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WorksEconomics, Econometrics and Finance

Identifying and disentangling 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-nn 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 Cox [16] and Rubin [40], 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 Mealli and Viviens [31]. 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 propose an identification approach that does not require clean controls when outcomes are observed in multiple pre-treatment periods. 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. Exposure is 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 neighbourhood. 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. Celli et al. [12] establish this identification result without covariates. 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.

Separating the total effect into its direct and spillover components is more 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-nn consistency and asymptotic normality. A simulation study shows the estimators to be close to unbiased, to converge at the root-nn 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, we find that licensing raised patenting both in the licensed subclasses and in technologically close ones, so that the comparison-group design of Moser and Voena [33] understates the total effect.

Mealli and Viviens [31] 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, and 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 [15], Butts [10], Huber and Steinmayr [25], Xu [48], Hettinger et al. [22] and Sun and Xiao [43], and in cross-sectional designs under randomization or selection on observables by Hudgens and Halloran [27], Tchetgen Tchetgen and VanderWeele [44], Forastiere et al. [19] and Leung and Loupos [29], all requiring comparison units the treatment does not reach. Counterfactual forecasting without a comparison group goes back to the intervention analysis of Box and Tiao [8] and is developed by Brodersen et al. [9], Menchetti et al. [32], Cerqua et al. [13] and Botosaru et al. [7], and applied to interference by Celli et al. [12], the paper closest to ours. They show that forecast-based counterfactuals identify total effects on the treated and exposure-specific spillovers on the non-treated without uncontaminated comparison units, and characterize what survives when exposure is latent or universal. Their results are unconditional and come without estimation theory or testing, which is what we add, along with the decomposition of the total effect and its conditions. Grossi et al. [20] pursue a related synthetic control strategy. The statistics we use arise as specification contrasts without interference (Huber and Oeb, [24]), and the covariate-specific test builds on Apfel et al. [3] and Armendariz and Huber [4].

The remainder of the paper is organized as follows. Sections 2 to 6 present the effects of interest, the assumptions, identification, doubly robust estimation and the testable restrictions, Sections 7 and 8 the simulation study and the empirical application, and Section 9 concludes.

Causal effects of interest

We consider nn units observed in K+1≥2K+1 \ge2 pre-treatment periods t∈{−K,…,−1,0}t \in\{-K,\ldots,-1,0\} and one post-treatment period t=1t=1, and denote by YtY_t the outcome and by D∈{0,1}D \in\{0,1\} a unit’s own treatment, which is realized between t=0t=0 and t=1t=1. Let D−i\mathbf{D}_{-i} be the treatment vector of all units other than ii. 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

Gi=g(D−i,Fi)∈G,(1)G_i = g(\mathbf{D}_{-i}, F_i) \in\mathcal{G}, \tag*{(1)}

which maps the treatments of all other units into a low-dimensional measure of how intensely unit ii is reached by them. Here FiF_i collects the characteristics determining which units can reach ii, such as spatial coordinates or network positions, and G\mathcal{G} is a finite set containing the element 0, 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 [34] and Rubin [41] are indexed by own treatment and exposure, Yt(d,g)Y_t(d,g), which replaces the no-interference part of SUTVA by the weaker restriction that G\mathcal{G} is a sufficient summary of D−i\mathbf{D}_{-i} for unit ii’s outcome. See Halloran and Struchiner [21] and Manski [30] for the general formulation of interference. The observed post-treatment outcome is Y1=Y1(D,G)Y_1 = Y_1(D,G). We also observe covariates XX, which may be time-varying, in which case XX 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 XX be unaffected by DD and GG, which is innocuous for pre-treatment values but needs scrutiny for post-treatment ones, as discussed without interference by Caetano et al. [11]. Interference enlarges the set of affected covariates, since a post-treatment covariate may respond to the treatment of others as well as to a unit’s own. Covariates plausibly unaffected by any treatment may therefore enter at post-treatment values, the others at pre-treatment values only.

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 T=1T = 1 in the definitions and make it explicit in the identification results. The total effect on the treated,

τT1(x)=E[Y1(1,G)−Y1(0,0)∣X=x,D=1],τT1=E[τT1(X)∣D=1],(2)\tau_T^1(x) = E[Y_1(1,G) - Y_1(0,0) \mid X = x, D = 1], \qquad\tau_T^1 = E[\tau_T^1(X) \mid D = 1], \tag*{(2)}

comprises the direct effect of own treatment and the interference, or spillover, effect of the treatment of others. We write τD\tau_D for direct and τI\tau_I for interference effects, superscripted 1 for effects on the treated and 0 for effects on the non-treated. The interference effect on the non-treated with exposure gg is

τI0(x,g)=E[Y1(0,g)−Y1(0,0)∣X=x,D=0,G=g],(3)\tau_I^0(x,g) = E[Y_1(0,g) - Y_1(0,0) \mid X = x, D = 0, G = g], \tag*{(3)}

with aggregate τI0(g)=E[τI0(X,g)∣D=0,G=g]\tau_I^0(g) = E[\tau_I^0(X,g) \mid D = 0, G = g]. Its argument gg 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,

τD1(g)=E[Y1(1,g)−Y1(0,g)∣D=1],τI1(d)=E[Y1(d,G)−Y1(d,0)∣D=1],(4)\tau_D^1(g) = E[Y_1(1,g) - Y_1(0,g) \mid D = 1], \qquad\tau_I^1(d) = E[Y_1(d,G) - Y_1(d,0) \mid D = 1], \tag*{(4)}

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

τT1=τD1(G)+τI1(0)=τD1(0)+τI1(1),(5)\tau_T^1 = \tau_D^1(G) + \tau_I^1(0) = \tau_D^1(0) + \tau_I^1(1), \tag*{(5)}

