Causal Inference When Counterfactuals Depend on the Proportion of All Subjects Exposed

SUMMARY:

The assumption that no subject’s exposure affects another subject’s outcome, known as the no-interference assumption, has long held a foundational position in the study of causal inference. However, this assumption may be violated in many settings, and in recent years has been relaxed considerably. Often this has been achieved with either the aid of a known underlying network, or the assumption that the population can be partitioned into separate groups, between which there is no interference, and within which each subject’s outcome may be affected by all the other subjects in the group via the proportion exposed (the stratified interference assumption). In this paper, we instead consider a complete interference setting, in which each subject affects every other subject’s outcome. In particular, we make the stratified interference assumption for a single group consisting of the entire sample. We show that a targeted maximum likelihood estimator for the i.i.d. setting can be used to estimate a class of causal parameters that includes direct effects and overall effects under certain interventions. This estimator remains doubly-robust, semiparametric efficient, and continues to allow for incorporation of machine learning under our model. We conduct a simulation study, and present results from a data application where we study the effect of a nurse-based triage system on the outcomes of patients receiving HIV care in Kenyan health clinics.

1. Introduction

Historically, the field of causal inference has relied on an assumption of no interference between subjects, meaning that one subject’s exposure may not affect another subject’s out-come (Cox, 1958). This is one part of the stable unit treatment value assumption (SUTVA) (Rubin, 1980), which is invoked to ensure that counterfactuals (or potential outcomes) are well-defined. Counterfactuals are the hypothetical outcomes that would be observed had, possibly contrary to fact, a subject’s exposure been set to a certain value. Under SUTVA, for a binary exposure there are two possible counterfactuals for each subject: the outcome we would see had he or she been exposed, and the outcome had he or she not been exposed. The fundamental problem of causal inference is that only one of these is observed for each subject, and a primary aim of causal inference is to borrow information from the unexposed to learn about exposed subjects’ outcomes had they not been exposed, and vice versa.

However, when subjects’ exposures affect other subjects’ outcomes, these two counterfactuals are not well defined, since the outcome we would observe had a subject been exposed may differ depending on other subjects’ exposure levels. Thus, traditional causal estimands relying on these counterfactuals are not well defined, and there is ambiguity in what the causal quantity of interest should be. Further, without additional assumptions regarding the nature of the interference, there is no possibility of borrowing information across exposure levels to learn about counterfactuals under exposure levels that are not observed, since all subjects share the same observed exposure vector.

The reality is that SUTVA may often be violated in practice. In fact, in many cases, effects due to interference (often referred to as spillover effects) are themselves of interest, such as the herd immunity that can arise from vaccinations. Recently, a literature has emerged relaxing the assumption of no interference (Rosenbaum, 2007; Hudgens and Halloran, 2008; Tchetgen Tchetgen and VanderWeele, 2012; Basse and Feller, 2017, among others). Many methods rely on the assumption of partial interference (Sobel, 2006), i.e., that subjects can be partitioned into groups such that a subject in one group may not interfere with a subject in another. These methods tend to rely on the number of distinct groups being relatively large, rather than relying on the sample sizes of the groups themselves being large (one exception is discussed in Liu and Hudgens (2014)). One general approach for relaxing the partial interference assumption uses data on the underlying network connecting the subjects (Toulis and Kao, 2013; van der Laan, 2014; Aronow and Samii, 2017; Ogburn et al., 2017; Sofrygin et al., 2017). The network is assumed to characterize the structure of the interference by specifying that only subjects who are connected in the network may interfere with one another.

In this paper, we consider an alternative approach to relaxing the partial interference assumption. Instead of assuming an explicit network structure through which interference operates, we allow for direct interference between all pairs of units, which we refer to as complete interference. That is, we consider a trivial network that is completely connected. To make progress toward identification, we make the commonly-invoked stratified interference assumption (Hudgens and Halloran, 2008), which states that each subject’s outcome may be affected by all other subjects’ exposures, but only via the proportion (or equivalently, the total number) of subjects who are exposed. This reduces the dimension of the function of all subjects’ exposures upon which the counterfactuals are assumed to depend from n to two, recovering identifiability. This assumption is especially plausible when the interference is due to the strength of the exposure varying with how many subjects are receiving it, for instance when the exposure is a shared resource.

Examples of treatment effects varying with the proportion of subjects exposed are prevalent in the economics literature (see Heckman et al. (1998) and references in Abbring and Heckman (2007)). This literature overcomes the above identifiability challenge by leveraging stronger assumptions in the form of general equilibrium models, which model how treatment effects vary with the proportion of subjects exposed due to market mechanisms, permitting one to extrapolate effect estimates to settings with proportions of exposed subjects not observed. By contrast, our approach is agnostic toward this relationship.

Our setting is closely related to one considered by Liu and Hudgens (2014). Namely, they consider one setting in which partial interference holds, and the number of groups is not large, but the number of subjects in each group is. They develop asymptotic results for certain interference causal parameters under the stratified interference assumption, including group-specific causal parameters, which corresponds to the single group setting we consider here. Three primary differences in our work are that (i) we consider an observational study setting, whereas they assume randomization at the group level; (ii) our causal framework is model based, whereas they operate under the Neyman-Rubin causal model, wherein potential outcomes are typically regarded as fixed quantities rather than random; and (iii) we consider effects under a broader class of interventions, including dynamic interventions, which depend on a subject’s covariates, e.g., treat only if a patient’s CD4 count is above a certain threshold.

When only one group of completely connected units is observed, we find that only a certain class of effects is identifiable under our model without invoking stronger assumptions. This is a class of effects under interventions that preserve the overall proportion of subjects exposed, since the data only support one observation of this proportion. We refer to such interventions as exposure reallocation schemes. We show that despite the dependence induced by inter-ference, under stratified interference and standard causal assumptions, certain traditional i.i.d. causal estimators can be used to estimate interference causal parameters. This is novel and important for two reasons: (i) it is a first solution for the problem of complete interference (i.e., a single block with a completely-connected network) in an observational study setting, and (ii) it is interesting and elucidating that a traditional estimator can be used for a non-traditional estimand. In particular, we focus on a targeted maximum likelihood estimator (TMLE), showing that it remains semiparametric efficient, doubly robust, and permits the use of data-adaptive estimation of nuisance functions.

