Epidemiology is the study of the distribution and determinants of disease in the population. Because it is the science of public health, the epidemiologist’s end goal is to change something in the world so as to improve population health [1, 2]. Social epidemiology is the study of how social factors, broadly writ, are related to health and disease. Many social epidemiologists seek to improve the health and well-being of all individuals, with a particular emphasis on the deprived and disenfranchised, usually defined with reference to some characteristic that classifies individuals as belonging to a certain group, such as gender, race/ethnicity, or social rank. Social rank or position is often defined as a function of education, income, and occupation, each of which can be measured at a fixed point in time during the study time scale (e.g., baseline), or repeatedly over a study’s follow-up.

Observational research findings in social epidemiology have been traditionally used to reason about the effects of interventions aimed at reducing the impact of deleterious social exposures, or increasing the impact of beneficial ones. Recently, this practice has led to some disquieting observations [3••]. Rigorous intervention trials seeking to estimate the effects of policies to improve social determinants of health in epidemiology [4–6] as well as decades of work seeking to reduce health disparities [7–9] have shown results that diverge from expectations set by observational analyses. This has led to much debate on how to analyze data in social epidemiology [3••, 10–14]. From this debate, several routes have been identified as a way forward. Among them include the analysis of observational data using a formal approach outlined in the field of causal inference [11–15].

Since the late 1990s, several authors examined the implications of causal inference concepts in social epidemiology [16–18]. A number of challenges in defining, identifying, and estimating counterfactual-based causal effects were found to be especially problematic in social epidemiology. The purpose of this article is to revisit these issues in light of the conceptual and analytic advancements in causal inference over the last two decades. We focus on a central assumption in causal inference known as the stable unit treatment value assumption, which can be divided into two component assumptions: counterfactual consistency and the absence of interference. We give simple hypothetical examples to illustrate how and why these assumptions are often violated in research on the social determinants of health (e.g., education, race/ethnicity, socioeconomic position) and provide strategies that can be used to sidestep these assumptions. In particular, we note that a recently proposed mediation analysis strategy can be used to explore questions about health disparities in a more formal causal inference framework [19, 20]. We emphasize that a central obstacle to estimating causal effects of commonly used variables such as race, education (e.g., high school versus no high school), or occupation is the need to identify an intervention (possibly hypothetical) that will lead to changes in the exposure of interest [3••, 21].

Inferring Causal Effects from Observational Data

In this review, we consider as an example the educational disparity in preterm birth (defined as less than 37 weeks of completed gestation). A number of studies have examined the relation between maternal education and preterm birth [22–29], all of which found that low education is associated with an increased risk of preterm birth. Some interpreted their results to suggest public health interventions to increase maternal education would yield reductions in the risk of preterm birth [22, 24, 28]. However, while increasing levels of maternal education will undoubtedly have numerous social benefits, several problems arise when making inferences about the effects of public health interventions aimed at increasing maternal education.

To frame the specifics of our discussion, we introduce the hypothetical dataset of 15 subjects presented in Table 1. For didactic purposes, assume these are surveillance data acquired from birth certificates in a well-defined geographic region using gold standard measurement tools. Birth certificates often contain measures of gestational age and maternal education (e.g., number of years attained) at the time of birth. These two measured and observable variables are represented in columns 2 and 3 of Table 1, where: X is an indicator of whether the woman had a high-school education or more (X = 1) or less than high school (X = 0) at the time of birth; and Y is an indicator of whether the woman gave birth preterm (Y = 1). As we explain in more details below: column 3 represents an unmeasured but observable variable denoting the mechanism by which each woman attained their observed level of education, and we let columns 4 and 5 represent the unobservable potential outcomes under exposure Y(x = 1) and no exposure Y(x = 0).

Table 1 Hypothetical dataset of 15 subjects with an observed exposure level of maternal education (X), an observed preterm birth outcome (Y), an observable but unmeasured assignment mechanism variable (J x ), and the potential outcomes that would have been observed under exposure [Y(x = 1)] and no exposure [Y(x = 0)]
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SUTVA: Counterfactual Consistency

Potential outcomes, such as those listed in Table 1, have become central to defining causal effects in epidemiology. Because our exposure is whether a woman had at least a high-school education (X = 1), the potential outcome in column 4, Y(x = 1) might be interpreted as what would have been observed if a woman had attained this level of education. Furthermore, for the same woman, Y(x = 0) might represent what would have happened if she had not reached this educational threshold. However, we will show that these definitions require certain assumptions that are not met in our hypothetical example.

