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Estimating Treatment Effects Under Bounded Heterogeneity
\noindentKey words: heterogeneous treatment effects, limited overlap, ridge regression
\noindentJEL classification codes: C12, C21, C51.
In many empirically relevant settings for causal inference, correctly specifying the model requires allowing for fully flexible treatment effect heterogeneity as a function of covariates. However, estimating such rich models often leads to imprecise estimates, and can become infeasible under limited overlap in covariate distributions. Consequently, estimating the fully flexible model may not be desirable in empirical applications, particularly when researchers are primarily interested in the average treatment effect (ATE) rather than the full distribution of heterogeneous effects. Consider the unconfoundedness design, where the treatment is assumed to be as good as randomly assigned conditional on the covariates. Many applied studies estimate a “short” regression of the form that assumes constant effects
and interpret the estimated regression coefficient $\hat \beta_{\text{short}}$ as an estimate of the ATE martinez2014role,favara2015credit,michalopoulos2016long,bobonis2016monitoring,xu2018costs.
There is growing recognition that treatment effect heterogeneity affects the interpretation of the “short” regression. In an influential study, angrist1998 shows that under unconfoundedness and discrete covariates, the “short” regression estimates a convex average of treatment effects associated with each covariate value, and therefore can differ from estimates based on matching that does not restrict treatment effect heterogeneity. sloczynski_interpreting_2022 further shows that this convex average corresponds to a weighted average of treatment effects on the treated and untreated, with counter-intuitive weights. Similar concerns have been raised in recent studies of the “short” regression for staggered adoption designs double_fe,goodman2021difference.
However, revisiting angrist1998, the textbook angrist2009mostly asserts that if treatment effect heterogeneity is limited, the “short” regression estimate may still be preferable to unbiased but noisier semi- and nonparametric estimators of the average effect. First, when treatment effects are constant, the “short” regression is unbiased and most efficient under homoskedasticity. Second, angrist2009mostly informally argue that the bias of the “short” regression remains small when treatment effects do not vary too much, and the resulting efficiency gain can still justify its use. An additional, and often overlooked, consideration is that in settings without overlap, semi- and nonparametric estimators may cease to be well defined, whereas the short regression remains feasible because it extrapolates treatment effect estimates to covariate values without overlap. Consequently, practitioners' intuition is that the confidence intervals (CIs) based on the “short” regression should have coverage close to the nominal level, making the “short” regression a pragmatic choice in applied work.
In this paper, we formalize the argument of angrist2009mostly. Under a restriction on treatment effect heterogeneity, specifically a bound on the variance of conditional average treatment effect heterogeneity (VCATE), we first show how to bias-correct the “short” regression CI such that the resulting CI has correct coverage and is heterogeneity-aware. This approach is feasible even when the average effect is not point identified due to a complete lack of overlap, since the bound on treatment effect heterogeneity provides partial identifying information on the treatment effect for the subsample without overlap.\footnote{When overlap fails completely, the ATE is not point identified. The VCATE bound provides partial identifying information that restricts the range of treatment effects in the non-overlapping sample, enabling valid inference even in this setting.} We denote this bound by $C^2$. As $C^2$ increases from zero, the associated bias-corrected “short” regression CI achieves correct coverage under each restriction, allowing one to assess the sensitivity of the “short” regression estimates to violations of constant effects.
However, as the “short” regression estimator does not adjust to the bound, bias correction can yield an excessively wide heterogeneity-aware CI. To provide a more informative sensitivity analysis, we propose a generalized ridge regression, regulaTE, which coincides with the “short” regression when heterogeneity is absent but otherwise can depart from the “short” regression if its bias is large. We propose selecting the ridge penalty to minimize the heterogeneity-aware CI length under a normal, homoskedastic setting, which facilitates rapid computation. We show in simulations and empirical illustrations that under more general error distributions, the resulting CI remains tighter than the bias-corrected “short” regression CI. We provide an implementation of sensitivity analysis based on regulaTE in our accompanying R package.\footnote{An R package implementing the regulaTE estimator is available online at \url{https://github.com/lsun20/regulaTEr}.}
An important input for our method is $C^{2}$, the bound on VCATE, which we primarily view as a sensitivity parameter rather than a quantity to be estimated. In practice, the researcher examines how the CIs change as $C^{2}$ varies over a user-specified range, thereby assessing how sensitive the empirical conclusions are to deviations from constant treatment effects. A useful summary is the “breakdown value” of $C^{2}$, the smallest value at which the ATE becomes statistically insignificant, following kline2013sensitivity and masten2020inference. Because $C^{2}$ has a clear interpretation as a bound on VCATE, which is frequently used in variance decomposition and welfare analyses kline2020leave, sanchezbecerra2023robust, dechaisemartin2024estimatingtreatmenteffectheterogeneitysites and about whose magnitude applied researchers often have intuition, the resulting sensitivity analysis is straightforward to interpret. We conduct sensitivity analysis based on our proposed regulaTE in two leading empirical applications under unconfoundedness and staggered adoption. We show how subgroup analyses reported in the original empirical studies can be used to inform a plausible range of bounds for the sensitivity analysis. We emphasize, however, that choosing $C^{2}$ in a data-driven manner generally leads either to invalid confidence intervals or to excessively wide intervals, reflecting the impossibility results of armstrong_optimal_2018.
\noindentRelated literature. Since the seminal work of angrist1998, a growing body of literature has characterized the bias of the “short” regression estimator under treatment effect heterogeneity, including gibbons_serrato_urbancic_jem2018, sloczynski_interpreting_2022, goldsmithpinkham2024contamination, double_fe, goodman2021difference. We show how to bias-correct the “short” regression under a restriction on treatment effect heterogeneity, and propose a sensitivity analysis to evaluate the impact of treatment effect heterogeneity on robust estimation of the average effect.
Several papers have proposed estimators for the average effect under restrictions on treatment effects. In the context of the unconfoundedness design, lechner2008note assumes outcomes are bounded and derives the Manski bound for the ATE. lee2021bounding improves the Manski bound by combining it with the inverse probability weighting (IPW) estimator using reference propensity scores. athey_approximate_2018 assume sparsity of effects, armstrong2021finite assume smoothness of effects with respect to covariates, and dechaisemartin2021tradingoff impose bounds on effects. In the context of difference-in-differences, manski_how_2018 impose bounds on the variation in outcomes over time and across states. In contrast to these papers, our method is tied directly to a measure of treatment effect heterogeneity by restricting the variance of treatment effects. This does not entail a functional form assumption on the heterogeneity, mimicking the common belief that effects are broadly similar.