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 τD1(G)−τD1(0)=τ1(1)−τ1(0)\tau_D^1(G)-\tau_D^1(0)=\tau^1(1)-\tau^1(0). Which decomposition is of interest depends on the policy question. τD1(G)\tau_D^1(G) is the effect of treating a unit in the realized configuration of the program, whereas τD1(0)\tau_D^1(0) is the effect of treating it in isolation, which is the relevant quantity when the program is to be scaled down or implemented elsewhere. τ1(1)\tau^1(1) 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 TT index the period, let a cell CC be a subpopulation defined by a value of (D,G)(D,G), and write μt(x,C)=E[Yt∣X=x,C,T=t]\mu_t(x,C)=E[Y_t\mid X=x,C,T=t] for the conditional mean outcome of cell CC in period t∈{−K,…,0,1}t\in\{-K,\ldots,0,1\}. 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) Yt=Yt(0,0)Y_t=Y_t(0,0) for t≤0t\le0 and Y1=Y1(D,G)Y_1=Y_1(D,G).

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 Yt(0,0)Y_t(0,0) 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 CC and all XX in its support,

E[Y1(0,0)∣X,C]=ν(X,C),(6)E[Y_1(0,0)\mid X,C]=\nu(X,C), \tag*{(6)}

where ν\nu is a known functional of the pre-treatment outcomes of cell CC given XX.

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 μt(X,C)\mu_t(X,C) on (1,t,…,tP)(1,t,\ldots,t^P) whose fitted value at t=1t=1 is taken as the forecast, ν\nu is the linear combination

ν(X,C)=∑t=−K0wtμt(X,C),(7)\nu(X,C)=\sum_{t=-K}^{0}w_t\mu_t(X,C), \tag*{(7)}

with projection weights wtw_t that depend neither on XX nor on the cell. For P=1P=1 and two pre-treatment periods this gives ν=2μ0−μ−1\nu=2\mu_0-\mu_{-1}, the leading case below, equivalent to a constant mean change of Yt(0,0)Y_t(0,0) across consecutive periods, and PP may be chosen by cross-validation. More generally, ν\nu 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 ν\nu may also be built from the unit’s own outcome path, ν(X,C)=f(Y0,…,Y−K,X,C)\nu(X,C)=f(Y_0,\ldots,Y_{-K},X,C) for a known $f satisfying (6); in repeated cross sections weighted conditional means as in (7) are the natural choice. The assumption restricts the evolution of Yt(0,0)Y_t(0,0) 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 gg and XX in the support among the treated,

E⁡[Y1(0,g)−Y1(0,0)∣X,D=1,G=g]=E⁡[Y1(0,g)−Y1(0,0)∣X,D=0,G=g],\operatorname{E}[Y_1(0,g)-Y_1(0,0)\mid X,D=1,G=g]=\operatorname{E}[Y_1(0,g)-Y_1(0,0)\mid X,D=0,G=g],

and Pr⁡(D=0,G=g∣X,T=1)>0\operatorname{Pr}(D=0,G=g\mid X,T=1)>0.

Assumption 4 (Outcome homogeneity across exposure levels among the treated) For all gg and XX in the support among the treated,

E⁡[Y1(1,0)∣X,D=1,G=g]=E⁡[Y1(1,0)∣X,D=1,G=0],\operatorname{E}[Y_1(1,0)\mid X,D=1,G=g]=\operatorname{E}[Y_1(1,0)\mid X,D=1,G=0],

and Pr⁡(G=0∣X,D=1,T=1)>0\operatorname{Pr}(G=0\mid X,D=1,T=1)>0.

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 gg and XX in the support among the treated,

E⁡[Y1(0,0)−Y0(0,0)∣X,D=1]=E⁡[Y1(0,0)−Y0(0,0)∣X,D=0,G=g],\operatorname{E}[Y_1(0,0)-Y_0(0,0)\mid X,D=1]=\operatorname{E}[Y_1(0,0)-Y_0(0,0)\mid X,D=0,G=g],

*and XX has common support across the cells {D=1}\{D=1\} and {D=0,G=g}\{D=0,G=g\}.

Assumption 5 is a conditional parallel trends assumption, see e.g. Abadie [1] and Lechner [28], 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 C\mathcal{C},

τT1(X)=μ1(X,T)−ν(X,T),T={D=1},\tau^{1}_{T}(X) = \mu_{1}(X,\mathcal{T}) - \nu(X,\mathcal{T}), \qquad\mathcal{T} = \{D = 1\},
τI0(X,g)=μ1(X,Ng)−ν(X,Ng),Ng={D=0,G=g},(8)\tau^{0}_{I}(X,g) = \mu_{1}(X,\mathcal{N}^{g}) - \nu(X,\mathcal{N}^{g}), \qquad\mathcal{N}^{g} = \{D = 0, G = g\}, \tag*{(8)}

where T\mathcal{T} and Ng\mathcal{N}^{g} denote the treated cell and the non-treated cell with exposure gg, 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. [12] 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 S=Y1−∑t≤0wtYtS = Y_{1} - \sum_{t \le0} w_{t}Y_{t}. For two pre-treatment periods and a linear trend this contrast is the second difference Y1−2Y0+Y−1Y_{1} - 2Y_{0} + Y_{-1}, and the aggregates are τT1=E[S∣D=1]\tau^{1}_{T} = E[S \mid D = 1] and τI0(g)=E[S∣D=0,G=g]\tau^{0}_{I}(g) = E[S \mid D = 0, G = g] without any covariate adjustment.

