A Comparison of Potential Outcome Approaches for Assessing Causal Mediation
Abstract
Mediation occurs as part of a hypothesized causal chain of events: An intervention or treatment, T, has an effect on the mediator, M, which then affects an outcome variable, Y. Within the potential outcomes framework for causal inference, three different definitions of the mediation effects have been proposed: principal strata effects (e.g., Rubin, Scand. J. Stat. 31:161–170, 2004; Jo, Psychol. Methods 13:314–336, 2008), natural effects (e.g., Pearl, Proceedings of the Seventeenth Conference on Uncertainty in Artificial Intelligence, 2001; Imai et al., Psychol. Methods 15:309–334, 2010), and controlled effects (e.g., Robins and Greenland, Epidemiology 3:143–155, 1992; VanderWeele, Epidemiology 20:18–26, 2009). We illustrate that each of these definitions answers a different scientific question. We examine five different estimators of the various definitions and discuss identifying assumptions about unmeasured confounding, the existence of direct effects (i.e., the effect of T on Y that is not due to M), iatrogenic effects of T on M, the existence of post-treatment confounders, and the existence of interactions. We assess the robustness of each of the estimators to violations of the assumptions using a simulation study that systematically challenges different aspects of these assumptions. We found that when no assumptions were violated, as may be expected, each approach was unbiased for its respective population value and 95 % confidence interval (CI) coverage was maintained. However, when assumptions are violated, the effects may be severely biased and 95 % CI coverage is not maintained. We suggest that researchers choose the appropriate definition based on the scientific question to be addressed and the identifying assumptions that are plausible given their data.
Mediation is fundamental to many areas of research because many interventions attempt to change one variable in order to cause another variable to change [1]. Mediation analysis helps identify the intermediary processes by which an intervention achieves its effects; understanding the causal mediation pathway can help design interventions that are more effective and less expensive. Given a hypothesized theory regarding the effect of an intervention on a mediator and outcome, mediation analysis can evaluate whether the intervention status affects the mediator and whether the mediator affects the outcome as predicted by theory. Because of its practical and theoretical importance, mediation analysis is now commonly applied in many research disciplines [1]. Recently, more attention has been devoted to the causal aspects of mediation (e.g., [2, 3, 4, 5, 6]) and this work has identified several serious shortcomings of traditional mediation analysis (see also [7]). Fortunately, this work has also generated new methods to deal with the shortcomings of traditional mediation analysis. A primary goal of this paper is to introduce and compare these new methods to estimate causal mediation effects so that researchers can make informed decisions about which method to use.
Most of the new approaches to mediation analysis focus on the potential outcomes framework [8, 9]. Within this framework, three definitions of mediation effects have been proposed: natural, controlled, and principal strata effects. Within each of these definitions, different assumptions have been proposed for identifying and estimating the causal effects. Given the variety of choices, it is difficult for researchers to determine the ideal method for a research question. We compare the various definitions in terms of the assumptions typically used to identify and estimate causal effects and to examine how robust each approach is to violations of assumptions in a simulation study. The data generation for the simulation study is designed to be very general to avoid favoring one approach over another.
This article is organized as follows. First, we review the potential outcomes framework and notation. Second, we describe each definition of causal mediation effects under the potential outcomes framework. Next, for each of these definitions, we introduce the assumptions typically used to identify causal effects and the methods for estimating them. Finally, we turn to the simulation study, including data generation and results, followed by a general discussion.
1 Potential Outcomes Framework for Causal Inference
In the potential outcomes framework (see [8, 9, 10]), each individual has a potential outcome for each possible treatment condition, namely the value of the outcome that would have occurred had the individual received the given treatment condition. For simplicity, consider a binary treatment indicator, T_{i}, where T_{i} = 1 denotes the intervention condition and T_{i} = 0 denotes the control condition for participant i, i = 1,…,n. The potential outcome if the individual receives the intervention is denoted Y_{i}(1), and the potential outcome if the individual is in the control condition is denoted Y_{i}(0). The individual causal effect is the difference between these two potential outcomes. Because each participant is observed in only one condition, only one of these potential outcomes is observed; the other is missing and, therefore, the individual causal effect cannot be computed. However, strategies have been implemented to estimate the causal effect averaged over participants in the study. This average causal effect (ACE) is defined as E[Y_{i}(1) − Y_{i}(0)]; that is, the expected (or average) difference between the two potential outcomes. Information on the potential outcomes framework outside of the context of mediation is provided by Little and Rubin [11], Schafer and Kang [12], and Winship and Morgan [13].
Extending the potential outcomes framework to mediation is more complicated because a mediator is an outcome of the intervention and, therefore, there are also potential values for the mediator under each treatment condition for each individual. The potential mediator under the intervention condition is denoted M_{i}(1), and the potential mediator under the control condition is denoted M_{i}(0). The notation for the potential outcomes is then expanded to include the potential mediators; this notation is referred to as nested potential outcomes. Thus, Y_{i}(1,M_{i}(1)) is the potential outcome if individual i receives the intervention and the potential mediator takes on the value that would have been obtained had they received the intervention; and Y_{i}(0,M_{i}(0)) is the potential outcome if individual i is in the control condition and the potential mediator takes on the value that would have been obtained had they been in the control condition. There are two other potential outcomes that can never be realized in practice and illustrate the challenge of identifying causal mediation effects. These two potential outcomes are needed to define the natural effects and correspond to Y_{i}(1,M_{i}(0)), the potential outcome if individual i receives the intervention and has the potential value of the mediator that would have been obtained had they been in the control condition, and Y_{i}(0,M_{i}(1)), the potential outcome if individual i is in the control condition and has the potential value of the mediator that would have been obtained had they received the intervention. The impossibility of ever observing these two potential outcomes is one of the reasons that causal mediation analysis is controversial.
Throughout the article, we use Y_{i} to denote the observed value of the outcome, M_{i} to denote the observed value for the mediator, and Y_{i}(t,M_{i}(t)) to denote the potential outcomes where t is one of the levels of treatment. We use X_{0} to denote measured baseline (i.e., pre-treatment) confounders. We assume throughout that if an individual receives the intervention, then Y_{i} = Y_{i}(1) = Y_{i}(1,M_{i}(1)) and M_{i} = M_{i}(1). Likewise, if an individual is in the control condition, then Y_{i} = Y_{i}(0) = Y_{i}(0,M_{i}(0)) and M_{i} = M_{i}(0). This assumption is usually referred to as the consistency assumption. In addition, the treatment variation irrelevant assumption [14] states that the potential mediator, M_{i}(t), for individual i when exposed to treatment T_{i} = t will be the same no matter what mechanism is used to assign treatment t to individual i. Similarly, the potential outcome, Y_{i}(t,M_{i}(t)), for individual i when exposed to treatment T_{i} = t and mediator level M_{i}(t) = m will be the same no matter what mechanism is used to assign t and m to individual i. The notation defined above is sufficient for describing the potential outcomes under each treatment level. Additionally we assume throughout that there is no interference among individuals, meaning that an individual’s potential outcomes do not depend on another individual’s treatment assignment. Thus, the potential outcome notation is a function of only T_{i} and not T_{j}, where i and j denote two different individuals. Finally, we assume common support, meaning that the probability of receiving the treatment, P[T_{i} = 1], is between 0 and 1. If P[T_{i} = 1] = 0 or P[T_{i} = 1] = 1, then a causal effect is not meaningfully defined for that individual. This assumption is often referred to as positivity (see, e.g., [15]). Similarly for the mediator, we assume that all individuals have non-zero probability for all levels of mediator.
2 Using the Potential Outcomes Framework to Define Mediation Effects
Principal Strata Effects
Principal stratification [16, 17, 18] was initially developed to handle non-compliance in intervention studies; recognizing that actual receipt of an intervention is a mediating variable between intervention assignment and the outcome, these methods have recently been applied to mediation analysis more broadly. Generally, the population is divided into subgroups, called principal strata, based on a cross-classification of the potential values for the mediator. A local ACE can then be defined within each principal stratum. Suppose that the mediator can take on values of 1 or 0. The four possible principal strata effects are defined as
- 1.
E[Y_{i}(1) − Y_{i}(0)|M_{i}(1) = M_{i}(0) = 1],
- 2.
E[Y_{i}(1) − Y_{i}(0)|M_{i}(1) = M_{i}(0) = 0],
- 3.
E[Y_{i}(1) − Y_{i}(0)|M_{i}(1) = 1, M_{i}(0) = 0], and
- 4.
E[Y_{i}(1) − Y_{i}(0)|M_{i}(1) = 0, M_{i}(0) = 1].