There are semi- and nonparametric estimators, such as the inverse propensity score weighted estimator, that remain unbiased for the average treatment effect even under unrestricted treatment effect heterogeneity. However, these estimators rely on strong overlap for consistency and asymptotic normality. When propensity scores approach 0 or 1, they can become highly variable, making the conventional normal approximation unreliable, as demonstrated in rothe2017robust or heiler2021valid. To address extreme values of propensity scores, crump_dealing_2009 propose trimming the inverse propensity score weighted estimator by removing observations with estimated propensity scores outside the range $(0.1,0.9)$. Since this approach only estimates the average effect for a subpopulation with strong overlap, several papers have characterized the resulting bias and, under certain smoothness conditions, proposed bias correction methods; see, e.g., ma2020robust and sasaki2022estimation. Our method provides an alternative route for dealing with limited overlap, which includes settings with complete lack of overlap: rather than focusing on a subpopulation with strong overlap, we restrict treatment effect heterogeneity and use this restriction to infer the worst-case heterogeneity for covariate cells with limited overlap.
The remainder of the paper is organized as follows. Section (ref) introduces the setup and formalizes the restriction on treatment effect heterogeneity. Section (ref) develops the proposed inference method and illustrates its finite-sample performance in calibrated simulations. Section (ref) applies the method to conduct sensitivity analysis for several empirical settings. Section (ref) concludes. Proofs and comparison to the adaptive estimator of armstrong2023adapting are found in the Appendix.
Consider the unconfoundedness setting where we observe a random sample of $n$ units, and each unit is characterized by a pair of potential outcomes $(Y_i(0), Y_i(1))$ under no treatment and treatment, respectively; a set of (possibly including flexible transformations of) covariates $X_i \in \mathbb{R}^{k+1}$ that includes a constant; and a treatment indicator $D_i \in \{0,1\}$. We assume unconfoundedness (also known as selection on observables): ${Y_i(0), Y_i(1)} \perp D_i \mid X_i$. As common in empirical practice wooldridge_econometric_2010, we further assume that $\ensuremath{\mathbb{E}}[Y_i(1) \mid X_i]$ and $\ensuremath{\mathbb{E}}[Y_i(0) \mid X_i]$ are both linear in $X_i$.\footnote{In principle, such linearity assumptions are not required, and our approach to estimating average effects under bounded treatment effect heterogeneity can be extended to more general settings. For example, assuming linearity only of $\ensuremath{\mathbb{E}}[Y_i(0)\mid X_i]$ leads to a related ridge-type estimation procedure. One could also adopt a fully nonparametric approach by imposing a bound on treatment effect heterogeneity in addition to the smoothness assumptions of armstrong2021finite. Nevertheless, given the prevalence of linear models in empirical practice, and the intuitive interpretation and computational efficiency afforded by this assumption, we view this as a useful trade-off between generality and practicality.} Let $\tau(x) = \ensuremath{\mathbb{E}}[Y_i(1)-Y_i(0)\mid X_i = x]$ denote the covariate-specific average treatment effect (CATE). As discussed in Section (ref), limited overlap remains a key empirical challenge even under the linearity assumption.
Unless stated otherwise, we condition on the realized values $\{x_i, d_i\}_{i=1}^n$ of the covariates and treatment $\{X_i, D_i\}_{i=1}^n$, where lowercase letters denote realizations. All probability statements are therefore taken with respect to the conditional distribution of $\{Y_i(0), Y_i(1)\}_{i=1}^n$. Under these assumptions, the DGP for the observed outcome $Y_i$ can be written as
where $\{\varepsilon_i\}_{i=1}^n$ is a sequence of mutually independent noise terms that are mean zero. This fixed-design framework follows, for example, rothe2017robust and armstrong2021finite, to investigate finite-sample properties. In Section (ref), we extend to settings where the covariates that parameterize treatment effect heterogeneity differ from the confounders $x_i$, but focus first on the case where they coincide to describe the challenge cleanly.
Our goal is to estimate a weighted average of the CATEs with known weights, where the weights reflect a predetermined target population. The leading example is the ATE, $\beta=\beta^{\text{ATE}}=\ensuremath{\mathbb{E}}_n[\tau(x_i)]=\frac{1}{n}\sum_{i=1}^n \tau(x_i)$.\footnote{This parameter is sometimes referred to as the conditional ATE (e.g., imbens2009recent). Since our analysis is always conditional on the realized covariates, we simply refer to it as the ATE without confusion, and reserve the term CATE for the function $\tau(x)$.} Here $\ensuremath{\mathbb{E}}_n$ denotes the “empirical” mean (i.e., $\ensuremath{\mathbb{E}}_n a_i = n^{-1} \sum_{i=1}^n a_i$ for any fixed or random sequence $\{a_i\}_{i=1}^n$). Under the linearity assumption, we can write $\tau(x_i) = \alpha+x_{i,-1}'\delta$, where $x_{i,-1}$ denotes the vector of covariates excluding the constant. Letting $\widetilde x_{i,-1}=x_{i,-1} - \ensuremath{\mathbb{E}}_n[{x}_{i,-1}]$ denote the demeaned covariates, deviations of the CATE from the ATE are given by $\tau(x_i)-\beta^{\text{ATE}} = \widetilde x_{i,-1}'\delta$. Therefore, the DGP (ref) can be reparameterized as the long regression as in imbens2009recent:
Other leading target parameters include the average treatment effect on the treated (ATT) and the average treatment effect on the untreated (ATU). Since the long regression (ref) handles all three targets through appropriate demeaning of the covariates, we focus on the ATE for simplicity.
We define the short regression as the specification that omits the interaction terms between treatment and covariates:
which is the most commonly used specification in empirical research.
While the long regression (ref) is the correct specification, estimating it can be practically challenging: the resulting estimates may be highly imprecise, and the model may not even be estimable under limited overlap. First, when the covariates $x_i$ are mixed, containing both continuous covariates and discrete covariates, the discrete covariates typically enter the long regression as fixed effects capturing confounding from, for example, location effects. If all units in a given location are treated, contributing to lack of overlap, then the interaction between treatment and the centered location fixed effect becomes multicollinear with the treatment indicator and the location fixed effect itself, rendering the long regression $\hat\beta_{\text{long}}$ undefined.