As a real data example, we examine the Low Risk Express Care (LREC) program implemented in Kenyan health clinics providing HIV care. Patients at clinics implementing the LREC program who were clinically stable (or “low-risk”) were eligible to have a subset of their clinical care tasks shifted from clinical officers to other health care professionals, such as nurses. Following program implementation, a non-randomized subset of eligible patients were enrolled in the task-shifting program. Previously, Tran et al. (2016) analyzed data collected from this program under an assumption of no interference. However, they expressed concern that interference might in fact be present, as the effect of individual-level enrollment in the program is likely to differ depending on the number of other patients enrolled, and the corresponding workloads of health providers. We demonstrate properties of our estimator in finite samples via a simulation study, and apply our methodology to the LREC data to study the effect of the nurse-based task-shifting program on risk of death or loss to follow-up among patients receiving HIV care at a Kenyan clinic that implemented the LREC program.

2. Defining the Model & Target Parameters

2.1. The Statistical and Causal Models

To formalize our setting, let the observed data be Oⁿ = {(W₁,A₁,Y₁),…, (W_n, A_n,Y_n)}, where n is the sample size, and for subject i, W_i is a vector of baseline covariates, A_i is a binary exposure indicator, and Y_i not for identi_cation. Consider a model forof interest, assumed to have bounded support. Boundedness of the outcome will be invoked for purposes of estimation and inference, but not for identification. Consider a model for Y_i that only depends on A_i, W_i, and $\overline{A}\equiv n^{-1}{\sum }_{i=1}^n{A}_i$. Thus, the dependence of each subject’s outcome on $\overline{A}$ reflects the complete interference setting, since $\overline{A}$ involves every other subject in the sample’s exposure. Let q_W,0 be the true probability density function of W, g₀ be the true observed conditional exposure-assignment mechanism given W_i (which is known under a randomized controlled trial, but is otherwise unknown), and q_Y,₀ be the true conditional probability density function of Y given A_i, W_i, and $\overline{A}$. Further, let ${\overline{Q}}_0\left\{{\mathit{W}}_{\mathit{i}},A_i,k_n(\overline{A})\right\}\equiv E_{Y,0}\left\{Y_i|{\mathit{W}}_{\mathit{i}},A_i,k_n(\overline{A})\right\}$, where each is a common function for all i and n, and k_n is some function that may depend on n.

The presence of the function k_n is a relaxation of the outcome regression function, permitting dependence on Aⁿ to vary with n rather than simply being a fixed function of $\overline{A}$ with respect to n. For instance, rather than depending on the proportion exposed, one might suspect that the outcome regression depends on the total number of subjects exposed. In the former case, k_n is simply the identity function; in the latter, $k_n(\overline{A})=n\overline{A}$.

It may often be the case that subjects’ outcomes depend not only on the exposures of the other subjects sampled, but on the exposures of all subjects in some larger population from which they were sampled. In this case, k_n can be thought of as a function mapping the proportion exposed in the sample to the proportion exposed in the larger population. We will only consider hypothetical interventions on the observed subjects, and so the exposures of subjects outside of the sample can be thought of as fixed. Our data example fits into this setting; in our case, it is more reasonable to model ${\overline{Q}}_0$ as a function of the proportion of all patients in the clinic who are task shifted, rather than of just the cohort of patients sampled. As such, $k_n(\overline{A})$ can be defined as the proportion of all patients in the clinic task shifted.

When only one causally-connecting group is observed, knowledge of k_n is in fact unnecessary for performing estimation, since we will be conditioning on $\overline{A}$, and hence on $k_n(\overline{A})$. However, specifying k_n is useful for the purposes of interpretation, as the causal estimands we consider will depend on $k_n(\overline{A})$, and will therefore only hold relevance to settings with a common value of $k_n(\overline{A})$. Also, its specification is required if, upon observing multiple groups with varying values of $k_n(\overline{A})$, one wishes to model how a causal parameter varies with $k_n(\overline{A})$ (see Web Appendix A for discussion of this setting).

In the LREC example, we discretize patients’ repeated observations from 2006 to 2009 into 90-day intervals (corresponding to the approximate frequency of clinic visits), and for each clinic select as baseline the discretized time period with the most observed exposed patients (or unexposed, if fewer). Patients were included in the analysis if they had at least one visit to the clinic during the baseline time period, were eligible to be task-shifted at their visit, and were not previously enrolled in the task-shifting program. The exposure A_i is defined as an indicator of enrollment into the task-shifting program at the baseline visit (irrespective of enrollment at subsequent time points). The outcome Y_i is an indicator that the patient died or was lost to follow up within 270 days of baseline. As noted in Tran et al. (2016), “Patients who do not return for continuing HIV care are subject to higher risk of complications and health decline, placing them at unnecessarily higher mortality rates.” Lastly, W_i consists of the static baseline covariates age, sex, adherence to antiretroviral therapy (ART), CD4 count, indicator of protease inhibitor-based ART regimen, WHO disease stage, and indicator of tuberculosis treatment at beginning of ART.

The stratified interference assumption implies that a patient’s retention and mortality is potentially influenced by their own enrollment in the program as well as the proportion of all HIV patients concurrently enrolled, but not by the specific allocation of the exposure to the other patients. This assumption is more plausible if all patients require an equal intensity of care. While this may not hold completely, it might be a reasonable approximation, since all patients in the analysis are clinically stable enough to meet eligibility criteria.

