WorksEconomics, Econometrics and Finance
Doubly robust estimation of direct and spillover effects using multiple pre-treatment periods
Abstract
Under interference, the treatment of some units affects the outcomes of others, so that the effect on a treated unit consists of a direct and a spillover component. A non-treated comparison group then generally identifies neither component, but the difference between the total effect on the treated and the spillover effect on the comparison units. Under certain identifying assumptions, both components may be identified separately when multiple pre-treatment periods are available, even in the absence of an uncontaminated comparison group. Under a no-anticipation assumption, pre-treatment outcomes are free of both components for every unit. Extrapolating the pre-treatment trend within a group, as in interrupted time-series approaches, therefore identifies the counterfactual outcome in the absence of any treatment, provided that the model used for the extrapolation is correctly specified. Applied to the treated it gives the total effect on them, applied to the non-treated at a given level of exposure the spillover effect on them. Disentangling the two components in addition requires effect homogeneity across treated and non-treated units with the same exposure and covariates, as well as common support in exposure. We derive doubly robust and Neyman-orthogonal expressions for the effects of interest, which permits controlling for possibly high-dimensional covariates by machine learning. A simulation study confirms the root- consistent behaviour of the estimators and the reliability of the standard errors under specific regularity conditions. We apply the framework to the compulsory licensing of enemy-owned patents in the United States in 1919. Licensing raised patenting in the licensed subclasses and in technologically close ones alike, so that a comparison-group design understates the total effect.
Introduction
Most studies in causal analysis and treatment evaluation explicitly or implicitly rule out interference or spillover effects, as implied by the stable unit treatment value assumption (SUTVA), see [15] and [39], which is frequently implausible in empirical applications. When treating some units affects the outcomes of others, the effect of the treatment on a treated unit consists of the direct effect of its own treatment and the spillover effect of the treatment of others, which together form the total effect on the treated. Moreover, a non-treated comparison group may itself be contaminated by spillovers, in which case the estimand of a causal inference method is in general the difference between the total effect on the treated and the spillover effect on the comparison units, see [30]. Neither component is identified separately, and the sign of the estimand is uninformative about the sign of either. The remedies proposed so far restrict the interference structure and require the existence, and the correct identification, of units that are clean controls in the sense of being unaffected by any spillover.
In this paper, we consider the evaluation of total, direct, and spillover effects based on approaches that require no clean controls but outcomes observed in multiple pre-treatment periods, while also controlling for observed covariates. The underlying intuition is that under no anticipation of treatment, the pre-treatment outcomes of every unit, treated or not, are realizations of the potential outcome in the absence of any treatment, such that interference contaminates the post-treatment outcomes of the comparison group but not its pre-treatment outcomes. Extrapolating the pre-treatment trend within a group, as in interrupted time series (ITS) approaches, therefore delivers the counterfactual outcome in the absence of any treatment, provided that the extrapolation is valid. Applied to the treated, this identifies the total effect on the treated; applied to the non-treated at a given level of exposure to the treatment of others, the spillover effect on them. Celli et al. [11] formally establish this identification result without covariates. With two pre-treatment periods and a linear trend the counterfactual conditional mean is a second difference of the cell’s own pre-treatment conditional means, and further periods permit richer trend specifications. Neither a comparison group nor a common support condition across groups is required. Our first contribution is a conditional version of this approach, which permits trends to differ across observed characteristics and the covariate composition of a group to change across periods, and thereby extends the argument from panels to repeated cross sections.
Exposure is frequently summarized by an exposure mapping in the sense of Aronow and Samii [5], a function of the treatments of all other units measuring how intensely a unit is reached by them, such as the number of treated units in its neighborhood. In this context, separating the total effect on the treatment into its direct and exposure-related spillover effects is demanding, as the difference between the two is the spillover treated units would experience in the absence of their own treatment, which is never observed. Our second contribution is to make precise what it takes to recover it. First, an effect homogeneity condition is required, namely that treated and non-treated units with the same exposure and covariates experience the same average spillover, which is restrictive whenever spillovers differ along unobserved characteristics in which the two groups differ. Second, exposure must be observed for both groups and have common support across them, which fails when treatment status mechanically determines exposure. Where either is implausible, the analysis is confined to the total effect on the treated and the spillover effect on the non-treated, which we regard as the main parameters.
Our third contribution is a testable restriction. When some units are classified as non-exposed, their spillover is zero by construction, so the corresponding estimate must not differ significantly from zero. A rejection indicates either that the identifying assumptions fail or that units classified as non-exposed are in fact reached by the treatment. The test thus assesses the design jointly with the exposure mapping. It requires the mapping to claim that some units are non-exposed, but not that this claim be correct. We state it conditional on covariates, because spillovers of opposite sign in different regions of the covariate space cancel upon averaging. A second restriction arises if conditional parallel trends are imposed in addition: the counterfactual is then overidentified, and the two routes agree if and only if the conditional pre-treatment trends coincide across groups, which is what placebo tests in difference-in-differences analysis assess.
Finally, we derive doubly robust and Neyman-orthogonal expressions for the effects of interest, permitting estimation of the conditional means and propensity scores by machine learning, and establish root- consistency and asymptotic normality. A simulation study shows the estimators to be close to unbiased, to converge at the root- rate and to have reliable standard errors when the assumptions hold, and the overidentification test to have power against violations of conditional parallel trends. In an application to the compulsory licensing of enemy-owned patents in the United States in 1919 previously analyzed by Moser and Voena [32], we find that licensing raised patenting both in the licensed subclasses and in technologically close ones.
Mealli and Viviens [30] show that comparison-group methods identify a difference between the total effect on the treated and the spillover on the non-treated under unrestricted interference. They also show that within-group before-and-after comparisons separate the two components under a constant-mean restriction, which we replace by a trend model. Identification of direct and spillover effects under a known exposure mapping is studied in difference-in-differences and related panel designs by Clarke [14], Butts [9], Huber and Steinmayr [24], Xu [47], Hettinger et al. [21] and Sun and Xiao [42]. Cross-sectional designs under randomization or selection on observables are considered by Hudgens and Halloran [26], Tchetgen Tchetgen and VanderWeele [43], Forastiere et al. [18] and Leung and Loupos [28]. In all of these, effects defined relative to the absence of any treatment are identified through comparison units the treatment does not reach. This also applies to the synthetic control approaches with spillovers of Grossi et al. [19] and ?.
