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Proximal Difference-in-Differences for Causal Learning under Confounding and Outcome Drift

Abstract

Estimating long-term treatment effects is essential in regulatory and healthcare decision-making, yet the limited follow-up duration of randomized controlled trials (RCTs) poses a significant challenge. Open-label extension studies attempt to capture additional information for treated subjects, but there is often significant systematic censoring and selection bias due to placebo crossover. While supplementing RCTs with real-world evidence is a common strategy, existing methods often rely on restrictive exchangeability assumptions that fail under latent confounding. We propose a novel proximal framework to integrate real-world evidence into an RCT with an open-label extension to estimate the long-term continued-control trajectory. Our approach successfully identifies long-term effects even in the presence of time-varying latent confounding effects and inter-study outcome drift. We provide a doubly robust locally efficient estimator that provides further resilience to model misspecification. Empirical results demonstrate that our framework maintains validity in complex data-generating processes where standard approaches may be biased.

Introduction

Background

Estimating long-term treatment effects is critical across scientific and industrial applications. In pharmaceutical sciences, sustained efficacy and safety profiles are vital for regulatory and healthcare decision-making. In the technology sector, online A/B tests excel at measuring immediate user responses but often fail to capture long-term strategic goals like customer lifetime value [13]. In both domains, running experiments over extended horizons is typically precluded by cost, attrition, and ethical constraints. In clinical trials specifically, open-label extension (OLE) studies are often added to randomized controlled trials (RCTs) to capture additional patient information after the double-blinded period of the trial. However, after the randomized double-blinded phase of an RCT, OLEs permit control group participants to cross over to the active therapy. While providing long-term longitudinal data for the treated arm, this mechanism censors the long-term counterfactual outcomes of the control arm. As a result, stakeholders must routinely extrapolate from short-term data, highlighting the necessity for robust methodological alternatives to estimate long-term counterfactuals.

To address this, emerging strategies leverage auxiliary observational data such as electronic health records in medicine or historical user logs in tech. These approaches, including propensity score integration [20, 32] and synthetic control methods [2], aim to bridge the gap between short-term experiments and long-term outcomes. However, these methods typically hinge on the strong, untestable assumption of no unmeasured confounding. The recent development of proximal causal inference offers a promising alternative, utilizing proxy variables to enable unbiased estimation even in the presence of unmeasured confounding [15, 16, 22].

Despite this progress, significant challenges remain. A primary limitation is the assumption of data homogeneity or no outcome drift, which implies that counterfactual trends align between the randomized and external populations. This is rarely satisfied in practice: clinical observational cohorts often differ from patients enrolled in RCTs, while in tech, historical logs suffer from non-stationarity due to platform evolution or shifting user behavior over time. While some methods account for outcome drift, they often impose restrictive assumptions such as time-invariant confounding effects [6] that are violated by common data-generating processes, or they focus on the observational population rather than the primary experimental population [16].

Related Work and Limitations

For clarity of exposition, we adopt the nomenclature of clinical research, denoting the experimental cohort with extended follow-up of the treated arm as the Randomized Controlled Trial (RCT) and the supplementary longer-horizon observational data as the External Control (EC). However, this formulation is directly applicable to industrial applications; for instance, in large-scale online experimentation, the “RCT” corresponds to a controlled A/B test, while the “EC” represents historical user logs leveraged to forecast long-term value.

While most approaches address some of the practical challenges, they typically assume a linear outcome-generating model or homogeneity between the RCT and EC. Even for methods that allow outcome drift, it is a common restriction to posit the absence of time-varying latent effects. Table 1 summarizes these requirements across the literature.

MethodologyNUCLinearityNo outcome driftTarget population
Abadie et al. [2]-✓✓RCT
Athey et al. [7]✓-✓RCT
Arkhangelsky et al. [6]-✓-RCT
Athey et al. [8]-✓-RCT
Imbens et al. [15]-✓✓RCT
Ghassami et al. [14]✓-✓EC
Xiong and Pelger [34]-✓✓RCT
Zhou et al. [37]✓--RCT
Imbens et al. [16]---EC

Table 1. Select methods and required assumptions. “NUC” stands for no unmeasured confounding between the study cohort and the outcome of interest. “✓” means the assumption is strictly required; “-” means the assumption is not required.