Let ${\mathcal{M}}_{si}$ be the nonparametric model under stratified interference that leaves (q_Y,g,q_W) unrestricted (apart from support conditions). We assume that the observed data follow the distribution $p_0\left(O^n\right)={\prod }_{i=1}^n{q}_{Y,0}\left\{Y_i|{\mathit{W}}_{\mathit{i}},A_i,k_n(\overline{A})\right\}{g}_0\left(A_i|{\mathit{W}}_{\mathit{i}}\right)q_{W,0}\left({\mathit{W}}_{\mathit{i}}\right)\in {\mathcal{M}}_{si}$. That is, we assume that patient i’s outcome depends on the exposure assignment vector Aⁿ ≡ (A₁,…, A_n) and covariate matrix Wⁿ ≡ (W₁,…, W_n) only through A_i, W_i, and $k_n(\overline{A})$.

Next, we define our causal model, a nonparametric structural equation model (NPSEM), which states that each observed variable is generated by a distinct, arbitrary function, denoted f, of (i) other observed variables, and (ii) a distinct random disturbance, denoted U. Specifically, we posit

$${\mathit{W}}_{\mathit{i}}={\mathit{f}}_{\mathit{W}}\left({\mathit{U}}_{\mathit{i}}^{\mathit{W}}\right),A_i=f_A\left({\mathit{W}}_{\mathit{i}},U_i^A\right),Y_i=f_Y\left\{{\mathit{W}}_{\mathit{i}},A_i,k_n(\overline{A}),U_i^Y\right\},$$ (1)

where the random disturbances ${\mathit{U}}_{\mathit{i}}^{\mathit{W}}$, $U_i^A$, and $U_i^Y$ are assumed to all be mutually independent both within and across i. The independence implies that a hypothetical intervention to set a variable to a certain value can impact all variables that are functions of the intervened variable in the NPSEM, and also that the only source of dependence between subjects is due to their outcomes’ common dependence on $\overline{A}$. This model is an extreme case of stratified interference under the partial interference assumption, which states that {1,…, n} can be partitioned into J groups {k₁,…, k_j} such that for each $i,Y_i=f_Y\left\{{\mathit{W}}_{\mathit{i}},A_i,k_n\left({\overline{A}}_j\right),U_i^Y\right\}$ for i ∈ k_j, where ${\overline{A}}_j$ is the sample mean of A among k_j. In our case J =1.

2.2. Interventions, counterfactuals, and causal estimands

We now consider hypothetical interventions and their implications under the NPSEM. These do not correspond to the true exposure assignment distribution, but are rather interventions under which we might be interested in summarizing and contrasting subjects’ outcomes. Consider a hypothetical intervention setting Aⁿ to a particular value aⁿ. The NPSEM implies that the system of equations (1) yields ${\mathit{W}}_{\mathit{i}}={\mathit{f}}_{\mathit{W}}\left({\mathit{U}}_{\mathit{i}}^{\mathit{W}}\right)$, $A_i=a_i$,$Y_i^{a_i,\overline{a}}=f_Y\{{\mathit{W}}_{\mathit{i}},a_i,k_n(\overline{a}),U_i^Y\}$, where $Y_i^{a_i,\overline{a}}$ is the counterfactual we would observe for subject i had they been assigned exposure level a_i and had $\overline{a}$ of subjects in the sample been exposed.

We will consider two types of counterfactuals. The first corresponds to the previous example and is denoted by a double superscript. The first argument in the superscript indicates subject i’s exposure level; the second indicates the proportion exposed in the sample. Under stratified interference, this counterfactual is the same for subject i for all exposure vectors that generate the same α_i and $\overline{a}$, so we need only conceive of a hypothetical intervention setting A_i to some level α and the proportion $\overline{A}$ to some level π to define the counterfactual under this intervention, viz.,$Y_i^{a,\pi }$. We denote its sample mean by ${\overline{Y}}^{a,\pi }$. Our first class of target causal parameters is the conditional mean of this sample average given ${\mathit{W}}^n:E\left({\overline{Y}}^{a,\pi }|{\mathit{W}}^n\right)$. These correspond to effects in populations of subjects with the same covariate values as those in our current sample, therefore inference for these parameters will not account for variability induced by the sampling of these covariates. We consider parameters that marginalize over the distribution of the baseline covariates in Web Appendix E.

For a given proportion of exposed subjects, π, we can define a direct effect as a contrast of two of the above parameters: $E\left({\overline{Y}}^{1,\pi }|{\mathit{W}}^n\right)-E\left({\overline{Y}}^{0,\pi }|{\mathit{W}}^n\right)$. This contrasts two parameters for which the proportion exposed is held fixed at π, and the individual exposure level is changed from unexposed to exposed. In our LREC example, this corresponds to the direct effect of an individual’s enrollment in the task-shifting program, holding the proportion of enrolled subjects constant at π. Relatedly, Hudgens and Halloran (2008) define a group average direct causal effect under complete randomization of a single group, which depends on the experimental exposure assignment mechanism. However, under stratified interference, this estimand is invariant to this assignment mechanism apart from the coverage level π, and using our notation, is equal to ${\overline{Y}}^{0,\pi }-{\overline{Y}}^{1,\pi }$. Our estimand differs in that we take the conditional expectation of counterfactuals, rather than considering them to be fixed.

More generally, we can consider counterfactuals arising from hypothetical interventions that are potentially dynamic and/or stochastic, rather than setting all subjects’ exposures to a fixed value. Stochastic interventions assign exposure with non-degenerate probability. A dynamic intervention is an intervention that depends on covariates. Consider a general hypothetical intervention g* that is a joint distribution that can be dependent across subjects. We denote an exposure vector generated under the intervention g* by A*ⁿ such that A*ⁿ | Wⁿ ~ g*. Throughout, we will only consider row-exchangeable interventions, meaning that the order in which subjects are listed in the data frame is irrelevant to their exposure probability (Imbens and Rubin, 2015). For such an intervention, we define the counterfactual $Y_i^{g^{*},\pi }\equiv f_Y\left\{{\mathit{W}}_{\mathit{i}},A_i^{*},k_n(\pi ),U_i^Y\right\}$, which is the outcome we would have seen had the exposure been assigned according to g*, and had the overall proportion of subjects exposed been π. This class of counterfactuals contains the two contrasted in our above definition of the direct effect, where the interventions being compared are g*(Aⁿ = 1 | Wⁿ) = 1 and g*(Aⁿ = 0 | Wⁿ) = 1. We define the analogous causal parameter to ψ^α,π that replaces the intervention setting A_i to a for all i with the more general intervention g* as ${\psi }^{g^{*},\pi }\equiv E\left({\overline{Y}}^{g^{*},\pi }|W^n\right)$.