Second, if the covariates $\{x_i\}_{i=1}^n$ are generated by saturating discrete covariates, when overlap fails entirely for a particular covariate value, the long regression $\hat\beta_{\text{long}}$ is again not well-defined. The long regression coefficient estimator is algebraically equivalent to the following IPW estimator: \[ \hat\beta_{\text{long}}^{\text{ATE}}=\ensuremath{\mathbb{E}}_{n}\left[\frac{d_{i}-p(x_{i})}{p(x_{i})\left(1-p(x_{i})\right)}Y_{i}\right] \] where $p(x_i)$ denotes the empirical propensity score for covariate value $x_i$. Therefore, if $p(x_{i})\in\{0,1\}$ for some $x_{i}$ due to lack of overlap, then the long regression $\hat\beta_{\text{long}}$ is not well-defined. Furthermore, because $p(x_{i}) (1-p(x_{i}))$ appears in the denominator, the variability of $\hat\beta_{\text{long}}^{\text{ATE}}$ is heavily influenced by observations for which $p(x_{i})$ is close to zero or one.
In contrast, the short regression estimator is less affected by limited overlap and remains well-defined even under complete lack of overlap at some covariate values. To see this, note that by the Frisch-Waugh-Lovell (FWL) theorem, the short regression estimator in (ref) can be written as \[ \hat\beta_{\text{short}}=\frac{\ensuremath{\mathbb{E}}_{n}\left[\left(d_{i}-p(x_{i})\right)Y_{i}\right]}{\ensuremath{\mathbb{E}}_{n}\left[\left(d_{i}-p(x_{i})\right)d_{i}\right]}. \] This representation highlights that the short regression places little weight on observations with extreme propensity scores. Moreover, it remains well-defined even when overlap fails for some covariate values, since such observations have no influence on the estimator. However, by omitting interactions between $d_i$ and $\tilde{x}_{i,-1}$, the short regression is generally misspecified in the presence of treatment effect heterogeneity. As a result, it may suffer from omitted variable bias, with the bias measured relative to the ATE. From angrist1998, the short regression estimand is:
This estimand coincides with $\beta$ only if one of the following holds: (i) $\tau(x_i)$ is constant, (ii) $p(x_i)$ is constant, or (iii) $p(x_i)(1-p(x_i))$ is uncorrelated with $\tau(x_i)$. In general, the short regression recovers a weighted average of heterogeneous treatment effects, with weights proportional to the conditional variance of treatment assignment. As discussed in poirier2024quantifyinginternalvalidityweighted, the subpopulation for which the short-regression estimand corresponds to a true average treatment effect can be small, limiting the internal validity of the estimator.
Nevertheless, when treatment effect heterogeneity is limited, the short regression remains nearly unbiased and typically yields more precise estimates. This point is made informally by angrist2009mostly: “Of course, the difference in weighting schemes is of little importance if $\tau(x)$ does not vary across cells (though weighting still affects the statistical efficiency of estimators).” This observation helps explain why the short regression is substantially more common than the long regression in empirical practice.
To formalize the belief that treatment effects are broadly similar across covariates, we impose an upper bound on the (sample) variance of the CATE $\tau(x_i)$, the VCATE, which we define as $\ensuremath{\mathbb{E}}_n [(\tau(x_i) - \ensuremath{\mathbb{E}}_n [\tau(x_i)])^2]$.
While any restriction that imposes that the vector of heterogeneous effects $\{\tau(x_i)-\ensuremath{\mathbb{E}}_n[\tau(x_i)]\}_{i=1}^n$ lies in a bounded set would, in principle, suffice to control the bias induced by misspecification of the short regression or other linear-in-outcome estimators, we focus on bounds on VCATE for several reasons. First, because variance is the most widely used and canonical measure of dispersion, VCATE provides an intuitive measure of treatment effect heterogeneity that captures how dispersed treatment effects are across covariate values, rather than imposing potentially opaque geometric restrictions on the entire vector of effects.\footnote{For example, levy2021fundamental and sanchezbecerra2023robust introduce VCATE as leading measures of treatment effect heterogeneity.} This makes the restriction easy to interpret and to vary in sensitivity analyses. In contrast, many alternative convex restrictions, such as $\ell_p$ balls, do not correspond to commonly interpreted notions of treatment effect heterogeneity and are therefore harder to calibrate in empirical applications.
Second, VCATE is a well-studied object in the treatment effects literature, and as a result researchers often have a clear sense of how to reason about its magnitude.\footnote{See kline2020leave, sanchezbecerra2023robust, and dechaisemartin2024estimatingtreatmenteffectheterogeneitysites for recent work on estimation and inference for VCATE.} VCATE arises naturally in variance decompositions and distributional analyses, and recent work has developed estimators and inference procedures for VCATE under a range of identifying assumptions. This existing body of work makes VCATE a familiar and interpretable sensitivity parameter: researchers can draw on prior results, empirical benchmarks, and domain knowledge to assess whether a given bound on VCATE is plausible in their setting. Moreover, Popoviciu's inequality gives a simple (yet conservative) bound \[ \ensuremath{\mathbb{E}}_n [(\tau(x_i) - \ensuremath{\mathbb{E}}_n [\tau(x_i)])^2] \le \frac{1}{4}(\max_i \tau(x_{i})-\min_i \tau(x_{i}))^2, \] providing a simple reference point for calibration.
Note that, under our maintained specification, VCATE can be expressed as a simple quadratic form in the heterogeneity coefficient $\delta$:
For notational convenience, define \( V_x := \ensuremath{\mathbb{E}}_n[\tilde{x}_{i,-1}\tilde{x}_{i,-1}'], \) which is the sample analogue of $\text{Var}(X_{i,-1})$. We assume that $V_x$ is invertible, which is a minimal condition ensuring that the short regression is well defined. Accordingly, imposing an upper bound on VCATE of the form \( \ensuremath{\mathbb{E}}_n\!\left[(\tau(x_i)-\ensuremath{\mathbb{E}}_n[\tau(x_i)])^2\right] \le C^2 \) is equivalent to imposing the weighted quadratic constraint \( \delta'\,V_x\,\delta \le C^2 \) on the parameter vector $\delta$. Throughout the paper, we report and plot results on the standard-deviation scale $C$ rather than the variance scale $C^2$, because $C$ shares the units of the outcome.
Although we do not pursue this direction here, the approach we introduce can be extended straightforwardly to more general restrictions that require $\delta$ to lie in a bounded, convex set. For example, one could replace the quadratic constraint above with coordinatewise bounds of the form $\max_{\ell}|\delta_\ell|\le C$ or other convex constraints on $\delta$ by following the general procedure described in armstrong2023biasaware.