The effect in the first stratum is the causal effect of the intervention on the outcome, among those who would have a value 1 on the mediator regardless of intervention condition. In other words, in this stratum, the intervention had no causal effect on the mediator because the mediator would be 1 regardless of intervention condition. In the compliance literature, this principal stratum is referred to as the always-takers, since they would take the treatment whether they were randomized to it or not. The effect in the second stratum is the causal effect of the intervention on the outcome among those who would have a value 0 on the mediator regardless of intervention condition. In the second stratum, the mediator would be 0 regardless of intervention condition so the intervention had no causal effect on the mediator in this stratum either. In the compliance literature, this principal stratum is referred to as the never-takers. The effect in the third stratum is the causal effect of the intervention on the outcome among those who would have a value of 1 on the mediator if they received the intervention and 0 if they did not. In the compliance literature, this principal stratum is referred to as the compliers. The effect in the fourth stratum is the causal effect of the intervention on the outcome among those who would have a value of 0 on the mediator if they received the intervention and a 1 if not. In the compliance literature, this principal stratum is referred to as the defiers, since their treatment status reflects the opposite of their randomization. For the latter two strata, the intervention does have a causal effect on the mediator. Thus, the principal strata effects in these two strata represent the causal effects of the intervention on the outcome among those for whom the intervention had an effect on the mediator. The distinction between these two strata is that the effect of the intervention on the mediator is in opposite directions. All of these are causal effects of the intervention on the outcome among a latent subgroup or stratum of individuals: stratum membership is latent because only one of the potential mediators is observed. Finally, the ACE, E[Y(1) − Y(0)], or total effect (TE), is defined as the sum of the four principal strata effects, E[Y(1) − Y(0)|M(0) = M(1) = 1] * P[M (0) = M (1) = 1] + E [Y (1) − Y(0) | M(0) =M(1) = 0] * P[M(0) = M(1) = 0] + E[Y(1) − Y(0)|M(0) = 0,M(1) = 1] * P[M(0) =0,M(1) = 1] + E[Y(1) − Y(0)|M(0) = 1, M(1) = 0] * P[M(0) = 1,M(1) = 0] = E[Y_{i}(1,M_{i}(1)) − Y_{i}(0,M_{i}(0))]. It is referred to as the intent-to-treat effect in the compliance literature.
Note that the principal strata effects do not rely on nested potential outcomes of the form, Y_{i}(t,M_{i}(t)). Principal strata effects rely only on the potential outcomes, Y_{i}(0), Y_{i}(1), M_{i}(1), and M_{i}(0). Thus, principal strata effects do not rely on Y_{i}(1,M_{i}(0)) or Y_{i}(0,M_{i}(1)), which cannot be realized for any individual. This focus on only possible potential outcomes is both a strength and a limitation of this approach; we return to this point later.
Natural Effects
Natural direct effects (NDEs) are defined by setting the mediator to one of its potential values and changing the intervention status. One NDE of interest, E[Y_{i}(1,M_{i}(0)) − Y_{i}(0,M_{i}(0))], often called the pure NDE (e.g., [19]), defines a causal effect of the intervention on the outcome when the mediator is held to the value that would have been obtained had the individual not received the intervention (i.e., the effect of the intervention on the outcome if the intervention did not cause a change in the mediator or if the effect of the intervention on the mediator was in some way blocked). Additionally E[Y_{i}(1,M_{i}(1)) − Y_{i}(0,M_{i}(1))], sometimes called the total NDE, defines a causal effect of the intervention on the outcome when the mediator is held to the value that would have been obtained had the individual received the intervention (i.e., the effect of the intervention on the outcome if absence of the intervention did not prevent a change in the mediator). Note that since each individual’s set of potential mediators may be unique, setting the mediator to one of the potential mediators (i.e., M_{i}(0) or M_{i}(1)) is not equivalent to setting the mediator to a given value of the mediator m. In other words, the value at which the mediator is set can be different for every individual. We will denote pure NDE and the total NDE as NDE_{M(0)} and NDE_{M(1)}, respectively, where the subscript indicates the potential value the mediator is set to.
Natural indirect effects (NIEs) are defined by setting the intervention condition and changing the values of the potential mediator, E[Y_{i}(1,M_{i}(1)) − Y_{i}(1,M_{i}(0))] or E[Y_{i}(0,M_{i}(1)) − Y_{i}(0,M_{i}(0))]. The former, sometimes referred to as the total NIE, defines the causal effect of receiving the intervention and having the value on the mediator that would be obtained under the intervention versus having the value on the mediator that would be obtained under the control condition; in other words, the effect of the intervention due to intervention-induced changes in the mediator. The latter, sometimes referred to as the pure NIE, defines the causal effect of receiving the control condition and having the value on the mediator that would be obtained under the intervention condition versus having the value on the mediator that would be obtained under the control condition. Note that again, these effects are defined with respect to potential mediators rather than a specific observed value of the mediator. Therefore, the value of the potential mediators may differ across individuals. We will denote the two NIEs as NIE_{1} and NIE_{0}, where the subscript denotes the value to which the intervention status is set.
Note that for NDEs and NIEs, there is an effect for each level of the intervention. For example, in the case of a binary treatment, there are two NDEs and two NIEs. The TE, defined as E[Y(1) − Y(0)] = E[Y_{i}(1,M_{i}(1)) − Y_{i}(0,M_{i}(0))], can be decomposed into E[Y_{i}(1,M_{i}(1)) − Y_{i}(1,M_{i}(0))] + E[Y_{i}(1,M_{i}(0)) − Y_{i}(0,M_{i}(0))] or E[Y_{i}(0,M_{i}(1)) − Y_{i}(0,M_{i}(0))] + E[Y_{i}(1,M_{i}(1)) − Y_{i}(0,M_{i}(1))]. That is, the TE is the sum of the total NIE, NIE_{1}, and the pure NDE, NDE_{M(0)}; or of the pure NIE, NIE_{0}, and the total NDE, NDE_{M(1)}. The terms pure and total refer to whether interaction effects are included with the direct or indirect effect. Specifically, pure means that the interaction effects are not included and total means that they are. Therefore, the TE must include a total and a pure effect.
Controlled Effects
The controlled direct effect (CDE; [20]) is the causal effect of the intervention on the outcome when setting the mediator to a specific value, m, for the entire population. That is, E[Y_{i}(1,m) − Y_{i}(0,m)] where Y_{i}(t,m) is the potential outcome when T = t and M = m. We will denote the controlled direct effect as CDE_{m}, where the subscript m denotes the particular value to which m is held or set. Note the difference between the CDE and the NDE. For the CDE, the value at which the mediator is set (i.e., held constant) is the same for every individual. Also, for a binary treatment, there are two NDEs, but there are as many CDEs as there are possible values of the mediator. We have continued to use the i subscript through this section to emphasize that the CDE sets the value of the mediator to be the same for all individuals, whereas the NDE allows the value at which the mediator is set to vary across individuals.
There is not a controlled indirect effect that is comparable to the NIE without further assumptions, which will be discussed below. To illustrate, consider defining the effect E[Y_{i}(1,m) − Y_{i}(1,m′)] for two different values, for example m = 0 and m′ = 1. We will denote this effect as θ_{M|t=1} and the corresponding E[Y_{i}(0,m) − Y_{i}(0,m′)] as θ_{M|t=0}. The former is the effect of, for example, a one-unit change in the mediator on the outcome when T_{i} = 1. This effect does not tell us how the one-unit difference between m and m′ has come about: it could have happened through the treatment intervention or through some other mechanism. On the other hand, consider the NIE, E[Y_{i}(1,M_{i}(1)) − Y_{i}(1,M_{i}(0))], the effect of the intervention due to intervention-induced changes in the mediator. This effect, unlike E[Y_{i}(1,m) − Y_{i}(1,m′)], does indicate that the intervention caused the difference in M_{i}(1) and M_{i}(0) because these are potential outcomes under two different levels of the intervention. This distinction may seem subtle but it is extremely important. The NIE is what behavioral scientists typically think of as the mediation effect, commonly denoted ab in the behavioral science literature, whereas E[Y_{i}(1,m) − Y_{i}(1,m′)] is the causal effect of the mediator on the outcome, holding constant the intervention status, and is commonly denoted as b in the behavioral science literature. The effects θ_{M|t=1} and θ_{M|t=0} also imply that it is possible to set the mediator to the same value for all individuals as mentioned above. For elaboration of these conceptual issues, see VanderWeele and Vansteelandt [21].
Summary of assumptions
Effects | |||||
---|---|---|---|---|---|
Natural effects | Controlled effects | Principal strata effects | |||
Assumptions | Imai et al. [4] | IPW | RPM | TSLS | Bayesian |
No unmeasured confounders of | |||||
(a) T & M | ✓ | ✓ | ✓ | ✓ | ✓ |
(b) T & Y | ✓ | ✓ | ✓ | ✓ | ✓ |
(c) M & Y | ✓ | ✓ | |||
No interactions between | |||||
T & M on Y | ✓ | ✓ | |||
T & X on Y | ✓ | ✓ | |||
M & X on Y | ✓ | ||||
Interactions between T & X on M | ✓ | ||||
(d) No post-T confounders | ✓ | ✓ | ✓ | ✓ | |
Monotonicity (no defiers) | ✓ | ||||
Exclusion restriction (full mediation) | ✓ |
3 Identification
The causal effects defined above are written in terms of potential outcomes, not all of which can be observed. If all the potential outcomes were observed, then all of the above effects could be easily estimated. In order to estimate causal effects based on the observed data, assumptions must be made in order to identify the causal effects.
Principal Strata Effects
Generally, principal strata effects are identified by assuming that there is no one for whom the intervention has an iatrogenic (i.e., undesirable) effect (e.g., P[M(0) = 1, M(1) = 0] = 0), which is typically referred to as the monotonicity assumption. Note that the CACE is the causal effect of interest under the hypothesis that the intervention will increase the value of the mediator (i.e., increasing values of the mediator are desirable). If the hypothesis happens to be that the intervention decreases the value of the mediator (i.e., decreasing values of the mediator are desirable), the monotonicity assumption is that P[M(0) = 0, M(1) = 1] = 0, and thus, scientific interest lies in DACE. That is, the DACE would be the causal effect of interest.