The potential outcome framework is also known as the Neyman-Rubin causal model [30], and it was Rubin who first recognized that use of this notation implicitly makes a “stable unit treatment value assumption” (SUTVA) or the assumption that [31]: (i) there is only one “version” of the exposure; and (ii) no subject’s exposure can affect another subject’s potential outcome. Regarding assumption (i), “version” is meant to connote, for example, different ways in which a subject might get exposed to a particular level of X, which may result in different causal effects. Multiple versions of the exposure could lead to many possible versions of the potential outcome, which would void the use of this simple notation, and violate what later became known as the counterfactual consistency assumption.

Counterfactual consistency is an unverifiable assumption requiring a subject’s potential outcome under the observed exposure value is indeed their observed outcome. This assumption is more likely to hold when the exposure corresponds to a well-defined intervention [32•, 33•, 34]. Counterfactual consistency allows researchers to link observed data collected for a given study to the potential outcomes. Specifically, if a mother’s observed exposure value is “high school or more,” counterfactual consistency requires that this mother’s potential outcome Y(x) under x = 1 = “high school or more” is equivalent to the observed outcome for this woman in our data, denoted Y. For example, if we examine subject with ID = 2 in Table 1, we note that this person’s exposure was x = 1 and that the potential outcome under exposure Y(x = 1) = 1 is equal to the observed outcome Y = 1. This might suggest that counterfactual consistency in our hypothetical example of the causal effect of maternal education on preterm birth was met.

However, if we examine subject with ID = 1 in Table 1, we note something different. This person’s exposure was x = 1, but their potential outcome Y(x = 1) = 0 is not equal to the observed outcome Y = 1. Thus, counterfactual consistency is violated in our example. The reason is explained by referring to column 4 of Table 1, which provides information on the two possible mechanisms by which each woman was able to attain a high-school education or more. If there are multiple ways of acquiring a high-school education (and thus of getting the value x = 1), each of which might have different impacts on the outcome, then—as is seen with subject ID = 1 in Table 1—it is not logical to assume that the observed value Y corresponds to the potential outcome under the observed exposure.

VanderWeele [33•] was the first to use this reasoning to propose a refinement to the counterfactual consistency assumption. He argued that, in making the assumption, researchers additionally assume (often implicitly) that the various ways in which a particular subject may have attained a particular level of the exposure are irrelevant. He called this assumption treatment variation irrelevance. For example, in our hypothetical data, subject ID = 2 may have acquired a high-school education or more because of, e.g., a governmental cash transfer conditional on graduating from high school. This mechanism, indexed in column 4 of Table 1, is denoted J x  = 1. On the other hand, subject ID = 1 graduated from high school because of some other mechanism, denoted J x  = 0. Treatment variation irrelevance requires that, for woman i, Y i (x, J x  = 1) = Y i (x, J x  = 0) = Y i (x, •), where the “•” denotes collapsing over all values of J x . In words, this assumption requires that the way in which a particular mother acquired a certain level of education is irrelevant to the outcome. If treatment variation irrelevance is met, then consistency follows naturally as Y = Y(X, •), where Y is the observed outcome and X is the observed exposure [32•].

This over-simplified example is meant to provide intuition on the counterfactual consistency assumption and emphasize the importance of well-defined interventions that can alter the value of the exposure of interest in causal inference [35••]. At times, one can get around mild violations of treatment variation irrelevance using stochastic counterfactuals [36], which allows for the assumption that \( {Y}_i\left(x,{J}_x=1\right)\ \overset{d}{=}\ {Y}_i\left(x,{J}_x=0\right)\ \overset{d}{=}\ {Y}_i\left(x,\bullet \right) \), where “\( \overset{d}{=} \)” stands for equal in distribution [33•]. This argument effectively assumes that the potential outcomes for a given exposure level attained by two different mechanisms may be different, but that they come from the same distribution. Thus, on average, one could expect the potential outcomes to be the same for different exposure mechanisms. However, for variables like maternal education that do not even approximate well-defined interventions, there may be countless ways in which a mother can attain a given level of education, each of which may have a dramatically different effect on the outcome of interest [37].

Our stated example is arguably a case in point. There is some evidence to suggest that early parental investment in children has a more dramatic impact on later health and well-being than incentives to increase skills at a later age [38–41]. Thus, if J x  = 0 in our hypothetical example includes a subset of women who were able to acquire a high-school education due to some intervention that occurred early in childhood (e.g., high-quality early education program [42]), there would likely be systematic differences in the distribution of potential outcomes between women with J x  = 0 and women who acquired a high-school education due to the conditional cash transfer, Pell grant, or scholarship (mechanism J x  = 1), even though they may all have the same value of X.