In this section, we develop inference methods that explicitly account for treatment effect heterogeneity. We begin by showing how to construct valid confidence intervals based on estimators that are linear in outcomes, while allowing for limited or even complete lack of overlap.
Building on (ref), we consider the regression model
where $Y_i$ is the outcome, $d_i$ is the (non-random) treatment indicator, and $x_i=(1,x_{i,-1}')'$ is the vector of non-random covariates including a constant. Define $D=(d_1,\ldots,d_n)'$ as the (realized) treatment vector and $X=(x_1,\ldots,x_n)'$ the matrix of (realized) covariates. We assume $X'X$ is invertible. To introduce our proposal cleanly, we assume $\varepsilon_i \overset{i.i.d.}{\sim} N(0,\sigma^2)$ throughout this subsection, an assumption we relax in Section (ref). That is, treatment effect heterogeneity is fully captured by the covariates $x_i$ under this specification.
In a fixed-design setting, estimating the ATE under a VCATE bound is equivalent to conducting inference on $\beta$ in (ref) subject to the constraint $\delta'V_x\delta \le C^2$ as explained in (ref). Equivalently, the restriction on the parameter space is $(\beta,\gamma',\delta')' \in \Theta_C$, where \[ \Theta_C := \{(\beta,\gamma',\delta')' \in \mathbb{R}^{2+2k}:\ \delta'V_x\delta \le C^2\}. \]
Let $Y=(Y_1,\ldots,Y_n)'$. We focus on linear estimators of the form $\hat\beta_a = a'Y$, where $a\in\mathbb{R}^n$ is non-random. Since $(d_i,x_i')'$ are treated as fixed, the weights $a$ may depend on them; this class includes typical estimators such as difference-in-means, the short regression, and the long regression (when defined).
The variance of the estimator $\hat\beta_a=a'Y$ is $\text{Var}(\hat\beta_a)=\sigma^2 a'a$ under homoskedasticity. From (ref), the worst-case bias of $\hat\beta_a$ over $\Theta_C$ is
where $D\circ\tilde X_{-1}$ is the matrix with $i$th row equal to $d_i\tilde x_{i,-1}'$. Hence, given the weights $a$, the worst-case bias of the corresponding estimator can be calculated explicitly. Since $\Theta_C$ leaves $\beta$ and $\gamma$ unrestricted, it is necessary that the weights satisfy $a'D=1$ and $a'X=0$ to achieve finite worst-case bias. Under these conditions, the remaining bias $a'(D\circ\tilde X_{-1})\delta$ is linear in $\delta$, and since $\Theta_C$ is centrosymmetric in $\delta$ (i.e., $\delta\in\Theta_C$ implies $-\delta\in\Theta_C$), the one-sided supremum in (ref) equals $\sup_{\Theta_C}|\ensuremath{\mathbb{E}}[\hat\beta_a]-\beta|$.
A fixed-length confidence interval (FLCI) is constructed as
where $\text{cv}_\alpha(B)$ denotes the $(1-\alpha)$ quantile of the folded normal distribution $|N(B,1)|$. The critical value therefore reflects the potential worst-case bias of $\hat\beta_a$. Importantly, the validity of the confidence interval does not rely on point identification of $\beta$. In cases of complete lack of overlap, $\beta$ is set identified rather than point identified under a VCATE bound; as shown in Lemma (ref), an immediate consequence of armstrong_optimal_2018, the FLCI attains correct coverage uniformly over the identified set.
Write $P_{X} = X(X'X)^{-1}X'$ and $H_{X} = I - P_{X}$. As shown in Lemma (ref) in the Appendix, the worst-case bias of the short regression estimator is \[ \operatorname{\overline{bias}}_{a_s,C} = C\sqrt{ a_s'(D\circ\tilde X_{-1})V_x^{-1}(D\circ\tilde X_{-1})'a_s}, \qquad a_s=(D'H_XD)^{-1}H_XD. \] Because the short-regression weights $a_s$ do not adjust as $C$ increases, bias-corrected short-regression confidence intervals can become excessively long. Since the length of any FLCI of the form $\hat\beta_a\pm\chi_{a,C}$ equals $2\chi_{a,C}$ and increases in both $\operatorname{\overline{bias}}_{a,C}$ and $\text{Var}(\hat\beta_a)$, improving performance for $C>0$ requires a better bias-variance trade-off.
To achieve a better bias-variance trade-off, we propose solving the generalized ridge least-squares problem
where $\lambda>0$ is chosen as discussed later in Section (ref). Let $\hat{\beta}_\lambda$ denote the resulting coefficient estimator for $\beta$. Since $\delta'V_x\delta$ equals the sample VCATE as shown in (ref), the penalty directly shrinks the heterogeneity coefficients $\delta$ toward zero, that is, toward the constant-effects model, with the degree of shrinkage governed by $\lambda$. It is not a priori obvious that such a penalty on the outcome regression should yield optimal inference for $\beta$, since penalized regression targets a prediction error objective rather than the bias-variance trade-off specific to $\beta$.\footnote{Under an $\ell_1$ bound on $\delta$, for instance, the LASSO-penalized outcome regression does not produce optimal inference for $\beta$. The coincidence between the ridge penalty on the outcome regression and the optimal inference procedure for $\beta$ is specific to the quadratic VCATE constraint, which has been pointed out in li1982minimaxity and armstrong2023biasaware.} However, the quadratic geometry of the VCATE restriction implies that $\hat{\beta}_\lambda$ lies on the bias-variance frontier for every $\lambda>0$: no linear estimator achieves simultaneously smaller variance and smaller worst-case bias. Moreover, all linear estimators that lie on the frontier can be written in this form. Before we formalize this optimality result in Theorem (ref) in Section (ref), we provide some intuition.
Lemma (ref) shows that the generalized ridge regression coefficient estimator $\hat{\beta}_{\lambda}$ can be written as
where the weights $a_{\lambda} := \frac{\tilde{D}_{\lambda}}{\tilde{D}_{\lambda}'D}$ and the residuals $\tilde{D}_{\lambda} := D - X\pi_{1,\lambda} - (D \circ \tilde{X}_{-1})\pi_{2,\lambda}$ are from a penalized propensity score regression:
For $\lambda>0$ define the shrinkage matrix
which maps any vector $v \in\mathbb R^n$ to the fitted values from the ridge regression of $H_X v$ on $H_X (D\circ \tilde X_{-1})$ with penalty matrix $n\lambda V_x$. With this notation, the residualized treatment used by the generalized ridge estimator can be written as
and therefore \[ \hat\beta_\lambda = \frac{\tilde D_\lambda'Y}{\tilde D_\lambda'D} = \frac{((I-S_\lambda)H_XD)'Y}{((I-S_\lambda)H_XD)'D}. \] Hence, the effect of $\lambda$ on $\hat\beta_\lambda$ operates entirely through the shrinkage operator $S_\lambda$.