Additionally, it is assumed that the only way in which the intervention can affect the outcome is through the mediator. This is known as the exclusion restriction and implies that E[Y_{i}(1) − Y_{i}(0)|M_{i}(1) = M_{i}(0)] = 0. That is, among those for whom there is no causal effect of the intervention on the mediator, there is no causal effect of the intervention on the outcome. However, the exclusion restriction also means that there is no direct effect of the intervention on the outcome, among those for whom there is a causal effect of the intervention on the mediator (i.e., those in either stratum 3 or 4; the compliers or defiers). In fact, the only way that the principal strata effects for stratum 3 or 4 can be interpreted as an indirect effect is if the exclusion restriction holds. Otherwise, the causal effect estimated is the total effect of the intervention on the outcome among those for whom the intervention had a causal effect on the mediator. The exclusion restriction is particularly difficult to rationalize given that most interventions are designed to affect multiple mediators that are hypothesized to affect the outcome. In addition, an interaction between T and M is a violation of the exclusion restriction [5, 24].
Finally, it is assumed that there are no unmeasured confounders of T and Y (e.g., there is random assignment to T), which can be stated formally as T ⏊ Y(0),Y(1)|X_{0}. This assumption allows T to be used as an instrumental variable (IV) in the two-stage least-squares (TSLS) estimation to be described below. Note that unlike other causal mediation methods, the principal strata approach does not require a no-unmeasured-confounding assumption for M and Y (given the other assumptions stated above).
Note that the assumptions stated above are not the only set that could be used for identification. Gallop et al. [25] proposed alternative identification assumptions. They do not require the exclusion restriction or monotonicity assumption. Instead, baseline covariates, which predict the principal strata, are used to identify the stratum-specific ACE. In addition, they assume that there are no interactions between these baseline covariates and T within each principal stratum and that there are no unmeasured confounders of T and Y.
Natural Effects
To identify the natural effects, it is usually assumed (e.g., [22, 26]) that (a) there are no unmeasured confounders of the intervention and the mediator, T ⏊ M(0),M(1)|X_{0}; (b) there are no unmeasured confounders of the intervention and the outcome; (c) there are no unmeasured confounders of the mediator and the outcome; and that (d) there are no measured or unmeasured confounders of the mediator and outcome that have themselves been influenced by the intervention (i.e., no post-treatment confounders, denoted X_{1}). Note that the set of variables in X_{0} do not need to be the same for (a) and (b) and that if X_{1} is not affected by the intervention, then it does not violate (d) [27]. If individuals are randomized to the intervention, then (a) and (b) will typically hold as long as the randomization does not fail (e.g., individuals comply with the assigned intervention and there is no selective attrition). However, unless individuals are also randomized to levels of the mediator, which is typically impossible in practice, (c) is not guaranteed to hold. These are obviously very strong assumptions that cannot be tested in any empirical application. Nevertheless, if the researcher has given careful thought to all potential confounders, measured them, and properly adjusted for them, assumptions (a)–(c) are plausible. Furthermore, sensitivity analyses have been developed and conducted to assess the impact of violations of these assumptions (e.g., [4, 28, 29]).
Assumption (d) of no post-treatment confounders of the mediator and outcome is more difficult to rationalize. Note that confounders of the mediator and outcome that have been influenced by the intervention are essentially mediators themselves, although they may not be of scientific interest (i.e., the investigator is not interested in their effects and simply wishes to control for them). Assumption (d) is problematic given that most interventions target multiple mediators and because the assumption is that there are no measured or unmeasured variables such as these. Even if they are known to exist and have been measured, they must be assumed not to exist. The mathematical proof of this identification assumption is given in Avin et al. [30].
As with principal strata effects, other assumptions may be used to identify the natural effects ([31, 32, 33], but these assumptions do not relax assumption (d). Parametric assumptions, such as linearity, can be used to relax assumption (d).
Controlled Effects
Identification of this approach for obtaining the indirect effect requires assuming that there are no unmeasured confounders of the intervention and the mediator (i.e., assumption (a) from above), the intervention and the outcome (i.e., assumption (b) from above), and the mediator and the outcome (i.e., assumption (c) from above); and (e) that there are no interactions between the intervention and the mediator. As discussed by VanderWeele [26], if there is no interaction between the intervention and the mediator, then the CDE is the same for every level of the mediator. In this case, the CDE is equal to the NDEs (NDE_{M(0)} = NDE_{M(1)} = CDE_{m}) and the CDE can be subtracted from the TE, via the decomposition for natural effects (e.g., TE-CDE_{m} = TE-NDE_{M(0)} = NIE_{1}), to obtain the indirect effect. If there is no interaction, the NIE_{1} = NIE_{0} and, therefore, the decomposition may also be written as TE-NDE_{M(1)} = NIE_{0}. Note that this approach does not, however, require assumption (d) but replaces it with a parametric assumption. As before, if individuals are randomized to levels of the intervention, then assumptions (a) and (b) will hold, and if individuals could be randomly assigned to levels of the mediator, then assumption (c) would also hold.
Assumptions (a) and (e) are not required for identification of the CDE or for θ_{M}, the causal effect of M on Y. These two assumptions are only needed to identify the indirect effect. Note that assumption (e) is not as innocuous as it may seem at first. For linear models, it requires the absence of a T by M interaction (i.e., a non-significant coefficient estimate for the product term, T × M). In non-linear models, this assumption is more restrictive; the controlled direct effects at every level, m, of the mediator must be equal.
As with natural effects and principal strata effects, other assumptions may be used to identify the causal effects instead of (a)–(c) and (e). Specifically, assumption (c) can be replaced by assuming that (f) there are no interaction effects between baseline covariates and the mediator, and between baseline covariates and intervention assignment on the potential outcomes; and that (g) there are strong interaction effects between the baseline covariates and intervention assignment on the mediator. The latter two assumptions are key for using the G-estimator proposed by Ten Have et al. [34], described below. All assumptions are summarized in Table 14.1.
When certain conditions or assumptions are met, some of the estimands discussed may be equivalent. For example, as discussed above, if there are no interactions between the intervention and the mediator, the NDE will equal the CDE. Jo [5] and Sobel [24] showed that the traditional behavioral science definitions correspond to the principal strata definitions of effects if there are no unmeasured confounders of M and Y, of T and Y, and of T and M; no interactions between T and M; and the exclusion restriction, monotonicity assumption, and linearity hold. VanderWeele [23] discusses the relations between definitions of principal strata effects and natural effects, and between principal strata effects and controlled effects. Lynch et al. [35] compared and contrasted direct effect definitions in the Ten Have et al. [34] approach with those of the traditional [29] approach and the principal stratification approach. Ten Have and Joffe [33] reviewed identifying assumptions for direct effects under each of the three approaches. However, to our knowledge, the comparisons presented here are the first to focus on definitions, identification assumptions, and estimation methods for all of the effects defined under each approach.
4 Estimation
For each of the definitions, different estimators have been proposed using different sets of identifying assumptions described above. We will consider only a few estimators for each definition. For principal strata effects, we will consider a TSLS IV estimator [36] and a Bayesian estimator [25]. For natural effects, we will consider the estimator proposed by Imai et al. [4]. For controlled effects, we will consider the G-estimator proposed by Ten Have et al. [34] and an inverse propensity weighted (IPW) estimator [3, 26].
Principal Strata Effects
Given the monotonicity and exclusion restriction identifying assumptions, the TSLS IV estimator [36], in which intervention assignment is the instrument, is typically used to estimate the principal strata effects. In order for the intervention assignment to be considered an instrumental variable, individuals should be randomly assigned to intervention conditions such that assumptions (a) and (b) hold. Further, for all practical purposes, the principal stratification framework requires a binary mediator.^{1} Even for a mediator that takes on, say, 5 values, the number of latent principal strata grows tremendously. Specifically, for a mediator that takes on 5 possible values, there would be 25 latent strata or subgroups of individuals and thus it would be difficult to identify and estimate principal strata effects. Given a binary mediator, monotonicity, the exclusion restriction, and random assignment to the intervention (i.e., no unmeasured confounders of T and M or T and Y), the latent subgroups of individuals are no longer latent because all but one stratum is eliminated.
In the recent statistical literature, there have been attempts to use different identifying assumptions and Bayesian estimation procedures (e.g., [25, 37]) in order to relax the exclusion restriction. The Elliott et al. estimator is limited to both binary mediators and outcomes. We use the Bayesian estimator proposed by Gallop et al. to estimate the principal strata effect. This approach was developed to estimate the direct effect, although it estimates all four principal strata effects. Because the authors were not interested in an unbiased causal estimate of the indirect effect, they did not need an assumption of no unmeasured confounders of M and Y. However, if interest lies in a causal estimate of the indirect effect, then this assumption is required. In addition, both the TSLS IV and Bayesian estimators require assumption (d). Although not explicitly stated in the previous literature, a post-T confounder violates the exclusion restriction because there is pathway from T to Y that does not go through M.
Natural Effects
Several estimators have now been proposed for estimating natural effects (e.g., [38, 39]) but we will focus on the estimator proposed by Imai and colleagues [4, 22] and implemented in the R package mediation [40], which uses identifying assumptions (a)–(d). This estimator involves generating bootstrapped samples and fitting models, which may be parametric or non-parametric, for the observed outcome and observed mediator. From these models, potential values of the mediator are simulated and then potential values of the outcome are simulated given the simulated values of the mediator. Once all of the potential values for the mediator and outcome have been simulated, the natural effects can be computed as defined previously.