Note that our focus on education is merely didactic. Other exposures of common interest in social epidemiology are subject to samilar counterfactual consistency problems. These include routinely used racial and ethnic classification measures [19, 43], measures of sex or gender [44], neighborhood-level variables [18], and socioeconomic status [45].

SUTVA: No Interference

A second component of the stable-unit treatment value assumption is that one person’s exposure does not affect another person’s potential outcome [46••]. Because of the nature of typical exposures of interest, interference poses several challenges for causal inference in social epidemiology. For instance, a subject’s health outcome after receiving a voucher to move to a more affluent neighborhood may depend on whether members of the subject’s social network (e.g., neighbors) were also given vouchers [47]. Similarly, the effects of an educational intervention in one subject may “spillover” into other subjects if, for example, the exposed subject influences the health behavior of other subjects because of their exposure status [48]. Indeed, educational interventions have long been identified as potentially subject to interference [49, 50].

Unlike violations of counterfactual consistency, however, interference is not merely a nuisance that requires resolution [46••]. Rather, the presence of interference among units gives rise to different causal effects that may be of interest to social epidemiologists. Hudgens and Halloran [51] defined direct, indirect, total, and overall effects in the presence of interference. Illustrating these effects requires defining new potential outcomes, as presented in Table 2.

Table 2 Hypothetical dataset of 10 subjects from five different groups with a group variable ID i , subject identifier ID j , an observed intervention variable (X) and preterm birth outcome (Y), and the unobserved potential outcomes Y(x 1) to Y(x 4) under four possible exposure allocation strategies
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The hypothetical data in Table 2 can be thought of as coming from a trial to assess the effect of a comprehensive intervention that engaged women in several healthy behaviors during pregnancy. In particular, we let ID i denote whether a woman came from one of five possible birthing classes in which the intervention took place. As in Table 1, Y denotes whether a woman experienced a preterm birth. We let X denote whether a woman was exposed to the intervention (X = 1) or whether she was subject to the standard birthing class protocol (X = 0). Thus, in contrast to Table 1, we assume X in Table 2 represents whether a subject was exposed to a well-defined educational intervention, and consistency is upheld.

The complexity caused by interference is due to how the potential outcomes are defined. When interference is present, one subject’s potential outcome becomes a function of their own exposure, and the exposure from other subjects in their group. In columns 5 to 8 of Table 2, there are 22 = 4 potential outcomes, each defined as a function of a possible exposure allocation strategy:

$$ \begin{array}{cc}\hfill {\boldsymbol{x}}^{(1)}=\left\{0,0\right\}\hfill & \hfill {\boldsymbol{x}}^{(2)}=\left\{1,0\right\}\hfill \\ {}\hfill {\boldsymbol{x}}^{(3)}=\left\{0,1\right\}\hfill & \hfill {\boldsymbol{x}}^{(4)}=\left\{1,1\right\}\hfill \end{array} $$

For example, x (2) denotes an exposure allocation strategy for a given group in which the first subject is exposed and the second is not. This corresponds to the realized exposure allocation strategy for group 4 in Table 2. To define the causal effect of such exposures, we require a measure that describes the outcome for subject j in group i that would have been observed had their exposure been set to x and had the exposure vector for all remaining subjects in group i been set to x i(j). Here, the vector x i(j) represents the exposure values for subjects in group i not including subject j. Because, in our example, there is only one other individual in each group, we refrain from using bold notation and use x i(j) instead. Following Hudgens and Halloran [51], we define

$$ {Y}_{ij}\left({x}_{i(j)},{x}_{ij}\right) $$

to be a preterm birth indicator for subject j in group i that would be observed had their exposure value been set to x ij and had the exposure for the remaining subject in group i been set to x i(j). For example, referring to Table 2, one potential outcome for subject 2 in group 3 can be written as: Y 32(0, 1), which corresponds to the outcome that would be observed if this subject had been exposed and the other subject in group 3 been unexposed. Because this corresponds to the observed exposure status for the group, under counterfactual consistency, the potential outcome Y 32(x 3) = Y 32(0, 1) is equal to the observed outcome Y = 0.

