fond of making, Merton ([1949] 1968: 43) wrote, "So far as one can tell, the theory of role-sets is not inconsistent with such broad theoretical orientations as Marxist theory, functional a.n.a.lysis, social behaviorism, Sorokin's integral sociology, or Parson's theory of action." Merton is not critical of the theory of role-sets, which he called a middle-range theory, rather he is arguing against those "broad theoretical orientations," with which almost any more specific theory or empirical observation is consistent. Merton favors "middle-range" theories but we believe he would agree that theories should be stated as broadly as possible as long as they remain falsifiable and concrete. Stating theories as broadly as possible is, to return to a notion raised earlier, a way of maximizing leverage. If the theory is testable-and the danger of very broad theories is, of course, that they may be phrased in ways that are not testable-then the broader the better; that is, the broader, the greater the leverage.

CHAPTER 4.

Determining What to Observe.

UP TO THIS POINT, we have presented our view of the standards of scientific inference as they apply to both qualitative and quant.i.tative research (chapter 1), defined descriptive inference (chapter 2), and clarified our notion of causality and causal inference (chapter 3). We now proceed to consider specific practical problems of qualitative research design. In this and the next two chapters, we will use many examples, both drawn from the literature and constructed hypothetically, to ill.u.s.trate our points. This chapter focuses on how we should select cases, or observations, for our a.n.a.lysis. Much turns on these decisions, since poor case selection can vitiate even the most ingenious attempts, at a later stage, to make valid causal inferences. In chapter 5, we identify some major sources of bias and inefficiency that should be avoided, or at least understood, so we can adjust our estimates. Then in chapter 6, we develop some ideas for increasing the number of observations available to us, often already available within data we have collected. We thus pursue a theme introduced in chapter 1: we should seek to derive as many observable implications of our theories as possible and to test as many of these as are feasible.

In section 3.3.2, we discussed "conditional independence": the a.s.sumption that observations are chosen and values a.s.signed to explanatory variables independently of the values taken by the dependent variables. Such independence is violated, for instance, if explanatory variables are chosen by rules that are correlated with the dependent variables or if dependent variables cause the explanatory variables. Randomness in selection of units and in a.s.signing values to explanatory variables is a common procedure used by some quant.i.tative researchers working with large numbers of observations to ensure that the conditional independence a.s.sumption is met. Statistical methods are then used to mitigate the Fundamental Problem of Causal Inference. Unfortunately, random selection and a.s.signment have serious limitations in small-n research. If random selection and a.s.signment are not appropriate strategies, we can seek to achieve unit h.o.m.ogeneity through the use of intentional selection of observations (as discussed in section 3.3.1). In a sense, intentional selection of observations is our "last line of defense" to achieve conditions for valid causal inference.

Recall the essence of the unit h.o.m.ogeneity a.s.sumption: if two units have the same value of the key explanatory variable, the expected value of the dependent variable will be the same. The stricter version of the unit h.o.m.ogeneity a.s.sumption implies, for example, that if turning on one light switch lights up a 60-watt bulb, so will turning a second light switch to the "on" position. In this example, the position of the switch is the key explanatory variable and the status of the light (on or off) is the dependent variable. The unit h.o.m.ogeneity a.s.sumption requires that the expected status of each light is the same as long as the switches are in the same positions. The less strict version of the unit h.o.m.ogeneity a.s.sumption-often more plausible but equally acceptable-is the a.s.sumption of constant effect, in which similar variation in values of the explanatory variable for the two observations leads to the same causal effect in different units, even though the levels of the variables may be different. Suppose, for instance, that our light switches have three settings and we measure the dependent variable according to wattage generated. If one switch is changed from "off" to "low," and the other from "low" to "high," the a.s.sumption of constant effect is met if the increase in wattage is the same in the two rooms, although in one observation it goes from zero to 60, in the other from 60 to 120.