Proposition 2 (Decompositions of the total effect). Let Assumption 1 and Assumption 2 hold for {D=1}\{D = 1\}.

(i) If Assumption 2 holds for {D=0,G=g}\{D = 0, G = g\} at each exposure level occurring among the treated and Assumption 3 holds, then

τI1(0)=∑g∈GqgE[τI0(X,g)∣D=1,G=g,T=1],τD1(G)=τT1−τI1(0),(9)\tau^{1}_{I}(0) = \sum_{g \in\mathcal{G}} q_{g} E\left[\tau^{0}_{I}(X,g) \mid D = 1, G = g, T = 1\right], \qquad\tau^{1}_{D}(G) = \tau^{1}_{T} - \tau^{1}_{I}(0), \tag*{(9)}

where qg=Pr⁡(G=g∣D=1,T=1)q_{g} = \Pr(G = g \mid D = 1, T = 1).

(ii) If Assumption 2 holds for {D=1,G=0}\{D = 1, G = 0\} and Assumption 4 holds, then

τD1(X,0)=μ1(X,T0)−ν(X,T0),T0={D=1,G=0},\tau^{1}_{D}(X,0) = \mu_{1}(X,\mathcal{T}^{0}) - \nu(X,\mathcal{T}^{0}), \qquad\mathcal{T}^{0} = \{D = 1, G = 0\},
τD1(0)=E[τD1(X,0)∣D=1,T=1],τI1(1)=τT1−τD1(0).(10)\tau^{1}_{D}(0) = E\left[\tau^{1}_{D}(X,0) \mid D = 1, T = 1\right], \qquad\tau^{1}_{I}(1) = \tau^{1}_{T} - \tau^{1}_{D}(0). \tag*{(10)}

Each part delivers both components of a decomposition in (5), as the one that is transferred determines the other as a residual from τT1\tau^{1}_{T}: part (i) the interference effect on the treated absent their own treatment, the contrast of (0,G)(0,G) with (0,0)(0,0), 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 τD1(G)−τD1(0)\tau_D^1(G)-\tau_D^1(0) 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, τD1(X,0)\tau_D^1(X,0) in (10) and τT1(X)−τD1(X,0)\tau_T^1(X)-\tau_D^1(X,0) still identify the pure direct and the interference effect for the subpopulation {D=1,G=0}\{D=1,G=0\}, 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 {D=1}\{D=1\} and 5,

τI0(X,g)=μ1(X,Ng)−μ0(X,Ng)−{ν(X,T)−μ0(X,T)}.(11)\tau_I^0(X,g)=\mu_1(X,\mathcal{N}^{g})-\mu_0(X,\mathcal{N}^{g})-\{\nu(X,\mathcal{T})-\mu_0(X,\mathcal{T})\}. \tag*{(11)}

If Assumption 2 holds for {D=0,G=g}\{D=0,G=g\} as well, expression (11) coincides with the expression of Proposition 1 if and only if ν(X,T)−μ0(X,T)=ν(X,Ng)−μ0(X,Ng)\nu(X,\mathcal{T})-\mu_0(X,\mathcal{T})=\nu(X,\mathcal{N}^{g})-\mu_0(X,\mathcal{N}^{g}) 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 [38, 37] and Neyman orthogonal [35], which permits machine learning estimation of the nuisance parameters. All objects of interest are of the following form. Let C\mathcal{C} and A\mathcal{A} be two disjoint cells defined by values of (D,G,T)(D,G,T), which we call the donor and the target cell, let VV be an observed random variable and let R=I{A∪C}R = I\{\mathcal{A} \cup\mathcal{C}\} with I{⋅}I\{\cdot\} the indicator function. We define within R=1R = 1 the probabilities p=Pr⁡(A∣R=1)p = \Pr(\mathcal{A} \mid R = 1) and π(X)=Pr⁡(A∣X,R=1)\pi(X) = \Pr(\mathcal{A} \mid X, R = 1) as well as the conditional mean m(X)=E[V∣X,C]m(X) = E[V \mid X,\mathcal{C}]. The parameter is ϑ(A,C;V)=E[m(X)∣A]\vartheta(\mathcal{A},\mathcal{C};V) = E[m(X) \mid\mathcal{A}], 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 π(X)\pi(X) be bounded away from zero and one on the support of A\mathcal{A} and let mm be square integrable. Then ϑ(A,C;V)\vartheta(\mathcal{A},\mathcal{C};V) solves E[ψ]=0E[\psi] = 0 for

ψ=I{A}pm(X)+I{C}π(X)(1−π(X))p{V−m(X)}−ϑ(A,C;V),(12)\psi= \frac{I\{\mathcal{A}\}}{p}m(X) + \frac{I\{\mathcal{C}\}\pi(X)}{(1-\pi(X))p}\{V-m(X)\} - \vartheta(\mathcal{A},\mathcal{C};V), \tag*{(12)}

and ψ\psi is Neyman orthogonal with respect to mm and π\pi.