The second type of counterfactual we consider is denoted with a single superscript, which indicates the hypothetical intervention distribution for the entire exposure vector. Intervening on Aⁿ according to g*, the NPSEM implies that the system of equations (1) yields, for all i, ${\mathit{W}}_{\mathit{i}}={\mathit{f}}_{\mathit{W}}\left({\mathit{U}}_{\mathit{i}}^{\mathit{W}}\right)$, ${\mathit{A}}^{*n}~g^{*}\left({\mathit{a}}^n|{\mathit{W}}^n\right)$,$Y_i^{g^{*}}=f_Y\left\{{\mathit{W}}_{\mathit{i}},A_i^{*},k_n\left({\overline{A}}^{*}\right),U_i^Y\right\}$, where $Y_i^{g^{*}}$ is the counterfactual we would observe for subject i had the entire exposure vector been assigned according to g*. We term these overall effect counterfactuals. We denote their sample average by ${\overline{Y}}^{g^{*}}$, and the corresponding overall effect parameter as ${\psi }^{g^{*}}\equiv E\left({\overline{Y}}^{g^{*}}|{\mathit{W}}^n\right)$. For any two interventions g* and g^†, we refer to the contrast ${\psi }^{g^{*}}-{\psi }^{g^{†}}$ as an overall effect.

Overall effect parameters and overall effects are superpopulation analogs to the marginal group average potential outcomes and group average overall causal effects, respectively, defined by Hudgens and Halloran (2008). They define the marginal group average potential outcome to be the expectation of ${\overline{Y}}^{g^{*}}$ only with respect to A*ⁿ, and implicitly condition on Wⁿ,U^Y,ⁿ. They define contrasts of any two such interventions to be group average overall causal effects. They focus on an experimental setting under complete randomization, such that g* corresponds to the observed experimental exposure assignment distribution. van der Laan (2014) extends these parameters to observational study settings, and potentially dynamic/stochastic interventions that do not correspond to the observed exposure distribution. Our definition of overall effect parameters are equivalent to the causal estimands of van der Laan (2014) that condition on the observed covariates.

3. Nonparametric Identification

Having defined the above causal parameters, we now wish to nonparametrically identify them with a consistently estimable quantity using observed data. To do so, we first distinguish between two senses of the term identification. We say a parameter is causally nonparametrically identifiable if it can be expressed as a functional of the observed data distribution under a nonparametric model. We say it is statistically nonparametrically identifiable if it can be consistently estimated (however slowly) from observed data under a nonparametric model. The former does not necessarily imply the latter, as we will see.

We begin with causal nonparametric identification. First, we fix some new notation for convenience. Due to the row-exchangeability of g*, the conditional distribution of a_i given Wⁿ marginalized over ${\mathit{a}}_{-\mathit{i}}^{\mathit{n}},{\sum }_{a_{-i}^n}{g}^{*}\left({\mathit{a}}^n|{\mathit{W}}^n\right)$, depends on i only through W_i for each i ∈ {1,…,n}, where $a_{-i}^n$ is the vector aⁿ with the ith element removed. Define ${\theta }_n\equiv \left\{{\mathit{W}}^{\mathit{n}},k_n(\overline{A})\right\}$, and $g_{{\theta }_n}^{*}(a|w)$ to be a function that is equal to ${\sum }_{a_{-i}^n}{g}^{*}\left({\mathit{a}}^{\mathit{n}}|{\mathit{W}}^{\mathit{n}}\right)$ at w = W_i for each i ∈ {1,…, n}. The (potential) dependence of $g_{{\theta }_n}^{*}$ on ${\mathit{W}}_{-\mathit{i}}^{\mathit{n}}$ is acknowledged notationally in the subscript θ_n. This is a known function, as g* is user-specified. For identification of ${\psi }^{g^{*}}{}^{,\pi }$ and ${\psi }^{g^{*}}$, respectively, we require the following positivity assumptions:

Assumption 1:$g_{{\theta }_n}^{*}\left(a|{\mathit{W}}_{\mathit{i}}\right)/ {\text{Pr}}_{p_0}\left\{A_i=a|{\mathit{W}}_{\mathit{i}},\overline{A}=\pi \right\}<\infty \text{ for all }i\text{ and }a\in \{0,1\}.$

Assumption 2:$g^{*}\left({\mathit{a}}^{\mathit{n}}|{\mathit{W}}^n\right)/ {\text{Pr}}_{p_0}\left(A_i=a,\overline{A}=\overline{a}|{\mathit{W}}_{\mathit{i}}\right)<\infty \text{ for all }i\text{ and }{a}^n\in {\{0,1\}}^n.$ We have the following causal identification result for these parameters.

