Extracted main text — title through conclusion, appendix excluded. This is what our citation measures are computed over, published so the extraction can be checked by eye.
106,181 characters · 25 sections · 102 citation commands
Long-term Causal Inference Under Persistent Confounding via Data Combination
\noindentKeywords: data combination, doubly robust estimation, long-term causal inference, proxy variables, unobserved confounding.
Empirical researchers and decision-makers are often interested in learning the long-term treatment effects of interventions. For example, labor economists are interested in the effect of early childhood education on lifetime earnings chetty2011does, marketers are interested in the effects of promotions on long-term revenue yang2020targeting, online platforms are interested in the effects of webpage designs on users' long-term behaviors hohnhold2015focusing. Since a long-term effect can be quite different from short-term effects kohavi2012trustworthy, accurately evaluating the long-term effect is both difficult and crucial for comprehensively understanding the intervention of interest.
Learning long-term treatment effects is very challenging in practice because long-term outcomes are seldom observed within the time frame of randomized experiments. For example, randomized experiments in online platforms (often termed A/B tests within that context) usually last for only a few weeks, and practitioners in the industry commonly recognize evaluation of long-term effects as a paramount challenge gupta2019top. In contrast, observational data are often easier and cheaper to acquire and can be collected retroactively, so they are more likely to include long-term outcome observations. Nevertheless, observational data are susceptible to unmeasured confounding, which can lead to biased treatment effect estimates. Therefore, long-term causal inference is very challenging using only experimental or observational data, either due to missing long-term outcome (in experimental data) or unmeasured confounding (in observational data).
In this paper, we study the identification and estimation of long-term treatment effects by combining both experimental and observational data. By combining these two different types of data, we hope to leverage their complementary strengths, i.e., the randomized treatment assignments in the experimental data and the long-term observations in the observational data. In particular, we aim to tackle the presence of persistent confounding in the observational data, which cannot be generally ruled out. That is, we allow some unobserved confounders to have persistent effects in the sense that they can affect not only the short-term outcomes but also the long-term outcome. Persistent confounders are prevalent in long-term studies. For example, in studying early childhood education's effect on lifetime earnings, students' innate intelligence and/or familial support systems can affect both short-term and long-term earnings. Our setup is summarized in the causal diagrams in (ref).
A few previous works also consider data combination for long-term causal inference. athey2019surrogate, in a setting where the observational sample contains no information on the treatment, rely on a surrogate criterion first proposed by prentice1989surrogate. athey2020combining, in the same setting as considered in the current paper, assume a latent unconfoundedness condition. {While these conditions make no explicit reference to persistent confounding and its absence, a nontrivial persistent confounder can generally violate these (see (ref) for details). At the same time, both settings are just identified, meaning the conditions imposed are minimal, {so that if a condition is dropped then another would be needed in its place to guarantee identification.}
{In this paper, we leverage an assumed sequential structure between multiple short-term outcomes to tackle long-term causal inference in the presence of persistent confounders. Our new identification and estimation strategies are based on using short-term outcomes as proxy variables for the persistent confounders.} To the best of our knowledge, this is the first time that the internal structure of short-term outcomes is used to address unmeasured confounding in long-term causal inference. Indeed, although athey2019surrogate,athey2020combining also advocate using multiple short-term outcomes, they view them as a whole without leveraging their internal structure. Our work therefore also provides new insights on the special role of using multiple short-term outcomes in long-term causal inference.
Our contributions are summarized as follows:
The rest of this paper is organized as follows. We first review the related literature in (ref) and set up our problem in (ref). Then we discuss our identification strategies in (ref), where each subsection features one different identification strategy. In (ref), we present our long-term treatment effect estimators and analyze their asymptotic properties. We further dicuss some extensions in (ref). In (ref), we illustrate the performance of methods in a semi-synthetic experiment. We finally conclude this paper in (ref).
Our paper is related to a large body of biostatistics literature on surrogate outcomes; see reviews in weir2006statistical,vanderweele2013surrogate,joffe2009related.
These literature consider using the causal effect of an intervention on a surrogate outcome (e.g., patients' short-term health) as a proxy for its treatment effect on the outcome of primary interest (e.g., long-term health). To this end, many criteria have been proposed to ensure the validity of the surrogate outcome. Examples include the {statistical surrogate criterion} prentice1989surrogate, principal surrogate criterion frangakis2002principal, consistent surrogate criterion chen2007criteria, among many others. However, these criteria can easily run into a logical paradox\footnote{{The paradox refers to the phenomenon that the sign of the treatment effect on the target outcome cannot be predicted by the sign of the treatment effect on the surrogate and the sign of the surrogate's effect on the target outcome. For example, it is possible that a treatment has a negative effect on the target outcome, even if both the treatment effect on the surrogate and the surrogate's effect on the target outcome are positive. }} chen2007criteria or rely on unidentifiable quantities, showing the challenge of causal inference when the primary outcome is completely missing. When multiple surrogates are available, wang2020model,price2018estimation consider transforming these surrogates to optimally approximate the primary outcome. Their approaches can avoid the surrogate paradox discussed in chen2007criteria. Nevertheless, learning surrogate transformations requires having experimental data with long-term outcome observations.
In contrast, our paper does not need long-term outcome observations in the experimental data but only need them in observational data. Moreover, our paper does not view short-term outcomes as proxies for the long-term outcome, so we avoid these previous surrogate criteria. {Instead, we consider three groups of short-term outcomes $(S_1, S_2, S_3)$, viewing $S_1$ and $S_3$ as proxies for unmeasured confounders and $S_2$ as a surrogate for the effect of $S_1$ on $S_3$ (it cannot, however, serve as a surrogate for the effect of $A$ on $Y$ due to unmediated effects).} See also discussions in (ref).
Following athey2019surrogate, some recent literature also combine experimental and observational data, and rely on the statistical surrogate criterion, either to estimate cumulative treatment effects in dynamic settings battocchi2021estimating or learn long-term optimal treatment policies yang2020targeting,cai2021gear. chen2021semiparametric derive the efficiency lower bound for average long-term treatment effect in settings of athey2019surrogate,athey2020combining. singh2021finite,singh2022generalized further develop debiased long-term treatment effect estimators based on machine learning nuisance estimation. In contrast, kallus2020role,cai2021coda combine two datasets that both satisfy unconfoundedness. Still, all of these works rule out persistent confounding, which is the main problem tackled in this paper.