Synthetic Control Synthetic control constructs a weighted combination of external control subjects to balance baseline characteristics and post-baseline outcome trajectories with the RCT control arm through the end of the double-blind period. Standard formulations [1, 2] rely on mean exchangeability, which ignores outcome drift. While extensions [6, 24] incorporate unit-level effects, from an asymptotic perspective, synthetic control methods require both the trial period and the EC sample size to increase indefinitely, a requirement that is restrictive in finite-sample clinical applications [15].

Difference-in-Differences Difference-in-differences (DID) relies on the parallel trends assumption to account for group-level outcome drift between RCT control and EC [14, 37]. However, the parallel trends assumption requires the influence of latent factors on the outcome to be time-invariant. This restriction precludes the modeling of dynamic, time-varying latent factors common in longitudinal clinical data.

Low-Rank Approximation Matrix completion and low-rank approximation methods [8, 34] treat long-term estimation as a data imputation problem. These approaches are typically constrained by rigid functional forms, requiring a linear relationship [4, 21], which limits their utility in complex, non-linear environments.

Surrogates and Instrumental Variable Methods Surrogate methods [7] and "bespoke" instrumental variable approaches [14, 26] identify long-term effects by transferring short-term results through mediators. However, they generally assume no unmeasured confounding between the study enrollment and the outcome, which is frequently violated when integrating external evidence. The method of Ye et al. [35] requires independence between the instrument and the untreated outcome trend conditional on observed covariates, the absence of an unmeasured common modifier of the instrument’s effect on exposure and the exposure’s effect on the outcome, and a CATE that is stable over time. These requirements limit applicability when treatment efficacy evolves over the study period.

Proximal Causal Inference Proximal causal methods use proxy variables to adjust for unmeasured confounding and identify treatment effects. Existing proximal frameworks [12, 15] often require complete data and assume latent ignorability of the study cohort. While Imbens et al. [16] relaxes latent ignorability of the study enrollment for long-term outcomes, their main identification results require three temporally ordered groups of short-term outcomes and impose external validity of the short-term potential outcomes and latent confounders.

Contributions

Our contribution centers on developing a methodology for estimating the long-term treatment effect on the experimental population via external data integration. This framework accommodates study-specific outcome levels and time-varying latent confounding effects and permits a proxy variable to be measured only in the EC. Unlike a typical framework that targets the outcome directly, our approach targets the trial-to-extension trend, i.e., the change of outcome from the trial period to the extension period. This allows us to identify long-term effects even when base-level outcomes differ significantly across studies.

  • First, we provide a novel framework for integrating data from possibly heterogeneous RCT and EC data (§ 2). This framework accommodates latent confounding without imposing parametric models, allowing flexible machine learning methods.

  • Second, we derive a nonparametric proximal identification strategy for the long-term counterfactual trajectory of the RCT control population (§ 3). This initial identification motivates the proximal outcome regression and the proximal inverse probability weighting estimator.

  • Third, we derive the proximal doubly robust estimator that is consistent for the counterfactual long-term outcome mean even when one of the involved nuisance functions is misspecified (Section 4). We derive the efficient influence function of the estimand and further show that the PDR estimator is locally efficient when all nuisance models are correctly specified. We extend these results for settings when the outcome measurements are partially unobserved (Appendix § 15).

  • Finally, the finite-sample properties and robustness of the proposed estimators are rigorously evaluated through a series of simulation studies (Section 5). These simulations examine performance across varying degrees of model misspecification to empirically validate the theoretical consistency and efficiency gains. We further demonstrate the practical utility of the proposed estimators by applying them to a plasmode simulation, a semi-synthetic study combining real-data features with modeled outcomes, for an Alzheimer’s disease

trial, showcasing how this methodology can facilitate reliable long-term effect estimation in complex neurodegenerative disease research.

Statistical Framework

Problem Statement

We integrate an RCT with OLE (S=1S = 1) and EC data (S=0S = 0), with combined sample size nn. Let XX denote baseline covariates, UU an unmeasured confounder, and Aˉ=(Apre,A0)\bar{A} = (A_{\mathrm{pre}}, A_0) the treatment assignments during the trial (t=pret = \mathrm{pre}) and extension (t=0t = 0) periods. We assume randomized assignment of ApreA_{\mathrm{pre}} in the RCT. We observe outcomes YtY_t for t∈{pre,0}t \in\{\mathrm{pre}, 0\}. The RCT provides a control arm only during the trial, while the EC extends into the extension period (Figure 1). This standard two-time-point framework [15, 37] accommodates multiple periods by aggregating trial-period and extension-period observations into composite outcomes [15, 6].