Counterfactual forecasting without a comparison group goes back to the intervention analysis of Box and Tiao [8] and is developed by Menchetti et al. [31], Cerqua et al. [12] and Botosaru et al. [7]. ?, for instance, apply such methods to assess the total effect of the COVID-19 shock on exporting firms. In their conclusion, they informally point out that these methods may also be used to investigate spillover effects, since they require no contemporaneous control group of untreated units. To the best of our knowledge, Celli et al. [11] are the first to formally analyze counterfactual forecasting under interference, and their paper is the closest to ours. They show that under specific conditions, counterfactual forecasting from pre-treatment outcomes identifies the total effect on the treated and the spillover effect on non-treated units at a given level of exposure, even if every non-treated unit is affected by the treatment. They also characterize which kinds of effects are identified when exposure to spillovers is latent, that is, unobserved for each unit, or when spillovers affect all units. We extend their identification results to condition on covariates, which also covers repeated cross sections, and derive doubly robust estimators. Furthermore, we provide conditions for decomposing the total effect on the treated into its direct and spillover components and formal tests of specific identifying assumptions. The test statistics arise as specification contrasts without interference [23], and the covariate-specific test builds on [3] and [4].
The remainder of the paper is organized as follows. § 2 to § 6 present the effects of interest, the assumptions, identification, doubly robust estimation and the testable restrictions, § 7 and § 8 the simulation study and the empirical application, and § 9 concludes.
Causal effects of interest
We consider units observed in pre-treatment periods and one post-treatment period , and denote by the outcome and by a unit’s own treatment, which is realized between and . Let be the treatment vector of all units other than . Rather than restricting the interference structure, we summarize it by an exposure mapping in the sense of Aronow and Samii [5], that is, a function
which maps the treatments of all other units into a low-dimensional measure of how intensely unit is reached by them. Here collects the characteristics determining which units can reach , such as spatial coordinates or network positions, and is a finite set containing the element , which denotes the absence of exposure. Leading examples are the share of treated households in a village or an indicator for having a treated neighbour in a network. Potential outcomes in the sense of Neyman [33] and Rubin [40] are indexed by own treatment and exposure, , which replaces the no-interference part of SUTVA by the weaker restriction that is a sufficient summary of for unit ’s outcome. See Halloran and Struchiner [20] and Manski [29] for the general formulation of interference. The observed post-treatment outcome is . We also observe covariates , which may be time-varying, in which case collects the values across the periods considered. Extrapolating the counterfactual outcome is a forecasting problem, in which post-treatment covariate values such as seasonality or local economic conditions are potential predictors. The requirement is that be unaffected by and , which is innocuous for pre-treatment values but needs scrutiny for post-treatment ones, as discussed without interference by Caetano et al. [10]. Interference enlarges the set of potentially affected covariates, since a post-treatment covariate may respond to the treatment of others as well as to a unit’s own.
Since interference generally rules out comparing a unit’s outcome to a world in which only that unit is non-treated, the effects are defined relative to the benchmark in which no unit is treated. We define all parameters conditional on the covariates and obtain the aggregates by averaging over the respective subpopulation observed in the post-treatment period; we suppress in the definitions and make it explicit in the identification results. The total effect on the treated,
comprises the direct effect of own treatment and the interference, or spillover, effect of the treatment of others. We write for direct and for interference effects, superscripted for effects on the treated and for effects on the non-treated. The interference effect on the non-treated with exposure is
with aggregate . Its argument is the exposure level at which the spillover is evaluated.
Among the treated, a direct effect switches own treatment at a fixed exposure level and an interference effect switches exposure at a fixed level of own treatment,
where the argument of each effect is the level at which the variable not switched is held, the switched one moving between its realized value and zero. The total effect then admits the two decompositions
which differ in the level at which the argument not being switched is held, and which coincide when own treatment and exposure do not interact, the interaction being . Which decomposition is of interest depends on the policy question. is the effect of treating a unit in the realized configuration of the program, whereas is the effect of treating it in isolation, which is the relevant quantity when the program is to be scaled down or implemented elsewhere. measures how much of the total effect is due to the treatment of others.
Throughout, we work with conditional mean outcomes rather than with unit-level differences, which keeps the analysis applicable to repeated cross sections, where a within-unit difference across periods cannot be formed. Let index the period, let a cell be a subpopulation defined by a value of , and write for the conditional mean outcome of cell in period . A cell is observed in every period, while the units composing it and their covariates may differ across periods, which is what the estimation of § 5 has to accommodate.
Identifying assumptions
Assumption 1 (No anticipation and consistency) for and .
Assumption 1 rules out that outcomes prior to the treatment respond to the treatment of any unit, such that pre-treatment outcomes are realizations of irrespective of a unit’s eventual treatment and exposure. Under interference the condition is stronger than its counterpart without spillovers, since it also excludes anticipation of the treatment of others, but it concerns the timing of the response alone and places no restriction on the interference structure. It restricts outcomes, so units may learn of the treatment in advance as long as their pre-treatment outcomes do not respond to it.
Assumption 2 (Valid extrapolation) For a cell and all in its support,
where is a known functional of the pre-treatment outcomes of cell given .
Assumption 2 states that the counterfactual conditional mean outcome in the absence of any treatment can be predicted from the pre-treatment outcomes of the same cell. For a polynomial trend fitted by least squares over the pre-treatment periods, that is a regression of on whose fitted value at is taken as the forecast, is the linear combination
with projection weights that depend neither on nor on the cell. For and two pre-treatment periods this gives , the leading case below, equivalent to a constant mean change of across consecutive periods, and may be chosen by cross-validation. More generally, may be any forecasting rule that is unbiased on average, see Botosaru et al. [7], and further pre-treatment periods permit placebo checks of the rule itself. With panel data may also be built from the unit’s own outcome path, for a known satisfying (6); in repeated cross sections weighted conditional means as in (7) are the natural choice. The assumption restricts the evolution of within one cell, which is why interference leaves it intact. Conditioning on covariates makes it more plausible, allows trends to differ with observed characteristics and permits the cell’s covariate composition to change across periods.
The next two assumptions transfer a counterfactual across cells and are needed only for the decompositions of the total effect. Assumption 3 is an effect homogeneity condition across treatment groups, Assumption 4 a selection-on-observables condition for exposure among the treated. The first carries the spillover from the non-treated to the treated and the second the pure direct effect from the non-exposed treated to all treated, which are the two routes of Proposition 2.
Assumption 3 (Spillover homogeneity across treatment groups) For all and in the support among the treated,
and .
Assumption 4 (Outcome homogeneity across exposure levels among the treated) For all and in the support among the treated,
and .