{A concurrent and independent work by ghassami2022combining uses alternative conditions or additional variables to alleviate latent confounding in long-term causal inference. They propose three different identification strategies, and their proximal data fusion strategy is closely related to our approach in (ref). Their approach requires auxiliary proxy variables satisfying certain generic conditions (in addition to the short-term outcomes). In contrast, our work specifically leverages the special sequential structure of multiple short-term outcomes and shows how such short-term outcomes can proxy the confounders. {This provides us with the necessary proxy variables for identification} and allows us to understand the different types of confounders and which need to be controlled (see (ref)). Importantly, we develop both estimation {and inference} methods with theoretical guarantees and validate them in a concret case study. Moreover, we provide an alternative control function identification strategy in (ref) and study how the short-term outcomes may help weaken a widely assumed external validity condition in (ref). These results have no analogues in ghassami2022combining.}
There is also growing interest in combining experimental and observational data to improve, rather than enable, causal inference chen2021minimax,cheng2021adaptive,yang2020elastic,yang2020improved,colnet2020causal,kallus2018removing,rosenman2022propensity,rosenman2020combining,yang2019combining. In these works, the outcome of interest is observed in both types of data, so causal-effect identification is already guaranteed by the experimental data. Instead, the aim of the data combination is to reduce variance. In contrast to these works, in our setting, data combination is crucial for causal identification since any one data set alone cannot identify the long-term treatment effect.
Our identification proposals are related to how proximal causal inference deals with unmeasured confounding by leveraging proxy variables tchetgen2020introduction. The seminal work of Miao2016 demonstrated the identification of treatment effects with unobserved confounders given two different types of proxy variables: negative control outcomes, which are not affected by the treatment, and negative control treatments, which do not affect the outcome. Since then, a series of works have proposed a variety of different estimation methods based on this identification strategy kallus2021causal,GhassamiAmirEmad2021MKML,deaner2021proxy,SinghRahul2020KMfU,miao2018a,shi2020multiply,mastouri2021proximal,cui2020semiparametric. The proximal causal inference framework has also been extended to longitudinal data analysis imbens2021controlling,ying2021proximal,shi2021theory, mediation analysis dukes2021proximal,ghassami2021proximal, and off-policy evaluation and learning bennett2021proximal,tennenholtz2020off,qi2021proximal,xu2021deep.
The existing proximal causal inference literature focus on a single observational dataset. In contrast, in this paper we consider combining observational and experimental data. We view short-term outcomes as proxy variables for persistent unmeasured confounders. However, all of these short-term outcomes can be affected by the treatment (see (ref) below), so they do not satisfy the proxy conditions in Miao2016. In this paper, we establish novel identification strategies that leverage the additional experimental data. See also discussions in (ref).
We consider a binary treatment $A \in \mathcal{A} = \braces{0, 1}$ where $A = 1$ stands for the treated group and $A = 0$ stands for the control group. We are interested in the treatment effect on a long-term outcome. Using the potential outcome framework rubin1974estimating, we postulate potential long-term outcomes $Y(0), Y(1) \in\mathcal{Y}\subseteq\Rl$, which would be realized were the treatment assignment equal $0$ and $1$, respectively. In reality, we observe at most one of the potential outcomes per unit, corresponding to the actual treatment assignment, $Y = Y(A)$.
We may in fact observe neither potential long-term outcome in short-term experiments that end before these long-term outcomes can be observed. Nevertheless, it is usually still possible to observe some short-term outcomes. We postulate potential short-term outcomes $S(1) \in \mathcal{S}, S(0)\in \mathcal{S}$, and denote the observable realized short-term outcomes as $S = S(A)$. In this paper, we consider multiple short-term outcomes, so we generally understand $S$ as a vector. We discuss our assumptions on the inner structure of these short-term outcomes in (ref). Additionally, we can observe some pre-treatment covariates denoted as $X \in \mathcal{X}$.
We have access to two samples: an observational (O) sample with $n_O$ units and an experimental (E) sample with $n_E$ units. We suppose that the observational sample is a random sample from the population of interest, where for each unit $i$ we can observe independently and identically distributed tuples $(X_i, A_i, S_i, Y_i)$. The experimental sample may be a selective sample from the same population, where for each unit $i$ we only observe $(X_i, A_i, S_i)$, but not the long-term outcome. We use a binary indicator $G_i \in \braces{E, O}$ to denote which sample a unit $i$ belongs to. Without loss of generality, we consider a combined i.i.d sample of size $n = n_O + n_E$ from an artificial super-population, namely, $\mathcal{D} = \braces{(G_i, X_i, A_i, S_i, Y_i\indic{G_i = O}): i = 1, \dots, n_O + n_E}$. We use $\mathbb{P}$ and $\mathbb{E}$ to denote the probability and expectation with respect to this super-population, and use $p(\cdot)$ to denote the associated probability density function or probability mass function, as appropriate. We also denote the observational and experimental subsamples as $\mathcal{D}_O$ and $\mathcal{D}_E$, respectively.
Our aim is to combine the observational and experimental samples in order to learn the long-term treatment effect on the population associated with the observational data:
Our results easily extend to the average on the experimental or combined population. We focus on $\tau$ for concreteness and we believe it captures the most commonly relevant estimand.
We now describe the basic assumptions that characterize the experimental and observational data sets as such. Unless otherwise stated, all of these assumptions are maintained throughout this paper.
The observational data is generally confounded, that is, conditioning only on $X$ does not render the treatment assignment independent of the potential short-term and long-term outcomes. Instead, there exist some unobserved confounders $U \in \mathcal{U}$ that are needed to account for the association between treatment and potential outcomes. {See (ref) for a single world intervention graph illustration richardson2013single when intervening on the variable $A$.}
(ref) means that $U$ and $X$ together account for all confounding in the observational data, and generally the observed covariates $X$ alone are not enough. Moreover, we impose the overlap condition $0 < \Prb{A = 1 \mid U, X, G = O} < 1$, which is a standard assumption in causal inference literature. Note that the existence of $U$ is without loss of generality because we can always take it to be the potential outcomes themselves. Because of the unobserved confounders $U$, the observational data alone is not enough to identify the treatment effect parameter $\tau$ in (ref).