Controlled Effects
VanderWeele [26] proposed using a marginal structural model (MSM; [41]) with an IPW estimator for defining and estimating the controlled direct effect in the mediation context. MSMs are models for the potential outcomes and are used to define causal effects. For example, for a continuous outcome, the MSMs may be given as \( E\left[M(t)\right]={\beta}_{0M}+{\beta}_1t \) and \( E\left[Y\left(t,m\right)\right]={\beta}_{0Y}+{\beta}_2t+{\beta}_3m \), where \( {\beta}_2=E\left[Y\left(1,m\right)-Y\left(0,m\right)\right]=\left({\beta}_{0Y}+{\beta}_2+{\beta}_3m\right)-\left({\beta}_{0Y}+{\beta}_3m\right) \) is the CDE defined above, \( {\beta}_1=E\left[M(1)-M(0)\right]=\left({\beta}_{0M}+{\beta}_1\right)-{\beta}_{0M} \) is the effect of the intervention on the mediator, and \( {\beta}_3=E\left[Y\left(t,m\right)-Y\left(t,{m}^{\prime}\right)\right] \) is the effect of the mediator on the outcome for T = t. A T × M interaction term can also be included in the MSM. MSMs are fit by choosing an appropriate model for the observed outcome (e.g., linear regression, logistic regression, survival model), but using the IPW estimator instead of the usual ordinary least squares or maximum likelihood estimator. As long as assumption (e) holds, an estimate of the indirect effect may be obtained by subtracting the CDE from the TE.
For controlled effects, we will also examine the modified G-estimator for the rank preserving model (RPM) described in Ten Have et al. [34]. This estimator does not require assumption (c); however, it does require that individuals are randomized to the intervention (i.e., assumptions (a) and (b)). It also assumes that there are no interaction effects between baseline covariates, X_{0}, and the mediator and between baseline covariates, X_{0}, and intervention assignment on the potential outcomes. However, there should be strong interaction effects between the baseline covariates, X_{0}, and intervention assignment on the mediator. Essentially, this estimator is using the interactions between baseline covariates, X_{0}, and intervention assignment as instrumental variables. The G-estimator also requires assumption (e). Thus, in summary, the G-estimator exchanges assumption (c) for an assumption of strong interaction effects between the baseline covariates and intervention assignment on the mediator. Although not a stated assumption of the G-estimator (see [34, 35]), assumption (d) is also required. The assumptions for each estimator are summarized in Table 14.1.
5 Simulation Study: Method
5.1 Simulation Study Conditions
The simulation study crosses four assumption violation conditions with four confounding conditions. The first confounding scenario (A) does not involve any confounders. The second confounding scenario (B) involves a pre-treatment confounder, X_{0}, of M and Y that has not been influenced by T. The third confounding scenario (C) involves a post-treatment but pre-mediator confounder, X_{1}, of M and Y that has been influenced by T. The fourth confounding scenario (D) involves a pre-treatment confounder of T, M, and Y, such that there is not random assignment to T. These confounding conditions are crossed with two sample size conditions, N = 100 and N = 500, and three other conditions that systematically violate the assumptions of the different approaches; specifically, monotonicity, the exclusion restriction, and the no-interaction between T and M assumption. A fourth condition in which none of these assumptions are violated is also included. To summarize, for each sample size, there are 16 simulation conditions as follows: no confounders/no violations, no confounders/exclusion restriction violated, no confounders/monotonicity violated, no confounders/no-interaction violated, unmeasured pre-T confounder of M and Y/no violations, unmeasured pre-T confounder of M and Y/exclusion restriction violated, unmeasured pre-T confounder of M and Y/monotonicity violated, unmeasured pre-T confounder of M and Y/no-interaction violated, post-T confounder of M and Y/no violations, post-T confounder of M and Y/exclusion restriction violated, post-T confounder of M and Y/monotonicity violated, post-T confounder of M and Y/no-interaction violated, unmeasured pre-T confounder of T, M, and Y/no violations, unmeasured pre-T confounder of T, M, and Y/exclusion restriction violated, unmeasured pre-T confounder of T, M, and Y/monotonicity violated, unmeasured pre-T confounder of T, M, and Y/no-interaction violated.
In each of the simulation conditions, we generated 1000 data sets and estimated the following causal effects: principal strata effects with TSLS IV estimator, principal strata effects with Bayesian estimator, controlled effects using the IPW estimator, controlled effects using the RPM G-estimator, and natural effects using the Imai et al. [4] estimator.
5.2 Data Generation
The goal is for the data generation to be general enough that it does not favor one approach over another. However, we also need to know the population values for each of the effects. Therefore, we generated all of the potential outcomes for each individual, including the ones that would never be observed for any individual—Y(1, M(0)) and Y(0, M(1))—so that the causal effects defined previously may be directly computed for each individual. By generating data for all potential outcomes, the true values in all conditions are known.
Population parameter values for simulation study
Population parameters | |||||||||||||||||||
---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|---|
Conf. scenario | Violation | β_{0} | β_{1} | β_{2} | β_{3} | β_{4} | β_{5} | p_{00} | p_{01} | p_{10} | p_{11} | ||||||||
No conf. | No violation | 0.2 | 0 | 0.39 | 0 | 0 | 0 | 0.33 | 0.33 | 0 | 0.33 | ||||||||
Exclusion rest. | 0.2 | 0.39 | 0.39 | 0 | 0 | 0 | 0.33 | 0.33 | 0 | 0.33 | |||||||||
Monotonicity 1 | 0.2 | 0 | 0.39 | 0 | 0 | 0 | 0.25 | 0.25 | 0.25 | 0.25 | |||||||||
Monotonicity 2 | 0.2 | 0 | 0.39 | 0 | 0 | 0 | 0.2 | 0.5 | 0.1 | 0.2 | |||||||||
No T-M interact. | 0.2 | 0.39 | 0.39 | 0.39 | 0 | 0 | 0.33 | 0.33 | 0 | 0.33 | |||||||||
γ_{0} | γ_{1} | γ_{2} | γ_{0} | γ_{1} | γ_{2} | γ_{0} | γ_{1} | γ_{2} | γ_{0} | γ_{1} | γ_{2} | ||||||||
Pre-T unmeasured conf. of M and Y | No violation | 0.2 | 0 | 0.39 | 0 | 0.2 | 0 | 0.3 | 0.3 | 0 | 0.3 | 1 | 0 | 0^{a} | 0.3 | 0.7 | 0 | ||
Exclusion rest. | 0.2 | 0.39 | 0.39 | 0 | 0.2 | 0 | 0.3 | 0.3 | 0 | 0.3 | 1 | 0 | 0^{a} | 0.3 | 0.7 | 0 | |||
Monotonicity | 0.2 | 0 | 0.39 | 0 | 0.2 | 0 | 0.3 | 0.3 | 0 | 0.3 | 1 | 0 | 0.3 | 0.3 | 0 | 0.3 | 0.7 | 0 | |
No T-M interact. | 0.2 | 0.39 | 0.39 | 0.39 | 0.2 | 0 | 0.3 | 0.3 | 0 | 0.3 | 1 | 0 | 0^{a} | 0.3 | 0.7 | 0 | |||
Post-T conf. of M and Y | No violation | 0.2 | 0 | 0.39 | 0 | 0.2 | 0.2 | 0.3 | 0.3 | 0.3 | 0.3 | 1 | 1 | 0^{a} | 0.3 | 0.7 | 0.7 | ||
Exclusion rest. | 0.2 | 0.39 | 0.39 | 0 | 0.2 | 0.2 | 0.3 | 0.3 | 0.3 | 0.3 | 1 | 1 | 0^{a} | 0.3 | 0.7 | 0.7 | |||
Monotonicity | 0.2 | 0 | 0.39 | 0 | 0.2 | 0.2 | 0.3 | 0.3 | 0.3 | 0.3 | 1 | 1 | 0.3 | 0.3 | 0.3 | 0.3 | 0.7 | 0.7 | |
No T-M interact. | 0.2 | 0.39 | 0.39 | 0.39 | 0.2 | 0.2 | 0.3 | 0.3 | 0.3 | 0.3 | 1 | 1 | 0^{a} | 0.3 | 0.7 | 0.7 |
5.3 Population Values
The population values for each condition of the simulation study are given in Table 14.2. For confounding scenario A in the conditions in which the monotonicity assumption holds, p_{10} = 0 and p_{00} = p_{11} = p_{01} = 1/3. The proportions for confounding scenario A when monotonicity was violated were set to p_{00} = 0.2, p_{11} = 0.2, p_{10} = 0.1, and p_{01} = 0.5. For confounding scenario A only, we also studied a condition in which the monotonicity assumption was violated and all proportions were set to 0.25. The purpose of this condition was to examine what happens as the proportion of defiers increases. In addition, because the proportions are equal, the indirect effect is zero because for 25 % of the sample the indirect effect is positive and for another 25 % of the sample, the indirect effect is equally negative. Thus, the effects cancel out. Although it is unlikely that the stratum proportions would ever be exactly equal or that the proportion of defiers would ever be as large as 0.25, this condition provides some idea of how extreme the bias may become. In the mediation context, the proportion of defiers represents the proportion of individuals for whom the intervention has an iatrogenic effect on the mediator.