Each parameter of Section 4 is a linear combination of terms (12) with V=YtV = Y_t for a single period, as (12) is linear in VV and in mm. Writing the exposure level as a superscript and the period as a subscript, Tt={D=1,T=t}\mathcal{T}_t = \{D = 1,T = t\}, Ttg={D=1,G=g,T=t}\mathcal{T}_t^g = \{D = 1,G = g,T = t\} and Ntg={D=0,G=g,T=t}\mathcal{N}_t^g = \{D = 0,G = g,T = t\}, the aggregate of Proposition 1 and the transfer in (9) are

T11=E[μ1(X,T)∣T1]−E[ν(X,T)∣T1]=E[Y1∣T1]−∑t≤0wtϑ(T1,Tt;Yt),\mathcal{T}_{1}^{1} = E[\mu_1(X,\mathcal{T}) \mid\mathcal{T}_1] - E[\nu(X,\mathcal{T}) \mid\mathcal{T}_1] = E[Y_1 \mid\mathcal{T}_1] - \sum_{t \le0} w_t\vartheta(\mathcal{T}_1,\mathcal{T}_t;Y_t),
E[τ10(X,g)∣T1g]=E[μ1(X,Ng)∣T1g]−E[ν(X,Ng)∣T1g]=ϑ(T1g,N1g;Y1)−∑t≤0wtϑ(T1g,Ntg;Yt).(13)E[\tau_1^0(X,g) \mid\mathcal{T}_1^g] = E[\mu_1(X,\mathcal{N}^g) \mid\mathcal{T}_1^g] - E[\nu(X,\mathcal{N}^g) \mid\mathcal{T}_1^g] = \vartheta(\mathcal{T}_1^g,\mathcal{N}_1^g;Y_1) - \sum_{t \le0} w_t\vartheta(\mathcal{T}_1^g,\mathcal{N}_t^g;Y_t). \tag*{(13)}

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 μt(X,C)\mu_t(X,\mathcal{C}) is the conditional mean m(X)=E[Yt∣X,Ct]m(X) = E[Y_t \mid X,\mathcal{C}_t] of the observed variable V=YtV = Y_t in the donor cell Ct\mathcal{C}_t, so that its average over the covariates of the target cell is ϑ\vartheta. 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 t=1t = 1 the two coincide and ϑ\vartheta is the cell mean of Y1Y_1. In the term with t=0t = 0, for instance, m(X)=E[Y0∣X,D=1,T=0]m(X) = E[Y_0 \mid X,D = 1,T = 0] is the mean outcome of the treated in the last pre-treatment period and ϑ\vartheta 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 V=SV = S. The remaining parameters are of the same form. Appendix A gives the split of T10(0)\mathcal{T}_1^0(0) by exposure used in (10) and the cells behind the two test statistics of Section 6, each of which is again a linear combination of terms (12) with a donor and a target cell defined by values of (D,G,T)(D,G,T).

Estimation proceeds by cross-fitting as in Chernozhukov et al. [14]. We split the sample into LL folds and estimate mm by regressing VV on XX in the donor cell, and π\pi within R=1R = 1, in all folds but one. Any machine learner satisfying the rate condition of Assumption 6 may be used, such as penalized regression Tikhonov, [45]; Belloni et al. [6], random forests Wager and Athey, [47], neural networks Farrell et al., [18] or an ensemble van der Laan et al., [46]. 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). (a) Units are sampled independently and the outcomes have finite fourth moments. (b) π(X)\pi(X) and pp are bounded away from zero and one on the relevant support. (c) The conditional variance of VV given XX is bounded away from zero. (d) The nuisance estimators are consistent and satisfy ∥π^−π∥2⋅∥m^−m∥2=op(n−1/2)\lVert\hat{\pi}-\pi\rVert_2 \cdot\lVert\hat{m}-m\rVert_2 = o_p(n^{-1/2}).

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 Savje et al. [42]. 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 τT1\tau_T^{1}, τI0(g)\tau_I^{0}(g) and ϑ(A,C;V)\vartheta(A,C;V) are n\sqrt{n}-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 τD1(G)\tau_D^{1}(G) under Assumption 3 and for τD1(0)\tau_D^{1}(0) and τI1(1)\tau_I^{1}(1) under Assumption 4, by the delta method applied to (9) and (A.1).

Testable restrictions

Since the spillover is zero for units classified as non-exposed, the framework implies the restriction

H0(1):τI(1)(X,0)=0almost surely.(14)H_0^{(1)}:\quad\tau_I^{(1)}(X,0)=0 \quad\text{almost surely}. \tag*{(14)}

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 XX, 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

H0(2):ν(X,Ng)−μ0(X,Ng)=ν(X,T)−μ0(X,T)a.s.,(15)H_0^{(2)}:\quad\nu(X,\mathcal{N}^{g})-\mu_0(X,\mathcal{N}^{g})=\nu(X,\mathcal{T})-\mu_0(X,\mathcal{T}) \quad\text{a.s.}, \tag*{(15)}

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 δ(X)\delta(X) denote the conditional quantity restricted to zero under the respective null and define

ϑ±=E[δ(X)2±δ(X)∣D=1],(16)\vartheta^{\pm}=E\left[\delta(X)^2\pm\delta(X)\mid D=1\right], \tag*{(16)}

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

ψ±=Dp{δ(X)2±δ(X)}+{2δ(X)±1}a(W)−ϑ±,(17)\psi^{\pm} = \frac{D}{p}\left\{\delta(X)^2 \pm\delta(X)\right\} + \left\{2\delta(X) \pm1\right\}a(W) - \vartheta^{\pm}, \tag*{(17)}

where a(W)a(W) is the second term in (12) with m=δm=\delta, the target cell being A={D=1}\mathcal{A}=\{D=1\} in both cases and the donor cell C={D=0,G=0}\mathcal{C}=\{D=0,G=0\} for (14) and the cells listed in Appendix A for (15), and pp is the share of treated units in R=1R=1. Under Assumption 6, the additional condition ∥δ^−δ∥2=op(n−1/4)\left\|\hat{\delta}-\delta\right\|_2=o_p(n^{-1/4}) and the conditions of Armendariz and Huber [4], the cross-fitted estimates of ϑ+\vartheta^+ and ϑ−\vartheta^- are jointly asymptotically normal and mirror images of each other under the null. Then max⁡{t+,t−}\max\{t^+,t^-\} converges to ∣Z∣|Z| with Z∼N(0,1)Z\sim N(0,1) and the test rejects at level α\alpha if max⁡{t+,t−}>z1−α/2\max\{t^+,t^-\}>z_{1-\alpha/2}. Joint testing across exposure cells stacks the statistics and applies Romano and Wolf [39].