Theorem 1: Suppose the NPSEM defined in (1) contains the true set of underlying counterfactual distributions. Under Assumptions 1 and 2, respectively, we have,

$${\psi }^{g^{*},\pi }=\frac{1}{n}\sum _{i=1}^n\sum _{a=0}^1{\overline{Q}}_0\left\{{\mathit{W}}_{\mathit{i}},a,k_n(\pi )\right\}{g}_{{\theta }_n}^{*}\left(a|{\mathit{W}}_{\mathit{i}}\right)$$

$${\psi }^{g^{*}}=\frac{1}{n}\sum _{i=1}^n\sum _{a^n}{\overline{Q}}_0\left\{{\mathit{W}}_{\mathit{i}},a_i,k_n(\overline{a})\right\}{g}^{*}\left({\mathit{a}}^{\mathit{n}}|{\mathit{W}}^{\mathit{n}}\right).$$

All proofs are provided in Web Appendix H. While Theorem 1 gives an expression for ${\psi }^{g^{*}}{}^{,\pi }$ as a functional of the observed data distribution, whether its identifying functional can be estimated consistently depends on the value of π. In order to estimate this quantity, it is necessary to have statistical support at $\overline{A}=\pi$. For instance, one could estimate ${\psi }^{g^{*}}{}^{,\pi }$ by plugging in an estimate of the outcome regression function ${\overline{Q}}_0\left\{\mathit{w},a,k_n(\pi )\right\}$ specifically at π, which requires observing Y_i and $\overline{A}=\pi$ simultaneously for some subjects. However, we only observe one value of $\overline{A}$ for all subjects, and so for a fixed π, we will rarely observe outcomes when $\overline{A}=\pi$, and will do so with decreasing probability as sample size grows. For a fixed π, this outcome regression cannot be consistently estimated. Similarly, statistical nonparametric identification for ${\psi }^{g^{*}}$ relies on the choice of the hypothetical intervention g*.If g* produces exposure vectors with a sample mean that do not correspond to the observed $\overline{A}$, then we encounter the same problem as for ${\psi }^{g^{*}}{}^{,\pi }$.

As a result, we will only be able to perform inference on ${\psi }^{g^{*}}{}^{,\pi }$ when $\pi =\overline{A}$ without invoking strong assumptions. Substituting for π, we express counterfactuals under the intervention setting the individual-level exposure by g* and setting the proportion exposed to the observed proportion of subjects exposed as $Y_i^{g^{*},\overline{A}}$, and the corresponding causal parameter as ${\psi }^{g^{*}}{}^{,\overline{A}}$.

This causal parameter is in fact equivalent to the overall effect parameter ${\psi }^{g^{*}}$ when g* assigns $\overline{A}$ of subjects to exposure with probability one. We refer to such interventions as exposure reallocation schemes (ERSs), as they define schemes for reallocating the same number of exposures among the sample. One example of an ERS is complete randomization with probability $\overline{A}$, in which the support for $g^{*}\text{\hspace{0.17em}is\hspace{0.17em}\hspace{0.17em}}\left\{{\mathit{a}}^{*\mathit{n}}:{\overline{a}}^{*}=\overline{A}\right\}$, and each exposureassignment vector has equal probability. In the LREC example, this would correspond to randomly shifting the care tasks of $\overline{A}$ of the patients. Another example is an intervention that takes a scalar function of each subject’s covariates, and assigns the exposure to the ${\sum }_{i=1}^n{A}_i$ subjects with the highest values of this function. Such a dynamic reallocation scheme makes it possible to define causal parameters that quantify how outcomes could be improved by reallocating a resource-constrained intervention to the patients most likely to benefit from it. In the LREC example, if this function of a patient’s covariates returned their CD4 count, this intervention would correspond to shifting the care tasks of the $\overline{A}$ with the highest CD4 counts, which could be viewed as a proxy for the healthiest A patients. The exposure reallocation criterion can in fact be relaxed, which we discuss in Web Appendix B.

We have the following statistical identification results for ${\psi }^{g^{*}}{}^{,\overline{A}}$ and, under an ERS, ${\psi }^{g^{*}}$:

Theorem 2: Suppose the NPSEM defined in (1) contains the true set of underlying counterfactual distributions, and Assumption 1 holds for $\pi =\overline{A}$. Then

$${\psi }^{g^{*},\overline{A}}=\frac{1}{n}\sum _{i=1}^n\sum _{a=0}^1{\overline{Q}}_0\left\{{\mathit{W}}_{\mathit{i}},a,k_n(\overline{A})\right\}{g}_{{\theta }_n}^{*}\left(a|{\mathit{W}}_{\mathit{i}}\right)\equiv {\Psi }^{g^{*},\overline{A}}\left({\overline{Q}}_0\right).$$

If g* is an ERS, ${\psi }^{g^{*}}={\psi }^{g^{*},\overline{A}}$, and is statistically nonparametrically identified by ${\Psi }^{g^{*},\overline{A}}\left({\overline{Q}}_0\right)$. These identifiable parameters will naturally vary with $\overline{A}$. Just how much will depend on the variability of $\overline{A}$ itself and the sensitivity of ${\overline{Q}}_0$ to $\overline{A}$, which will be setting-specific. Thus, the relevance of these parameters is subjective. However, we emphasize that unless one is willing to make stronger extrapolating assumptions, these data-dependent parameters are the only parameters we can hope to estimate consistently with data from a single group.

Spillover effects are not estimable when comparing interventions that result in different proportions of subjects assigned to exposure. We consider their estimation when many groups are observed, as well as the role of $k_n(\overline{A})$ as an effect modifier in Web Appendix A.