In contrast to the observational data, the treatments are assigned completely at random in the experimental data. {See (ref) for a single world intervention graph illustration.}
{In (ref), we will relax (ref) by allowing the treatment assignment in the experimental data to depend on the covariates $X$, so the conditions in (ref) hold conditioned on the covariates $X$.}
Although unconfounded, the experimental data do not contain long-term outcome observations, so the experimental data alone is not enough to identify the treatment effect either. This motivates us to combine the observational and experimental data. To this end, we further impose the following assumption permitting such combination.
(ref) ensures that the two samples have enough commonality so it is meaningful to combine them. (ref) in (ref) means that the experimental data has external validity, in that the distribution of $\prns{S\prns{a}, U, X}$ in the experimental data is the same as that in the observational data (i.e., the population of interest). Similar assumptions also appear in previous literature that attempt to combine different samples athey2020combining,athey2019surrogate,kallus2020role.
In (ref) we further relax (ref) to allow the distributions of covariates $X$ to be different in the two samples. Note that (ref) already allows the distributions of potential long-term outcome $Y(a)$ in the experimental and observational data to be different, so the long-term treatment effect on the experimental population can be different from our target.
(ref) in (ref) means that the conditional distributions of $(U, X) \mid A$ on the experimental and observational data have enough overlap, which is also a common assumption in missing data literature tsiatis2007semiparametric.
To address general persistent confounding, we need some additional structure on the short-term outcomes. In this paper, we consider leveraging multiple, sequential short-term outcomes. In particular, we consider a partitioning of the short-term outcomes into three groups sorted in a temporal order, writing the potential short-term outcomes as $S(a) = \prns{S_{1}(a), S_{2}(a), S_{3}(a)} \in \mathcal{S}_1 \times \mathcal{S}_2 \times \mathcal{S}_3$ and their observed counterparts as $S = \prns{S_{1}, S_{2}, S_{3}}$. Given this partitioning, we assume the following conditional independence structure for the potential short-term and long-term outcomes.
(ref) requires that the effect of the first short-term outcome on the last short-term outcome and the long-term outcome is mediated by the intermediate short-term outcome. Nonetheless, all outcomes can be related by unobserved confounders, even in the experimental data, and the treatment can affect all outcomes both directly and indirectly. This captures the sequential structure of the short-term and long-term outcomes (see (ref) for an example\footnote{{ (ref) is just one example diagram that satisfies (ref). The assumption could be also satisfied if there is an additional arrow from $S_2$ to $Y$. When $S_1(a), S_2(a), S_3(a), Y(a)$ follow a Markov process conditional on $U, X$ as discussed in this paragraph, the arrow from $S_2$ to $Y$ is indeed absent.}}). For example, it holds when the potential outcomes follow autoregressive structural equations of suitable orders (see (ref) below for a simple instance). {Moreover, it holds when the potential outcomes $S_1(a), S_2(a), S_3(a), Y(a)$ follow a Markov process, conditional on $U, X$. Markov models are widely used in social sciences such as for modeling the dynamics of labor markets poterba1986reporting,mohapatra2007rise, and in medical sciences for modeling chronic-disease progression marshall1995multi,liu2013glycemic,kay1986markov,liu2013glycemic.}
{ Note that (ref) significantly differs from the statistical surrogacy condition in athey2019surrogate. The latter requires short-term outcomes $S$ to block all dependence between the long-term outcome $Y$ and the treatment $A$ given the covariates $X$, ruling out any unmediated direct effect of the treatment on the long-term outcome and any confounding between short- and long-term outcomes. In contrast, our (ref) requires the potential short-term outcomes $S_2(a)$ to block the dependence between the potential outcomes $S_1(a)$ and $S_3(a), Y(a)$. This puts no restrictions on the treatment effect on the long-term outcome or the confounding between short- and long-term outcomes. See (ref) for a diagram illustration that compares our assumptions with the surrogacy assumption in athey2019surrogate. Moreover, previous work usually view multiple short-term outcomes as a single vector without any internal structure athey2019surrogate,athey2020combining,kallus2020role. In contrast, we introduce a sequential internal structure among the surrogates and the long-term outcome ((ref)) to address the challenge of persistent confounding, as we will demonstrate in the next section. }
We further assume that short-term outcomes $\prns{S_{1}, S_{3}}$ are sufficiently affected by the unobserved confounders $U$, formalized in the following completeness conditions.
These completeness conditions require that the short-term outcomes $\prns{S_{1}, S_{3}}$ are strongly dependent with the unobserved confounders, and they have sufficient variability relative to the unobserved confounders $U$. Under these conditions, $\prns{S_{1}, S_{3}}$ can be viewed as strong proxy variables\footnote{Note that we do not require $S_2$ to be strong proxy variables for the unobserved confounders $U$. Instead, we only require $S_2$ to block the path between $S_1$ and $S_3$ (see (ref)), so that (ref) is plausible.} for the unobserved confounders $U$. Completeness assumptions have been used extensively in recent literature on proximal causal inference Miao2016,shi2020multiply,miao2018a,cui2020semiparametric,kallus2021causal. However, these literature require proxy variables that are not causally affected by the treatment, termed negative controls. In contrast, here both of $\prns{S_{1}, S_{3}}$ can be affected by the treatment and thus do not directly fit into this previous literature.
{While in the main text we simply consider a single set of unobserved confounders $U$ that affect everything, in (ref) we further dissect persistent confounders into groups of variables and show that some unobserved confounders can be ignored and simply excluded from $U$, relaxing some of the above assumptions.}
In this section, we establish three novel identification strategies for the average long-term treatment effect in presence of general persistent confounding.
We first introduce the concept of an outcome bridge function, which will play an important role in our first identification strategy.
According to (ref), an outcome bridge function $h_0$ gives a transformation of short-term outcomes $\prns{S_3, S_2}$, treatment $A$, and covariates $X$, such that the confounding effects of the unmeasured variables $U$ on this transformation can reproduce those on the long-term outcome $Y$. So we can expect outcome bridge functions to be useful in tackling unmeasured confounding.