Assumption 3 states that treated and non-treated units sharing the same exposure and covariates experience the same average spillover, and Assumption 4 that exposure is as good as randomly assigned among the treated given covariates, as far as the outcome under non-exposure is concerned. Both fail when the relevant quantity differs along unobserved characteristics in which the compared cells differ, which is the case when treatment and exposure are selected on such characteristics. Conditioning on a rich set of covariates is the only remedy, which motivates the adjustment of § 5. Their second parts require common support in exposure, discussed in § 4 and frequently the binding constraint.
Assumption 5 (Conditional parallel trends) For all and in the support among the treated,
and has common support across the cells and .
Assumption 5 is a conditional parallel trends assumption, see e.g. Abadie [1] and Lechner [27], stated for the potential outcome in the absence of any treatment. We impose it only as an optional restriction, which overidentifies the spillover effect and generates a testable implication.
Identification
The total effect on the treated and the spillover on the non-treated follow from trend stability within the respective cell alone. Neither requires a comparison group, and the two are identified by the same argument applied to different cells. The result is conditional on the covariates, and the aggregates follow by averaging over the post-treatment covariate distribution of the cell considered.
Proposition 1 (Total and spillover effects) Under Assumptions 1 and 2 for the cell ,
where and denote the treated cell and the non-treated cell with exposure , and the aggregates follow by averaging over the post-treatment covariate distribution of the respective cell.
Identification thus requires nothing beyond the conditional mean outcomes of a single cell: the post-treatment mean minus a prediction of what it would have been had no unit been treated, formed from the cell’s own pre-treatment means. No comparison group and no common support condition across cells are needed, and interference is left unrestricted beyond (1). Celli et al. [11] establish both results without covariates; the conditional statement adds that trends may differ across observed characteristics and that the covariate composition of a cell may change across periods. Running through conditional means rather than within-unit differences, it also applies to repeated cross sections, requiring only that cell membership be observable in every period, which holds whenever treatment and exposure are defined at the level of a region, village or block.
The pre-treatment conditional means enter (8) evaluated at the covariate values of the post-treatment cell and must therefore be reweighted whenever the covariate composition of the cell changes across periods. This is the generic case in repeated cross sections and in unbalanced panels, and it is what the doubly robust estimation of Section 5 delivers. Only in a balanced panel with a unit-level covariate vector do the aggregates collapse, under (7), to group means of the within-unit contrast . For two pre-treatment periods and a linear trend this contrast is the second difference , and the aggregates are and without any covariate adjustment.
Proposition 2 (Decompositions of the total effect) Let Assumption 1 and Assumption 2 hold for .
(i) If Assumption 2 holds for at each exposure level occurring among the treated and Assumption 3 holds, then
where .
(ii) If Assumption 2 holds for and Assumption 4 holds, then
Each part delivers both components of a decomposition in (5), as the one that is transferred determines the other as a residual from : part (i) the interference effect on the treated absent their own treatment, the contrast of with , and part (ii) the pure direct effect. Both transfer a conditional effect from one cell to the covariate distribution of another, which is where machine learning adjustment enters, and differ in the direction of the transfer. By (4) and (5), neither decomposition requires a restriction on the interaction between own treatment and exposure, since each holds one argument fixed; the interaction is identified as when both apply.
Common support in exposure is typically the binding constraint, and it binds differently for the two parts: part (i) requires non-treated units at the exposure levels occurring among the treated, part (ii) treated units that are not exposed at all. Consider a conditional cash transfer program such as PROGRESA, where interference operates within the village [2]. Eligible households in a treated village receive the transfer, so a treated household linked only to ineligible non-recipients may not exist and the common support condition in Assumption 4 fails. Assumption 3 remains plausible there, since non-eligible households in treated villages are non-treated and as exposed as the treated ones. Designs that do deliver common support randomize the share of treated units across clusters.
Assumption 4 extends part (ii) from the non-exposed treated to all treated. Without it, in (10) and still identify the pure direct and the interference effect for the subpopulation , which needs nothing beyond Assumptions 1 and 2. When common support fails, or when the homogeneity conditions are implausible, the analysis is confined to the total effect on the treated and the spillover effect on the non-treated, which rest on Assumptions 1 and 2 alone. We regard these as the main parameters and the decompositions as available only under favourable designs. Finally, suppose the researcher is willing to impose Assumption 5 in addition, in which case the conditional spillover is overidentified.
Proposition 3 (Overidentification under parallel trends) Under Assumptions 1, 2 for and 5,
If Assumption 2 holds for as well, expression (11) coincides with the expression of Proposition 1 if and only if almost surely.
The two routes differ only in whose pre-treatment trend is used to extrapolate the counterfactual of the non-treated cell, its own or that of the treated. They therefore agree exactly when the conditional trends extrapolated from the pre-treatment periods coincide across the two groups, which is what placebo tests in conventional difference-in-differences analysis assess, and which by Assumption 1 involves only pre-treatment outcomes and can thus not be contaminated by spillovers. We treat (11) as a source of a testable restriction rather than as a substitute for Proposition 1, since there is no reason to expect the pre-treatment trend of the treated to approximate that of a non-treated cell better than the cell’s own.
Doubly robust estimation by double machine learning
All parameters of § 4 require averaging a conditional mean identified in one cell over the covariate distribution of another: the decompositions of Proposition 2 across treatment or exposure cells, and the aggregates of Proposition 1 across periods whenever a cell’s covariate composition changes. We therefore derive an expression that is doubly robust [37, 36] and Neyman orthogonal [34], which permits machine learning estimation of the nuisance parameters. All objects of interest are of the following form. Let and be two disjoint cells defined by values of , which we call the donor and the target cell, let be an observed random variable and let with the indicator function. We define within the probabilities and as well as the conditional mean . The parameter is , a conditional mean identified in the donor cell averaged over the covariate distribution of the target cell. The covariates may include pre-treatment outcomes, which by Assumption 1 are unaffected by treatment and exposure and are typically the most informative predictors here.
Proposition 4 (Doubly robust score). Let be bounded away from zero and one on the support of and let be square integrable. Then solves for
and is Neyman orthogonal with respect to and .