4. Estimation & Inference

We now show that an estimator one can use under no interference for a conditional average treatment effect (CATE) parameter under a potentially dynamic and/or stochastic intervention g* can also be used for ${\Psi }^{g^{*}}{}^{,\overline{A}}\left({\overline{Q}}_0\right)$. Define the i.i.d. causal and statistical models as the submodels of the NPSEM defined in (1) and ${\mathcal{M}}_{si}$, respectively, induced by imposing the no interference assumption. The NPSEM defined in (1) reduces to ${\mathit{W}}_{\mathit{i}}={\tilde{\mathit{f}}}_{\mathit{W}}\left({\mathit{U}}_{\mathit{i}}^{\mathit{W}}\right)$, $A_i={\tilde{f}}_A\left({\mathit{W}}_{\mathit{i}},U_i^A\right)$, $Y_i={\tilde{f}}_Y\left({\mathit{W}}_{\mathit{i}},A_i,U_i^Y\right)$, and the statistical model ${\mathcal{M}}_{iid}$ becomes ${\tilde{p}}_0\left({\mathit{O}}^{\mathit{n}}\right)={\prod }_{i=1}^n{\tilde{q}}_{Y,0}\left(Y_i|A_i,{\mathit{W}}_{\mathit{i}}\right){\tilde{g}}_0\left(A_i|{\mathit{W}}_{\mathit{i}}\right){\tilde{q}}_{W,0}\left({\mathit{W}}_{\mathit{i}}\right)$. The conditional-average causal target parameter is ${\psi }_{iid}^{g^{*}}\equiv n^{-1}{\sum }_{i=1}^{n}E\left(Y^{g^{*}}|{\mathit{W}}_{\mathit{i}}\right)$, where $Y^{g^{*}}\equiv {\tilde{f}}_Y\left(\mathit{W},A^{*},U^Y\right)$ and A* is the individual-level exposure assigned under intervention g*. The parameter ${\psi }_{iid}^{g^{*}}$ is identified by ${\Psi }_{iid}^{g^{*}}\left({\overline{Q}}_0\right)\equiv n^{-1}{\sum }_{i=1}^n{\sum }_{a=0}^1{\overline{Q}}_0\left(a,{\mathit{W}}_{\mathit{i}}\right)g^{*}\left(a|{\mathit{W}}_{\mathit{i}}\right)$, and the CATE is defined as the contrast in ${\psi }_{iid}^{g^{*}}$ comparing the interventions g*(1 | W) = 1 and g*(1 | W) = 0, i.e., $n^{-1}{\sum }_{i=1}^{n}E\left(Y^1-Y^0|{\mathit{W}}_{\mathit{i}}\right)$.(CATE is also often used to refer to E(Y¹ — Y⁰ | W = w).)

For a given semiparametric model and target estimand that is a functional of the observed data distribution, the TMLE is a semiparametric efficient substitution estimator. In the case of ${\Psi }_{iid}^{g^{*}}\left({\overline{Q}}_0\right)$, this involves an algorithm that generates an estimator ${\overline{Q}}_n^{*}$ to substitute for ${\overline{Q}}_0$ in ${\Psi }_{iid}^{g^{*}}$. We review the TMLE for ${\Psi }_{iid}^{g^{*}}\left({\overline{Q}}_0\right)$ in the i.i.d. setting in Web Appendix C. The following theorem formalizes the asymptotic properties of the i.i.d. TMLE when applied in our setting. We discuss the intuition behind this result in Web Appendix D.

Theorem 3: Suppose the technical conditions listed in Web Appendix G hold. Then for ${\Psi }^{g^{*}}{}^{,\overline{A}}\left({\overline{Q}}_0\right)$_, the TMLE ${\psi }_n={\Psi }_{iid}^{g_{{\theta }_n}^{*}}\left({\overline{Q}}_n^{*}\right)for{\Psi }_{iid}^{g_{{\theta }_n}^{*}}\left({\overline{Q}}_0\right)$ under ${\mathcal{M}}_{iid}$ is semiparametric efficient, consistent, and asymptotically normal under ${\mathcal{M}}_{si}$, with asymptotic variance

$${\sigma }^2\equiv \underset{n\to \infty }{\text{lim}}{n}^{-1}\sum _{i=1}^n{\left[\frac{g_{{\theta }_n}^{*}\left(A_i|{\mathit{W}}_{\mathit{i}}\right)}{g_{{\theta }_n,0}\left(A_i|{\mathit{W}}_{\mathit{i}}\right)}\left\{Y_i-{\overline{Q}}_{{\theta }_n,0}\left(A_i,{\mathit{W}}_{\mathit{i}}\right)\right\}\right]}^2.$$

One can then use the argument of the limit in the expression for σ², which is the variance estimator one would use for the TMLE as an estimator of ${\Psi }_{iid}^{g_{{\theta }_n}^{*}}\left({\overline{Q}}_0\right)$ under ${\mathcal{M}}_{iid}$. Thus, inference based on the model with no interference will be valid in the sense that for a given underlying true distribution p₀, Wald-based confidence intervals and hypothesis tests one would use for ${\Psi }_{iid}^{g_{{\theta }_n}^{*}}\left({\overline{Q}}_0\right)$ under ${\mathcal{M}}_{iid}$ converge to the correct level asymptotically. The augmented-inverse probability weighted (A-IPW) estimator for ${\Psi }_{iid}^{g_{{\theta }_n}^{*}}\left({\overline{Q}}_0\right)$ (defined in Web Appendix C) has the same asymptotic properties, and its proof follows analogously to that of Theorem 3. A consequence of Theorem 3 is that if one is to naively estimate the CATE with a TMLE or A-IPW estimator ignoring the presence of interference, the resulting estimate can be interpreted as the direct effect of exposure in a setting in which $\overline{A}$ of the sample is exposed. Other estimators (if they are consistent) share this interpretation, though their asymptotic properties appear to be more challenging to derive.

5. Simulation Study

We now study the empirical performance of our method. A more detailed review of the study is available in Web Appendix F. Our simulation design combines different sample sizes (50, 500, and 5000) and interference levels governed by β (0, 1, 10). The setting with β = 0 corresponds to no interference, while β =1 corresponds to a setting in which shifting everyone would completely negate the effect of the exposure. When β > 1, the direction of the individual exposure effect reverses when enough individuals are exposed.

We consider two causal parameters depending on the observed $\overline{A}$: (i) the direct effect when $\overline{A}$ of subjects are exposed, and (ii) the overall effect under the ERS that assigns subjects with the $S_n\equiv {\sum }_{i=1}^n{A}_i$ highest (scalar) W values to exposure. For this data generating process, the intervention assigning the exposure to subjects with the highest values of W corresponds with the optimal exposure reallocation scheme (OERS) within the class of all ERSs. We consider three different parametric models for estimation: one in which the outcome regression is correctly specified, but the propensity score is not, one in which the reverse is true, and one in which both are correctly specified.