In general nonparametric settings, (ref) holds as a consequence of (ref) condition (ref) and some additional technical conditions. See (ref) for details. In some special cases detailed below, we can both directly guarantee (ref) and describe the functional form of outcome bridge functions.
Note that outcome bridge functions in (ref) are defined in terms of unobserved confounders, so we cannot directly use this definition to learn outcome bridge functions from observed data. In the following lemma, we give an alternative characterization of outcome bridge functions, only in terms of distributions of observed data.
In (ref), we assume the completeness condition in (ref) condition (ref), which requires the short-term outcomes $S_1$ to be informative enough for the unobserved confounders $U$. Under this additional assumption, outcome bridge functions can be equivalently characterized by the conditional moment equation in (ref). Note that (ref) simply replaces the unobserved confounders $U$ in (ref) by the observed short-term outcomes $S_1$. The resulting conditional moment equation only depends on observed variables.
We finally establish the identification of the average long-term treatment effect in the following theorem.
(ref) states that the average long-term treatment effect can be recovered by marginalizing any outcome bridge function (which is defined on the observational data distribution) over the experimental data distribution. This shows how observational and experimental data can be combined together to identify the long-term treatment effect.
The second identification strategy involves an alternative bridge function below.
According to (ref), a selection bridge function $q_0$ gives a transformation of short-term outcomes $\prns{S_2, S_1}$, treatment $A$, and covariates $X$, which can adjust for distributional differences between the experimental and observational data. In (ref) (ref), we prove that under (ref), the density ratio in left hand side of (ref) is almost surely finite, so (ref) is well-defined.
In general nonparametric models, the existence of a selection bridge function can be ensured by the completeness condition in (ref) condition (ref) and some additional technical conditions. See (ref) for details. This means that a selection bridge function exists when the short-term outcomes $S_1$ are sufficiently informative for the unobserved confounders $U$. We can also derive more specialized existence conditions for (ref) (see (ref)).
Again, selection bridge functions in (ref) are defined in terms of unobserved confounders. Below, we derive alternative characterizations in terms of distributions of observed variables.
In (ref), we assume the completeness condition in (ref) condition (ref), which requires the short-term outcomes $S_3$ to be informative enough for the unobserved confounders $U$. Under this additional assumption, selection bridge functions can be equivalently characterized by the conditional moment equation in (ref), which involves only observed variables. (ref) is a direct analogue to (ref), replacing $U$ in (ref) by $S_3$ in (ref). We can also equivalently express (ref) as follows
(ref) is a more convenient formulation for estimation as it does not involve any conditional density function.
(ref) states that the average long-term treatment effect can be also identified by any selection bridge function. This provides an alternative to the identification strategy based on outcome bridge functions in (ref).
In (ref), we present two different identification strategies, based on outcome bridge functions and selection bridge functions, respectively. We now combine them into a doubly robust identification strategy.
(ref) shows that (ref) identifies the average long-term treatment effect when it uses either a valid outcome bridge function or a valid selection bridge function. But it does not need both bridge functions to be valid. This is why it is called doubly robust.
In this section, we provide three different estimators for the average long-term treat effect, corresponding to the three different identification strategies in (ref) respectively. This involves combining two samples, so we assume that as $n \to \infty$, $n_E/n_O \to \lambda$ where $0 < \lambda < \infty$. This is a common assumption in the data combination literature angrist1992effect,graham2016efficient.
In order to estimate the average long-term treatment effect, we need to first estimate the outcome and/or selection bridge functions. Estimating these bridge functions amounts to solving the conditional moment equations in (ref) based on a finite sample of data{, which corresponds to an ill-posed inverse problem Carrasco2007}. A variety of estimation strategies can be used for this task, which we review in (ref) below. For now, we consider any generic bridge function estimators, which may be any from those reviewed in (ref), and discuss different ways to use these to construct the long-term treatment effect estimator.
Below, we define three different estimators for the counterfactual mean parameter $\mu(a)$, $a \in \mathcal{A}$. They all use the cross-fitting technique when constructing bridge function estimators, {so that the data used to construct the bridge function estimators are independent with the data at which the estimators are evaluated}. This technique has been widely used to accommodate complex nuisance function estimators while preserving strong asymptotic guarantees chernozhukov2019double,zheng2011cross. {Note that we need to split only the observational data and not the experimental data. This is because only the outcome bridge function is evaluated on the experimental data, and it is estimated only from observational data. The experimental and observational datasets are already independent, rendering the bridge-function estimate and the data on which it is evaluated independent without any cross-fitting.}
Based on the counterfactual mean estimators in (ref), we can construct average long-term treatment effect estimators:
{To analyze the asymptotic properties of these treatment effect estimators, we need to impose some high level conditions on the estimation errors of the bridge function estimators. Since these estimators solve ill-posed conditional moment equations, we quantify their estimation errors in terms of both weak metrics and the strong metrics, as this is a common practice in the literature chen2012estimation,DikkalaNishanth2020MEoC,bennett2023minimax. In particular, we define a projection operator $T$ and its adjoint operator $T^\star$ given by $[Th](S_2, S_1, A, X) = \Eb{h(S_3, S_2, A, X) \mid S_2, S_1, A, X, G = O}$ and $[T^\star q](S_3, S_2, A, X) = \Eb{q(S_2, S_1, A, X) \mid S_3, S_2, A, X, G = O}$. For a given outcome bridge function estimator $\hat h$ and a given selection bridge function estimator $\hat q$, we can quantify their estimation errors relative to $h$ and $q$ in terms of the weak metrics $\|T(\hat h - h)\|_{\mathcal{L}_2(\mathbb{P})}$ and $\|T^\star (\hat q - q)\|_{\mathcal{L}_2(\mathbb{P})}$ respectively. We can also quantify their estimation errors in terms of the strong metrics $\|\hat h - h\|_{\mathcal{L}_2(\mathbb{P})}$ and $\|\hat q - q\|_{\mathcal{L}_2(\mathbb{P})}$ respectively. The strong-metric errors can be much larger (even infinitely larger) than the corresponding weak-metric errors due to ill-posedness of the conditional moment equations. {See also (ref) for more discussions on the error rates. } }
{
}
{ (ref) specifies that the outcome bridge function estimator and selection bridge function estimator converge to some limits $\tilde h$ and $\tilde q$ respectively, in terms of both weak metrics and strong metrics. Note that we do not necessarily require these estimators to be consistent, i.e., we allow $\tilde h \ne h_0$ or $\tilde q \ne q_0$, as we show in the following theorem. }
(ref) shows that if the outcome bridge function estimator is consistent (i.e., $\tilde h = h_0$), then the corresponding treatment effect estimator $\hat\tau_\text{OTC}$ is consistent. Similarly, if the selection bridge function estimator is consistent (i.e., $\tilde q = q_0$), then the corresponding treatment effect estimator $\hat\tau_\text{SEL}$ is also consistent. In contrast, the estimator $\hat\tau_\text{DR}$ is more robust, in that it is consistent if either of the two bridge function estimators is consistent.