When neither the a.s.sumption of conditional independence nor the a.s.sumption of unit h.o.m.ogeneity is met, we face serious problems in causal inference. However, we face even more serious problems-indeed, we can literally make no valid causal inferences-when our research design is indeterminate. A determinate research design is the sine qua non of causal inference. Hence we begin in section 4.1 by discussing indeterminate research designs. After our discussion of indeterminate research designs, we consider the problem of selection bias as a result of the violation of the a.s.sumptions of conditional independence and unit h.o.m.ogeneity. In section 4.2, we a.n.a.lyze the limits of using random selection and a.s.signment to achieve conditional independence. In section 4.3, we go on to emphasize the dangers of selecting cases intentionally on the basis of values of dependent variables and provide examples of work in which such selection bias has invalidated causal inferences. Finally, in section 4.4, we systematically consider ways to achieve unit h.o.m.ogeneity through intentional case selection, seeking not only to provide advice about ideal research designs but also offering suggestions about "second-best" approaches when the ideal cannot be attained.

The main subject of this chapter: issues involved in selecting cases, or observations, for a.n.a.lysis deserves special emphasis here. Since terminology can be confusing, it is important to review some terminological issues at the outset. Much discussion of qualitative research design speaks of "cases"-as in discussions of case studies or the "case method." However, the word "case" is often used ambiguously. It can mean a single observation. As explained in section 2.4, an "observation" is defined as one measure on one unit for one dependent variable and includes information on the values of the explanatory variables. However, a case can also refer to a single unit, on which many variables are measured, or even to a large domain for a.n.a.lysis.

For example, a.n.a.lysts may write about a "case study of India" or of World War II. For some purposes, India and World War II may const.i.tute single observations; for instance, in a study of the population distribution of countries or the number of battle deaths in modern wars. But with respect to many questions of interest to social scientists, India and World War II each contain many observations that involve several units and variables. An investigator could compare electoral outcomes by parties across Indian states or the results of battles during World War II. In such a design, it can be misleading to refer to India or World War II as case studies, since they merely define the boundaries within which a large number of observations are made.

In thinking about choosing what to observe, what really concern us are the observations used to draw inferences at whatever level of a.n.a.lysis is of interest. Hence we recommend that social scientists think in terms of the observations they will be able to make rather than in the looser terminology of cases. However, what often happens in qualitative research is that researchers begin by choosing what they think of as "cases," conceived of as observations at a highly aggregated level of a.n.a.lysis, and then they find that to obtain enough observations, they must disaggregate their cases.

Suppose, for example, that a researcher seeks to understand how variations in patterns of economic growth in poor democratic countries affect political inst.i.tutions. The investigator might begin by thinking of India between 1950 and 1990 as a single case, by which he might have in mind observations for one unit (India) on two variables-the rate of economic growth and a measure of change or stability in political inst.i.tutions. However, he might only be able to find a very small number of poor democracies, and at this level of a.n.a.lysis have too few observations to make any valid causal inferences. Recognizing this problem, perhaps belatedly, he could decide to use each of the Indian states as a unit of a.n.a.lysis, perhaps also disaggregating his time period into four or five subperiods. If these disaggregated observations were implications of the same theory he set out to test, such a procedure would give him many observations within his "case study" of India. The resulting study might then yield enough information to support valid causal inferences about Indian politics and would be very different from a conventional case study that is narrowly conceived in terms of observations on one unit for several variables.

Since "observation" is more precisely defined than "case," in this chapter we will usually write of "selecting observations." However, since investigators often begin by choosing domains for study that contain multiple potential observations, and conventional terminology characteristically denotes these as "cases," we often speak of selecting cases rather than observations when we are referring to the actual practice of qualitative researchers.

4.1 INDETERMINATE RESEARCH DESIGNS.

A research design is a plan that shows, through a discussion of our model and data, how we expect to use our evidence to make inferences. Research designs in qualitative research are not always made explicit, but they are at least implicit in every piece of research. However, some research designs are indeterminate; that is, virtually nothing can be learned about the causal hypotheses.