For confounding scenario D, the parameter settings were the same as confounding scenario B. However, in confounding scenario D, T was generated from a Bernoulli distribution with p = 1/(1 + exp(−0.2 * X_{0})) so that the pre-T confounder had an effect on intervention assignment. For only the N = 500 sample size condition, we examined a large effect size condition in which we replaced 0.39 with 0.59 for β_{1}, β_{2}, and β_{3} in Table 14.2.
6 Simulation Study: Results
Confounding scenario A (no unmeasured confounders) results (N = 500) for medium effect size
NIE | NDE | TE | IPW CDE | IPW θ_{M} | RPM θ_{M} | RPM CDE | TSLS IV | Bayesian | |
---|---|---|---|---|---|---|---|---|---|
No violations | |||||||||
TRUE | 0.13 | 0 | 0.13 | 0 | 0.39 | 0.39 | 0 | 0.39 | 0.39 |
MEAN | 0.131 | −0.002 | 0.129 | −0.002 | 0.391 | 0.391 | −0.002 | 0.383 | 0.390 |
BIAS | 0.001 | −0.002 | −0.001 | −0.002 | 0.001 | 0.001 | −0.002 | −0.007 | 0.000 |
SD | 0.037 | 0.094 | 0.090 | 0.095 | 0.095 | 0.095 | 0.095 | 0.273 | 0.146 |
MSE | 0.001 | 0.009 | 0.008 | 0.009 | 0.009 | 0.009 | 0.009 | 0.072 | 0.021 |
Coverage | 94.4 % | 94.9 % | 94.8 % | 94.0 % | 93.9 % | 93.9 % | 94.0 % | 95.9 % | 99.8 % |
Exclusion restriction violated | |||||||||
TRUE | 0.13 | 0.39 | 0.52 | 0.39 | 0.39 | 0.39 | 0.39 | 0.78 | 0.78 |
MEAN | 0.130 | 0.391 | 0.521 | 0.391 | 0.392 | 0.392 | 0.391 | 1.591 | 0.783 |
BIAS | −0.000 | 0.001 | 0.001 | 0.001 | 0.002 | 0.002 | 0.001 | 0.811 | 0.003 |
SD | 0.034 | 0.096 | 0.091 | 0.095 | 0.095 | 0.095 | 0.095 | 0.318 | 0.151 |
MSE | 0.001 | 0.009 | 0.0083 | 0.009 | 0.008 | 0.008 | 0.009 | 0.771 | 0.023 |
Coverage | 96.2 % | 95.3 % | 95.2 % | 95.6 % | 95.7 % | 95.7 % | 95.6 % | 23.2 % | 99.9 % |
Monotonicity violated (all proportions equal) | |||||||||
TRUE | 0 | 0 | 0 | 0 | 0.39 | 0.39 | 0 | 0.39 | 0.39 |
MEAN | −0.000 | 0.003 | 0.003 | 0.003 | 0.388 | 0.388 | 0.003 | 1.444 | 0.365 |
BIAS | −0.000 | 0.003 | 0.003 | 0.003 | −0.002 | −0.002 | 0.003 | 1.054 | −0.025 |
SD | 0.018 | 0.094 | 0.097 | 0.090 | 0.090 | 0.090 | 0.090 | 43448.8 | 0.285 |
MSE | 0.000 | 0.009 | 0.009 | 0.009 | 0.008 | 0.008 | 0.009 | 2236.32 | 0.082 |
Coverage | 95.1 % | 92.9 % | 92.7 % | 93.4 % | 95.7 % | 95.7 % | 93.4 % | 99.7 % | 99.3 % |
Monotonicity violated (p_{10} = 0.1, p_{01} = 0.5, p_{00} = p_{11} = 0.2) | |||||||||
TRUE | 0.156 | 0 | 0.156 | 0 | 0.39 | 0.39 | 0 | 0.39 | 0.39 |
MEAN | 0.154 | −0.001 | 0.154 | −0.001 | 0.387 | 0.387 | −0.001 | 0.387 | 0.390 |
BIAS | −0.002 | −0.001 | −0.002 | −0.001 | −0.003 | −0.003 | −0.001 | −0.003 | −0.001 |
SD | 0.042 | 0.100 | 0.093 | 0.098 | 0.098 | 0.098 | 0.098 | 0.227 | 0.159 |
MSE | 0.002 | 0.010 | 0.009 | 0.010 | 0.010 | 0.010 | 0.010 | 0.054 | 0.025 |
Coverage | 96.3 % | 94.7 % | 94.7 % | 94.8 % | 95.3 % | 95.3 % | 94.8 % | 94.8 % | 97.8 % |
Results for violation of no-interaction between T and M assumption for all confounding scenarios
NIE_{0} | NIE_{1} | NDE_{M(0)} | NDE_{M(1)} | TE | CDE_{0} | CDE_{1} | IPW θ_{M|t=0} | IPW θ_{M|t=1} | TSLS IV | Bayesian | |
---|---|---|---|---|---|---|---|---|---|---|---|
Scenario A (no confounders) | |||||||||||
TRUE | 0.13 | 0.26 | 0.52 | 0.65 | 0.78 | 0.39 | 0.78 | 0.39 | 0.78 | 1.17 | 1.17 |
MEAN | 0.129 | 0.260 | 0.513 | 0.645 | 0.773 | 0.380 | 0.778 | 0.386 | 0.785 | 2.356 | 1.166 |
BIAS | −0.001 | 0.000 | −0.007 | −0.005 | −0.007 | −0.010 | −0.002 | −0.004 | 0.005 | 1.186 | −0.004 |
SD | 0.049 | 0.056 | 0.101 | 0.098 | 0.091 | 0.134 | 0.136 | 0.135 | 0.135 | 0.363 | 0.147 |
MSE | 0.002 | 0.003 | 0.010 | 0.010 | 0.008 | 0.019 | 0.018 | 0.018 | 0.019 | 1.543 | 0.021 |
Coverage | 94.7 % | 96.1 % | 94.6 % | 95.8 % | 95.9 % | 95.4 % | 95.4 % | 95.0 % | 95.3 % | 2.2 % | 99.8 % |
Scenario B (unmeasured pre-T confounder of M and Y) | |||||||||||
TRUE | 0.132 | 0.263 | 0.515 | 0.647 | 0.779 | 0.39 | 0.78 | 0.39 | 0.78 | 1.17 | 1.17 |
MEAN | 0.135 | 0.295 | 0.480 | 0.640 | 0.775 | 0.327 | 0.804 | 0.405 | 0.882 | 2.339 | 1.245 |
BIAS | 0.004 | 0.031 | −0.035 | −0.007 | −0.004 | −0.063 | 0.024 | 0.015 | 0.102 | 1.169 | 0.075 |
SD | 0.051 | 0.059 | 0.103 | 0.106 | 0.097 | 0.135 | 0.140 | 0.138 | 0.137 | 0.357 | 0.149 |
MSE | 0.003 | 0.004 | 0.012 | 0.011 | 0.009 | 0.022 | 0.021 | 0.021 | 0.029 | 1.494 | 0.028 |
Coverage | 94.8 % | 92.6 % | 94.1 % | 93.9 % | 94.4 % | 92.5 % | 93.2 % | 94.6 % | 89.5 % | 3.2 % | 99.7 % |
Scenario C (post-T confounder of M and Y) | |||||||||||
TRUE | 0.154 | 0.307 | 0.711 | 0.864 | 1.018 | 0.59 | 0.98 | 0.39 | 0.78 | 1.37 | 1.37 |
MEAN | 0.176 | 0.345 | 0.509 | 0.677 | 0.854 | 0.475 | 1.048 | 0.316 | 0.889 | 2.102 | 1.165 |
BIAS | 0.023 | 0.038 | −0.202 | −0.187 | −0.164 | −0.115 | 0.068 | −0.074 | 0.109 | 0.732 | −0.205 |
SD | 0.061 | 0.076 | 0.119 | 0.120 | 0.105 | 0.159 | 0.144 | 0.146 | 0.157 | 0.318 | 0.234 |
MSE | 0.004 | 0.007 | 0.055 | 0.049 | 0.038 | 0.039 | 0.025 | 0.025 | 0.037 | 0.652 | 0.097 |
Coverage | 95.3 % | 93.6 % | 58.7 % | 63.8 % | 65.2 % | 88.0 % | 92.1 % | 93.4 % | 89.2 % | 33.5 % | 98.1 % |
Scenario D (unmeasured pre-T confounder of T, M, and Y) | |||||||||||
TRUE | 0.132 | 0.264 | 0.515 | 0.647 | 0.779 | 0.39 | 0.78 | 0.39 | 0.78 | 1.17 | 1.17 |
MEAN | 0.140 | 0.306 | 0.522 | 0.688 | 0.828 | 0.367 | 0.846 | 0.402 | 0.881 | 2.403 | 1.24 |
BIAS | 0.008 | 0.042 | 0.007 | 0.041 | 0.049 | −0.023 | 0.066 | 0.012 | 0.101 | 1.233 | 0.07 |
SD | 0.052 | 0.057 | 0.107 | 0.108 | 0.099 | 0.137 | 0.139 | 0.138 | 0.138 | 0.347 | 0.15 |
MSE | 0.003 | 0.005 | 0.012 | 0.013 | 0.012 | 0.020 | 0.025 | 0.020 | 0.028 | 1.644 | 0.027 |
Coverage | 93.5 % | 90.5 % | 94.2 % | 92.3 % | 90.6 % | 95.0 % | 91.5 % | 94.0 % | 89.6 % | 1.4 % | 99.8 % |
Confounding scenario B (unmeasured pre-T confounder of M and Y) results (N = 500) for medium effect size
NIE | NDE | TE | IPW CDE | IPW θ_{M} | RPM θ_{M} | RPM CDE | TSLS IV | Bayesian | |