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 [36] invoked for the same purpose in Huber and Kueck [23] and Huber and Oeß [24]. A zero τ01(X,g)\tau^1_0(X,g) 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.

Simulation study

In this section, we consider a simulation study based on repeated cross sections. We draw nn units in clusters of five, Q=20Q=20 independent standard normal covariates XX fixed at the unit level and an unobservable U=0.7X1−0.5X2+ϵU=0.7X_1-0.5X_2+\epsilon. A cluster is activated if 0.6Xˉ1+η>00.6\bar{X}_1+\eta>0, with Xˉ1\bar{X}_1 its mean of X1X_1 and η\eta a cluster-level shock, and a unit in an activated cluster is treated if 0.5X1+0.3X3−0.2X4+U+ζ>00.5X_1+0.3X_3-0.2X_4+U+\zeta>0 with ζ\zeta 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 Yt(0,0)=X′β+λtU+α+ϵtY_t(0,0)=X'\beta+\lambda_tU+\alpha+\epsilon_t for t∈{−1,0,1}t\in\{-1,0,1\}, that is K=1K=1, with βq=0.5/q\beta_q=0.5/q and (λ−1,λ0,λ1)=(0,a,2a+c)(\lambda_{-1},\lambda_0,\lambda_1)=(0,a,2a+c). The observed post-treatment outcome adds a direct effect of one, a spillover (1+0.5X5)G(1+0.5X_5)G and an interaction 0.5DG0.5DG, so Assumption 3 holds while own treatment and exposure interact. Each unit enters period tt with probability [1+exp⁡{−(0.8tX6−0.4t)}]−1[1+\exp\{-(0.8tX_6-0.4t)\}]^{-1} 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 UU given XX, the conditional pre-treatment trend of a cell is aE[U∣X,C]aE[U\mid X,C], so Assumption 5 and hence (15) hold if and only if a=0a=0. The second difference of the loading is cc, so Assumption 2 holds if and only if c=0c=0. We report all four combinations of a∈{0,0.5}a\in\{0,0.5\} and c∈{0,0.4}c\in\{0,0.4\}. With two pre-treatment periods and a linear trend, (7) is ν(X,C)=2μ0(X,C)−μ−1(X,C)\nu(X,C)=2\mu_0(X,C)-\mu_{-1}(X,C): each cell is extrapolated from its own two conditional means μt(X,C)=E[Y∣X,C,T=t]\mu_t(X,C)=E[Y\mid X,C,T=t], each a cross-fitted ridge regression (Tikhonov, [45]) on the rows of that cell and period. The parameters estimated are τT1\tau^1_T and τ01(1)\tau^1_0(1) as in (13) and the direct effect τD1(G)=τT1−qE[τ01(X,1)∣T11]\tau^1_D(G)=\tau^1_T-qE[\tau^1_0(X,1)\mid T^1_1] of Proposition 2(i), where (9) has no term at g=0g=0, with population values 2.42, 1.00 and 1.47. Estimation follows § 5.

The nuisances of the design are estimated as follows. Every mm is a cross-fitted ridge regression on the rows of the donor cell and every π\pi a cross-fitted ℓ2\ell_2-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.. (2009) and Huber et al. [26]; each ϑ\vartheta is the sample mean of (12), the aggregates are the linear combinations in (13) with standard errors from the corresponding influence functions, and τD1(G)\tau_D^1(G) follows by the delta method. For the test of (15), δ(X)\delta(X) is the difference between the extrapolated conditional trends of {D=0,G=1}\{D = 0, G = 1\} and of the treated, evaluated on the post-treatment treated.

Table 1 reports the results of 300 replications for n∈{4000,16000}n \in\{4000, 16000\}. When c=0c = 0 the three estimators are close to unbiased and their root mean squared error halves when the number of units quadruples, as implied by the n\sqrt{n}-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 c=0.4c = 0.4 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 UU, which drives the missed curvature. The overidentification test behaves as intended and responds to aa alone: it never rejects (15) in the 600 replications with a=0a = 0, so it is conservative under the null, and rejects in 3.7 percent at n=4000n = 4000 and 71.7 percent at n=16000n = 16000 when a=0.5a = 0.5. A violation of Assumption 2 through cc leaves the rejection rate unchanged, since the statistic uses pre-treatment outcomes alone.

(a,c)(a,c)nnτT1\tau_T^1τO1(1)\tau_O^1(1)τD1(G)\tau_D^1(G)Test
biassdrmseavsebiassdrmseavsebiassdrmseavse{(15)}
(0,0)4000-0.0010.1560.1560.177-0.0120.1770.1770.1880.0170.3010.3010.3220.000
16000-0.0070.0730.0740.079-0.0020.0860.0860.084-0.0010.1440.1430.1490.000
(0.5,0)4000-0.0070.1640.1640.186-0.0140.1820.1820.1970.0100.3140.3140.3430.037
16000-0.0080.0760.0760.084-0.0020.0930.0920.0890.0020.1500.1500.1570.717
(0,0.4)40000.2920.1570.3310.178-0.2740.1770.3260.1890.3530.3060.4670.3240.000
160000.2860.0750.2960.080-0.2660.0880.2800.0850.3370.1440.3660.1500.000
(0.5,0.4)40000.2860.1670.3310.190-0.2760.1850.3320.2010.3460.3250.4750.3510.037
160000.2850.0780.2960.086-0.2660.0950.2820.0910.3400.1530.3730.1610.717

Table 1. Monte Carlo results, 300 replications. 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 a=0a = 0. Assumption 2 holds if and only if c=0c = 0. The number of observed unit-period rows is about 1.5n1.5n. Nuisances are estimated by cross-fitted ridge and penalized logistic regression, Q=20Q = 20.