Unfortunately, indeterminate research designs are widespread in both quant.i.tative and qualitative research. There is, however, a difference between indeterminancy in quant.i.tative and qualitative research. When quant.i.tative research is indeterminate, the problem is often obvious: the computer program will not produce estimates.44 Yet computer programs do not always work as they should and many examples can be cited of quant.i.tative researchers with indeterminate statistical models that provide meaningless substantive conclusions. Unfortunately, nothing so automatic as a computer program is available to discover indeterminant research designs in qualitative research. However, being aware of this problem makes it easier to identify indeterminate research designs and devise solutions. Moreover, qualitative researchers often have an advantage over quant.i.tative researchers since they often have enough information to do something to make their research designs determinant.

Suppose our purpose in collecting information is to examine the validity of a hypothesis. The research should be designed so that we have maximum leverage to distinguish among the various possible outcomesrelevant to the hypothesis. Two situations exist, however, in which a research design is indeterminate and, therefore, gives us no such leverage:1. We have more inferences to make than implications observed.

2. We have two or more explanatory variables in our data that are perfectly correlated with each other-in statistical terms, this is the problem of multicollinearity. (The variables might even differ, but if we can predict one from the other without error in the cases we have, then the design is indeterminate).

Note that these situations, and the concept of indeterminate research designs in general, apply only to the goal of making causal inferences. A research design for summarizing historical detail cannot be indeterminate unless we literally collect no relevant observations. Data-collection efforts designed to find interesting questions to ask (see section 2.1.1) cannot be indeterminate if we have at least some information. Of course, indeterminancy may still occur later on when reconceptualizing our data (or collecting new data) to evaluate a causal hypothesis.

4.1.1 More Inferences than Observations.

Consider the first instance, in which we have more inferences than implications observed. Inference is the process of using facts we know to learn something about facts we do not know. There is a limit to how much we can learn from limited information. It turns out that the precise rule is that one fact (or observable implication) cannot give independent information about more than one other fact. More generally, each observation can help us make one inference at most; n observations will help us make fewer than n inferences if the observations are not independent. In practice, we usually need many more than one observation to make a reasonably certain causal inference.

Having more inferences than implications observed is a common problem in qualitative case studies. However, the problem is not inherent in qualitative research, only in that research which is improperly conceptualized or organized into many observable implications of a theory. We will first describe this problem and then discuss solutions.

For example, suppose we have three case studies, each of which describes a pair of countries' joint efforts to build a high-technology weapons system. The three case studies include much interesting description of the weapons systems, the negotiations between the countries, and the final product. In the course of the project, we list seven important reasons that lead countries to successful joint collaboration on capital-defense projects. These might all be very plausible explanatory variables. We might also have interviewed decision-makers in the different countries and learned that they, too, agreed that these are the important variables. Such an approach would give us not only seven plausible hypotheses, but observations on eight variables: the seven explanatory variables and the dependent variable. However in this circ.u.mstance, the most careful collection of data would not allow us to avoid a fundamental problem. Valuable as it is, such an approach-which is essentially the method of structured, focused comparison-does not provide a methodology for causal inference with an indeterminate research design such as this. With seven causal variables and only three observations, the research design cannot determine which of the hypotheses, if any, is correct.

Faced with indeterminate explanations, we sometimes seek to consider additional possible causes of the event we are trying to explain. This is exactly the opposite of what the logic of explanation should lead us to do. Better or more complete description of each case study is not the solution, since with more parameters than observations, almost any answer about the impact of each of the seven variables is as consistent with the data as any other. No amount of description, regardless of how thick and detailed; no method, regardless of how clever; and no researcher, regardless of how skillful, can extract much about any of the causal hypotheses with an indeterminate research design. An attempt to include all possible explanatory variables can quickly push us over the line to an indeterminate research design.