This notation enables us to define four different outcome measures for preterm birth in our hypothetical study. The individual average potential outcome is:

$$ {\overline{Y}}_{ij}\left({x}_{i(j)},x\right)\equiv {\displaystyle \sum_k}Y\left({x}_{i(j)}={x}_k,{x}_{ij}=x\right) Pr\left({X}_{i(j)}={x}_k\Big|{X}_{ij}=x\right), $$

where Pr(X i(j) = x k |X ij  = x) is the probability that subjects in group i other than subject j received a particular exposure x k . For example, the individual average potential outcome for subject 2 in group 3 if they had been exposed is:

$$ \begin{array}{l}{\overline{Y}}_{32}\left({x}_{3(2)},1\right)=Y\left({x}_{3(2)}=\kern0.5em 0,1\right) Pr\left({X}_{3(2)}=0\Big|{X}_{32}=1\right)+\hfill \\ {}\kern9em Y\left({x}_{3(2)}=1,1\right) Pr\left({X}_{3(2)}=1\Big|{X}_{32}=1\right).\hfill \end{array} $$

Similarly, the group average potential outcome \( {\overline{Y}}_i\left({x}_{i(j)},x\right)={\displaystyle {\sum}_{j=1}^{n_i}{\overline{Y}}_{ij}\left({x}_{i(j)},x\right)/{n}_i} \), where n i is the total number of subjects in group i. For example, the group 3 average potential outcome under exposure is: \( {\overline{Y}}_3\left({x}_{3(j)},1\right)=\left[{\overline{Y}}_{32}\left({x}_{3(2)},1\right)+{\overline{Y}}_{31}\left({x}_{3(1)},1\right)\right]/2 \). Finally, we can average over all groups to get the population average potential outcome, as: \( \overline{Y}\left({x}_{i(j)},x\right)={\displaystyle {\sum}_{i=1}^N{\overline{Y}}_i\left({x}_{i(j)},x\right)/N} \), where N is the total number of groups. Thus, the population average potential outcome under exposure for Table 2 is:

$$ \overline{Y}\left({x}_{i(j)},1\right)=\left[{\overline{Y}}_1\left({x}_{1(j)},1\right)+{\overline{Y}}_2\left({x}_{2(j)},1\right)+{\overline{Y}}_3\left({x}_{3(j)},1\right)+{\overline{Y}}_4\left({x}_{4(j)},1\right)+{\overline{Y}}_5\left({x}_{5(j)},1\right)\right]/5. $$

We refer the reader to Box 1 for a summary and interpretation of these measures of occurrence.

Box 1: Measures of Occurrence Under Interference.

\( {\overline{Y}}_{ij}\left({x}_{i(j)},x\right) \)

Individual average potential outcome. The potential outcome for individual j in group i, averaged over the set of exposure scenarios for other group members.

\( {\overline{Y}}_i\left({x}_{i(j)},x\right) \)

Group average potential outcome. The mean of all individual average potential outcomes for group i.

\( \overline{Y}\left({x}_{i(j)},x\right) \)

Population average potential outcome. The mean of all group average potential outcomes.

The counterfactual measures of occurrence outlined in Box 1 can be used to define four different causal effects when interference is present. Hudgens and Halloran [51] introduced causal effects in the presence of interference that consist of overall and total effects, and a decomposition of the total effect into direct and indirect components. Tchetgen Tchetgen and VanderWeele [46••] provide a technical review of these effects and derive finite-sample confidence interval estimators. VanderWeele and Tchetgen Tchetgen [52] provide alternative definitions of direct and indirect effects in the presence of interference that rely on a decomposition of the overall rather than the total effect. We summarize the effects presented by Hudgens and Halloran [51] here and provide some intuition on the exposure effects they capture. The individual average direct effect is defined as the effect of switching a subject’s exposure status, averaged over all possible exposure states for other subjects in the group:

$$ {\overline{DE}}_{ij}\left({\boldsymbol{x}}_{i(j)},{x_i}_j\right)\equiv {\overline{Y}}_{ij}\left({x}_{i(j)},1\right)-{\overline{Y}}_{ij}\left({x}_{i(j)},0\right) $$

In our example, this equation captures the average effect of the educational intervention on the subjects who received it. For instance, subject j’s educational intervention may impact subject j’s outcome because it induces a beneficial change in subject j’s behavior. This effect excludes any average effects that may have occurred through other individuals in the group. For instance, subject j’s educational intervention may impact subject j ′’s outcome because the change in subject j’s behavior also induced a change in subject j ′’s behavior (where j and j ′ index different individuals). To capture this latter type of effect, one has the individual average indirect effect, defined as:

$$ {\overline{IE}}_{ij}\left({\boldsymbol{x}}_{i(j)},{{\boldsymbol{x}}_i^{\prime}}_{(j)}\right)\equiv {\overline{Y}}_{ij}\left({x}_{i(j)},0\right)-{\overline{Y}}_{ij}\left({{\boldsymbol{x}}_i^{\prime}}_{(j)},0\right). $$