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 [33]: 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 [33] 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 q=Pr⁡(G=1∣D=1,T=1)=0.72q = \Pr(G = 1 \mid D = 1, T = 1) = 0.72 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 T0T^{0} 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-R2R^2 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 ν\nu by (7) as a linear trend in calendar time, evaluated at the mean of 1931 to 1939. Moser and Voena [33] 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 S=Y1−∑t≤0wtYtS = Y_1 - \sum_{t \le0} w_tY_t 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 § 5,

τT1=E[S∣T1],τI0(1)=E[S∣N11],τI0(0)=E[S∣N10],τI1(0)=q ϑ(T11,N11;S)+(1−q) ϑ(T10,N10;S),τD1(G)=τT1−τI1(0),(18)\begin{aligned} \tau^{1}_{T} &= E[S \mid T_{1}], \qquad\tau^{0}_{I}(1) = E[S \mid\mathcal{N}^{1}_{1}], \qquad\tau^{0}_{I}(0) = E[S \mid\mathcal{N}^{0}_{1}],\\ \tau^{1}_{I}(0) &= q\,\vartheta(T^{1}_{1},\mathcal{N}^{1}_{1};S) + (1-q)\,\vartheta(T^{0}_{1},\mathcal{N}^{0}_{1};S), \qquad\tau^{1}_{D}(G) = \tau^{1}_{T} - \tau^{1}_{I}(0), \tag*{(18)} \end{aligned}

with m(X)=E[S∣X,C]m(X) = E[S \mid X,C] in the donor cell CC. A conditional mean mm and a propensity score π\pi 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 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 PP of the polynomial in (7) is selected by cross-validation inside the pre-treatment era. For each of the origins t0=1907,…,1910t_0 = 1907,\ldots,1910 the polynomial of order PP is fitted on the years from 1904 to t0t_0 and used to predict the mean outcome over the years t0+4t_0 + 4 to t0+8t_0 + 8, 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 (1,t,…,tP)(1,t,\ldots,t^P) has a condition number above 101110^{11} already at P=2P = 2 and a least squares routine then returns the weights of the linear rule.

Table 2 reports the results. The level rule P=0P = 0 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 −0.028 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 P=1P = 1 throughout.

PPmean prediction errorroot mean squared error
T\mathcal{T}N1\mathcal{N}^{1}N0\mathcal{N}^{0}T\mathcal{T}N1\mathcal{N}^{1}N0\mathcal{N}^{0}
00.0860.0920.1250.471.100.78
10.058−0.008−0.0281.301.331.69
20.065−0.029−0.0466.557.0111.07
3−0.7710.1311.93260.1165.82111.15

Table 2. Cross-validation of the order PP inside the pre-treatment era

Notes: T\mathcal{T} denotes the treated subclasses, N1\mathcal{N}^{1} the non-treated subclasses that are exposed and N0\mathcal{N}^{0} those that are not. The polynomial of order PP is fitted on [1904,t0][1904,t_0] and used to predict the mean outcome over [t0+4,t0+8][t_0+4,t_0+8], for the four origins t0=1907,…,1910t_0 = 1907,\ldots,1910. The left block reports the mean prediction error within each cell, the right block its root mean square across subclasses, both averaged over origins. P=0P = 0 is the level rule ν=μ0\nu= \mu_0. No outcome after 1918 is used.

The estimators are those of (18) and the nuisance functions are estimated as in the simulation, every mm by a cross-fitted ridge regression on the rows of the donor cell and every π\pi by a cross-fitted ℓ2\ell_2-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 (σ^s2+(ϑ^s−ϑ^)2)1/2(\hat{\sigma}_s^2 + (\hat{\vartheta}_s - \hat{\vartheta})^2)^{1/2} across those draws. This is the aggregation of Chernozhukov et al. [14].

Table 3 reports the estimates of the effects and the placebo tests. Licensing raised domestic patenting in a treated subclass by 0.799 (0.105) patents per year and in an exposed non-treated subclass by 0.354 (0.138), while the non-exposed subclasses gain 0.032 (0.048) on average. Against all non-treated subclasses together the treated gain 0.693 (0.107), understating the total effect by the average spillover of 0.107 (0.049) in that group. The decomposition attributes 0.418 (0.120) of the total effect to the direct channel and 0.382 (0.094) to exposure. The second component exceeds qτI0(1)=0.255q \tau_{I}^{0}(1) = 0.255 because each transfer evaluates a non-treated cell at the covariates of the treated at the same exposure level: the non-exposed cell contributes ϑ(T10,N10;S)=0.286\vartheta(\mathcal{T}_{1}^{0},\mathcal{N}_{1}^{0}; S) = 0.286 (0.064) rather than its unweighted mean of 0.032, and the exposed cell 0.419 (0.128). The spillover on the non-exposed subclasses is thus close to zero over that cell as a whole and positive where the treated are, so neither non-treated group is uncontaminated. The three effects on the treated differ from zero at the one percent level and the spillover on the exposed non-treated at the five percent level, while the gain of the non-exposed subclasses does not. They are sizeable against the mean of 0.62 patents per subclass and year over 1919 to 1939, and the direct channel accounts for slightly more than half of the total effect on the treated.