Each parameter of § 4 is a linear combination of terms (12) with for a single period, as (12) is linear in and in . Writing the exposure level as a superscript and the period as a subscript, , and , the aggregate of Proposition 1 and the transfer in (9) are
The first equality in each case averages (8) over the covariates of the target cell by the law of iterated expectations. The second inserts (7) and uses that is the conditional mean of the observed variable in the donor cell , so that its average over the covariates of the target cell is . In the first line donor and target are the same cell in different periods, so its own pre-treatment means are reweighted to its post-treatment covariate distribution. At the two coincide and is the cell mean of . In the term with , for instance, is the mean outcome of the treated in the last pre-treatment period and is that conditional mean averaged over the covariates of the post-treatment treated. In the second line the donor and the target differ in treatment status at a common exposure level and period, so the conditional spillover is carried from the non-treated to the treated. In a balanced panel with a unit-level covariate vector the combination can be formed within units, so each line reduces to a single term with . The remaining parameters are of the same form. Appendix A gives the split of by exposure used in (10) and the cells behind the two test statistics of § 6, each of which is again a linear combination of terms (12) with a donor and a target cell defined by values of .
Estimation proceeds by cross-fitting as in Chernozhukov et al. [13]. We split the sample into folds and estimate by regressing on in the donor cell, and within , in all folds but one. Any machine learner satisfying the rate condition of Assumption 6 may be used, such as penalized regression (Tihonov, [44]; Belloni et al., [6]), random forests (Wager and Athey, [46]), neural networks (Farrell et al., [17]) or an ensemble (van der Laan et al., [45]). We then evaluate (12) in the held-out fold and average over folds. The conditional means entering (11) are estimated in the same way. Cross-fitting removes the own-observation bias of the nuisance estimates, so that the rate condition of Assumption 6(d) is all the machine learner must satisfy.
Assumption 6 (Regularity) Units are sampled independently and the outcomes have finite fourth moments. and are bounded away from zero and one on the relevant support. The conditional variance of given is bounded away from zero. The nuisance estimators are consistent and satisfy .
Interference induces dependence across units in the outcomes, such that Assumption 6(a) refers to the sampling of units and their characteristics, with exposure a fixed function of the realized assignment, as in the assignment-conditional perspective of Sävje et al. [41]. Under spatial or network dependence, the variance is clustered at the level at which the exposure mapping operates. In the application of § 8 this is the branch of the patent classification, within which a subclass can reach another.
Theorem 1 (Asymptotic normality) Under Assumptions 1, 2 and 6, the cross-fitted estimators of , and are -consistent and jointly asymptotically normal, with a covariance matrix given by that of the corresponding scores and consistently estimated by its empirical analogue. The same holds for under Assumption 3 and for and under Assumption 4, by the delta method applied to (9) and (A.1).
Theorem 1 takes the weights in (7) as known, which holds for a polynomial trend of given order . When is selected by cross-validation, the candidate orders are bounded by the number of pre-treatment periods and thus form a finite set. The asymptotic distribution is unaffected if the population cross-validation criterion has a unique minimizer , such that its value at any other order exceeds that at by a positive margin. Any consistent estimator of the criterion then selects with probability approaching one. On this event, the estimator coincides with the one based on the known order , and the two therefore share the limiting distribution in Theorem 1.
The weights may also depend on an estimated parameter. An example is the damped trend , with weights and . It nests the level rule for and the linear rule for . The parameter is the autoregressive coefficient of the first differences of the mean outcomes of cell across the pre-treatment periods, which requires at least three such periods. If is -consistent, all estimators involving remain -consistent and asymptotically normal. Each such parameter contains the term , where denotes the target cell and the cell in period . Its influence function therefore gains the term , where denotes the influence function of . This term is of the same order as the score and enters the asymptotic variance. Standard errors are therefore obtained from the sum of the influence functions.
Testable restrictions
Since the spillover is zero for units classified as non-exposed, the framework implies the restriction
A rejection indicates either that Assumption 2 fails for that cell or that (1) is not a sufficient summary of the interference structure, such that units classified as non-exposed are in fact reached by the treatment. The restriction thus assesses the design jointly with the exposure mapping, and requires the mapping to claim that some units are non-exposed but not that the claim be correct. We state it conditional on , because a misclassification concentrated in a region of the covariate space may be small on average.
A second restriction follows from Proposition 3. If Assumption 5 is imposed in addition to trend stability in both subpopulations, the conditional spillover is overidentified, and the two routes agree if and only if
the equality across groups of the conditional trends extrapolated from the pre-treatment periods, which for two such periods and a linear trend is the equality of the conditional pre-treatment first differences. This is what placebo tests assess in conventional difference-in-differences analysis.
We aggregate the conditional restriction into a pair of global statistics following Armendariz and Huber [4], who build on Apfel et al. [3]. Let denote the conditional quantity restricted to zero under the respective null and define
both of which are zero under the null. The quadratic term ensures consistency against all alternatives and the linear term a non-degenerate limiting distribution under the null, while the pair is required because a single statistic vanishes whenever the two components offset each other. The orthogonal score is
where is the second term in (12) with , the target cell being in both cases and the donor cell for (14) and the cells listed in Appendix A for (15), and is the share of treated units in . Under Assumption 6, the additional condition and the conditions of Armendariz and Huber [4], the cross-fitted estimates of and are jointly asymptotically normal and mirror images of each other under the null. Then converges to with and the test rejects at level if . Joint testing across exposure cells stacks the statistics and applies Romano and Wolf [38]. Joint validity of the assumptions implies the restriction; the converse requires excluding that two non-zero biases coincide, a faithfulness condition in the sense of Pearl [35] invoked for the same purpose in Huber and Kueck [22] and Huber and Oel [23]. A zero where exposure is believed positive is consistent with no spillover and with a spillover offsetting a failure of trend stability, which is why estimates are reported across all exposure cells.
Notes: ‘bias’, ‘sd’ and ‘rmse’ are the Monte Carlo bias, standard deviation and root mean squared error of the estimator relative to the population effect, ‘avse’ is the average estimated standard error, and the last column gives the rejection rate of the test of (15) at the five percent level, which holds if and only if . Assumption 2 holds if and only if . The number of observed unit-period rows is about . Nuisances are estimated by cross-fitted ridge and penalized logistic regression, .
Simulation study
In this section, we consider a simulation study based on repeated cross sections. We draw units in clusters of five, independent standard normal covariates fixed at the unit level and an unobservable . A cluster is activated if , with its mean of and a cluster-level shock, and a unit in an activated cluster is treated if with logistic, so selection depends on unobservables. Exposure is binary, G = I{\text{at least one other unit in the cluster is treated}}, so non-treated units in activated clusters are exposed and exposure has common support across treatment groups. Potential outcomes in the absence of any treatment are for , that is , with and . The observed post-treatment outcome adds a direct effect of one, a spillover and an interaction , so Assumption 3 holds while own treatment and exposure interact. Each unit enters period with probability and only the selected rows are observed, so the covariate composition of every cell differs across periods and no within-unit difference can be formed.