---|---|---|---|---|---|---|---|---|---|
No violations | |||||||||
TRUE | 0.132 | 0 | 0.132 | 0 | 0.39 | 0.39 | 0 | 0.39 | 0.39 |
MEAN | 0.153 | −0.021 | 0.132 | −0.021 | 0.450 | 0.450 | −0.021 | 0.388 | 0.462 |
BIAS | 0.021 | −0.021 | −0.000 | −0.021 | 0.060 | 0.060 | −0.021 | −0.002 | 0.072 |
SD | 0.038 | 0.097 | 0.094 | 0.097 | 0.097 | 0.097 | 0.097 | 0.276 | 0.158 |
MSE | 0.002 | 0.010 | 0.009 | 0.010 | 0.012 | 0.012 | 0.010 | 0.077 | 0.030 |
Coverage | 93.3 % | 93.5 % | 94.5 % | 94.0 % | 91.7 % | 91.7 % | 94.0 % | 95.6 % | 99.8 % |
Exclusion restriction violated | |||||||||
TRUE | 0.132 | 0.390 | 0.522 | 0.39 | 0.39 | 0.39 | 0.39 | 0.78 | 0.78 |
MEAN | 0.150 | 0.369 | 0.519 | 0.369 | 0.449 | 0.449 | 0.369 | 1.567 | 0.815 |
BIAS | 0.019 | −0.021 | −0.002 | −0.021 | 0.059 | 0.059 | −0.021 | 0.787 | 0.035 |
SD | 0.038 | 0.099 | 0.095 | 0.097 | 0.097 | 0.097 | 0.097 | 0.315 | 0.165 |
MSE | 0.002 | 0.010 | 0.009 | 0.010 | 0.013 | 0.013 | 0.010 | 0.719 | 0.028 |
Coverage | 93.0 % | 94.5 % | 95.0 % | 94.6 % | 90.1 % | 90.1 % | 94.6 % | 25.7 % | 99.7 % |
Monotonicity violated | |||||||||
TRUE | 0.005 | 0 | 0.005 | 0 | 0.39 | 0.39 | 0 | 0.39 | 0.39 |
MEAN | 0.005 | −0.001 | 0.005 | −0.001 | 0.427 | 0.427 | −0.001 | 0.300 | 0.426 |
BIAS | 0.000 | −0.001 | −0.000 | −0.001 | 0.037 | 0.037 | −0.001 | −0.090 | 0.036 |
SD | 0.020 | 0.092 | 0.094 | 0.091 | 0.091 | 0.091 | 0.091 | 277.276 | 0.233 |
MSE | 0.000 | 0.009 | 0.009 | 0.009 | 0.010 | 0.010 | 0.009 | 795.214 | 0.056 |
Coverage | 94.5 % | 94.9 % | 95.0 % | 95.1 % | 91.9 % | 91.9 % | 95.1 % | 98.5 % | 99.7 % |
Confounding scenario C (post-T confounder of M and Y) results (N = 500) for medium effect size
NIE | NDE | TE | IPW CDE | IPW θ_{M} | RPM θ_{M} | RPM CDE | TSLS IV | Bayesian | |
---|---|---|---|---|---|---|---|---|---|
No violations | |||||||||
TRUE | 0.153 | 0.2 | 0.353 | 0.2 | 0.39 | 0.39 | 0.2 | 0.59 | 0.59 |
MEAN | 0.173 | 0.003 | 0.176 | 0.200 | 0.392 | 0.401 | 0.000 | 0.398 | 0.389 |
BIAS | 0.020 | −0.197 | −0.177 | 0.000 | 0.002 | 0.011 | −0.200 | −0.192 | −0.201 |
SD | 0.047 | 0.109 | 0.103 | 0.107 | 0.107 | 0.966 | 0.397 | 0.260 | 0.235 |
MSE | 0.003 | 0.051 | 0.042 | 0.012 | 0.010 | 0.932 | 0.197 | 0.107 | 0.096 |
Coverage | 94.4 % | 55.4 % | 59.6 % | 94.9 % | 96.3 % | 96.5 % | 94.9 % | 88.5 % | 97.8 % |
Exclusion restriction violated | |||||||||
TRUE | 0.153 | 0.590 | 0.743 | 0.59 | 0.39 | 0.39 | 0.59 | 0.98 | 0.98 |
MEAN | 0.171 | 0.388 | 0.559 | 0.583 | 0.388 | 0.387 | 0.389 | 1.390 | 0.772 |
BIAS | 0.018 | −0.203 | −0.185 | −0.007 | −0.002 | −0.003 | −0.201 | 0.410 | −0.208 |
SD | 0.050 | 0.111 | 0.104 | 0.107 | 0.107 | 0.925 | 0.379 | 0.287 | 0.228 |
MSE | 0.003 | 0.053 | 0.045 | 0.012 | 0.011 | 0.854 | 0.184 | 0.258 | 0.095 |
Coverage | 94.4 % | 52.2 % | 55.8 % | 93.2 % | 95.8 % | 95.9 % | 93.0 % | 74.1 % | 99.6 % |
Monotonicity violated | |||||||||
TRUE | 0.040 | 0.2 | 0.240 | 0.2 | 0.39 | 0.39 | 0.2 | 0.59 | 0.59 |
MEAN | 0.055 | 0.004 | 0.058 | 0.199 | 0.389 | 0.412 | 0.001 | −1.278 | 0.362 |
BIAS | 0.014 | −0.196 | −0.182 | −0.001 | −0.001 | 0.022 | −0.199 | −1.868 | −0.228 |
SD | 0.023 | 0.100 | 0.101 | 0.095 | 0.096 | 0.438 | 0.110 | 3539.23 | 0.344 |
MSE | 0.001 | 0.048 | 0.043 | 0.009 | 0.009 | 0.193 | 0.359 | 5859.25 | 0.170 |
Coverage | 96.0 % | 51.9 % | 58.0 % | 95.4 % | 94.9 % | 94.2 % | 56.0 % | 99.3 % | 95.6 % |
Confounding scenario D (unmeasured pre-T confounder of T, M, and Y) results (N = 500) for medium effect size
NIE | NDE | TE | IPW CDE | IPW θ_{M} | RPM θ_{M} | RPM CDE | TSLS IV | Bayesian | |
---|---|---|---|---|---|---|---|---|---|
No violations | |||||||||
TRUE | 0.132 | 0 | 0.132 | 0 | 0.39 | 0.39 | 0 | 0.39 | 0.39 |
MEAN | 0.157 | 0.014 | 0.171 | 0.014 | 0.452 | 0.452 | 0.014 | 0.492 | 0.468 |
BIAS | 0.026 | 0.014 | 0.040 | 0.014 | 0.062 | 0.062 | 0.014 | 0.102 | 0.078 |
SD | 0.039 | 0.097 | 0.093 | 0.098 | 0.098 | 0.098 | 0.098 | 0.267 | 0.152 |
MSE | 0.002 | 0.010 | 0.010 | 0.010 | 0.013 | 0.013 | 0.010 | 0.082 | 0.029 |
Coverage | 91.3 % | 94.6 % | 92.3 % | 94.5 % | 90.5 % | 90.5 % | 94.5 % | 93.8 % | 99.5 % |
Exclusion restriction violated | |||||||||
TRUE | 0.132 | 0.390 | 0.522 | 0.39 | 0.39 | 0.39 | 0.39 | 0.78 | 0.78 |
MEAN | 0.158 | 0.404 | 0.561 | 0.404 | 0.452 | 0.452 | 0.404 | 1.624 | 0.851 |
BIAS | 0.026 | 0.014 | 0.040 | 0.014 | 0.062 | 0.062 | 0.014 | 0.844 | 0.071 |
SD | 0.039 | 0.097 | 0.093 | 0.098 | 0.098 | 0.098 | 0.098 | 0.304 | 0.150 |
MSE | 0.002 | 0.010 | 0.010 | 0.010 | 0.013 | 0.013 | 0.010 | 0.803 | 0.027 |
Coverage | 91.7 % | 94.4 % | 92.4 % | 94.5 % | 90.5 % | 90.5 % | 94.5 % | 13.9 % | 99.3 % |
Monotonicity violated | |||||||||
TRUE | 0.005 | 0 | 0.005 | 0 | 0.39 | 0.39 | 0 | 0.39 | 0.39 |
MEAN | 0.008 | 0.041 | 0.049 | 0.041 | 0.426 | 0.426 | 0.041 | 0.152 | 0.452 |
BIAS | 0.004 | 0.041 | 0.045 | 0.041 | 0.036 | 0.036 | 0.041 | −0.238 | 0.062 |
SD | 0.019 | 0.091 | 0.092 | 0.091 | 0.091 | 0.091 | 0.091 | 134.72 | 0.237 |
MSE | 0.000 | 0.010 | 0.011 | 0.010 | 0.010 | 0.010 | 0.010 | 212.72 | 0.060 |
Coverage | 95.2 % | 92.2 % | 92.4 % | 92.5 % | 93.4 % | 93.4 % | 92.5 % | 51.3 % | 99.6 % |
6.1 No Confounders
The results for the no confounders/no violations, no confounders/exclusion restriction violated, and no confounders/monotonicity violated conditions are reported in Table 14.3. For these conditions, there is no interaction between T and M. Therefore, NIE_{1} = NIE_{0} and only one value, NIE, is reported; likewise for NDE and CDE. In the no confounders/no-interaction violated condition, there are two NIEs, NDEs, and CDEs, and results are reported in the top panel of Table 14.4. For the principal strata effects, the results reported in the tables are for the estimand, E[Y(1) − Y(0)|M(1) = 1, M(0) = 0].