When $\lambda=0$ and $(D\circ \tilde X_{-1})'H_X(D\circ \tilde X_{-1})$ is invertible (i.e., the long regression is well-defined), \( S_0 = H_X(D\circ \tilde X_{-1})((D\circ \tilde X_{-1})'H_X (D\circ \tilde X_{-1}))^{-1}(D\circ \tilde X_{-1})'H_X \) is the orthogonal projection onto $\mathrm{span}(H_X (D\circ \tilde X_{-1}))$, and $(I-S_0)H_XD$ equals the residual from regressing $D$ on $(X, D\circ \tilde X_{-1})$. Consequently, $\hat\beta_0$ coincides with the long-regression coefficient on $D$.\footnote{When the long regression is not well-defined due to lack of overlap, in the case of discrete covariates, it is possible to analytically characterize the limit of $\hat\beta_\lambda$ as $\lambda\to0$, which is the long regression estimator $\hat{\beta}_{\text{long}}$ restricted to the trimmed subsample with overlap as shown in Lemma (ref).} On the other hand, as $\lambda\to\infty$, it is clear that $\tilde D_\lambda\to H_XD$ and $\hat\beta_\lambda$ converges to the short regression estimator.
To gain more intuition about our estimator, for fixed $\lambda>0$, suppose $X$ is generated from saturating discrete covariates. Lemma (ref) shows the weights in (ref) can be written as $a_{\lambda,i}=\frac{1}{n}\frac{ (d_i-p(x_i))(1-\widetilde{x}_{i,-1}'\pi_{2, \lambda}) }{\ensuremath{\mathbb{E}}_n\left[ (d_i-p(x_i))(1-\widetilde{x}_{i,-1}'\pi_{2, \lambda}) d_{i}\right]}.$ The estimand of $\hat{\beta}_{\lambda}$ is therefore a weighted average of CATEs:
As shown in Lemma (ref), expression (ref) further simplifies to
The weight on each unit's CATE is proportional to $p(x_i)(1-p(x_i))/(p(x_i)(1-p(x_i))+\lambda) \in [0,1]$, which equals $1/(1+\lambda/[p(x_i)(1-p(x_i))])$. This factor is close to one for well-overlapped cells where $p(x)(1-p(x))$ is large relative to $\lambda$, and close to zero for poorly overlapped cells where $p(x)(1-p(x))$ is small relative to $\lambda$. As $\lambda\to 0$, the shrinkage factor approaches one for all cells and the weights converge to cell shares, recovering the ATE. As $\lambda\to\infty$, the weights converge to the short regression weights in (ref), proportional to $p(x)(1-p(x))$. For intermediate $\lambda$, the ridge estimand overweights well-overlapped cells relative to the ATE, but less so than the short regression: cells with $p(x)(1-p(x)) \gg \lambda$ receive weight close to their cell shares, while cells with $p(x)(1-p(x)) \ll \lambda$ are heavily downweighted. Note that the weights are always non-negative and sum to one. Later in Section (ref), we illustrate these weights in the context of angrist1998 (see Figure (ref)).
It remains to choose the penalty parameter $\lambda$. We select it to minimize the half-length of the resulting FLCI in the homoskedastic Gaussian setting. By the same argument as Lemma (ref) in the Appendix, the worst-case bias of $\hat{\beta}_\lambda$ takes the form \[ \operatorname{\overline{bias}}_{a_{\lambda},C}=C\cdot\sqrt{a_{\lambda}'(D\circ\tilde{X}_{-1})V_{x}^{-1}(D\circ\tilde{X}_{-1})'a_{\lambda}}. \] Let $\lambda^{\ast}_{C}$ denote the penalty parameter value that minimizes the half-length of the corresponding fixed-length CI:
and construct the corresponding CI $\hat{\beta}_{\lambda^*_{C}} \pm \chi_{a_{\lambda^{\ast}_{C}},C}$. We refer to this inference procedure as regulaTE, for its ability to regularize treatment effect heterogeneity.
The regulaTE CI is in fact the shortest possible fixed-length CI based on any linear estimator in the homoskedastic Gaussian setting. We formalize this in the following theorem.
The first part of the theorem establishes that $\hat{\beta}_\lambda$ lies on the bias-variance frontier for every $\lambda > 0$: at bias level $B = \operatorname{\overline{bias}}_{a_\lambda, C}$, no linear estimator achieves smaller variance. This follows from the modulus of continuity characterization of optimal inference donoho1994statistical,armstrong_optimal_2018: the generalized ridge regression solves the modulus problem associated with the VCATE constraint. The second part follows because the family $\{\hat{\beta}_\lambda : \lambda > 0\}$ spans the entire bias-variance frontier. Since the FLCI half-length $\chi_{a,C}$ depends on the weights $a$ only through the variance $a'a$ and worst-case bias $\operatorname{\overline{bias}}_{a,C}$, minimizing CI length over all linear estimators reduces to minimizing over the ridge family, which is what (ref) achieves.