RCT and EC study design

Figure 1. RCT and EC study design: the RCT control arm crosses over to treatment during the OLE, while the EC remains untreated.

Following the convention of Zhou et al. [37], we define the counterfactual outcomes: Y0s,(apre,a0)Y_0^{s,(a_{\mathrm{pre},}a_0)} as the extension period outcome if the subject originated from ss and received (apre,a0)(a_{\mathrm{pre}}, a_0), and Ypres,(apre)Y_{\mathrm{pre}}^{s,(a_{\mathrm{pre}})} as the trial period outcome if the subject originated from ss and received (apre)(a_{\mathrm{pre}}). Note that Ypres,(apre)=Ypres,(apre,a0)Y_{\mathrm{pre}}^{s,(a_{\mathrm{pre}})} = Y_{\mathrm{pre}}^{s,(a_{\mathrm{pre}},a_0)} for all a0a_0, since the trial period outcome is not influenced by the treatment during the extension period. We posit the Stable Unit Treatment Value Assumption (SUTVA), asserting that the observed YtY_t is consistent with the assigned treatment and study cohort: YpreS,(Apre)=YpreY_{\mathrm{pre}}^{S,(A_{\mathrm{pre}})} = Y_{\mathrm{pre}} and Y0S,(Apre,A0)=Y0Y_0^{S,(A_{\mathrm{pre}},A_0)} = Y_0. This is a standard assumption in causal inference [5] and implies no interference or spillover effect between units, and the implementation of the treatment and study participation remains consistent across all units.

Our primary objective is to estimate the long-term average treatment effect (LTATE) among the experimental population at the extension period t=0t = 0. This is formally defined as LTATE =E[Y01,(1,1)−Y01,(0,0)∣S=1]= \mathbb{E}[Y_0^{1,(1,1)} - Y_0^{1,(0,0)} \mid S = 1]. We only observe specific counterfactuals from each study cohort; for subjects in the RCT, we observe Y01,(1,1)Y_0^{1,(1,1)} (treatment arm) and Y01,(0,1)Y_0^{1,(0,1)} (control arm, where crossover occurs); for subjects in the EC, we observe Y00,(0,0)Y_0^{0,(0,0)} (unexposed to the treatment).

Since the counterfactual mean E[Y01,(1,1)∣S=1]=E[Y0∣S=1,Aˉ=(1,1)]\mathbb{E}[Y_0^{1,(1,1)} \mid S = 1] = \mathbb{E}[Y_0 \mid S = 1, \bar{A} = (1,1)] can be directly estimated from the observed data, the primary source of bias and uncertainty in estimating LTATE is the counterfactual mean τ:=E[Y01,(0,0)∣S=1]\tau:= \mathbb{E}[Y_0^{1,(0,0)} \mid S = 1]. Consequently, the remainder of this article focuses on the methodology for identifying and estimating τ\tau.

Conditional Parallel Trend Given Latent Factors

A common assumption in data integration is conditional exchangeability, which posits that the untreated counterfactual mean is the same regardless of the study cohort, conditional on confounders: E[Y01,(0,0)∣X,U]=E[Y00,(0,0)∣X,U]\mathbb{E}[Y_0^{1,(0,0)} \mid X,U] = \mathbb{E}[Y_0^{0,(0,0)} \mid X,U] [2, 15]. However, this is often violated in practice due to outcome drift. Such heterogeneity arises from differences between the data, including placebo effects or study bias [3, 28], which result in distinct trends even for individuals with identical covariates.

