Скачать 126.01 Kb.
|Mechanisms and Causal Explanation|
Social scientists have recognized for decades that adequate explanations for how causes bring about their effects must, at some level, specify in empirically verifiable ways the causal pathways between causes and their outcomes. This requirement of depth of causal explanation applies to the counterfactual tradition as well. Accordingly, it is widely recognized that a consistent estimate of a counterfactually-defined causal effect of on may not qualify as a sufficiently deep causal account of how effects , based on the standards that prevail in a particular field of study.
In this chapter, we first discuss the dangers of insufficiently deep explanations of causal effects, re-considering the weak explanatory power of some of the natural experiments discussed already in Chapter 7. We then consider the older literature on intervening variables in the social sciences as a way to introduce the mechanism-based estimation strategy proposed by Pearl (2000). In some respects, Pearl's approach is completely new, as it shows in a novel and sophisticated way how causal mechanisms can be used to identify causal effects even when unblocked back-door paths between a causal variable and an outcome variable are present. In other respects, however, Pearl's approach is refreshingly familiar, as it helps to clarify the appropriate usage of intervening and mediating variables when attempting to deepen the explanation of a causal claim.
Independent of Pearl's important work, a diverse group of social scientists has appealed recently for the importance of mechanisms to all explanation in social science research. Although some of these appeals are not inconsistent with the basic counterfactual approach (e.g., Reskin 2003; Sørensen 1998), some of the more extended appeals (e.g., Goldthorpe 2000) claim to be at odds with some of the basic premises of the counterfactual model. We will argue instead that there is no incompatibility between causal mechanisms and counterfactual thinking. Finally, we draw on Machamer, Darden, and Craver (2000) and introduce their concept of a mechanism sketch as well as the process of bottoming out in mechanistic explanation. This terminology helps to frame our final discussion of how mechanisms can be used to sustain and deepen causal explanation, which draws together Pearl's front-door criterion with standards for sufficient causal depth.
The Dangers of Insufficiently Deep Explanations
Before considering how mechanisms can be used to identify causal effects, we first discuss the importance of explanatory depth in counterfactual causal analysis. To do so, we return to the important critical work of Rosenzweig and Wolpin (2000) on the limited appeal of many natural experiments.
As discussed throughout in Chapter 7, the natural experiment literature in economics uses naturally occurring forms of randomness as instrumental variables in order to identify and then estimate causal effects of long-standing interest. Initially, this literature was heralded as the arrival of a new age of econometric analysis, where it now appeared possible to consistently estimate some of the causal effects of greatest interest to economists, such as the effect of human capital investments in education on earnings. Looking back on these bold claims, Rosenzweig and Wolpin (2000:829-30) conclude: The impression left by this literature is that if one accepts that the instruments are perfectly random and plausibly affect the variable whose effect is of interest, then the instrumental-variables estimates are conclusive. They then argue that these estimates are far from conclusive and, in fact, are far more shallow than was initially recognized.
To somewhat overstate the case, the initial over-confidence of the natural experiment movement was based on the mistaken belief that the randomness of a natural experiment allows one to offer valid causal inference in the absence of any explicit theory. One might say that some econometricians had been seduced by a position implicit in some writing in statistics: We do not need explicit theories in order to perform data analysis. Rosenzweig and Wolpin (2000) counter this position by arguing that the theory that underlies any model specification is critical to the interpretation of an estimate of a causal effect, and almost all examples of estimation via natural experiments have model specifications that make implicit theoretical claims.
Here, we provide an informal presentation of two of the examples analyzed by Rosenzweig and Wolpin -- the effect of education on earnings and the effect of military service on earnings -- each of which was already introduced and discussed briefly in Chapter 7. We will use causal diagrams here in order to demonstrate the issues involved.
Angrist and Krueger (1991) address the ability bias issue in the estimation of the causal effect of schooling on subsequent labor market earnings. They assert that the quarter in which one is born is random but nonetheless predicts one's level of education because of compulsory school entry and dropout laws (see the quotation in section Traditional IV Estimators that gives the rationale). Angrist and Krueger's estimates of the increase in log earnings for each year of education fall between and , values which are consistent with those found by others using different methods (see Card 1999).
As discussed already in Chapter 7, the first limitation of their results is that their IV estimates apply only to a narrow segment of the population: those individuals whose schooling would have changed if their birth date was in a different quarter. Again, this is a local average treatment effect (LATE) estimate that applies to those individuals whose years of schooling are responsive to school entry and dropout laws. No one maintains that this narrow population is simply a random sample of all individuals, and most would argue that Angrist and Krueger estimated the returns to schooling only for disadvantaged youth prone to dropping out of high school for other reasons. There are, however, complications of how to interpret their estimates even for this population.