A large number of additional case studies might solve the problem of the research design in the previous paragraph, but this may take more time and resources than we have at our disposal, or there may be only three examples of the phenomena being studied. One solution to the problem of indeterminacy would be to refocus the study on the effects of particular explanatory variables across a range of state action rather than on the causes of a particular set of effects, such as success in joint projects. An alternative solution that doesn't change the focus of the study so drastically might be to add a new set of observations measured at a different level of a.n.a.lysis. In addition to using the weapons system, it might be possible to identify every major decision in building each weapon system. This procedure could help considerably if there were significant additional information in these decisions relevant to the causal inference. And, as long as our theory has some implication for what these decisions should be like, we would not need to change the purpose of the project at all. If properly specified, then, our theory may have many observable implications and our data, especially if qualitative, may usually contain observations for many of these implications. If so, each case study may be converted into many observations by looking at its subparts. By adding new observations from different levels of a.n.a.lysis, we can generate multiple tests of these implications. This method is one of the most helpful ways to redesign qualitative research and to avoid (to some extent) both indeterminacy and omitted variable bias, which will be discussed in section 5.2. Indeed, expanding our observations through research design is the major theme of chapter 6 (especially section 6.3).

A Formal a.n.a.lysis of the Problem of More Inferences than Observations. The easiest way to understand this problem is by taking a very simple case. We avoid generality in the proof that follows in order to maximize intuition. Although we do not provide the more general proof here, the intuition conveyed by this example applies much more generally.

Suppose we are interested in making inferences about two parameters in a causal model with two explanatory variables and a single dependent variable (4.1).

but we have only a single observation to do the estimation (that is, n = 1). Suppose further that, for the sake of clarity, our observation consists of X1 = 3, X2 = 5, and Y = 35. Finally, let us suppose that in this instance Y happens to equal its expected value (which would occur by chance or if there were no random variability in Y). Thus, E(Y) = 35. We never know this last piece of information in practice (because of the randomness inherent in Y), so if we have trouble estimating 1 and 2 in this case, we will surely fail in the general case when we do not have this information about the expected value.

The goal, then, is to estimate the parameter values in the following equation: (4.2).

The problem is that this equation has no unique solution. For example, the values (1 = 10, 2 = 1) satisfy this equation, but so does (1 = 5, 2 = 4) and (1 = -10, 2 = 13). This is quite troubling since the different values of the parameters can indicate very different substantive implications about the causal effects of these two variables; in the last case, even a sign changed. Indeed, these solutions and an infinite number of others satisfy this equation equally well. Thus nothing in the problem can help us to distinguish among the solutions because all of them are equally consistent with our one observation.

4.1.2 Multicollinearity.

Suppose we manage to solve the problem of too few observations by focusing on the effects of pre-chosen causes, instead of on the causes of observed effects, by adding observations at different levels of a.n.a.lysis or by some other change in the research design. We will still need to be concerned about the other problem that leads to indeterminate research designs-multicollinearity. We have taken the word "multicollinearity" from statistical research, especially regression a.n.a.lysis, but we mean to apply it much more generally. In particular, our usage includes any situation where we can perfectly predict one explanatory variable from one or more of the remaining explanatory variables. We apply no linearity a.s.sumption, as in the usual meaning of this word in statistical research.

For example, suppose two of the hypotheses in the study of arms collaboration mentioned above are as follows: (1) collaboration between countries that are dissimilar in size is more likely to be successful than collaboration among countries of similar size; and (2) collaboration is more successful between nonneighboring than neighboring countries. The explanatory variables behind these two hypotheses both focus on the negative impact of rivalry on collaboration; both are quite reasonable and might even have been justified by intensive interviews or by the literature on industrial policy. However, suppose we manage to identify only a small data set where the unit of a.n.a.lysis is a pair of countries. Suppose, in addition, we collect only two types of observations: (1) neighboring countries of dissimilar size and (2) nonneighboring countries of similar size. If all of our observations happen (by design or chance) to fall in these categories, it would be impossible to use these data to find any evidence whatsoever to support or deny either hypothesis. The reason is that the two explanatory variables are perfectly correlated: every observation in which the potential partners are of similar size concerns neighboring countries and vice versa. Size and geographic proximity are conceptually very different variables, but in this data set at least, they cannot be distinguished from each other. The best course of action at this point would be to collect additional observations in which states of similar size were neighbors. If this is impossible, then the only solution is to search for observable implications at some other level of a.n.a.lysis.