We begin with an initial estimator $\hat{\theta}^{\mathrm{init}} = (\hat{\beta}^{\mathrm{init}}, \hat{\gamma}^{\mathrm{init}}{}', \hat{\delta}^{\mathrm{init}}{}')'$ for $\theta = (\beta, \gamma', \delta')'$, obtained either from the long regression (when defined) or from a cross-validated generalized ridge regression that penalizes the weighted $\ell_{2}$ norm $\ensuremath{\mathbb{E}}_n[(\widetilde{x}_{i,-1}'\delta)^2]$. Define the residuals from this initial estimator $\hat{\varepsilon}_{\mathrm{init},i} = Y_{i} -d_i\hat{\beta}^{\mathrm{init}} - x_{i}'\hat{\gamma}^{\mathrm{init}}- d_{i}\widetilde{x}_{i,-1}'\hat{\delta}^{\mathrm{init}}$, and the corresponding initial variance estimator $\hat{\sigma}^2 = \frac{1}{n} \sum_{i=1}^n \hat{\varepsilon}_{\mathrm{init},i}^2.$
For each $\lambda$, compute $\hat{\beta}_\lambda$ as before and obtain $\lambda^*_{C}$ via (ref) by plugging in $\hat{\sigma}$. Form the robust variance estimator \[ \hat{V}_{\lambda^{\ast}_{C},\text{rob}} = \sum_{i=1}^n a_{\lambda^{\ast}_{C},i}^2 \hat{\varepsilon}_{\mathrm{init},i}^2, \quad \text{where } a_{\lambda^{\ast}_{C}} = \frac{\tilde{D}_{\lambda^{\ast}_{C}}}{\tilde{D}_{\lambda^{\ast}_{C}}'D}. \] The feasible CI is then $\hat{\beta}_{\lambda^*_{C}} \pm \text{cv}_\alpha \left( \operatorname{\overline{bias}}_{a_{\lambda^*_{C}},C}/\hat{V}_{\lambda^*_{C},\text{rob}}^{1/2} \right) \cdot \hat{V}_{\lambda^*_{C},\text{rob}}^{1/2}$. Cluster-robust versions follow analogously.
The asymptotic validity of the feasible CI is formally stated in Appendix (ref), which follows from a central limit theorem (CLT) applied to $\hat{\beta}_{\lambda^*_{C}}$. The key requirement is that the maximal Lindeberg weight associated with the estimator,
shrinks sufficiently quickly relative to the error of the initial estimator used to form the residuals. While we provide formal conditions for asymptotic validity in Appendix (ref), the Lindeberg weights can be computed in any given application and serve as a diagnostic for the reliability of the normal approximation; see noack2024bias for an analogous discussion in the context of fuzzy regression discontinuity designs. The companion R package reports the maximal Lindeberg weight and issues a warning when it is large. Note that, due to limited overlap, the convergence rate may be slower than the parametric rate of $n^{-1/2}$.
The previous sections demonstrate how to construct regulaTE CIs given a bound on VCATE. One might instead wish to construct a “wider” CI that remains valid under unrestricted treatment effect heterogeneity, or a CI that adapts to the true underlying VCATE, shrinking in length according to the true bound while still guaranteeing coverage over a broader class of heterogeneity. We show that neither approach is feasible, thereby establishing the necessity of imposing an a priori bound on VCATE.
Intuitively, absent any restriction on the parameter space, the worst-case bias of any linear estimator must be unbounded when overlap fails. The reason is that the data contain no information about treatment effects for strata in which only treated (or untreated) units are observed. Formally, recall from (ref) that the bias is linear in the parameters. Thus, only unbiased estimators have bounded bias (in fact, zero) when the parameter space is unrestricted. As evident from the expression, unbiasedness requires $a'D =1$, $a'X = 0$ and $a'(D \circ \tilde{X}_{-1}) = 0$. Suppose overlap fails for the binary $j$th covariate so that $X_{j+1} \leq D$, where $\leq$ is interpreted elementwise. Writing $\bar{x}_{j+1} := \ensuremath{\mathbb{E}}_{n}[x_{i, j+1}]\neq 0$, the conditions for unbiasedness imply $a'D = 1$, $a'X_{j+1} = 0$ and $a'(X_{j+1} - D\bar{x}_{j+1}) = 0$, but it is clear that no weight vector $a$ can satisfy these conditions.\footnote{This is because due to lack of overlap $D \circ \tilde{X}_{-1} = X_{j+1} - D\bar{x}_{j+1}$.} Hence, no unbiased linear estimator exists, and the worst-case bias of any linear estimator is unbounded. A formal statement and proof of this result can be found in Appendix (ref).
Moreover, it turns out that it is impossible to construct a CI that adapts to the true VCATE. By definition, an adaptive CI has length that automatically reflects the true magnitude of VCATE while maintaining coverage under a conservative a priori bound on VCATE. However, Corollary 2.1 of armstrong2023biasaware implies that any valid CI must have expected length that reflects the conservative a priori bound $C^2$, even when VCATE is much smaller than $C^2$. In other words, one cannot automate the choice of the VCATE bound $C^2$ when constructing the CI.
Therefore, while $C$ is an important input to our method, it cannot be set to $C = \infty$, nor can it be selected in a data-driven way with the goal of adapting to the true VCATE. In Section (ref), we discuss how to conduct sensitivity analysis with respect to $C$.
We illustrate the theoretical results so far in realistic settings through simulations calibrated to the data generating process in angrist1998. angrist1998 links social security earnings records to administrative data on a sample of U.S. military applicants from 1979 to 1982 to estimate the effects of voluntary military service on veterans' earnings. The following discrete characteristics are controlled for confounding: year of application, year of birth, education at the time of application, race, and Armed Forces Qualification Test (AFQT) score group. The paper documents heterogeneity in treatment effects: military service modestly increased the civilian earnings of non-white veterans while reducing those of white veterans. Further heterogeneity is observed across background characteristics such as education and AFQT scores, which prompted angrist1998 to theoretically analyze the different estimands of the short regression and the long regression (referred to therein as the controlled contrast estimator). The estimates were found to be significantly different, both statistically and economically.
For simplicity, our simulation exercises focus on inference for the average treatment effect on earnings in 1988 among white applicants. Within this population, there are approximately 400 covariate cells. The public replication data from angrist1998 report cell-level summary statistics, such as the mean and standard deviation of earnings, the share of veterans, and the cell frequency, constructed from administrative records covering roughly 100,000 individuals.
To calibrate the simulation to angrist1998 and to construct a micro-level dataset, we draw 2,000 individuals, which can be interpreted as a 2% subsample of the original population. Treatment status is assigned using the cell-level share of veterans as the true propensity score, which ranges from 4.6% to 81.2%. Given a fixed realization of treatment assignments, the relatively small sample size leads to a lack of overlap at some covariate values, equivalent to 12.4% of the sample size. As a result, the long regression is not well defined and the ATE is not point identified.
To preserve both heteroskedasticity and treatment effect heterogeneity from the original data of angrist1998 in the data-generating process, outcomes are generated by treating the cell-level summary statistics as the true means and standard deviations of earnings and assuming normally distributed earnings within each cell. We treat the cell-level standard deviations as known for the simulation. The true standard deviation of the CATEs is $C_0=1452.195$ dollars.