This contrast would yield the causal effect of switching the other subject’s exposure from, say, x i(j) = 1 to x′ i(j) = 0. This contrast has also been termed “spillover” effects [47] because the intervention effects are indirectly transmitted to other individuals. Such indirect or spillover effects may be of particular interest to social epidemiologists because of the roles that peer influence and social interaction play in human societies [53–55]. We may also be interested in the individual average total effect, which combines both the direct and indirect effect as:

$$ {\overline{TE}}_{ij}\left({\boldsymbol{x}}_{i(j)},{{\boldsymbol{x}}_i^{\prime}}_{(j)}\right)\equiv {\overline{Y}}_{ij}\left({x}_{i(j)},1\right)-{\overline{Y}}_{ij}\left({x_i^{\prime}}_{(j)},0\right). $$

Finally, we may be interested in the individual average overall effect, defined as:

$$ {\overline{OE}}_{ij}\left({\boldsymbol{x}}_i,{\boldsymbol{x}}_i^{\prime}\right)\equiv {\overline{Y}}_{ij}\left({\boldsymbol{x}}_i\right)-{\overline{Y}}_{ij}\left({\boldsymbol{x}}_i^{\prime}\right), $$

which compares, for example, the effect of exposure assignment strategies x (2) to x (4), as defined above.

While the presence of interference leads to several interesting causal contrasts, it can also add a substantial degree of complexity to the definition of individual-level potential outcomes [46••]. This complexity depends in part on the size of the cluster. For a binary exposure, there are 2k possible potential outcomes for a cluster of size k. For cluster sizes of greater than 2, definitions of individual average direct and indirect effects are more nuanced [56, 52], and statistical inference for these effects is more involved, but still possible [46••]. Finally, as noted by Sobel [47], ignoring interference might lead researchers to conclude that an exposure under study is beneficial, even when it is actually harmful for all individuals in a given group.

A Mediation Approach

Counterfactual consistency violations in social epidemiology are often due to how social exposures are defined. Because typical exposures in social epidemiology are difficult to construe as intervention-based exposures, the counterfactuals of interest are not well-defined [35••]. It is unclear how one might manipulate adult socioeconomic status (SES), especially when defined as a composite measure of education, income, and occupation. In particular, one can often identify several different ways of manipulating each component of SES. For example, income can be increased in one lump sum or via regular installments during a specific period. For those social exposures that do correspond to well-defined interventions, the assumption of no interference can be difficult to satisfy because of the nature of the connections between human beings in society. These challenges curtail our ability to define and estimate counterfactually based causal effects in social epidemiology. Yet, despite these challenges, both causal inference and counterfactual thinking remain central features of social epidemiology [16, 57•, 58].

One potential strategy to deal with these issues was introduced recently in a conceptual paper by VanderWeele and Robinson [19] and implemented in a study seeking to assess strategies to mitigate educational disparities in preterm birth [20]. The general objective of this work is to facilitate the process of addressing questions about health disparities in a formal counterfactual framework. The basic logic of the approach follows from a few commonly accepted principles in social epidemiology:

  1. 1.

    Social exposures such as race, income, education, or occupation, or commonly used measures of socioeconomic position act as “fundamental causes” of a range of health outcomes [59, 60] and thus affect a host of potential factors that subsequently affect the health outcome under study. These factors are often identified as potential mediators of the relation between the social exposure and health outcome of interest.

  2. 2.

    A subset of these potential mediators may be variables that correspond more easily to well-defined interventions and that better satisfy the no interference assumption.

  3. 3.

    In spite of the violation of counterfactual consistency and no interference, associations based on social exposures are critical to understanding how health outcomes are distributed across populations and can contain decisive information on the severity or trajectory of a health disparity in a given population.

It follows from these observations that a formal causal mediation analysis [61] can be used to assess the magnitude of the disparity that would remain under an intervention (possibly hypothetical) on a modifiable mediator of interest, thus enabling a reconciliation of analysis and action from within the counterfactual framework in social epidemiology.