Even if the problem of an indeterminate research design has been solved, our causal inferences may remain highly uncertain due to problems such as insufficient numbers of observations or collinearity among our causal variables. To increase confidence in our estimates, we should always seek to maximize leverage over our problem. Thus, we should always observe as many implications of our theory as possible. Of course, we will always have practical constraints on the time and resources we can devote to data collection. But the need for more observations than inferences should sensitize us to the situations in which we should stop collecting detailed information about a particular case and start collecting information about other similar cases. Concerns about indeterminancy should also influence the way we define our unit of a.n.a.lysis: we will have trouble making valid causal inferences if nearly unique events are the only unit of a.n.a.lysis in our study, since finding many examples will be difficult. Even if we are interested in Communism, the French Revolution, or the causes of democracy, it will also pay to break the problem down into manageable and more numerous units.

Another recommendation is to maximize leverage by limiting the number of explanatory variables for which we want to make causal inferences. In limiting the explanatory variables, we must be careful to avoid omitted variable bias (section 5.2). The rules in section 5.3 should help in this. A successful project is one that explains a lot with a little. At best, the goal is to use a single explanatory variable to explain numerous observations on dependent variables.

A research design that explains a lot with a lot is not very informative, but an indeterminate design does not allow us to separate causal effects at all. The solution is to select observations on the same variables or others that are implications of our theory to avoid the problem. After formalizing multicollinearity (see box), we will turn to a more detailed a.n.a.lysis of methods of selecting observations and the problem of selection bias.

A Formal a.n.a.lysis of Multicollinearity. We will use the same strategy as we did in the last formal a.n.a.lysis by providing a proof of only a specific case in order to clarify understanding. The intuition also applies far beyond the simple example here. We also use an example very similar to the one above.

Let us use the model in equation (4.1), but this time we have a very large number of observations and our two explanatory variables are perfect linear combinations of one another. In fact, to make the problem even more transparent, suppose that the two variables are the same, so that X1 = X2. We might have coded X1 and X2 as two substantively different variables (like gender and pregnancy), but in a sample of data they might turn out to be the same (if all women surveyed happened to be pregnant). Can we distinguish the causal effects of these different variables?

Note that equation (4.1) can be written as follows: (4.3).

As should be obvious from the second line of this equation, regardless of what E(Y) and X1 are, numerous values of 1 and 2 can satisfy it. (For example, if 1 = 5 and 2 = -20 satisfy equation (4.3), then so does 1 = -20 and 2 = 5.) Thus, although we now have many more observations than parameters, multicollinearity leaves us with the same problem as when we had more parameters than units: no estimation method can give us unique estimates of the parameters.

4.2 THE LIMITS OF RANDOM SELECTION.

We avoid selection bias in large-n studies if observations are randomly selected, because a random rule is uncorrelated with all possible explanatory or dependent variables.45 Randomness is a powerful approach because it provides a selection procedure that is automatically uncorrelated with all variables. That is, with a large n, the odds of a selection rule correlating with any observed variable are extremely small. As a result, random selection of observations automatically eliminates selection bias in large-n studies. In a world in which there are many potential confounding variables, some of them unknown, randomness has many virtues for social scientists. If we have to abandon randomness, as is usually the case in political science research, we must do so with caution.

Controlled experiments are only occasionally constructed in the social sciences.46 However, they provide a useful model for understanding certain aspects of the design of nonexperimental research. The best experiments usually combine random selection of observations and random a.s.signments of values of the explanatory variables with a large number of observations (or experimental trials). Even though no experiment can solve the Fundamental Problem of Causal Inference, experimenters are often able to select their observations (rather than having them provided through social processes) and can a.s.sign treatments (values of the explanatory variables) to units. Hence it is worthwhile to focus on these two advantages of experiments: control over selection of observations and a.s.signment of values of the explanatory variables to units. In practice, experimenters often do not select randomly, choosing instead from a convenient population such as college soph.o.m.ores, but here we focus on the ideal situation. We discuss selection here, postponing our discussion of a.s.signment of values of the explanatory variables until the end of chapter 5.