The existing parallel trends assumption is commonly adopted to handle such heterogeneity. The additive equiconfounding formulation of parallel trends assumes [30, 37]: for s=0,1s = 0, 1,

E[Y0s,(0,0)−Ypres,(0)∣X,U]=E[Y0s,(0,0)−Ypres,(0)∣X],(1)\mathbb{E}[Y_{0}^{s,(0,0)} - Y_{\mathrm{pre}}^{s,(0)} \mid X,U] = \mathbb{E}[Y_{0}^{s,(0,0)} - Y_{\mathrm{pre}}^{s,(0)} \mid X], \tag*{(1)}
E[Y01,(0,0)−Ypre1,(0)∣X]=E[Y00,(0,0)−Ypre0,(0)∣X].(2)\mathbb{E}[Y_{0}^{1,(0,0)} - Y_{\mathrm{pre}}^{1,(0)} \mid X] = \mathbb{E}[Y_{0}^{0,(0,0)} - Y_{\mathrm{pre}}^{0,(0)} \mid X]. \tag*{(2)}

(1) requires the conditional mean untreated trend to be independent of UU after conditioning on XX. It therefore excludes latent effects, including XX–UU interactions, that change between the trial and extension periods. This limits the model’s applicability, as observed covariates may interact with latent factors in ways that differentially affect outcomes across the trial and extension periods. This constraint specifically invalidates the commonly employed linear factor model, μt(X,U)=Xβt+Uγt\mu_t(X,U) = X\beta_t + U\gamma_t, as it necessitates that the loading γt\gamma_t be constant over time. We address this limitation by introducing a relaxation, Conditional Parallel Trend given Latent factors (CPTL), which allows time-varying latent effects as well as UU–XX interactions.

Assumption 2.1 (Conditional parallel trend given latent factors). The conditional bias given XX and UU remains the same across time. That is, E[Yt1,(0,0)−Yt0,(0,0)∣X,U]≡b(X,U)\mathbb{E}[Y_t^{1,(0,0)} - Y_t^{0,(0,0)} \mid X,U] \equiv b(X,U) for t∈{0,pre}t \in\{0,\mathrm{pre}\}.

CPTL relaxes standard assumptions by requiring trends to be parallel only after accounting for both observed and latent factors. The distinction is the level at which untreated trends are assumed transferable. Assumption 2.1 permits the common conditional trend to depend on UU and on interactions between XX and UU through the unrestricted function μt(X,U)\mu_t(X,U) in the model above. Thus, it relaxes the combination of (1) and (2). Different latent-factor distributions across cohorts can produce different trends given XX alone even when the trends agree given (X,U)(X,U), which allows the model to dispense with the restrictive condition in (1). Thus, while preserving the core benefits of the parallel trend, CPTL accommodates more realistic data-generating processes, such as:

Yts,(0,0)=μt(X,U)+s⋅b(X,U)+εt,s,Y_t^{s,(0,0)} = \mu_t(X,U) + s \cdot b(X,U) + \varepsilon_{t,s},

where the error term εt,s\varepsilon_{t,s} is exogenous. Notably, if b(X,U)=0b(X,U) = 0, this framework reduces to strict exchangeability. Furthermore, this structure generalizes two prominent models in panel data analysis: it simplifies to a linear factor model when the underlying functions are linear, and it reduces to an additive equiconfounding model ((1) and (2)) when the underlying functions are independent of UU.

Our framework further accommodates complex dynamics beyond existing methods. In neurodegenerative disease research, UU may represent unobserved environmental or socioeconomic stressors that affect the rate of functional decline. CPTL is plausible when patients with the same observed clinical state and latent stressors have the same untreated progression rate in both cohorts, even if their initial outcome levels differ. For cognitive outcomes, XX may include education and UU latent intellectual capability; their interaction may affect cognitive reserve and subsequent decline. In digital platforms, observed demographics may modify the effect of latent seasonality or user intent on engagement trends. In each example, our framework permits these effects to change across phases, provided the conditional untreated trend remains common across study cohorts.

Falsification test Although the CPTL assumption is fundamentally untestable, we propose a falsification test based on a necessary condition that can be employed when multiple trial-period outcomes are available. Further details are provided in Appendix H.

Nonparametric Proximal Identification

Proximal causal inference provides a technique to remove the unmeasured confounding effect on the outcome by a set of proxy variables [22, 31]. Suppose a trend-confounding proxy WW and a source-confounding proxy ZZ exist that satisfy the following conditions.

Assumption 3.1 Y0−Ypre⊥ ⁣ ⁣ ⁣⊥Z∣U,X,S=0Y_0 - Y_{\mathrm{pre}} \perp\!\!\!\perp Z \mid U,X,S=0 and W⊥ ⁣ ⁣ ⁣⊥(S,Z)∣U,X,Apre=0W \perp\!\!\!\perp(S,Z) \mid U,X,A_{\mathrm{pre}}=0.