Results from this study are summarized in Table 1. Coverage probabilities in correctly-specified-model settings with interference are quite comparable to those without interference. Coverage is generally better for the overall effect parameter than for the direct effect. This is likely a result of the probability weights being more stable for the overall effect parameter, due to the OERS being closer to the actual propensity score than the interventions assigning all subjects to exposure and no exposure. Double robustness merely implies consistency, so correct coverage is not necessarily expected in the settings with model misspecification, though we do still see fairly decent coverage in these settings. In practice, we recommend estimating the nuisance functions under more adaptive models using machine learning tools such as super learner, so as to avoid model misspecification, and preserve valid inference.

Table 1.

Simulation results for the direct effect and overall effect under the optimal exposure reallocation scheme (OERS) based on 5000 samples. MSE is mean squared error, and CP is the Monte Carlo coverage probability of the 95%confidence interval.

$\overline{Q}$	g	n	β	Target parameter
				Direct effect			Overall effect - OERS
				Bias	MSE	CP	Bias	MSE	CP
Correctly specified	Correctly specified	50	0	0.010	0.10	0.916	2.2e-4	0.027	0.948
			1	4.6e-3	0.10	0.917	8.4e-5	0.027	0.951
			10	−0.17	0.16	0.837	0.026	0.028	0.942
		500	0	2.0e-3	9.7e-3	0.955	3.0e-4	2.7e-3	0.960
			1	−1.8e-3	9.6e-3	0.958	1.4e-3	2.7e-3	0.962
			10	−0.026	0.011	0.942	5.7e-3	2.7e-3	0.960
		5000	0	1.1e-4	9.7e-4	0.958	−1.5e-4	2.6e-4	0.964
			1	8.6e-5	9.6e-4	0.961	6.9e-5	2.6e-4	0.965
			10	−3.0e-3	9.8e-4	0.961	6.3e-4	2.7e-4	0.960
Mis- specified	Correctly specified	50	0	8.7e-3	0.10	0.884	4.5e-3	0.032	0.940
			1	8.0e-4	0.10	0.885	2.5e-3	0.031	0.938
			10	−0.16	0.15	0.806	5.0e-3	0.048	0.983
		500	0	−2.4e-4	9.8e-3	0.919	8.6e-4	3.3e-3	0.952
			1	−3.2e-3	9.7e-3	0.924	−9.3e-4	3.1e-3	0.953
			10	−0.025	0.011	0.902	−1.0e-3	4.5e-3	0.991
		5000	0	3.5e-4	9.9e-4	0.921	−1.8e-4	3.1e-4	0.956
			1	−2.7e-4	9.8e-4	0.922	−1.4e-4	3.1e-4	0.950
			10	−4.7e-3	1.0e-3	0.915	−1.2e-4	4.5e-4	0.991
Correctly specified	Mis- specified	50	0	0.025	0.10	0.934	4.2e-3	0.030	0.954
			1	0.011	0.10	0.919	1.8e-3	0.029	0.955
			10	−0.18	0.28	0.933	4.1e-3	0.030	0.952
		500	0	8.3e-3	9.9e-3	0.966	−6.6e-4	3.0e-3	0.968
			1	1.6e-3	9.8e-3	0.959	8.0e-5	3.1e-3	0.965
			10	−0.082	0.029	0.973	−3.1e-4	2.9e-3	0.968
		5000	0	7.6e-3	1.1e-3	0.963	2.9e-4	3.0e-4	0.967
			1	1.8e-3	9.8e-4	0.964	−1.8e-4	3.1e-4	0.967
			10	−0.054	5.4e-3	0.916	3.2e-4	2.9e-4	0.966

There is a general trend of bias increasing with β, likely due to the increase in variance of Y. MSE remains relatively stable across β values, indicating that the conditional variance given $\overline{A}$ is stable with respect to β, and that bias is small relative to conditional variance. The double robustness property of our estimator is evidenced by the decrease in bias and MSE with sample size in each setting.

6. Data Application

Health care worker shortages are a widespread problem, particularly in sub-Saharan Africa, and pose serious public health challenges among populations with HIV and otherwise. To combat this issue, clinics have increasingly adopted task-shifting programs, in which patients identified as being at low risk for poor health outcomes have designated health care tasks shifted from a higher-cadre health care provider to a lower-cadre provider (e.g., from physician to mid-level provider; mid-level provider to nurse; nurse to lay worker; or in our case, mid-level provider to nurse) (World Health Organization et al., 2012).

Clearly, it is of great public health interest to understand the effects of task shifting, and in particular whether this practice is harmful for patients whose care is being shifted. If it is harmful, then this practice may not be advisable for widespread use; otherwise, it may be a viable option for mitigating health care worker shortages. Indeed, according to World Health Organization et al. (2012), “Action on human resources for health is imperative if global commitments to the Millennium Development Goals, and to providing universal access to HIV services, are to be met. Action on task shifting is imperative as it provides the only realistic possibility of increasing the human resources fast enough to meet the urgent need.”

In their systematic review and meta-analysis of task-shifting studies, Lassi et al. (2013) concluded, “No difference between the effectiveness of care provided by mid-level health workers and that provided by higher-level health workers was found.” However, they qualified these findings as being largely based on studies in developed countries, and highlighted a need for more studies conducted in Africa. In the LREC program, task-shifting was adopted in clinics in Kenya, and data were collected on eligible low-risk patients. As we described previously, an analysis of the data from this program was conducted in Tran et al. (2016), but the authors expressed concern that interference may have been present in this study due to the potential for the number of task-shifted patients to affect the time and quality of care nurses are able to provide. We apply the methodology developed in this paper, which accounts for this form of interference, to study the effects of task shifting.

We conduct our analysis on these data independently within each clinic, estimating various effects using the TMLE defined in Section 4. The nuisance functions g* and $\overline{Q}$ are estimated using a super learner with a library consisting of the marginal mean, generalized linear models, LASSO, random forest, generalized boosted models, and support vector machines.