prepostτT1\tau_{T}^{1}τD1(G)\tau_{D}^{1}(G)τI1(0)\tau_{I}^{1}(0)τI0(1)\tau_{I}^{0}(1)τI0(0)\tau_{I}^{0}(0)
1904–19181931–19390.799***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
1904–19161917–19180.030−0.0010.031***0.0110.008
(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 P=1P = 1 and the covariates described above, with branch-clustered standard errors in parentheses and the two transfers aggregated over nine fold draws. τI0(1)\tau_{I}^{0}(1) and τI0(0)\tau_{I}^{0}(0) are the mean contrasts in the exposed and in the non-exposed non-treated cell, while the decomposition reported under τD1(G)\tau_{D}^{1}(G) and τI1(0)\tau_{I}^{1}(0) 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-nn 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,

τD1(0)=q0E[τD1(X,0)∣T0,T=1]+(1−q0)ϑ(T∖T0,T0;V),(19)\tau_D^1(0)=q_0 E[\tau_D^1(X,0)\mid\mathcal{T}^0,T=1]+(1-q_0)\vartheta(\mathcal{T}\setminus\mathcal{T}^0,\mathcal{T}^0;\mathcal{V}), \tag*{(19)}

where q0=Pr⁡(G=0∣D=1,T=1)q_0=\Pr(G=0\mid D=1,T=1). 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 {D=1,G=0,T=t}\{D=1,G=0,T=t\} and target {D=1,G≠0,T=1}\{D=1,G\ne0,T=1\}. The statistic underlying the test of (14) is of the same form with target {D=1,T=1}\{D=1,T=1\} and donor cells {D=0,G=0,T=t}\{D=0,G=0,T=t\}, and the statistic underlying (15) combines the donor cells {D=0,G=g,T=t}\{D=0,G=g,T=t\} and {D=1,T=t}\{D=1,T=t\} for t≤0t\le0 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 ϑ(T∖T0,T0;S)\vartheta(\mathcal{T}\setminus\mathcal{T}^0,\mathcal{T}^0;S) and the statistic underlying the test of (14) becomes ϑ(T1,N0;S)\vartheta(\mathcal{T}_1,\mathcal{N}^0;S), both with V=SV=S. The statistic underlying (15) becomes the difference between E[V∣X,Ng]E[V\mid X,\mathcal{N}^g] and E[V∣X,T]E[V\mid X,\mathcal{T}] with V=∑t≤0wtYt−Y0V=\sum_{t\le0}w_tY_t-Y_0, the extrapolated pre-treatment trend of a unit.

Proofs

Proof of Proposition 1. By Assumption 1, Yt=Yt(0,0)Y_t=Y_t(0,0) for t≤0t\le0 in every cell, such that the pre-treatment conditional means μt(X,C)\mu_t(X,C) are conditional means of Yt(0,0)Y_t(0,0) and ν(X,C)\nu(X,C) is identified. Assumption 2 then gives E[Y1(0,0)∣X,C]=ν(X,C)E[Y_1(0,0)\mid X,C]=\nu(X,C). With C={D=1}C=\{D=1\} and Y1=Y1(1,G)Y_1=Y_1(1,G) among the treated, τD1(X)=E[Y1(1,G)∣X,D=1,T=1]−E[Y1(0,0)∣X,D=1,T=1]=μ1(X,T)−ν(X,T)\tau_D^1(X)=E[Y_1(1,G)\mid X,D=1,T=1]-E[Y_1(0,0)\mid X,D=1,T=1]=\mu_1(X,\mathcal{T})-\nu(X,\mathcal{T}), and with C={D=0,G=g}C=\{D=0,G=g\} and Y1=Y1(0,g)Y_1=Y_1(0,g) in that cell the same argument gives τD0(X,g)\tau_D^0(X,g). 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 E[μt(X,C)∣C,T=1]=E[Yt∣C,T=t]E[\mu_t(X,C)\mid C,T=1]=E[Y_t\mid C,T=t] for all tt by the law of iterated expectations, such that under (7) the aggregates collapse to E[S∣C]E[S\mid C] with S=Y1−∑t≤0wtYtS=Y_1-\sum_{t\le0}w_tY_t, which in a balanced panel is the mean of a within-unit contrast. □

Proof of Proposition 2. (i) By (5), τT1−τD1(G)=τI1(0)=E[Y1(0,G)−Y1(0,0)∣D=1]\tau_T^1-\tau_D^1(G)=\tau_I^1(0)=E[Y_1(0,G)-Y_1(0,0)\mid D=1], which holds by the definitions alone. By the law of iterated expectations, Assumption 3 and ς(X,g)=E[Y1(0,g)−Y1(0,0)∣X,D=1,G=g]\varsigma(X,g)=E[Y_1(0,g)-Y_1(0,0)\mid X,D=1,G=g],

τI1(0)=∑g∈GPr⁡(G=g∣D=1,T=1)E[ς(X,g)∣D=1,G=g,T=1]=∑g∈GPr⁡(G=g∣D=1,T=1)E[τI0(X,g)∣D=1,G=g,T=1],\begin{aligned} \tau_I^1(0)=\sum_{g\in\mathcal{G}}\Pr(G=g\mid D=1,T=1)E[\varsigma(X,g)\mid D=1,G=g,T=1] \\ &=\sum_{g\in\mathcal{G}}\Pr(G=g\mid D=1,T=1)E[\tau_I^0(X,g)\mid D=1,G=g,T=1], \end{aligned}