(ref) establishes the consistency of treatment effect estimators given only high level conditions on the bridge function estimators, regardless of how they are actually constructed. However, the actual ways to construct bridge function estimators generally do impact the asymptotic distributions of estimators $\hat\tau_\text{OTC}$ and $\hat\tau_\text{SEL}$. So we only focus on the asymptotic distribution of estimator $\hat\tau_\text{DR}$, which can be derived even under generic high level conditions.
(ref) shows that if both bridge function estimators are consistent (i.e., $\tilde h = h_0$ and $\tilde q = q_0$), and the product of their convergence rates {in terms of one strong-metric error and one weak-metric error} is $o(n^{-1/2})$, then the doubly robust treatment effect estimator $\hat\tau_\text{DR}$ is asymptotically normal with a closed-form asymptotic variance. {Note that the rate condition is weaker than requiring the product of two strong-metric error rates to be $o(n^{-1/2})$.} We can easily estimate this asymptotic variance by plugging estimates into all unknowns therein:
where $\hat\pi_E$ and $\hat\pi_O$ are sample frequency estimates for $\Prb{A=1\mid G=E}$ and $\Prb{A=1\mid G=O}$ respectively. Then we can accordingly construct confidence intervals.
In the following theorem, we further show that the asymptotic variance in (ref) actually attains the local semiparametric efficiency lower bound, provided that the bridge functions uniquely exist and an additional regularity condition holds.
(ref) implies that under the asserted assumptions, treatment effect estimator $\hat\tau_\text{DR}$ is asymptotically optimal, in the sense that it achieves the smallest asymptotic variance among all regular and asymptotically linear estimators van2000asymptotic.
In this section, we extend our previous identification results. {We first relax (ref) in (ref). Then in (ref) we provide an alternative identification via control functions rather than bridge functions. This can identify not only the average long term treatment effect but also the entire distribution of the counterfactual long term outcomes.}
We now extend our identification results by relaxing (ref). In particular, we relax (ref) by allowing the covariate distribution to be different in the experimental and observational data. This is an important extension because these two types of data are often collected from different environments, where the covariate distributions are likely to be different. {For example, because observational data are usually easier to collect and have larger scale than experimental data, the observational covariate distribution may be more representative of the entire population of interest, while experimental data may only correspond to a selective sub-population.} Therefore, we consider the following assumption to allow for different covariate distributions in two types of data.
Moreover, we relax (ref) by allowing the treatment assignment in the experimental data to depend on covariates $X$, instead of being completely at random. This permits us to also accommodate stratified randomized designs for the experimental data.
Below we extend the doubly robust identification in (ref), which shows that the long-term average treatment effect is identifiable under the weaker (ref).
(ref) shows that even under the weaker (ref), outcome and selection bridge functions can still be used to identify the average long-term treatment effect. This again has the doubly robust property in that it only requires one of the bridge functions to be correct rather than both. Compared to (ref), (ref) additionally incorporates the ratio $\nu(X) = \Prb{G=O\mid X}/\Prb{G=E\mid X}$ to adjust for the discrepancy in the covariate distribution of the two types of data ((ref)). It also uses the propensity score $e_a(X) = \Prb{A=a\mid X, G=E}$ to account for the dependence of treatment $A$ on covariates $X$ in the experimental data ((ref)).
In (ref), we further show that by setting $q = 0, h = h_0$ or $h = 0, q = q_0$ in (ref), we can obtain direct analogues of (ref) that involve only a single bridge function. In (ref), we prove that the estimating equation based on the doubly robust identification strategy in (ref) satisfies the Neyman orthogonality property chernozhukov2019double, and show that the resulting treatment effect estimator has appealing asymptotic properties and is amenable to inference.
In (ref), we present some additional extensions. In (ref), we extend our identification strategies to the setting where pre-treatment outcomes are available. In (ref), we show that it is possible to relax completeness conditions in (ref) so that short-term outcomes need only be rich enough to capture some of the unobserved confounders rather than all of them.
{
In previous parts, we identify the long-term treatment effect using bridge functions. In this part, we provide an alternative identification approach based on a control function. Control functions are special variables constructed from existing variables that can help correct for confounding bias by conditioning on them wooldridge2015control. Control functions are often constructed from instrumental variables blundell2001endogeneity,imbens2009identification,florens2008identification, but nagasawa2018treatment recently proposes control functions based on proxy variables under assumptions similar to those in the proximal causal inference literature (see the review in (ref)). We extend this approach to our setting of long term causal inference. This extension is not straightforward, noting that the assumptions of proximal causal inference are not exactly satisfied in our setting (see (ref)). }
{ Specifically, we will show that we can identify the long term treatment effect by using the stochastic process $\mathcal{V} \coloneqq \braces{p(s_3 \mid S_2, S_1, A, X, G = O): s_3 \in \mathcal{S}_3}$ as a control function. Here we consider identifying the expectation of any arbitrary transformation of the long term potential outcome, a more general parameter than the average effect parameter considered so far.