In qualitative research, and indeed in much quant.i.tative research, random selection may not be feasible because the universe of cases is not clearly specified. For instance, if we wanted a random sample of foreign policy elites in the United States, we would not find an available list of all elites comparable to the list of congressional districts. We could put together lists from various sources, but there would always be the danger that these lists would have built-in biases. For instance, the universe for selection might be based on government lists of citizens who have been consulted on foreign policy issues. Surely such citizens could be considered to be members of a foreign policy elite. But if the research problem had to do with the relationship between social background and policy preferences, we might have a list that was biased toward high-status individuals who are generally supportive of government policy. In addition, we might not be able to study a sample of elites chosen at random from a list because travel costs might be too high. We might have to select only those who lived in the local region-thus possibly introducing other biases.

Even when random selection is feasible, it is not necessarily a wise technique to use. Qualitative researchers often balk (appropriately) at the notion of random selection, refusing to risk missing important cases that might not have been chosen by random selection. (Why study revolutions if we don't include the French Revolution?) Indeed, if we have only a small number of observations, random selection may not solve the problem of selection bias but may even be worse than other methods of selection. We believe that many qualitative researchers understand this point intuitively when they complain about what they perceive as the misguided preaching of some quant.i.tative researchers about the virtues of randomness. In fact, using a very simple formal model of qualitative research, we will now prove that random selection of observations in small-n research will often cause very serious biases.

Suppose we have three units that have observations on the dependent variable of (High, Medium, Low), but only two of these three are to be selected into the a.n.a.lysis (n = 2). We now need a selection rule. If we let 1 denote a unit selected into the a.n.a.lysis and 0 denote an omitted unit, then only three selection rules are possible: (1,1,0), which means that we select the High and Medium choices but not the Low case, (0,1,1), and (1,0,1). The problem is that only the last selection rule, in which the second unit is omitted, is uncorrelated with the dependent variable.47 Since random selection of observations is equivalent to a random choice of one of these three possible selection rules, random selection of units in this small-n example will produce selection bias with two-thirds probability! More careful selection of observations using a priori knowledge of the likely values of the dependent variable might be able to choose the third selection rule with much higher probability and thus avoid bias.

Qualitative researchers rarely resort explicitly to randomness as a selection rule, but they must be careful to ensure that the selection criteria actually employed do not have similar effects. Suppose, for example, that a researcher is interested in those East European countries with Catholic heritage that were dominated by the Soviet Union after World War II: Czechoslovakia, Hungary, and Poland. This researcher observes substantial variation in their politics during the 1970s and 1980s: in Poland, a well-organized antigovernment movement (Solidarity) emerged; in Czechoslovakia a much smaller group of intellectuals was active (Charter 77); while in Hungary, no such large national movement developed. The problem is to explain this discrepancy.

Exploring the nature of antigovernment movements requires close a.n.a.lysis of newspapers, recently decla.s.sified Communist Party doc.u.ments, and many interviews with partic.i.p.ants-hence, knowledge of the language. Furthermore, the difficulty of doing research in contemporary Eastern Europe means that a year of research will be required to study each country. It seems feasible, therefore, to study only two countries for this work. Fortunately, for reasons unconnected with this project, the researcher already knows Czech and Polish, so she decides to study Charter 77 in Czechoslovakia and Solidarity in Poland. This is obviously different from random a.s.signment, but at least the reason for selecting these countries is probably unrelated to the dependent variable. However, in our example it turns out that her selection rule (linguistic knowledge) is correlated with her dependent variable and that she will therefore encounter selection bias. In this case, a non-random, informed selection might have been better-if it were not for the linguistic requirement.