where the common support part of Assumption 3 ensures that τI0(X,g)\tau_I^0(X,g) 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 {D=1,G=0}\{D=1,G=0\}, in which Y1=Y1(1,0)Y_1=Y_1(1,0), gives μ1(X,T0)−ν(X,T0)=E[Y1(1,0)−Y1(0,0)∣X,D=1,G=0]\mu_1(X,\mathcal{T}^0)-\nu(X,\mathcal{T}^0)=E[Y_1(1,0)-Y_1(0,0)\mid X,D=1,G=0]. Under Assumption 4 the first term of this difference does not vary with GG within the treated given XX, and the second does not either, since E[Y1(0,0)∣X,D=1]E[Y_1(0,0)\mid X,D=1] does not involve GG, such that it equals τD1(X,0)=E[Y1(1,0)−Y1(0,0)∣X,D=1]\tau_D^1(X,0)=E[Y_1(1,0)-Y_1(0,0)\mid X,D=1]. Averaging over the covariate distribution of the treated in the post-treatment period gives τD1(0)\tau_D^1(0), and τI1(1)=τT1−τD1(0)\tau_I^1(1)=\tau_T^1-\tau_D^1(0) follows from (5). The common support part of Assumption 4 ensures that τD1(X,0)\tau_D^1(X,0) is well defined on the support of XX among the treated.

Proof of Proposition 3. In the cell {D=0,G=g}\{D=0,G=g\}, Y1=Y1(0,g)Y_1=Y_1(0,g), such that

μ1(X,Ng)=E[Y1(0,0)∣X,D=0,G=g]+τI0(X,g).(20)\mu_1(X,\mathcal{N}^g)=E[Y_1(0,0)\mid X,D=0,G=g]+\tau_I^0(X,g). \tag*{(20)}

Under Assumptions 5 and 1,

E[Y1(0,0)∣X,D=0,G=g]=μ0(X,Ng)+E[Y1(0,0)−Y0(0,0)∣X,D=1],E[Y_1(0,0)\mid X,D=0,G=g]=\mu_0(X,\mathcal{N}^g)+E[Y_1(0,0)-Y_0(0,0)\mid X,D=1],

and by Assumption 2 for {D=1}\{D=1\} the last term equals ν(X,T)−μ0(X,T)\nu(X,\mathcal{T})-\mu_0(X,\mathcal{T}), which gives (11). If Assumption 2 also holds for {D=0,G=g}\{D=0,G=g\}, then E[Y1(0,0)∣X,D=0,G=g]=ν(X,Ng)E[Y_1(0,0)\mid X,D=0,G=g]=\nu(X,\mathcal{N}^g) and τI0(X,g)\tau_I^0(X,g) is as in Proposition 1; the two expressions coincide if and only if the two extrapolated conditional trends coincide.

Proof of Proposition 4. Write u1=I{A}/pu_1=I\{A\}/p and u0=I{C}π(X)/{(1−π(X))p}u_0=I\{C\}\pi(X)/\{(1-\pi(X))p\}, both defined within R=1R=1. Since E[u1∣X]=E[u0∣X]=π(X)/pE[u_1\mid X]=E[u_0\mid X]=\pi(X)/p by Bayes’ theorem, E[u1h(X)]=E[u0h(X)]=E[h(X)∣A]E[u_1h(X)]=E[u_0h(X)]=E[h(X)\mid A] for any integrable hh. Hence E[u1m(X)]=ϑ(A,C;V)E[u_1m(X)]=\vartheta(A,C;V) and, using E[V−m(X)∣X,C]=0E[V-m(X)\mid X,C]=0,

E[u0{V−m(X)}]=E[π(X)pE[V−m(X)∣X,C]]=0,E[u_0\{V-m(X)\}]=E\left[\frac{\pi(X)}{p}E[V-m(X)\mid X,C]\right]=0,

which gives E[ψ]=0E[\psi]=0. For Neyman orthogonality, let ηr=η0+r(η−η0)\eta_r=\eta_0+r(\eta-\eta_0) and let ∂r\partial_r denote the derivative at r=0r=0, with hmh_m and hπh_\pi the directions of mm and π\pi. The direction hmh_m contributes E[u1hm(X)]−E[u0hm(X)]=0E[u_1h_m(X)]-E[u_0h_m(X)]=0 by the display above, and hπh_\pi contributes

E[I{C}hπ(X)(1−π(X))2p{V−m(X)}]=E[hπ(X)Pr⁡(C∣X)(1−π(X))2p⋅E[V−m(X)∣X,C]]=0.E\left[\frac{I\{C\}h_\pi(X)}{(1-\pi(X))^2p}\{V-m(X)\}\right] =E\left[\frac{h_\pi(X)\Pr(C\mid X)}{(1-\pi(X))^2p}\cdot E[V-m(X)\mid X,C]\right]=0.

Since the score is linear in mm and smooth in π\pi, 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 argument closely follows the one for the average treatment effect on the treated in Chernozhukov et al. [14], as (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 τD1\tau_D^1 and τI0(g)\tau_I^0(g) are sample means and are n\sqrt{n}-consistent and asymptotically normal by the central limit theorem under Assumption 6(a); otherwise they are linear combinations of terms of the form ϑ(A,C;V)\vartheta(A,C;V) and covered by the argument below. For ϑ(A,C;V)\vartheta(A,C;V), the score (12) is linear in the parameter with Jacobian −1-1, such that by Proposition 4 and Assumption 6 the conditions of Theorem 3.1 of Chernozhukov et al. [14] 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 op(n−1/2)o_p(n^{-1/2}) by Assumption 6(d). Stacking the influence functions and applying the multivariate central limit theorem gives joint asymptotic normality. The results for τD1(G)\tau_D^1(G), τD1(0)\tau_D^1(0) and τI1(1)\tau_I^1(1) follow from the delta method applied to (9) and (A.1), whose weights Pr⁡(G=g∣D=1,T=1)\Pr(G=g\mid D=1,T=1) are estimated at the parametric rate.

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