Because all covariates are discrete in the data-generating process, the regulaTE estimand admits a transparent interpretation as a weighted average of the cell-level treatment effects $\tau(x)$, as characterized in (ref). Figure (ref) plots these cell-level regulaTE weights, after excluding cell shares, under several values of the heterogeneity bound $C$ against the within-cell treatment variance $p(x)(1-p(x)).$ When $C=0$, to minimize variance regulaTE coincides with the short regression, placing weights proportional to $p(x)(1-p(x)).$ As $C$ increases, regulaTE moves away from the short regression, but still places relatively high weight on well-overlapped cells and aggressively shrinking contributions from poorly overlapped ones where $p(x)(1-p(x))$ is small. With $C=C_0$ where treatment effect heterogeneity can be large, the regulaTE weights become closer to cell shares due to the increasing importance of worst-case bias relative to variance in the bias-variance trade-off.
On the horizontal axis of Figure (ref), we consider various heterogeneity bounds $C$ and use them both to bias-correct the short-regression CI and to construct the heteroskedasticity-robust regulaTE CI. When no correction is applied, the short-regression CI, while quite short, exhibits substantial undercoverage, reflecting bias induced by omitting treatment effect heterogeneity. As the bound $C$ increases, both the bias-corrected short-regression CI and the regulaTE CI achieve coverage close to the nominal level. But across the range of $C$, in this heteroskedastic setting, the bias-corrected short-regression CI is longer than the regulaTE CI, as shown in the left panel. Correct coverage is attained for values of $C$ that are strictly smaller than the true heterogeneity level $C_0$ because the validity guarantee is derived under worst-case heterogeneity, whereas the data-generating process considered here is less adversarial.
In Appendix (ref), we illustrate the behavior of regulaTE in settings with overlap and compare it with the long regression, which is now well-defined. We also compare with the adaptive estimator of armstrong2023adapting, which combines the short and long regression estimators for efficiency gain. regulaTE is constructed to adjust the CI based on the user-specified bound $C$ for sensitivity analysis. Therefore, it connects the long and short regression CIs as $C$ increases from zero. The adaptive estimator does not adjust to the user-specified bound $C$ and remains close to the long regression in this DGP, while the bias-corrected short-regression CI is again overly long.
Researchers often use the short regression to estimate the ATE under the (frequently implicit) assumption that treatment effect heterogeneity is not too large. Our method provides a formal way to assess this assumption. In this case, rather than taking a definitive stand on $C$, one can begin with $C = 0$ (which corresponds to using the short regression) and gradually increase $C$ until the results become insignificant.\footnote{Note that we take $C$, rather than $C^2$, as our sensitivity parameter because it has the same units as the outcome.} We denote the smallest value of $C$ that renders the estimated treatment effect insignificant as $C^\ast$. One can then evaluate whether the corresponding breakdown point $C^\ast$ is plausible, which is feasible since VCATE is a highly interpretable quantity. This is analogous to the breakdown frontier analysis considered in, e.g., kline2013sensitivity, masten2020inference and li2021linear. Our R package provides a plotting functionality that aids such sensitivity analysis.
aizer2016 evaluate the long-run effects of early 20th-century Mothers' Pension (MP) cash transfers on children's lifetime outcomes, using administrative data. Their study compares children of approved MP applicants to those whose approvals were subsequently reversed, accounting for observed characteristics, to estimate causal effects. The original study estimates the following short regression as in aizer2016: \[ \log(\textit{Age at Death})_{ifts} = \theta_0 + \theta_1 MP_f + \theta_2 \boldsymbol{X}_{if} + \theta_3\boldsymbol{Z}_{st} + \boldsymbol{\theta}_c + \boldsymbol{\theta}_t + \varepsilon_{if}, \] where the outcome is the natural logarithm of the age at death for a given individual $i$ in family $f$ born in year $t$ living in a county $c$ (state $s$), and the treatment $MP_f$ indicates MP receipt. The authors control linearly for $\boldsymbol{X}$, a vector of relevant family characteristics (marital status, number of siblings, etc.) and child characteristics (year of birth and age at application), and $\boldsymbol{Z}_{st}$, a vector of county-level characteristics in 1910 and state characteristics in the year of application. The authors also control for county and cohort fixed effects ($\boldsymbol{\theta}_{c}$ and $\boldsymbol{\theta}_{t}$). To illustrate our method, we focus on child longevity, which is one of the authors' main outcome of interest.
We assess the sensitivity of the estimate for ATT, which is the average impact of MP receipt among MP recipients, as it is the most relevant target parameter for program evaluation. Based on the short regression, the ATT is estimated to be $1.82$% and is statistically significant at the $5$% significance level. Note that the long regression is infeasible because in eleven counties, accounting for about 9% of the sample, all applicants received the MP. This lack of overlap renders the long regression undefined due to collinearity among the MP receipt indicator, interaction terms and county fixed effects.
After reporting their ATT estimates based on the short regression aizer2016, the authors examine heterogeneous effects of the MP program across subgroups defined by family income, the child's age, and urban residence. Some subgroup estimates are statistically insignificant, and the magnitudes are broadly similar, ranging between 1% and 2% aizer2016.
To formalize the robustness checks based on the subgroup analysis originally conducted by the authors, Figure (ref) conducts the sensitivity analysis based on the regulaTE CI. We also present the bias-corrected short regression CI for comparison. Standard errors are clustered at the county-level, as in the original analysis. As $C$ increases, the regulaTE CI for ATT expands to account for the possibility of greater worst-case bias. Note that the bias-corrected short regression CI is substantially wider, underscoring the efficiency gains from regulaTE. The breakdown point is around 0.75% ($C^\ast=0.0075$). To put this breakdown frontier value into perspective, note that given an average age at death of 72.44 years, even a 2% increase represents a substantively meaningful effect. This consideration motivates a benchmark on the standard deviation of heterogeneous percentage effects of $C^{\text{ref}} = 1\%$, corresponding to bounding the effects to be between 0% and 2% and applying Popoviciu's inequality on variances. The breakdown point is only marginally smaller than $C^{\text{ref}}$, suggesting the statistically significantly positive impact of MP receipt on child longevity among receiving families is robust to economically meaningful treatment effect heterogeneity to some extent.
The recent literature on staggered adoption designs also emphasizes the bias in common specifications from omitting treatment effect heterogeneity; see roth2023s for a review. Consider a staggered adoption setting where we observe a sample of i.i.d. draws $\left\{ \{Y_{it}, d_{it}\}_{t=0}^{T}\right\}_{i=1}^n$ over $\mathcal T =T+1$ total time periods. Define $e_i := \min\{ t : d_{it} = 1 \}$ as the period in which unit $i$ first receives treatment. Let $\mathcal{E}$ denote the set of all such first treatment periods, and define a cohort as the set of units treated for the first time in the same period: $\{ i : e_i = e \}$.