For the condition in which all assumptions hold (i.e., exclusion restriction, monotonicity, no interaction between T and M), all approaches give the same unbiased results for all effects. For the condition in which the exclusion restriction is violated, the TSLS IV results are biased with 24 % coverage but the Bayesian principal strata effects are unbiased. Natural and controlled effect estimates are all unbiased.
For the no confounders/monotonicity violated condition, we examined different values (0.1 and 0.25) for the proportion of defiers. Thus, Table 14.3 reports two sets of results for this condition. When monotonicity is violated, the TSLS IV results are biased, with the bias increasing as the proportion of defiers increases from 0.1 to 0.25. The TSLS IV estimates are only slightly biased when the proportion of defiers is small (0.1). When the proportion of defiers is larger (0.25), the MC SD and therefore the MSE became very large. A proportion of defiers of 0.25 is an extreme case, as it is unlikely that the proportions in each stratum would be equal or that the intervention would have an iatrogenic effect on this many individuals. Also note that in this case, because the proportions for all strata were equal, the NIE true value is zero because there is an equal proportion with a positive indirect effect and a negative indirect effect and they cancel out. Natural and controlled effect estimates are all unbiased regardless of the proportion of defiers.
For the condition in which the no-interaction between T and M assumption is violated, TSLS IV estimates are biased with 2 % coverage. As mentioned previously when discussing principal strata effects, this condition is also a violation of the exclusion restriction. All other effect estimates were unbiased (see Table 14.4) including the Bayesian principal strata estimate.
6.2 Pre-T Confounder of M and Y
The models fitted to the simulated data in this confounding scenario did not adjust for the pre-T confounder. Thus, this set of conditions represents a violation of the no unmeasured confounding assumption. Results are reported in Table 14.5 for the unmeasured pre-T confounder of M and Y/no violations, unmeasured pre-T confounder of M and Y/exclusion restriction violated, and unmeasured pre-T confounder of M and Y/monotonicity violated conditions. Results for the unmeasured pre-T confounder of M and Y/no-interaction violation condition are reported in the second panel of Table 14.4.
For the unmeasured pre-T confounder of M and Y/no violations condition, the TSLS IV estimates and the natural direct and indirect, and controlled direct effects are unbiased. However, the Bayesian principal strata effects, and the estimates of θ_{M} using either IPW or the RPM are slightly biased.
For the condition in which the exclusion restriction is violated, the TSLS IV estimates are more severely biased, and the IPW and RPM estimates of θ_{M} are moderately biased. The remaining effects are unbiased. Coverage for the TSLS IV estimate is 26 % but the NIE, NDE, and CDE have adequate coverage (approx. 93–95 %).
For the condition in which monotonicity is violated, the NIE, NDE, and CDE are unbiased. However, the TSLS IV and Bayesian principal strata estimates and the estimates of θ_{M} using either IPW or RPM are biased. The TSLS IV estimate is more biased than the RPM or IPW estimates of θ_{M} and the Bayesian estimate. Again, the MC SD and therefore MSE for the TSLS IV estimate are extremely large.
For the condition in which the no-interaction between T and M assumption is violated, the NIE_{1}, NDE_{M(0)}, CDE_{0}, θ_{M|t=1}, and the Bayesian principal strata estimates were slightly biased, the NIE_{0}, NDE_{M(1)}, CDE_{1}, and θ_{M|t=0} estimates were unbiased, and the TSLS IV estimate was severely biased with unacceptable 95 % coverage (3 %, see Table 14.4).
6.3 Post-T Confounder of M and Y
In this confounding scenario, the exclusion restriction is violated in all the conditions due to the post-T confounder. For this confounding scenario, the models fit to the simulated data included both the pre- and post-T confounders. Thus, the no-unmeasured confounding assumptions are not violated. Results are reported in Table 14.6 for the post-T confounder of M and T/no violations, post-T confounder of M and T/exclusion restriction violated, and post-T confounder of M and T/monotonicity violated conditions. Results for the post-T confounder of M and T/no-interaction violated condition are reported in the third panel of Table 14.4.
For the post-T confounder of M and T/no violations condition (however, the exclusion restriction is violated due to the post-T confounder although there is not otherwise a direct effect of T on Y), the TSLS IV and Bayesian principal strata estimates, the NDE, and the CDE estimated via the RPM are biased to approximately the same degree. The CDE estimated via IPW, the NIE, and θ_{M} estimated via either IPW or the RPM are unbiased although the MSE of θ_{M} for the RPM is much larger than the MSE for the IPW estimates. The 95 % coverage for the NDE and TSLS IV estimates is unacceptable.
For the condition in which the exclusion restriction is violated (i.e., there is a direct effect of T on Y in addition to the effect through the post-intervention confounder), the TSLS IV and Bayesian principal strata estimates, the NDE, and the CDE estimated via the RPM are biased. The CDE estimated via IPW, the NIE, and θ_{M} estimated via either IPW or the RPM are unbiased although the MSE of θ_{M} for the RPM is much larger than the MSE for the IPW estimates. The 95 % coverage for the NDE and TSLS IV estimates is unacceptable.
For the condition in which monotonicity is violated, the TSLS IV and Bayesian principal strata estimates, the NDE, and the CDE estimated via the RPM are biased. The CDE estimated via IPW, the NIE, and θ_{M} estimated via either IPW or the RPM are unbiased although the MSE of θ_{M} for the RPM is much larger than the MSE for the IPW estimate. The 95 % coverage for the NDE and TSLS IV estimates is unacceptable.
For the condition in which the no-interaction between T and M assumption is violated, all effects are biased to some degree. The TSLS IV estimate is the most severely biased with unacceptable 95 % coverage (33.5 %, see Table 14.4). The NDE_{M(0)}, NDE_{M(1)}, CDE_{0}, the IPW θ_{M|t=1}, and the Bayesian principal strata effect estimates were moderately biased. Coverage for these effects was also unacceptable. The NIE_{1}, NIE_{0}, CDE_{1}, and IPW θ_{M|t=0} estimates were slightly biased.
6.4 Pre-T Confounder of T, M, and Y
Results of empirical data analysis for natural effects
Without interaction | With interaction | |||||
---|---|---|---|---|---|---|
Estimate | 95 % CI | Estimate | 95 % CI | |||
NIE_{0} | 1.384 | 0.215 | 2.825 | 2.251 | 0.348 | 4.859 |
NIE_{1} | 1.384 | 0.215 | 2.825 | 0.898 | −0.494 | 2.588 |
NDE_{M(0)} | 1.313 | −1.249 | 3.680 | 1.595 | −0.885 | 4.334 |
NDE_{M(1)} | 1.313 | −1.249 | 3.680 | 0.242 | −2.631 | 3.034 |
TE | 2.697 | 0.321 | 4.917 | 2.493 | 0.300 | 4.870 |
For the unmeasured pre-T confounder of T, M, and Y/no violations condition, the TSLS IV estimate is biased. In this confounding scenario, the use of T as an IV is not justified for the TSLS IV estimator. All other estimates are slightly biased. The bias is most notable when compared to the corresponding bias in Tables 14.3 and 14.5. For example, in Table 14.3, the no-unmeasured-confounding assumption holds and there is no bias. In Table 14.5, the no-unmeasured-confounding assumption holds with regard to T but not M. Bias for the NIE and θ_{M} estimates using either IPW or the RPM are essentially the same between Tables 14.5 and 14.7. However, the bias for the NDE and CDE estimated using either IPW or the RPM are larger in Table 14.7 than in Table 14.5 because the no-unmeasured-confounding assumption for T is also violated in Table 14.7. Finally, the bias for the Bayesian principal strata estimates increased in Table 14.7 compared to Table 14.5.
Results of empirical data analysis for controlled effects using inverse propensity weighted estimator
Without interaction | With interaction | |||||||
---|---|---|---|---|---|---|---|---|
Estimate | SE | 95 % CI | Estimate | SE | 95 % CI | |||
CDE_{0} | 2.879 | 1.063 | 0.796 | 4.963 | 3.824 | 1.076 | 1.714 | 5.933 |
CDE_{1} | 2.879 | 1.063 | 0.796 | 4.963 | 0.972 | 2.228 | −3.394 | 5.338 |
θ_{M|t=0} | 2.194 | 1.183 | −0.125 | 4.513 | 3.847 | 2.073 | −0.216 | 7.911 |
θ_{M|t=1} | 2.194 | 1.183 | −0.125 | 4.513 | 0.996 | 1.350 | −1.650 | 3.641 |
Results of empirical data analysis for Bayesian principal strata effects
Estimate | SE | 95 % CI | ||
---|---|---|---|---|
CACE | 5.1318 | 2.6897 | −0.5840 | 10.4499 |
AACE | −1.3870 | 4.8571 | −9.7951 | 10.0298 |
NACE | 2.4501 | 2.9214 | −3.2872 | 8.5401 |
DACE | 0.3493 | 6.1052 | −11.2820 | 13.2813 |
6.5 Additional Overall Observations Regarding Results of Simulation Study
The MC SD for the Bayesian estimates was generally larger than the MC SD for the other methods. The MC SD for the TSLS IV estimates were much larger than that for the other methods when there was an interaction between T and M. Coverage for the Bayesian principal strata estimates was over 99 % in almost all simulation conditions. The results were similar for the N = 100 sample size condition, which are included in supplementary online materials. We also examined a large effect size, 0.59 (see [42]), and obtained similar results. That is, all 0.39 values in Table 14.2 were replaced with 0.59. These results are included in supplementary online materials.