As the groups differ in their composition in given , the conditional pre-treatment trend of a cell is , so Assumption 5 and hence (15) hold if and only if . The second difference of the loading is , so Assumption 2 holds if and only if . We report all four combinations of and . With two pre-treatment periods and a linear trend, (7) is : each cell is extrapolated from its own two conditional means , each a cross-fitted ridge regression Tibshirani, 1963 on the rows of that cell and period. The parameters estimated are and as in (13) and the direct effect of Proposition 2, where (9) has no term at , with population values 2.42, 1.00 and 1.47. Estimation follows Section 5.
The nuisances of the design are estimated as follows. Every is a cross-fitted ridge regression on the rows of the donor cell and every a cross-fitted -penalized logistic regression on the union of the two cells, with three folds and propensity scores trimmed at 0.02 and 0.98 as in Crump et al. [16] and Huber et al. [25]; each is the sample mean of (12), the aggregates are the linear combinations in (13) with standard errors from the corresponding influence functions, and follows by the delta method. For the test of (15), is the difference between the extrapolated conditional trends of and of the treated, evaluated on the post-treatment treated.
Table 1 reports the results of 300 replications for . When the three estimators are close to unbiased and their root mean squared error halves when the number of units quadruples, as implied by the -rate of Theorem 1. The average estimated standard error is within a tenth of the Monte Carlo standard deviation, so the influence functions of § 5 deliver reliable inference in a design in which every aggregate requires reweighting across periods. When all three estimators are biased by about 0.3, with opposite signs for the total and the spillover effect, because the treated and the exposed non-treated differ in their composition in , which drives the missed curvature. The overidentification test behaves as intended and responds to alone: it never rejects (15) in the 600 replications with , so it is conservative under the null, and rejects in 3.7 percent at and 71.7 percent at when . A violation of Assumption 2 through leaves the rejection rate unchanged, since the statistic uses pre-treatment outcomes alone.
| bias | sd | rmse | avse | bias | sd | rmse | avse | bias | sd | rmse | avse | Test (15) | ||
| 4000 | -0.001 | 0.156 | 0.156 | 0.177 | -0.012 | 0.177 | 0.177 | 0.188 | 0.017 | 0.301 | 0.301 | 0.322 | 0.000 | |
| 16000 | -0.007 | 0.073 | 0.074 | 0.079 | -0.002 | 0.086 | 0.086 | 0.084 | -0.001 | 0.144 | 0.143 | 0.149 | 0.000 | |
| 4000 | -0.007 | 0.164 | 0.164 | 0.186 | -0.014 | 0.182 | 0.182 | 0.197 | 0.010 | 0.314 | 0.314 | 0.343 | 0.037 | |
| 16000 | -0.008 | 0.076 | 0.076 | 0.084 | -0.002 | 0.093 | 0.092 | 0.089 | 0.002 | 0.150 | 0.150 | 0.157 | 0.717 | |
| 4000 | 0.292 | 0.157 | 0.331 | 0.178 | -0.274 | 0.177 | 0.326 | 0.189 | 0.353 | 0.306 | 0.467 | 0.324 | 0.000 | |
| 16000 | 0.286 | 0.075 | 0.296 | 0.080 | -0.266 | 0.088 | 0.280 | 0.085 | 0.337 | 0.144 | 0.366 | 0.150 | 0.000 | |
| 4000 | 0.286 | 0.167 | 0.331 | 0.190 | -0.276 | 0.185 | 0.332 | 0.201 | 0.346 | 0.325 | 0.475 | 0.351 | 0.037 | |
| 16000 | 0.285 | 0.078 | 0.296 | 0.086 | -0.266 | 0.095 | 0.282 | 0.091 | 0.340 | 0.153 | 0.373 | 0.161 | 0.717 |
Table 1. Monte Carlo results, 300 replications
Empirical application
We revisit the compulsory licensing of enemy-owned patents under the Trading with the Enemy Act with the data of Moser and Voena [32]: the 7,248 chemical subclasses of the United States patent classification, with domestic patent counts as the outcome and licensing in 336 subclasses in 1919. The trend is fitted on the 15 pre-treatment periods 1904 to 1918, with 1899 to 1903 supplying the covariates. Moser and Voena [32] regress patents on treatment interacted with the post-1918 indicator, with subclass and year fixed effects and a foreign-patent control, reporting 0.151 to 0.255 additional patents per year. Their comparison group is every subclass without a licensed patent and so contains those closest to the treated, where a spillover is most likely, while identification rests on that group being unaffected. We define exposure from the classification itself: a subclass is exposed if its branch, a main class combined with the first two digits of the subclass code, contains a licensed subclass other than itself. On this definition 1,594 non-treated subclasses are exposed and 5,318 are not, and a share of the treated are exposed as well.
The panel records for each subclass the number of patents granted in each year, separately for domestic and for foreign inventors, and an indicator of whether the subclass contains a patent licensed under the Trading with the Enemy Act. The mean of the outcome over 1919 to 1939 is 0.62 patents per subclass and year. The 824 branches hold a median of nine subclasses each, and 28 percent of the treated subclasses are not exposed, so that is not empty and the common support required by Proposition 2 is available. All 19 main classes contain licensed subclasses, so the main class is too coarse a notion of proximity to leave a non-exposed cell, while the full subclass code is the unit itself; the branch is the coarsest level in between. The 23 covariates are the logged average number of own and of foreign patents over 1899 to 1901 and over 1902 to 1903, the logged branch size and 18 main-class indicators. They are pre-treatment outcomes and characteristics, which Assumption 1 makes admissible as covariates, and they lie before the fitting window of every specification reported here. For the transfer from the exposed non-treated to the exposed treated the estimated propensity score ranges from 0.02 to 0.82 with a cross-fitted McFadden pseudo- of 0.10, and for the transfer from the non-exposed cell to the 94 non-exposed treated from 0.02 to 0.27 with 0.02, so the trimming of Assumption 6(b) binds on few observations.