Under standard assumptions of parallel trends and no anticipation, the DGP for the observed outcome can be written as
where $\alpha_e$ and $\lambda_t$ are cohort and time fixed effects respectively. The framework developed earlier for unconfoundedness settings in (ref) assumes $\tau(\cdot)$ is a linear function of the confounders $x_i$. Here $\tau(\cdot)$ is a linear function of group and relative time indicators, rather than the confounders. Specifically, $\tau_{e,\ell} = \ensuremath{\mathbb{E}}[ Y_{i,e+\ell}(1) - Y_{i,e+\ell}(0) \mid e_i = e ]$ is the conditional average treatment effect (CATE) for cohort $e$ at relative time $\ell$, which can vary across cohorts and over time in an unrestricted fashion. Therefore, the original framework continues to hold for the following “short” and “long” regressions.
Rather than the unrestricted (ref), researchers often estimate a simpler specification also known as the “static” two-way fixed effects (TWFE) regression
which omits the interactions between $d_{it}$ and cohort and relative-time indicators. Analogous to the short regression in the unconfoundedness setting, as argued in double_fe and goodman2021difference, the “static” specification (ref) implicitly assumes constant effects across cohorts and over time (i.e., $C = 0$). When the effects indeed vary, the “static” specification (ref) can be severely biased for a class of reasonable estimands due to negative weighting of $\tau_{e,\ell}$ for large $\ell$.
One reasonable estimand in this setting is the average effect over treated cohorts (ATT), defined as \[ \text{ATT} = \frac{ \sum_{t \in \mathcal{T}} \sum_{e \in \mathcal{E}} \mathbb{P}_n\{d_{it}=1\}\cdot\mathbb{P}_n\{e_i = e \mid d_{it} = 1 \} \cdot \tau_{e,t-e} } { \sum_{t \in \mathcal{T}} \mathbb{P}_n\{d_{it}=1\}, } \] where $\mathbb{P}_n$ denotes empirical frequencies. That is, the ATT is a weighted average of the cohort-by-event-time effects $\tau_{e,t-e}$, where the weights reflect the empirical distribution of treated observations across cohort-time cells. To recover this estimand, we can reparameterize (ref) as the “long” regression \[ Y_{it} = \alpha_e + \lambda_t + d_{it} \beta^{\text{ATT}}_{\text{long}} + \left( d_{it} \cdot \tilde{x}_{it} \right)'\delta + \varepsilon_{it} \] where $\tilde{x}_{it}$ collects all but one of the re-centered cohort and relative time indicators: \[ \tilde{x}_{it} =
. \] This long regression coincides with the extended TWFE specification from wooldridge2025twfe. However, this long regression can be noisy or even infeasible in practice. Estimation of (ref) corresponds to aggregating cohort- and time-specific DID estimators $\hat{\tau}_{e,t-e}$ for each $\tau_{e,\ell}$, which can be noisy when few units are treated at a given time. Moreover, if all units are treated after time $t$, the required counterfactuals are not identified, similar to a lack of overlap in cross-sectional settings, and the ATT is no longer identified without further assumptions on treatment effect heterogeneity. To address this, we impose a bound $C > 0$ on the variance of treatment effect heterogeneity, restricting the deviation of $\tau_{e,t-e}$ from the ATT. Under this assumption, we can construct valid confidence intervals using our regulaTE procedure, thereby extending the sensitivity analysis to the staggered adoption setting.
To illustrate, we revisit the empirical application in sun_estimating_2020, which builds on dobkin_finkelstein_kluender_notowidigdo_aer2018 to estimate the average effect of an unexpected hospitalization on out-of-pocket medical spending among adults who experienced at least one such hospitalization between waves 8 and 11 of the Health and Retirement Study (HRS). Each wave corresponds to approximately two calendar years. Using a balanced panel from wave 7 through wave 11 ($T=5$), all individuals are treated in the final period ($t=5$), so the ATT from waves 8 to 11 is not point identified and the long regression (ref) is not well defined. Nevertheless, the “static” specification delivers a statistically significant and positive estimate, as shown in Figure (ref).
To evaluate the robustness of this estimate to treatment effect heterogeneity, Figure (ref) reports sensitivity analysis based on the regulaTE CIs. Again, we present the bias-corrected short regression CIs as well for comparison. Standard errors are clustered at the individual level, as in the original analysis of dobkin_finkelstein_kluender_notowidigdo_aer2018. The CIs based on regulaTE remain significant up to a breakdown value of $C^\ast = \$1{,}583$. To interpret this breakdown value, consider the original analysis in dobkin_finkelstein_kluender_notowidigdo_aer2018, which focuses on heterogeneity over time. They report an increase in out-of-pocket spending of roughly \$3{,}000 in the first year after hospitalization and \$1{,}000 by the third year. Under the assumption that heterogeneity operates primarily over time, treating these magnitudes as rough bounds and applying Popoviciu's inequality on variances, we get a reference treatment effect heterogeneity value of $C^{\text{ref}} = \$1{,}000$. Therefore, using sensitivity analysis based on the regulaTE CIs, we find the statistically significant average increase in out-of-pocket spending due to unexpected hospitalization remains robust to substantial treatment effect heterogeneity. In contrast, the bias-corrected short regression CIs widen substantially, and a sensitivity analysis based on them would suggest a lack of robustness to treatment effect heterogeneity, potentially overstating the fragility of the original results.
Many specifications commonly used in empirical research implicitly restrict treatment effects to be constant, often favoring precision at the expense of robustness. While such a restriction yields narrower confidence intervals, the resulting estimates may be substantially biased in the presence of heterogeneity. This paper develops a sensitivity analysis based on the proposed regulaTE CIs by varying the bound on treatment effect heterogeneity.
There are several directions for future work. One natural extension is to consider alternative forms of restrictions on treatment effect heterogeneity. While variance bounds naturally capture the dispersion in heterogeneous effects, one could instead impose an absolute bound on the deviation of individual treatment effects from the average effect if such prior knowledge is available. Another promising direction is to generalize the framework to accommodate multiple treatments or layered sources of heterogeneity, as in goldsmithpinkham2024contamination and sun_estimating_2020.