The IPW CDE and θ_{M} estimates were unbiased when the no-interaction between T and M assumption is violated (see top panel of Table 14.4). These estimates were also unbiased when there was a post-T confounder of M and Y (see Table 14.6). However, when both of these assumptions were violated, these estimates were biased (see third panel of Table 14.4). We examined this situation further by generating 1000 replications for a sample size N = 10,000 and estimating the IPW CDE and θ_{M} effects. Although the MC SD decreased as would be expected due to the increased sample size, the bias did not decrease. In fact, it remained consistent with the bias reported in the third panel of Table 14.4. Thus, IPW CDE and θ_{M} estimates are not robust for the post-T confounder of M and Y/no-interaction violation condition.
7 Discussion
The simulation study results illustrate that if the identifying assumptions used by an estimator hold, then the estimator performs well in terms of bias, and if they do not hold, then the estimator does not perform well in terms of bias. In addition, some estimators seem to be more robust than others when assumptions are violated. Specifically, the simulation study illustrates that the TSLS IV estimator of the principal strata effects and the RPM G-estimator, which relies on interaction terms that act as instrumental variables, require that the instrumental variable assumptions hold and if they do not, these methods are just as biased as those that rely on sequential ignorability. This problem has been known for quite some time when attempting to estimate the causal effect of an endogenous variable on an outcome [43] and it carries over to mediation analysis as well. Unfortunately, many of the assumptions cannot be verified in empirical data, leaving the researcher to attempt to justify the assumptions based on rational argument. However, we suggest that researchers who use instrumental variable methods, such as the RPM, report the strength of the interaction term on the mediator, as well as the strength of the interaction term on the outcome. Note that the lack of an effect of the interaction term on the outcome does not guarantee that the exclusion restriction holds and that violation of the exclusion restriction cannot be verified or refuted from the observed data [44]. Furthermore, weak instruments may actually amplify bias in comparison with an unadjusted estimate (see e.g., [43, 44, 45]). In other words, using no instrument can be better than using a weak instrument. We propose that researchers take the following steps: define the causal estimand, justify the identification assumptions, and try several estimators.
7.1 Comparison of Approaches in Terms of Definitions
The definitions of the various approaches coincide in very limited situations in which all assumptions of the various approaches hold. Specifically, when there are no confounders and all assumptions hold (i.e., exclusion restriction, monotonicity, no interaction between T and M), then NIE_{0} = NIE_{1} = CACE and NDE_{M(0)} = NDE_{M(1)} = CDE_{m}. Thus, one consideration in choosing an approach is clearly articulating the scientific question of interest. For example, if the researcher is interested in the causal effect of the intervention on the outcome among those individuals for whom the intervention had an effect on the mediator in the intended direction, then the principal strata effects are of interest. If the researcher is interested in the effect of the mediator on the outcome, then the controlled effects are of interest, because the natural effects do not define this effect separately from the indirect effect. If the researcher is interested in the causal effect of the intervention on the outcome that is due to the mediator, then the NIEs are of interest.
7.2 Comparison of Approaches in Terms of Identification
For different empirical data sets, certain assumptions are more likely to hold than others. For example, in some studies the exclusion restriction may be plausible, and in other studies no post-intervention confounders may be more plausible. Thus, one consideration in choosing an approach is the plausibility of the various assumptions for a particular data set. For an extensively studied research area, scientists may have knowledge about the validity of model assumptions but this knowledge is unlikely in relative new research areas.
The assumption of no post-treatment confounders (assumption (d)), in which there might be multiple mediators or confounders of the mediator and outcome that have been influenced by the intervention, is likely to be violated in many studies. Suppose a researcher is interested in the NIE, but assumption (d) is not plausible. If instead assumption (e), no T × M interaction, is plausible, then an estimate of the CDE can be obtained and subtracted from the TE to obtain an estimate of the indirect effect. Another alternative is to include measures of the additional mediators of the intervention in the statistical analysis, known as a multiple mediator model. Accurate estimation of causal effects in this model is an active research area in the field of causal inference (e.g., [46, 47]).
If a researcher is not able to justify any of the identifying assumptions, or is particularly interested in a specific estimand and cannot justify the identifying assumptions for that estimand, then it is important to find ways to assess the sensitivity of the estimates to violations of the assumptions. In some cases, sensitivity analysis has been developed. For instance, Imai et al. [4] proposed sensitivity analysis to the no-unmeasured-confounding assumptions used in identifying natural effects and implemented it in the R mediation package. VanderWeele [28] has proposed a sensitivity analysis for the no-unmeasured-confounding assumptions used in identifying controlled effects. Sensitivity analysis for the presence of a post-treatment confounder for natural effect estimates has recently been developed [46]. However, one type of sensitivity analysis that researchers could try is using several different estimators that rely on different identifying assumptions for the particular definition of interest. If the results generally agree, it seems safe to conclude that either the assumptions are not violated or that the estimates are not sensitive to violations of them. Of course, if the results do not agree, the researcher does not know which are correct. In any case, identifying causal effects will require assumptions; thus, it seems development of sensitivity analysis is an important direction for future research. Another alternative is to design future research studies in order to reduce or eliminate the violation of assumptions.
7.3 Comparison of Approaches in Terms of Estimation
If one particular definition of mediation is of scientific interest and the identifying assumptions of a particular estimator are not plausible, then a different estimator using different identifying assumptions may be used. For example, if controlled effects are of interest and the no-unmeasured-confounders assumption is not plausible, then the RPM using intervention-by-baseline-covariate interaction effects on the mediator as IVs may be more plausible. New estimators for each of the approaches that use different identifying assumptions are rapidly being developed in the statistical literature (see e.g., [38, 39, 48]). However, none of these estimators relaxes the no post-treatment confounders assumption for estimation of the natural effects. If natural effects are of interest, and the no post-treatment confounders assumption is unlikely to hold, then investigators may be able to define and estimate the NDEs and NIEs on the treated as described in Vansteelandt and VanderWeele [32].
7.4 Limitations and Future Directions
In this study, we only considered estimation—we did not consider hypothesis testing and power. This and sensitivity analysis are directions for future work. We also did not vary the strength of the confounding because the size of the simulation study was already large. We would expect that as the effect of the unmeasured pre-T confounder of M and Y (confounding scenario B), or of T, M, and Y (confounding scenario D) increases, the bias resulting from not accounting for the confounder would also increase. We also did not vary the strength of post-T confounder of M and Y or of the interaction between T and M; rather we examined only the presence or absence of violations of these assumptions.
There are other estimators for each approach that we did not consider here. For the principal stratification approach, we did not implement the Jo et al. [49] estimator, which uses reference stratification and propensity scores. Elliott et al. [37] proposed a Bayesian estimator for principal strata effects, although this estimator is only applicable when there is a binary mediator and a binary outcome. For estimating the natural effects, Hogan [39] proposed an imputation-based estimator, Daniels et al. [38] proposed a Bayesian estimator, Vansteelandt et al. [50] proposed an imputation-based estimator, and VanderWeele and Vansteelandt [51] and Valeri and VanderWeele [52] proposed an estimator for dichotomous outcomes based on the mediation formula [6, 53]. Several other estimators for the CDEs have been proposed, including a sequential G-estimation approach proposed by Vansteelandt [54] and an estimator proposed by Emsley et al. [55] that is very similar to the RPM G-estimator. Albert [56] proposed a TSLS estimator that is similar to those proposed by Dunn and Bentall [57] and Joffe and Greene [58].
8 Conclusions
We examined three different definitions of causal effects in the mediation context. For each of these definitions, we presented commonly used identifying assumptions along with estimation methods using different sets of these identifying assumptions. Specifically, we examined the TSLS IV and a Bayesian estimator for principal strata effects, the Imai et al. [4] estimator for natural effects, and IPW and the RPM G-estimator for controlled effects. In conclusion, we demonstrated that effect estimates may be biased when the identifying assumptions underlying each method are violated. We recommend that researchers specify which definition (i.e., causal effect) they wish to estimate along with consideration of the plausibility of assumptions made. For the mediation case with randomized T, two critical assumptions are the extent to which there is confounding of the M to Y relation and the extent to which there are effects of the treatment (i.e., post-treatment confounders) that confound the M to Y relation. Mediation analysis from a potential outcomes framework provides a more detailed approach to understanding mediating processes by specifying the definitions and assumptions necessary for causal inferences. Finally, we suggest that whenever possible researchers conduct sensitivity analyses.
Footnotes
Supplementary material
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