These conditions concern Y0−YpreY_0 - Y_{\mathrm{pre}} rather than each outcome level, allowing study-specific level differences under CPTL. Figure 2 illustrates these conditions.

Figure 2. Causal directed acyclic graphs illustrating a possible proxy structure. (a) All variables are shown. (b) Variables are shown conditional on Aˉ=(0,0)\bar{A} = (0, 0). Dashed edges represent associations that may or may not exist. CPTL requires equal conditional untreated counterfactual trends across studies given X,UX, U.

Guidelines for proxy selection In clinical research, we advise selecting WW from baseline comorbidities, secondary clinical measurements, or physiological biomarkers. These variables are typically recorded during the trial but are assumed to be conditionally independent of the therapy given other baseline factors. Conversely, we recommend choosing ZZ from instruments or negative control variables that influence trial participation without directly affecting the outcome trend. Examples include the spatial proximity to health providers or historical referral rates at the clinical site. We also suggest that researchers consult specific trial inclusion and exclusion criteria to identify additional candidate proxies suited to their particular study context.

In the domain of online experimentation and A/B testing, we advise choosing WW from historical engagement metrics with unrelated platform features or baseline activity levels recorded prior to the experiment. Meanwhile, ZZ can be chosen from exogenous technical factors such as network latency, the specific timing of exposure to a promotional banner, or engagement rates observed in historical, unrelated tests. These factors are often predictive of selection into a specific user segment or experiment but do not have a direct causal path to the long-term metric of interest.

Assumption 3.2 (Latent ignorability). Yts,(0,0)⊥ ⁣ ⁣ ⁣⊥S∣(X,U)Y_{t}^{s,(0,0)} \perp\!\!\!\perp S \mid(X, U) for t=pre,0t = \mathrm{pre}, 0, s=0,1s = 0, 1.

Assumption 3.3 (Positivity). P(S=1,Apre=0∣X,U)>0\mathbb{P}(S = 1, A_{\mathrm{pre}} = 0 \mid X, U) > 0, P(S=0∣X,U)>0\mathbb{P}(S = 0 \mid X, U) > 0 almost surely over the support of (X,U)(X, U) in the RCT population.

Assumption 3.2 states that the counterfactual outcome is independent of the study membership, given all confounders. This allows confounding to be explained by both measured XX and unmeasured UU, thus allowing the existence of unmeasured confounders in the analysis. Assumption 3.3 states that for each subject, the probability that a subject belongs to trial control or external control must be positive. This requires overlap between the studies within finer strata of (X,U)(X, U).

We define a trend-confounding bridge function dd and a source-confounding bridge function qq to connect unmeasured confounding to the observed variables without explicitly modeling UU. Here, “source” refers to the study cohorts. In the absence of unmeasured confounding and proxies, these simplify to the outcome regression (OR) model or inverse probability weighting (IPW).

Definition 3.4 (Bridge functions). d(w,x)d(w, x) and q(z,x)q(z, x) are the solutions of the integral equations:

E[Y0−Ypre−d(W,X)∣Z,X,S=0]=0,(3)\mathbb{E}[Y_0 - Y_{\mathrm{pre}} - d(W, X) \mid Z, X, S = 0] = 0, \tag*{(3)}
E[(1−S)q(Z,X)−S(1−Apre)∣W,X]=0.(4)\mathbb{E}[(1 - S)q(Z, X) - S(1 - A_{\mathrm{pre}}) \mid W, X] = 0. \tag*{(4)}

Existing methods do not differentiate outcomes into transferable and non-transferable components. Our approach decouples outcomes into a non-transferable base outcome mean and a transferred mean trend. This specific decomposition, which enables heterogeneous data integration, has no analogue in prior proximal methods. Specifically, we establish that modeling a single trend-confounding bridge function for the difference Y0−YpreY_0 - Y_{\mathrm{pre}} is sufficient. A naïve application of existing theory would require two separate bridge functions, one for Y0Y_0 and another for YpreY_{\mathrm{pre}}. By leveraging the trend, our approach avoids this unnecessary complexity, improving statistical efficiency and alleviating the burden of additional model specification.

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