We estimate by (7) as a linear trend in calendar time, evaluated at the mean of 1931 to 1939. Moser and Voena [32] find a lag of six to nine years and attribute it to the time domestic firms needed to acquire the knowledge and skills to work the licensed inventions, and to the two to three years between application and grant. We do not treat the non-exposed subclasses as a cell that licensing leaves untouched, since the classification is only a proxy for technological proximity, so (9) is evaluated at both exposure levels. The data form a balanced panel, so by Proposition 1 the first three effects are means of the within-unit contrast in their own cell. The decomposition of Proposition 2(i) transfers each conditional spillover to the treated at the same exposure level and is therefore a doubly robust term of Section 5,
with in the donor cell . A conditional mean and a propensity score are therefore needed only in the two transfers, where the donor and the target cell differ. Standard errors are clustered at the branch level rather than at the subclass, the unit of observation, because the exposure mapping operates within branches, as discussed after Assumption 6.
Figure 1 plots the mean outcome of each cell together with the linear rule fitted on 1904 to 1918 and extended through 1939. The treated and the exposed non-treated lie above their own extrapolated trends in the 1930s, by 0.80 and 0.35 patents per subclass and year. The non-exposed cell lies 0.03 above its own trend.
Figure 1. Mean domestic patents per subclass and year by cell, with the linear rule fitted on 1904–1918 (light band) and extrapolated through 1939. The arrow is the gap over the post-treatment window 1931–1939 (dark band); the dotted line marks the licensing year 1919.
The order of the polynomial in (7) is selected by cross-validation inside the pre-treatment era. For each of the origins the polynomial of order is fitted on the years from 1904 to and used to predict the mean outcome over the years to , which is then compared with the realised mean in each cell. The validation years always follow the fitting years and no outcome after 1918 is used, so the exercise mimics the forecast the application performs, over fitting windows of four to seven years and a horizon of four to eight years. These are the origins at which the fitting window holds at least four years, so that every order is identified at every origin. The polynomial is fitted in centred and scaled time, since on raw calendar years the basis has a condition number above already at and a least squares routine then returns the weights of the linear rule.
Table 2 reports the results. The level rule leaves a mean prediction error of 0.125 in the non-exposed cell and 0.086 among the treated, which the linear rule reduces to and 0.058. The quadratic rule attains a comparable bias but is five to seven times as dispersed across subclasses, and the cubic rule is worse on both counts. We therefore use throughout.
| 0 | 0.086 | 0.092 | 0.125 | 0.47 | 1.10 | 0.78 |
| 1 | 0.058 | 1.30 | 1.33 | 1.69 | ||
| 2 | 0.065 | 6.55 | 7.01 | 11.07 | ||
| 3 | 0.131 | 1.932 | 60.11 | 65.82 | 111.15 |
Table 2. Cross-validation of the order inside the pre-treatment era. Mean prediction error; root mean squared error. Notes: denotes the treated subclasses, the non-treated subclasses that are exposed and those that are not. The polynomial of order is fitted on and used to predict the mean outcome over , for the four origins . The left block reports the mean prediction error within each cell, the right block its root mean square across subclasses, both averaged over origins. is the level rule . No outcome after 1918 is used.
The estimators are those of (18) and the nuisance functions are estimated as in the simulation, every by a cross-fitted ridge regression on the rows of the donor cell and every by a cross-fitted -penalized logistic regression on the union of the two cells, with the same trimming at 0.02 and 0.98 and with five folds in place of three. Both transfers depend on the assignment of subclasses to folds, which matters here because only 94 treated subclasses are non-exposed. Each is therefore reported as the median over nine fold draws, and its standard error as the median of across those draws. This is the aggregation of Chernozhukov et al. [13].
Table 3 reports the estimates of the effects and the placebo estimates. Licensing raised domestic patenting in a treated subclass by 0.799 (0.105) patents per year, which is significant at the one percent level. In an exposed non-treated subclass, patenting rose by 0.354 (0.138), which is significant at the five percent level. Both effects are sizeable relative to the mean of 0.62 patents per subclass and year over 1919 to 1939. The non-exposed subclasses gain 0.032 (0.048) on average, which is statistically insignificant. Using all non-treated subclasses as the comparison group, the estimated effect of licensing on the treated subclasses amounts to 0.693 (0.107). By construction, this falls short of the total effect by the average spillover among the non-treated, which amounts to 0.107 (0.049) and is significant at the five percent level. The decomposition attributes 0.418 (0.120) of the total effect on the treated to the direct channel and 0.382 (0.094) to exposure, both significant at the one percent level. The direct channel thus accounts for slightly more than half of the total effect. The second component exceeds because each transfer evaluates the spillover of a non-treated cell at the covariates of the treated with the same exposure level. At these covariates, the exposed cell contributes 0.419 (0.128) rather than its unweighted mean of 0.354, and the non-exposed cell contributes (0.064) rather than 0.032. The spillover in the non-exposed cell is thus close to zero on average but positive at the covariate values of the non-exposed treated, so both non-treated groups are contaminated.
| pre | post | |||||
| 1904–1918 | 1931–1939 | 0.799*** | 0.418*** | 0.382*** | 0.354** | 0.032 |
| (0.105) | (0.120) | (0.094) | (0.138) | (0.048) | ||
| placebo: extrapolation within the pre-treatment era | ||||||
| 1904–1916 | 1917–1918 | 0.030 | -0.001 | 0.031*** | 0.011 | 0.008 |
| (0.028) | (0.032) | (0.012) | (0.016) | (0.013) |
Table 3. Compulsory licensing: estimates and placebo test
The placebo test in Table 3 applies the same estimators entirely within the pre-treatment era, fitting the rule on the thirteen years 1904 to 1916 and extrapolating to 1917 and 1918. The total effect on the treated is 0.030 (0.028) and the direct effect −0.001 (0.032), against 0.80 and 0.42 in the main specification, and the two spillover effects on the non-treated are 0.011 (0.016) and 0.008 (0.013). Only the interference effect on the treated, 0.031 (0.012), differs from zero, and it is a twelfth of the 0.382 of the main specification.
Notes: both rows use the linear rule and the covariates described above, with branch-clustered standard errors in parentheses and the two transfers aggregated over nine fold draws. and are the mean contrasts in the exposed and in the non-exposed non-treated cell, while the decomposition reported under and transfers each of them to the treated at the same exposure level, as in (18). Stars denote significance at the ten (), five () and one () percent level, based on the normal approximation to the ratio of the estimate to its standard error.
Conclusion
Under interference, comparison-group methods identify only the difference between the total effect on the treated and the spillover effect on the non-treated. We have shown that extrapolating the counterfactual conditional mean within a group identifies both effects separately, in repeated cross sections as in panels and without uncontaminated comparison units. The argument rests on no anticipation and on a valid extrapolation of the pre-treatment trend of the cell considered. Decomposing the total effect into a direct and an interference component is more demanding. It requires effect homogeneity conditional on observables across treated and non-treated units at the same exposure level, as well as common support in exposure, which is why we regard the total effect on the treated and the spillover on the non-treated as the main parameters of the framework.