Besides the running (ref), (ref) also imposes the completeness condition in (ref) condition (ref) and a common support condition. This completeness condition requires $S_3$ to be sufficiently informative for the unobserved confounders $U$, after taking into account other relevant variables. The common support condition enables us to vary $A$ while holding constant the control function $\mathcal{V}$ after conditioning on $S_2, X, G = O$. It is equivalent to the overlap condition that $0 < \Prb{A = 1 \mid \mathcal{V}, S_2, X, G = O} < 1$ almost surely. This condition is possible only when $S_1$ can induce sufficient extra variations in $\mathcal{V}$, or alternatively, when $S_1$ has a large support and it is sufficiently informative for $U$ nagasawa2018treatment. Common support conditions like this are prevalent in the control function literature. See nagasawa2018treatment,imbens2009identification for more discussions and justifications. }
{ We note that the identification formula in (ref) can be used to identify not only the average effect, but also the entire distribution of the counterfactual long term outcome $Y(a)$. This can be achieved by applying (ref) to the indicator function $r(\cdot) = \indic{\cdot \le y}$ for all $y \in \mathcal{Y}$. Actually, under the condition $2$ in (ref), we can also use a selection bridge function to identify the entire distribution of $Y(a)$ (see (ref) in (ref)). The condition $2$ in (ref) (i.e., the existence of a selection bridge function and the completeness condition in (ref) condition (ref)) has similar qualitative implications as the completeness condition and common support condition in (ref): they require both $S_1$ and $S_3$ to be sufficiently strong proxies for the unobserved confounders $U$. However, these two set of conditions are in general not directly comparable. See nagasawa2018treatment for more discussions on the connections between conditions in the control function approach and conditions in the bridge function approach. }
{ Finally, we remark that estimating the target parameter based on the identification formula in (ref) may be challenging. On the one hand, the common support condition may fail in practical applications chernozhukov2020semiparametric. We may follow nagasawa2018treatment,newey2021control and impose additional (semi)-parametric restrictions on the function $\Eb{r(Y) \mid \mathcal{V}, S_2, A = a,X, G = O}$. These assumptions can allow for model extrapolation across different values of $\mathcal{V}$, thereby relaxing the common support condition. Another possibility is to derive partial identification bounds when the common support function is violated. On the other hand, the control function approach requires controlling for an infinitely dimensional stochastic process $\mathcal{V}$, which cannot be implemented exactly in practice. nagasawa2018treatment proposes a dimension reduction technique for the estimation of causal effects in the proximal causal inference setting. Similar techniques may be also useful in our setting. We leave the development of practical estimation methods based on the control function for the future study. }
In this section, we illustrate the performance of our proposed estimators using data for the Greater Avenues to Independence (GAIN) job training program in California. GAIN is a job assistance program from the late 1980s designed to help low-income population. To evaluate its real impacts on employment, MDRC conducted a randomized experiment in 6 California counties. {We use the dataset analyzed in athey2019surrogate and focus on two counties: San Diego and Riverside.} For each experiment participant, the dataset records a binary treatment variable indicating enrollment in the GAIN program, quarterly job employment information after treatment assignment, and other covariate information (e.g., age, education, marriage). See hotz2006evaluating,athey2019surrogate for more information about the GAIN program.
In our numerical studies, we consider the San Diego data as our experimental dataset $\mathcal{D}_E$, and construct an observational dataset $\mathcal{D}_O$ based on the Riverside data via a biased subsampling described below. Then we apply our proposed estimators $\hat\tau_{\text{OTC}}$, $\hat\tau_{\text{SEL}}$, and $\hat\tau_{\text{DR}}$ to estimate the average treatment effect of the GAIN program on the long-term employment. Since the original data are from randomized experiments, we consider the average treatment effect thereof as the “ground truth” and use it to evaluate the errors of different estimators.
For the experimental dataset, we directly use data from San Diego, which include $n^{(1)}_{E} = 6978$ people in the treatment group and $n^{(0)}_{E} = 1154$ people in the control group. For the observational dataset, we subsample from the Riverside data, which originally include $N_{1} = 4405$ people in the treatment group and $N_{0} = 1040$ people in the control group.
We randomly subsample units from the Riverside data according to a sampling probability function $\pi(A, U) \in (0, 1)$, where $A \in \braces{0, 1}$ is the treatment assignment and $U \in \braces{0, 1, 2, 3}$ is the highest education level (“$0$” means below 9-th grade, “$1$” means $9$-th to $11$-th grade, “$2$” means $12$-th grade, and “$3$” means above $12$-th grade). This creates dependence between the treatment assignment and the education level for the units subsampled into $\mathcal{D}_O$. We choose education because it is quite likely to have persistent effects on participants' potential employment in all quarters following the treatment. Then we drop the education level data from $\mathcal{D}_O$ (and also $\mathcal{D}_E$). As a result, the education level becomes a plausible persistent unmeasured confounder in $\mathcal{D}_O$.
To quantify the strength of unmeasured confounding in $\mathcal{D}_O$, we index the sampling probability function $\pi\prns{A, U}$ by a non-negative parameter $\eta$. We set the sampling probability for control units as $\pi(0, U) = \max \{1 - {\eta U}/{3}, 0.2\}$ and the sampling probability for treated units as $\pi(1, U)$ that satisfies the following equation: \[ \frac{N_0}{N_0 + N_1} \pi(0, U) + \frac{N_1}{N_0 + N_1} \pi(1, U) = \frac{N_1}{N_1 + N_0} + \frac{N_0}{N_1 + N_0} \max\{1 - \eta, 0.2\}. \] It is easy to show that as $\eta$ grows, the discrepancy between $\pi(0, U)$ and $\pi(1, U)$ also grows. This implies stronger dependence between $U$ and $A$ in the observational dataset $\mathcal{D}_O$, thus stronger unmeasured confounding. In (ref) (ref), we prove that with this choice of $\pi(1, U)$, the subsampling procedure does not shift the distribution of education level $U$, so that it does not violate (ref). Moreover, the subsampling procedure does not influence (ref) since the sampling probability function only depends on $A, U$.
In our numerical studies, we consider the short-term otucomes $(S_1, S_2, S_3)$ as the employment status in the first two quarters, in the third and fourth quarters, and in the fifth and sixth quarters after the treatment respectively. We consider the long-term outcome $Y$ as the $20$-th quarter employment. These are all binary variables indicating whether the participants are employed in the corresponding quarters after the treatment assignments.