Our results are summarized in Figure 1. In addition to the individual clinic-level effect estimates, each panel depicts an estimated marginal structural model (MSM) summarizing each effect across the different clinics as a function of the proportion of all patients task shifted. We relegate discussion of the MSMs to Web Appendix A. The plot in panel (a) depicts the estimated direct effects of task shifting in settings in which only the observed number of patients are task shifted. We observe significant effects in all but one clinic, suggesting that task-shifting is beneficial in these clinics. The only non-significant effect estimate was found in the clinic with the lowest proportion of patients task-shifted.

Figure 1.

(a) The estimated direct effects of task shifting on risk of death or loss to follow up in each clinic when the observed proportion of all patients task shifted is held fixed. (b) The estimated overall effect of a complete randomization intervention on risk of death or loss to follow up compared to the observed proportion of cases. (c) The estimated overall effect comparing an intervention task shifting only the S_n patients with the highest CD4 counts to complete randomization on risk of death or loss to follow up. The vertical bars represent the corresponding 95% confidence intervals. Solid lines indicate results for urban clinics; dashed lines indicate results for non-urban clinics. Estimates are plotted against the proportion of all patients task-shifted in each clinic. The lines spanning the plot horizontally represent the fitted MSMs, summarizing how these effects vary as functions of the proportion of patients task-shifted given the urban designation of the clinic.

It is also of interest to compare the effects of various ERSs. The plots in panels (b) and (c) depict estimates of such contrasts. In panel (b) complete randomization is contrasted with the observed risk of death or loss to follow up. This effect contrast essentially tells us how different outcomes would have been if the observed number of task-shift assignments had been allocated randomly (in contrast to the observed non-random assignment mechanism). No effect is statistically significant among any of the clinics. The contrast depicted in panel (c) is between the ERS assigning the S_n patients with the highest CD4 counts to be task shifted compared with complete randomization. If one were to believe that task shifting is most beneficial to healthy patients, then using CD4 count as a proxy for patients’ health status, one might be interested in this intervention, which corresponds to only task shifting the healthiest S_n patients. The effect contrast essentially tells us how much outcomes could be improved if task shifting were assigned according to CD4 count over an intervention completely ignoring covariate information. Three of these clinics have statistically-significant effect estimates. This suggests an improvement in outcomes under the CD4 count-based intervention in these particular clinics.

7. Discussion

In this paper, we have developed new methodology to perform causal inference in settings with stratified interference when the number of causally-separated groups is small or only one, but the sample sizes of these groups are moderate to large. A central challenge in the setting of a single causally-dependent group under stratified interference is that the statistical support for the outcome regression is limited to a single observed proportion of subjects receiving the exposure. Our proposed methodology overcomes this by focusing on identification and estimation of causal parameters that summarize the distribution of counterfactual outcomes under interventions that preserve the observed proportion of subjects exposed.

Our proposed methodology does not require the implementation of a new estimator, but rather utilizes the existing TMLE developed for the average counterfactual outcome in the absence of interference. For the overall effect of an exposure reallocation scheme, one need only derive the appropriate marginal intervention rule from the user-specified joint rule. Our methodology is semiparametric efficient and doubly robust, the latter of which permits the use of machine learning tools to estimate the response surface and propensity score.

Our methodology is particularly relevant to situations in which the efficacy of an exposure varies with the proportion of subjects receiving it. This may often occur when the exposure is a limited, shared resource, such as in our task-shifting data example. Task shifting is a potentially widely useful approach to combat health care worker shortages worldwide, thus our methodology may be useful in other such studies.

In our data application, we observed a statistically-significant improvement in risk of death or loss to follow up as a result of shifting patients from clinical officers to nurses, provided the proportion of patients task shifted remains fixed, in all but one clinic. This finding is consistent with the results reported by Tran et al. (2016) in their analysis of longitudinal interventions on enrollment, in which they accounted for time-dependent confounding, but not potential interference. While this result may reflect a truly beneficial effect, due for example to improved quantity or quality of care that nurses are able to provide, it may also reflect unmeasured confounding, with patients at lower risk in ways not captured by baseline covariates more likely to be enrolled in the task-shifting program (Tran et al., 2016).

We have shown how to estimate the overall effects of interventions within the class of exposure reallocation schemes, which reallocate the observed number of exposure assignments based on some user-specified rule. If the effect of the individual-level exposure varies depending on an individual’s covariates, such schemes have the potential to improve outcomes by assigning the same number of interventions to the individuals most likely to benefit. For instance, healthier patients may respond better to task shifting, in which case an exposure reallocation scheme based on CD4 count might be preferable to complete randomization, as we have demonstrated evidence of in some clinics. (In practice, the eligibility criteria include CD4 count, and the observed task-shifting decisions used some subsequent assessment of illness beyond that initial cut off.) Even in this case, however, task-shifting might still be beneficial for sicker patients as well, in which case it is possible that we should be task-shifting more than just the observed number of patients. Yet, without additional causal assumptions and observations from other groups with higher task-shifting rates, the effect of task shifting more patients cannot be estimated without extrapolating beyond the support of the observed data. Therefore, assertions regarding effects under interventions that task shift more than the observed proportion of patients must be interpreted with care.

The proposed methodology has several limitations. The inability to estimate causal parameters under interventions in which a different proportion of subjects is exposed than is actually observed is a limitation inherited directly from the data. When subjects are enlisted over an extended period of time, our methodology can only be applied to a subset of subjects enlisted within a limited time frame, as was done in our data example, rather than the entire population enlisted over the duration of the study. While we allow for subjects’ exposures to affect one another’s outcomes, we do not account for subjects’ covariates affecting one another’s exposures or outcomes. Finally, our methodology relies on the stratified interference assumption, the plausibility of which will vary widely from application to application. Simply because one lacks knowledge of the underlying structure of interference, does not mean one should blithely assume stratified interference. However, as we have argued, we believe it can be a reasonable approximation, especially in settings in which interference is induced by an exposure being a limited resource being shared among subjects.