The framework delivers two testable restrictions. The spillover must be zero for the units the exposure mapping classifies as non-exposed, which assesses the identifying assumptions jointly with the measurement of exposure. If conditional parallel trends are imposed in addition, the conditional spillover is overidentified, and the two routes agree if and only if the extrapolated pre-treatment trends coincide across groups. We derived doubly robust and Neyman-orthogonal expressions for all parameters, which permit estimating the conditional means and the propensity scores by machine learning, and established root- consistency and asymptotic normality. The simulation study confirms this behaviour and shows the overidentification test to have power against violations of conditional parallel trends.
In the application to the compulsory licensing of enemy-owned patents in the United States, licensing raised domestic patenting in a licensed subclass by 0.80 patents per year and in a technologically close one by 0.35. Against all non-treated subclasses the treated gain 0.69, which understates the total effect by the average spillover in that comparison group. Two limitations remain. The decomposition rests on an effect homogeneity condition that the data cannot test, and the extrapolation over a horizon of thirteen to twenty-one years is only as good as the linear trend it assumes, which the placebo test checks at shorter horizons alone.
Use of AI tools. Generative AI was used to improve the language of the manuscript and to assist with the code for the simulation and the application.
Instantiations of the doubly robust score
Two further instances complete the list. For (10) the target average is over all treated, which we split by exposure,
where . The first term needs no adjustment. The second carries the conditional pure direct effect from the non-exposed to the exposed treated, again as a linear combination of period-specific terms with donor cells and target . The statistic underlying the test of (14) is of the same form with target and donor cells , and the statistic underlying (15) combines the donor cells and for with the same target. In a balanced panel with a unit-level covariate vector each combination reduces to a single term. The transfer in (A.1) becomes and the statistic underlying the test of (14) becomes , both with . The statistic underlying (15) becomes the difference between and with , the extrapolated pre-treatment trend of a unit.
Proofs
Proof of Proposition 1. By Assumption 1, for in every cell, such that the pre-treatment conditional means are conditional means of and is identified. Assumption 2 then gives . With and among the treated, , and with and in that cell the same argument gives . The aggregates are the averages of the conditional effects over the covariate distribution of the respective cell in the post-treatment period, by definition in (2) and (3). If that distribution is the same in all periods, then for all by the law of iterated expectations, such that under (7) the aggregates collapse to with , which in a balanced panel is the mean of a within-unit contrast. □
Proof of Proposition 2. (i) By (5), , which holds by the definitions alone. By the law of iterated expectations, Assumption 3 and ,
where the common support part of Assumption 3 ensures that is well defined at the covariate values and exposure levels occurring among the treated, and the second equality uses Proposition 1.
(ii) Applying Proposition 1 to the cell , in which , gives . Under Assumption 4 the first term of this difference does not vary with within the treated given , and the second does not either, since does not involve , such that it equals . Averaging over the covariate distribution of the treated in the post-treatment period gives , and follows from (5). The common support part of Assumption 4 ensures that is well defined on the support of among the treated.
Proof of Proposition 3. In the cell , , such that
Under Assumptions 5 and 1,
and by Assumption 2 for the last term equals , which gives (11). If Assumption 2 also holds for , then and is as in Proposition 1; the two expressions coincide if and only if the two extrapolated conditional trends coincide.
Proof of Proposition 4. Write and , both defined within . Since by Bayes’ theorem, for any integrable . Hence and, using ,
which gives . For Neyman orthogonality, let and let denote the derivative at , with and the directions of and . The direction contributes by the display above, and contributes
Since the score is linear in and smooth in , which is bounded away from one, the Gateaux derivative in a general direction is the sum of the two and hence zero.
Proof of Theorem 1. The proof is only sketched, since it closely follows the argument for the average treatment effect on the treated in Chernozhukov et al. [13]. The score (12) has the same structure as the doubly robust score for that parameter. If the covariate composition of a cell is stable across periods, the estimators of and are sample means and are -consistent and asymptotically normal by the central limit theorem under Assumption 6(a); otherwise they are linear combinations of terms of the form and covered by the argument below. For , the score (12) is linear in the parameter with Jacobian , such that by Proposition 4 and Assumption 6 the conditions of Theorem 3.1 of Chernozhukov et al. [13] hold: the empirical process term vanishes by cross-fitting and consistency of the nuisance estimators, and the bias term is bounded by the product of their estimation errors by orthogonality, which is by Assumption 6(d). Stacking the influence functions and applying the multivariate central limit theorem gives joint asymptotic normality. The results for , and follow from the delta method applied to (9) and (A.1), whose weights are estimated at the parametric rate.
References
- [1]A. Abadie. Semiparametric difference-in-differences estimators. Review of Economic Studies, 72: 1–19, 2005.DOI
- [2]M. Angelucci and G. De Giorgi. Indirect effects of an aid program: How do cash transfers affect ineligibles’ consumption? American Economic Review, 99(1):486–508, 2009.
- [3]N. Apfel, J. Hatamyar, M. Huber, and J. Kueck. Learning control variables and instruments for causal analysis in observational data. arXiv preprint 2407.04448, 2024.arxiv.org/abs/2407.04448
- [4]A. Armendariz and M. Huber. Testing effect homogeneity and confounding in high-dimensional experimental and observational studies. working paper, University of St. Gallen and University of Fribourg, 2026.arxiv.org/abs/2602.19703
- [5]P. M. Aronow and C. Samii. Estimating average causal effects under general interference, with application to a social network experiment. The Annals of Applied Statistics, 11:1912–1947, 2017.DOI
- [6]A. Belloni, V. Chernozhukov, and C. Hansen. Inference on treatment effects after selection among high-dimensional controls. The Review of Economic Studies, 81:608–650, 2014.DOI
- [7]I. Botosaru, R. Giacomini, and M. Weidner. Forecasted treatment effects. arXiv preprint 2309.05639, 2023.
- [8]G. E. P. Box and G. C. Tiao. Intervention analysis with applications to economic and environmental problems. Journal of the American Statistical Association, 70:70–79, 1975.DOI
- [9]K. Butts. Difference-in-differences with spatial spillovers. arXiv preprint 2105.03737, 2021.arxiv.org/abs/2105.03737
- [10]C. Caetano, B. Callaway, S. Payne, and H. S. Rodrigues. Difference in differences with time-varying covariates. arXiv preprint 2202.02903, 2022.arxiv.org/abs/2202.02903
- [11]V. Celli, A. Cerqua, and G. Pellegrini. Identifying treatment and spillover effects with control-based and forecast-based counterfactuals. arXiv preprint 2607.20156, 2026.arxiv.org/abs/2607.20156
- [12]A. Cerqua, M. Letta, and F. Menchetti. Losing control (group)? The machine learning control method for counterfactual forecasting. working paper, Sapienza University of Rome, 2022.