One previously published example of this approach involves the relation between education and preterm birth. Low levels of maternal education have consistently been associated with an elevated risk of preterm birth in a range of settings [25–28, 62]. Some have speculated that increasing the duration between births in a given woman may reduce the social disparities in preterm birth [63, 64], since several markers of social status—including race and education—are also associated with short birth intervals. Naimi et al. used a causal mediation framework to formally address this question [20] and estimate a parameter that corresponds to the magnitude of the educational disparity in preterm birth that would be observed under hypothetical interventions to alter birth intervals in the population. They defined a contrast:

$$ \psi =\mathbb{E}\left[Y(m)\Big|X=1\right]-\mathbb{E}\left[Y(m)\Big|X=0\right] $$

where X ∈ {0, 1} denotes whether a given woman had a high-school education or more, M denotes a birth interval variable, and Y(m) is the preterm birth status that would be observed under an intervention that sets birth intervals of all women in the population to a value m. Thus, referring to Fig. 1, ψ corresponds to the risk difference for the X–Y relation that would be observed under an intervention on M, thus blocking the association between X and Y that occurs through paths 2a and 2b, as well as paths 4a, 3, and 2b. The approach can also be modified to estimate the risk difference for a disparity that would be observed under a more realistic intervention on the mediator in which only a subset of the population is affected by the hypothetical intervention of potential interest [20].

Fig. 1
figure 1

Diagram representing the relations between exposure (X), mediator (M), and outcome (Y), as well as the exposure-outcome confounders (C) and mediator-outcome confounders affected by the exposure (L). This scenario commonly encountered in the causal mediation literature can be used to address questions in social epidemiology in a formal counterfactual framework using causal mediation analysis tools, when the exposure is a social determinant of health (e.g., race, education, income, occupation)

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Discussion: The First Causal Inference Problem

Understanding cause–effect relations is arguably one of the most important objectives of epidemiologic research. Yet, using observational data to do so is subject to well known difficulties. Two challenges that are most commonly identified in social epidemiology are unmeasured confounding and reverse causation [e.g., 58]. While they are challenging issues, the first challenge when dealing with observational data to estimate counterfactually defined causal effects is the non-manipulable exposure problem [19, 45, 65]. In the counterfactual framework, confounding is defined as the presence of statistical dependence between the exposure and the potential outcomes [66••, §7.4]. Thus, concepts of confounding are logically dependent on the clearly defined potential outcomes, which depend on the ability to identify an intervention that can lead to changes in the exposure. Moreover, reverse or reciprocal causation, sometimes misleadingly referred to as “simultaneity” [58, 67], refers to a process in which the exposure and outcome are related in a time-dependent feedback loop. Such circumstances commonly arise in epidemiologic research with longitudinal data [68]. These circumstances can sometimes be dealt with analytically [69], but require at least being able to clearly define the potential outcomes as a function of the exposure of interest. Hence, the emphasis on the need to identify (possibly hypothetical) interventions that can lead to changes in the exposure [3••, 35••] and the difficulty of estimating the causal effects of non-manipulable exposures such as race/ethnicity or sex/gender [65].

Characterizing social exposures (such as, e.g., race/ethnicity) as non-manipulable has not been without its critics. For example, Krieger has argued that considering race as a non-manipulable exposure “in effect relegate[s] ‘race’ to an intrinsic trait” [70, p196] and relies on the “unsubstantiated claim that ‘race’ is an a priori innate biological (i.e., genetic) property of individuals” [71, p937]. Such “essentialist” notions of race/ethnicity are indeed problematic in medical research [72], but they are not implied by counterfactual concepts such as non-manipulability. The causal inference literature defines a non-manipulable parameter as one that cannot be estimated in a randomized trial with (possibly sequential) exposure assignments [73]. As it would be impossible to conduct a randomized trial in which individuals are assigned to commonly used racial/ethnic classifications, it follows that race is not a manipulable exposure.

The solution to this problem would be to identify variables of interest in social epidemiology that fit better into the paradigm of intervention-based effect estimation [3••]. Indeed, Krieger has pointed out [70] such variables can include several manipulable characteristics related (either directly or indirectly) to commonly used racial classifications, including discriminatory practices [74], social policies [75], or even behavioural practices [63]. Though no panacea, use of manipulable exposure variables would do much to resolve the confusion over the interpretation of results in social epidemiology [1, 12, 13, 14].

Decades of work in social epidemiology has now established that disadvantaged social groups—whether defined by racial/ethnic classifications, education, income, occupation, or other characteristics related to the social, political, or economic realms—are strongly associated with a host of adverse health outcomes. Causal inference theory has much to offer social epidemiologists in their pursuit of reducing health disparities and the overall burden of disease.