(ref) reports the performance of different estimators over 1000 replications\footnote{{When $\eta = 0$, the sampling probabilities satisfy $\pi(0, U) = \pi(1, U) = 1$, so there is no subsampling and all replications are identical.}} of the data subsampling. Each replication results in a different observational dataset $\mathcal{D}_{O}$ with different number of treated units $n_O^{(1)} < N_1$ and different number of control units $n_O^{(0)} < N_0$. For evaluation we consider two criterions over the $1000$ replications: Mean Absolute Error (MAE) and Median of Abolute Errors (MedAE).
In (ref), we compare the performance of our proposed estimators $\hat\tau_{\text{OTC}}$, $\hat\tau_{\text{SEL}}$ and $\hat\tau_{\text{DR}}$ in (ref) with two benchmarks: the naive difference-in-mean estimator that uses only the observational dataset and the imputation estimator proposed in Section 4.1 of athey2020combining, which uses both datasets and information of all short-term outcomes $S=\prns{S_1, S_2, S_3}$. The naive estimator completely ignores confounding, and the estimator in athey2020combining can only account for short-term confounding but not persistent confounding. To evaluate the performance of our estimators and athey2020combining, we consider the percentage decrease in either of our error criteria relative to the naive difference-in-mean estimator. A positive value corresponds to improvement over the naive estimator, and a larger value indicates better performance. A negative value means worse error than the naive estimator.
In our estimators and the imputation estimator in athey2020combining, we need to first estimate some nuisance functions. We specify the outcome bridge function in our estimators and the imputation function in athey2020combining to be linear functions, and specify the selection bridge function in our estimators to be of the form $q(s_2, s_1, a, x) = \exp(\beta^\top_{2, a} s_2 + \beta_{1, a}^\top s_1 + \beta_{0, a}^\top x + \gamma_a)$. Since these are all simple parametric functions, we do not need the cross-fitting technique described in (ref), but instead use the same data for nuisance estimation and the final plug-in estimation. To estimate the bridge functions, we employ the generalized method of moment (GMM) approach in cui2020semiparametric. We consider a standard GMM apporach and the approach with additional ridge regularization, i.e., regularizing the $L_2$ norms of bridge function coefficients in the GMM objectives, as suggested by imbens2021controlling. When we estimate the bridge function corresponding to the treatment level $a\in\braces{0, 1}$, we set the regularization tuning parameter as $\lambda = \lambda_0 (n^{(a)}_O)^{-1}$ for $\lambda_0 \in\{ 0, 0.33, 0.67, 1\}$ (here $\lambda_0 = 0$ corresponds to no regularization). For the imputation function of athey2020combining, we implement it using either ordinary least squares or cross-validated ridge regression, for which we use the default options in the R package glmnet glmnet.
From (ref), we observe that with $\lambda_0 \neq 0$, the performance of our proposed estimators $\hat\tau_{\text{OTC}}, \hat\tau_{\text{SEL}}, \hat\tau_{\text{DR}}$ is stable. They consistently outperform the benchmarks, in terms of both criteria. In particular, the doubly robust estimator $\hat\tau_{\text{DR}}$ performs the best, reducing the estimation errors of benchmark methods by large margins. Notably, although the benchmark estimator proposed by athey2020combining improves upon the naive estimator, it is always outperformed by our proposed estimators. This may be due to the fact that the estimator in athey2020combining cannot handle persistent confounding. We also observe that as the unmeasured confounding becomes stronger (i.e., as $\eta$ grows), all estimators have higher estimation errors, especially the naive estimator.
We observe that the MAE of our estimators when not using regularization is sometimes worse than the estimator of athey2020combining and even the naive estimator. This is because unregularized estimators can be unstable and MAE is sensitive to outlier estimates. Indeed, estimating bridge functions requires solving inverse problems defined by conditional moment equations, which can be intrinsically difficult. This problem is common in proximal causal inference, and regularization has been shown to be sometimes key for valid inference imbens2021controlling. Nevertheless, the MedAE, which is robust to outliers, for our estimators is still lower than the benchmarks. This shows that our proposed estimators, regularized or not, all effectively address the confounding bias. {In the supplementary material (ref), we heuristically probe the plausibility of (ref) according to the characterization of bridge functions in a discrete setting (see (ref)). Moreover, we also report the performance of different estimators by varying the number of quarters used for surrogate construction. Our result shows that our approach is consistently more accurate than the approach in athey2020combining.}
{In (ref), we focus on parametric estimation of bridge functions. In this part, we use a simulation study to further demonstrate the performance of our approach when bridge functions are nonlinear and estimated by more flexible neural networks.}
{ Specifically, for both the experimental and observational data, we first generate random vectors $\tilde X$ and $U$ from the multivariate normal distribution with mean zero and covariance matrix $0.5 \mathbf{I}$, where $\mathbf{I}$ is an identity matrix with suitable size. We fix the dimension of $U$ as $5$ and vary the dimension of $\tilde{X}$ over $\{5, 10, 15, 20\}$. We further generate $Y(a) \in \R{}, \tilde S_1(a) \in \R{5}, \tilde S_2(a) \in \R{}, \tilde S_3(a) \in \R{5}$ according to the following process:
where $\tau_y, (\tau_j, \alpha_y, \beta_y, \gamma_y), (\alpha_j, \beta_j, \gamma_j)$ are scalers, vectors, and matrices of conformable sizes, and $\epsilon_y, \epsilon_j$ are independent mean-zero Gaussian terms with variance $0.5$. We generate the entries in $\tau_y, (\tau_j, \alpha_y, \beta_y, \gamma_y), (\alpha_j, \beta_j, \gamma_j)$ by first drawing numbers from the uniform distribution over the $[0, 1]$ interval and then rescaling them so that the $\ell_2$-norms of the vectors $(\tau_j, \alpha_y, \beta_y, \gamma_y)$ and the columns of $(\alpha_j, \beta_j, \gamma_j)$ are all equal to $0.5$. Moreover, we draw the treatment indicator $A$ according to $\mathbb{P}({A = 1 \mid \tilde{X}, U, G = E}) = \frac{1}{2}$ and $\mathbb{P}({A = 1 \mid \tilde{X}, U, G = O}) = ({1 + \exp(\kappa_1^\top \tilde{X} + \kappa_2^\top U)})^{-1}$, where the coefficients $\kappa_1$ and $\kappa_2$ are similarly generated by sampling and rescaling. According to (ref) and (ref), the outcome and selection bridge functions exist under certain rank conditions. Moreover, the outcome bridge function is linear in $\tilde S_3, \tilde S_2, \tilde X, A$ and the selection bridge function is an exponential transformation of a linear function of $\tilde S_2, \tilde S_1, \tilde X, A$. To introduce nonlinear bridge functions, we apply a nonlinear transformation $g(\cdot) = \op{sign}(\cdot)\abs{\cdot}^q$ for $q \in \{1, 1.5, 2\}$ to each element of $\tilde X, \tilde S_1, \tilde S_2, \tilde S_3$, leading to $X, S_1, S_2, S_3$ respectively. This is an invertible transformation that ensures a one-to-one correspondence between the original variables and transformed variables. With these transformations, the bridge functions with respect to the transformed variables $X, S_1, S_2, S_3$ are linear when $q = 1$ and nonlinear when $q = 1.5$ or $2$. }