- [13]V. Chernozhukov, D. Chetverikov, M. Demirer, E. Duflo, C. Hansen, W. Newey, and J. Robins. Double/debiased machine learning for treatment and structural parameters. The Econometrics Journal, 21:C1–C68, 2018.
- [14]D. Clarke. Estimating difference-in-differences in the presence of spillovers. MPRA Paper 81604, 2017.
- [15]D. Cox. Planning of Experiments. Wiley, New York, 1958.
- [16]R. Crump, J. Hotz, G. Imbens, and O. Mitnik. Dealing with limited overlap in estimation of average treatment effects. Biometrika, 96:187–199, 2009.DOI
- [17]M. H. Farrell, T. Liang, and S. Misra. Deep neural networks for estimation and inference. Econometrica, 89:181–213, 2021.
- [18]L. Forastiere, E. M. Airoldi, and F. Mealli. Identification and estimation of treatment and interference effects in observational studies on networks. Journal of the American Statistical Association, 116:901–918, 2021.arxiv.org/abs/1609.06245
- [19]G. Grossi, M. Mariani, A. Mattei, P. Lattarulo, and O. Oner. Direct and spillover effects of a new tramway line on the commercial vitality of peripheral streets. A synthetic-control approach. arXiv preprint 2004.05027, 2023.arxiv.org/abs/2004.05027
- [20]M. E. Halloran and C. J. Struchiner. Study designs for dependent happenings. Epidemiology, 2:331–338, 1991.pubmed.ncbi.nlm.nih.gov/1742381
- [21]G. Hettinger, C. Roberto, Y. Lee, and N. Mitra. Doubly robust estimation of policy-relevant causal effects under interference. Journal of the Royal Statistical Society Series C: Applied Statistics, 2024.DOI
- [22]M. Huber and J. Kueck. Testing the identification of causal effects in observational data. arXiv preprint 2203.15890, 2023.arxiv.org/abs/2203.15890
- [23]M. Huber and E.-M. Oeb. A joint test of unconfoundedness and common trends. working paper, University of Fribourg and University of Cologne, 2025.arxiv.org/abs/2404.16961
- [24]M. Huber and A. Steinmayr. A framework for separating individual-level treatment effects from spillover effects. Journal of Business & Economic Statistics, 39:422–436, 2021.
- [25]M. Huber, M. Lechner, and C. Wunsch. The performance of estimators based on the propensity score. Journal of Econometrics, 175:1–21, 2013.DOI
- [26]M. G. Hudgens and M. E. Halloran. Toward causal inference with interference. Journal of the American Statistical Association, 103:832–842, 2008.pubmed.ncbi.nlm.nih.gov/19081744
- [27]M. Lechner. The estimation of causal effects by difference-in-difference methods. Foundations and Trends in Econometrics, 4:165–224, 2011.
- [28]M. P. Leung and P. Loupos. Graph neural networks for causal inference under network confounding. arXiv preprint 2211.07823, 2025.
- [29]C. F. Manski. Identification of treatment response with social interactions. The Econometrics Journal, 16:S1–S23, 2013.
- [30]F. Mealli and J. Vivien s. Difference-in-differences in the presence of unknown interference. arXiv preprint 2512.21176, 2026.arxiv.org/abs/2512.21176
- [31]F. Menchetti, F. Cipollini, and F. Mealli. Combining counterfactual outcomes and ARIMA models for policy evaluation. The Econometrics Journal, 26:1–24, 2022.DOI
- [32]P. Moser and A. Voena. Compulsory licensing: Evidence from the trading with the enemy act. American Economic Review, 102(1):396–427, 2012.
- [33]J. Neyman. On the application of probability theory to agricultural experiments. Essay on principles. Statistical Science, Reprint, 5:463–480, 1923.
- [34]J. Neyman. Optimal asymptotic tests of composite statistical hypotheses, pages 416–444. Wiley, 1959.
- [35]J. Pearl. Causality: Models, Reasoning, and Inference. Cambridge University Press, Cambridge, 2000.DOI
- [36]J. M. Robins and A. Rotnitzky. Semiparametric efficiency in multivariate regression models with missing data. Journal of the American Statistical Association, 90:122–129, 1995.DOI
- [37]J. M. Robins, A. Rotnitzky, and L. Zhao. Estimation of regression coefficients when some regressors are not always observed. Journal of the American Statistical Association, 90:846–866, 1994.DOI
- [38]J. P. Romano and M. Wolf. Exact and approximate stepdown methods for multiple hypothesis testing. Journal of the American Statistical Association, 100:94–108, 2005.DOI
- [39]D. Rubin. Comment on ’randomization analysis of experimental data: The Fisher randomization test’ by D. Basu. Journal of the American Statistical Association, 75:591–593, 1980.
- [40]D. B. Rubin. Estimating causal effects of treatments in randomized and nonrandomized studies. Journal of Educational Psychology, 66:688–701, 1974.DOI
- [41]F. Sävje, P. M. Aronow, and M. G. Hudgens. Average treatment effects in the presence of unknown interference. The Annals of Statistics, 49(2):673–701, 2021.DOI
- [42]K. Sun and Z. Xiao. Difference-in-differences under network interference. arXiv preprint 2509.24259, 2025.arxiv.org/abs/2509.24259
- [43]E. J. Tchetgen Tchetgen and T. J. VanderWeele. On causal inference in the presence of interference. Statistical Methods in Medical Research, 21:55–75, 2012.
- [44]Andrei Nikolajevits Tihonov. Solution of incorrectly formulated problems and the regularization method. Soviet Mathematics, 4:1035–1038, 1963.
- [45]M. van der Laan, E. Polley, and A. Hubbard. Super learner. Statistical Applications in Genetics and Molecular Biology, 6:1–21, 2007.
- [46]S. Wager and S. Athey. Estimation and inference of heterogeneous treatment effects using random forests. Journal of the American Statistical Association, 113:1228–1242, 2018.arxiv.org/abs/1510.04342
- [47]R. Xu. Difference-in-differences with interference: A finite population perspective. arXiv preprint 2306.12003, 2023.