Consider the causal diagram presented in Figure 8.1, which is based loosely on the critique offered by Rosenzweig and Wolpin (2000), and which is a summary of the debate that unfolded in the years following the publication of Angrist and Krueger (1991). The causal diagram is not meant to represent a full causal account of how education determines wages, but rather only the casual diagram that is applicable to compliers. As discussed in Chapter 7, for this example, compliers are those members of the population whose education is (or would be) responsive to a switch in their quarter of birth. Thus, this diagram takes it for granted that this particular LATE is the only parameter that is informed by this analysis.1
[ INSERT FIGURE 8.1 HERE ]
For the causal diagram in Figure 8.1, schooling has a both direct and indirect effects on wages. Most importantly, as is maintained in the human capital literature, schooling is thought to have a negative indirect effect on wages through work experience; going to school longer reduces the amount of work experience one acquires by any particular age. Accordingly, there is a causal pathway from schooling to wages via work experience. The quarter of birth IV does not provide a separate estimate of this distinct pathway, since a change in schooling in response to one's birth date also changes work experience. At best, the quarter of birth IV estimates only the total effect of schooling on wages, not its direct effect.2 The IV yields a LATE estimate that likely mixes together two distinct and countervailing causal pathways: a positive direct effect of schooling on wages and a negative indirect effect via work experience. Given the long-standing interest of economists in the interaction between investments in formal schooling and the provision of on-the-job training, this total effect estimate is regarded by many as an insufficiently deep causal account of the effect of education on earnings (even if one is convinced, as we are, that learning about compliers in this case is still illuminating).
For a second example, consider the effect of military service on lifetime earnings, as analyzed by Angrist (1990) and introduced in section Traditional IV Estimators. The question of interest here is whether or not military service provides important training that increases later earnings in civilian life or rather whether military service is simply a period of lost civilian work experience. Military service, however, is not random. On the one hand, individuals must pass a mental ability test and a health examination in order to enlist. On the other hand, individuals with attractive schooling opportunities and civilian labor market opportunities are less likely to enlist. To deal with the problem of nonrandom selection into the military, Angrist (1990) considers individuals who were potentially eligible to be drafted into the military via a lottery during the later stages of the Vietnam war. In order to ensure that the draft was fair, the US government decided to draft individuals based on a lottery that selected birth dates (see our earlier discussion in section Traditional IV Estimators).
Consider now the causal diagram in Figure 8.2, again based on the summary of critiques of the study compiled by Rosenzweig and Wolpin (2000). Here, there are three issues to consider. First, as we noted for the last example, the draft lottery identifies a LATE, and thus it is not applicable to the causal effect for always takers (those who voluntarily enlist) and never takers (those who are draft dodgers, those who failed the mental ability test, and those who failed the physical examination). Accordingly, as for Figure 8.1, the causal diagram in Figure 8.2 also applies to compliers only.
Second, note that there is a potential path from the draft lottery to civilian experience/training. If this path exists, then the draft lottery is not a valid IV for military service. As we noted earlier in Chapter 7, Heckman (1997) argues that employers would be likely to invest less in individuals with unfavorable lottery numbers. For example, it is plausible that employers may have given less on-the-job training to those most likely to be drafted and/or may have assigned such individuals to short-run tasks that did not require the accumulation of skill to master. If this effect exists, then the draft lottery would be an invalid instrument for military service.
Third, and most important for our consideration here, there are four separate causal pathways between military service and wages. In addition to the direct causal effect of military service on wages, there are two causal pathways solely mediated by civilian experience and schooling respectively. Here, it is generally thought that military service reduces civilian labor force experience and schooling, both of which then reduce wages. But, there is then a countervailing effect of military service that snakes through the causal diagram in a fourth causal pathway: military service reduces schooling, which then increases work experience, and which then increases wages. Because all four of these pathways are activated by the shock induced by the draft lottery, Angrist's only resort is to assert that his estimates are for the total effect of military service on wages. But, given the inherent interest in untangling how the military service effect interacts with both schooling and the accumulation of civilian experience, a total effect estimate is insufficiently deep to end all future research, even though this natural experiment was informative and an important contribution to the literature.
[ INSERT FIGURE 8.2 HERE ]
Rosenzweig and Wolpin (2000) consider many other examples, all of which emphasize the same basic points as these two examples. Instrumental variable analyses of this type provide estimates of very specific parameters that are often not of fundamental interest because they apply to non-random segments of the population. Moreover, instrumental variable analyses typically provide total causal effect estimates, often in substantive areas where scholars have an inherent interest in the separable causal pathways that generate the outcome in response to the cause. Understanding the separable causal pathways that make up these total effects requires an explicit specification of additional intervening and mediating variables.
Now consider these two issues more generally, moving away from IV estimates toward more general estimates of average causal effects. Consider an optimistic scenario where one obtains what all agree is a consistent estimate of the average causal effect of on (as warranted, for example, by a consensus that one has conditioned on all variables that block all back-door paths from to ). Even in this scenario, where the causal claim is valid by the standards of the counterfactual model, there are two related ways in which such an estimate can be regarded as insufficiently deep.
First, the average causal effect may not be a parameter of any fundamental interest. This point has been made most forcefully by Heckman (2000, 2005). If treatment effects are heterogeneous, which often is the case as we have noted in prior chapters, then the average causal effect will be population-specific. To over-simplify the argument, it may be that what is of fundamental interest are conditional average treatment effects of some form (perhaps even just the average treatment effect for the treated and the average treatment effect for the untreated). The overall average treatment effect is then simply a weighted average of any such underlying effects, where the weights are a function of whatever pattern of causal exposure may prevail in the particular population from which one's sample is drawn. Heckman and many others note that the average causal effect of on may be of limited use for predicting the outcomes of policy interventions, either for new populations or in different contexts. But, the point is in fact much more general and is applicable outside of policy research. Average causal effects are tied to particular populations, and quite often social scientists desire explanations for outcomes that can be modified in straightforward ways when populations shift or contexts change in ways that are separable from the fundamental conditional average causal effects.
The second issue, and which is our primary focus in the remainder of this chapter, is that a consistent estimate of the average causal effect of on does not necessarily entail any particular mechanism that explains how brings about . If a theory suggests why and how brings about