{We repeat generating data according to the process above for 200 times. In each replicate, we draw new values for all the model parameters and generate observational data and experimental data accordingly with equal sizes $n_O = n_E = 2000$. We apply our proposed doubly robust estimator and associated confidence intervals to the datasets. We estimate the bridge functions in two ways. One way is to use the minimax learning estimators in kallus2021causal,DikkalaNishanth2020MEoC. Specifically, a minimax bridge function estimator is obtained as the solution to a minimax optimization problem derived from the corresponding conditional moment equation. In our study, we follow kallus2021causal and specify the outer minimization function class (i.e., the class used to model the bridge function) as a neural network class and the inner maximization function class (i.e., the class used to guarantee the equivalence between the minimax optimization formulation and the conditional moment equation formulation) as a Reproducing Kernel Hilbert Space (RKHS). For implementation details, we refer the readers to (ref). The other way is to use parametric estimators for the bridge functions, where the specifications are identical to those in (ref). These model specifications are correct when $q = 1$ but wrong when $q \in \{1.5, 2\}$. In both approaches, we also use a ridge regularization with $\lambda = 1 / n_O^{(a)}$, i.e., same as the “1” column in (ref). }
{ Table (ref) reports the performance of our estimator and confidence intervals based on two kinds of bridge estimators, over the $200$ replicates. When the covariate dimension is relatively low (i.e., $\dim(X) = 5, 10$ or $15$), the empirical coverage of the minimax based approach is close to the $95\%$ nominal level in most of the specifications. For the higher dimensional regime $\dim(X) = 20$, the empirical coverage is slightly worse, which could be due to the curse of dimensionality, especially for the inner maximization over RKHS. }
{ When $q = 1$, the average bias of the parametric model based approach is consistently smaller than the minimax based approach. This is expected as the parametric model is correctly specified in this case. In contrast, in the nonlinear settings with $q = 1.5$ and $2$, the parametric models are misspecified, so the RMSE and the average bias of the parametric based approach are overall worse than the minimax based approach, especially for the more nonlinear scenario $q = 2$. This shows the benefit of using flexible function classes to model complex bridge functions. }
{ Interestingly, when $q = 1.5, 2$, the confidence intervals based on the parametric bridge function estimators do not under-cover the truth, even though the corresponding point estimators have larger bias and RMSE. Actually, they tend to over-cover the truth in many specifications. This is perhaps due to the fact that the asymptotic variance tends to be over-estimated, leading to excessively conservative confidence interval lengths. As shown in (ref), the average confidence interval length produced by the parametric based approach is much larger than the minimax based approach; sometimes, it can even be 4 times larger. Consequently, even with higher average bias, the parametric based approach is still able to get high empirical coverage.} {In (ref), we include additional results when we increase the dimension of $S_1, S_2, U$ from $5$ to $10$. The estimators and confidence interval coverage perform slightly worse in the higher dimensional setting.}
{
}
In this paper, we consider combining experimental and observational data for long-term causal inference. We are particularly interested in the challenge of persistent confounding, i.e., the presence of unobserved confounders that affect both the short-term and long-term outcomes. To overcome this challenge, we leverage the sequential structure of multiple short-term outcomes and use part of them as proxy variables for the unobserved confounders. We propose several novel identification strategies for the average long-term treatment effect. Based on them, we design flexible treatment effect estimators and inference methods, for which we provide asymptotic guarantees. Our results show that the long-term treatment effect can be identified and estimated under much more general conditions than before.
Beyond these specific results, our work reveals an interesting role for the structure of short-term outcomes in long-term causal inference. To the best of our knowledge, the structure of repeated outcome measurements is largely unexplored in the long-term causal inference literature. We hope that our work will inspire other researchers to study other plausible structures for short-term outcomes and benefits these can have for long-term causal inference.
The authors thank the associate editor and two anonymous reviewers for their insights and suggestions, which have led to significant improvement of this paper. \\
Guido Imbens thanks the Office of Naval Research for support under grant numbers N00014-17-1-2131 and N00014-19-1-2468 and Amazon for a gift. Nathan Kallus acknowledges that this material is based upon work supported by the National Science Foundation under Grant No. 1846210. Xiaojie Mao is supported in part by National Natural Science Foundation of China (grant numbers 72201150, 72322001, and 72293561) and National Key R&D Program of China (grant number 2022ZD0116700). Yuhao Wang is supported in part by National Key R & D Program of China (2022YFA1008100), the 2030 Innovation Megaprojects of China (Programme on New Generation Artificial Intelligence) Grant No. 2021AAA0150000, and the grant of National Natural Science Foundation of China (NSFC) 12201341.
The California GAIN dataset analyzed in (ref) contains sensitive individual data and cannot be shared publicly. It may be shared upon request. The data analyzed in (ref) are simulated according to the processes described in that section. The code script used to generate the simulated data is available at \url{https://github.com/CausalML/LongTermCausalInference}.