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Estimation and Inference for Synthetic Control Methods with Spillover Effects

The synthetic control method is often used in treatment effect estimation with panel data where only a few units are treated and a small number of post-treatment periods are available. Current estimation and inference procedures for synthetic control methods do not allow for the existence of spillover effects, which are plausible in many applications. In this paper, we consider estimation and inference for synthetic control methods, allowing for spillover effects. We propose estimators for both direct treatment effects and spillover effects and show they are asymptotically unbiased. In addition, we propose an inferential procedure and show it is asymptotically unbiased. Our estimation and inference procedure applies to cases with multiple treated units or periods, and where the underlying factor model is either stationary or cointegrated. In simulations, we confirm that the presence of spillovers renders current methods biased and have distorted sizes, whereas our methods yield properly sized tests and retain reasonable power. We apply our method to a classic empirical example that investigates the effect of California's tobacco control program as in Abadie et al. (2010) and find evidence of spillovers.


Introduction
The synthetic control method is often used in treatment effect estimation with panel data where only a few units are treated and a small number of post-treatment periods are available. Current estimation and inference procedures for synthetic control methods do not allow for the existence of spillover effects, which are plausible in many applications. This paper alleviates these concerns by showing that given some knowledge about the spillover effects, it is possible to provide asymptotically unbiased estimators and inference in the presence of spillovers. Our results extend to scenarios with multiple treated units and periods, and cases with stationary or cointegrated factor models.
The synthetic control method (SCM) has gained popularity in empirical studies since its introduction in Abadie and Gardeazabal (2003). When we observe panel data with only a few treated units and post-treatment periods, the SCM can estimate treatment effects. This setting is common in program evaluation, where we often consider state-level policies and have state-level aggregate data. The SCM models the relationship between the treated and untreated units using pre-treatment data. Then the SCM uses the post-treatment data from untreated units to predict the counter-factual values of the treated unit. This process gives us the synthetic control, while the difference between the outcome and predicted counter-factual outcome is the treatment effect estimate. The SCM exploits the pre-treatment data to form better counter-factual values, and so in comparative case studies it is often favored over other program evaluation methods such as difference-in-differences. See Abadie and Cattaneo (2018) for review and comparison of econometric methods used in program evaluation.
However, the SCM and its variants assume explicitly or implicitly that untreated units are not affected by the treatment. That is, they rely on the Stable Unit Treatment Value Assumption (SUTVA). This dependence is natural since the SCM uses post-treatment control units to predict the counter-factual values of the treated units, which, however, is not always realistic. In our empirical example in Section 6, when California imposes a cigarette tax, SUTVA implies (among other things) that nobody decides to shift their cigarette purchases to Nevada.
Under SUTVA and a few other regularity conditions within a factor model, treatment effect estimators using a demeaned version of SCM are shown to be inconsistent but asymptotically unbiased by Ferman and Pinto (2019), even when the pre-treatment fit is imperfect. Unfortunately, in the presence of a spillover effect, this estimator can be severely biased. Intuitively, the reason is that post-treatment controls are contaminated by the spillover effect, resulting in a biased estimator of the counter-factual value of the treated unit in post-treatment periods, which implies a biased treatment effect estimate.
Contamination inducing bias is a standard problem in program evaluation, even within difference-indifferences and RCTs. This problem is worse for the SCM. If by chance the spillover is concentrated in control units that the synthetic control method puts significant weight on, the bias will be substantially worse than in difference-in-differences. Moreover, it is possible the spillovers propagate along the same channels as the underlying factor model, which would mean that the SCM may actively select for units which will induce bias. In our simulation section, we will explore this bias in more depth.
It is worth noting that the problem caused by spillover effects cannot fully solved by naïve methods such as not including contaminated units in estimation. This is because the contaminated units are often the most important control units that can be useful in forming the synthetic control. Simply not including them in estimation can potentially cause efficiency loss. Moreover, there are cases where most or even all control units are affected by the spillover, which cannot be solved by throwing away affected control units. This is also true for synthetic control methods that are modified to estimate treatment effects with multiple treated units, since the current methods in the literature use only the units that are not affected by the treatment in order to form the synthetic control. For examples of multivariate synthetic control methods, see Cavallo et al. (2013), Firpo and Possebom (2018), Kreif et al. (2016), Robbins et al. (2017), and Xu (2017).
The goal of this paper is to relax the SUTVA condition and to perform estimation and testing. Particularly, we look at the cases where there are spillover effects, which are defined by a Rubin model as the difference between the actual outcomes and the counterfactual ones. To facilitate estimation, we assume some knowledge about the spillover effects is known. More specifically, the treatment effect and the spillover effects are linear in some unknown parameters. We give examples where this assumption is plausible. For each unit of observation, we estimate a model between it and all the other units, using the SCM with pre-treatment data. Thanks to the known spillover structure, we obtain asymptotically unbiased estimators for the treatment and spillover effects. We also characterize the asymptotic distribution of the estimator. Unlike the current methods, our method uses information from all control units in estimation.
In addition, we propose an inferential procedure based on Andrews (2003)'s end-of-sample instability test, or P -test. We first generalize the P -test to the synthetic control method without spillover effects and then generalize it further to incorporate cases with spillover effects. Similar to the P -test, our testing procedures use the idea of approximating the null distribution of the statistic using pre-treatment data.
We give high-level conditions under which our methods are valid. Specifically, our conditions adapt to factor models with either stationary or cointegrated common factors, which are often used to justify the usage of synthetic control methods. Furthermore, we consider extensions where treatment applies to multiple units or periods, and where there are extra covariates.
We examine an empirical example from Abadie et al. (2010). In 1989 California implemented a cigarette tax. Abadie et al. (2010) gather data from 38 states starting in 1970 for comparison. They dismiss 12 states for potentially being affected by spillovers or later treatment. Despite this precaution, we find evidence of spillover effects in every year after 1990. Moreover, those spillovers appear to have a substantial impact on the treatment effect estimate in 4 of the first 5 years after treatment.
This paper mainly contributes to three developing literatures. First, it complements the fast-developing literature on synthetic control inference by relaxing SUTVA. Due to its popularity among empirical researchers, many formal results have been developed for statistical inference in similar settings. For example, Conley and Taber (2011) consider hypothesis testing in a similar data structure where only a few units are treated and both pre-and post-treatment periods are short. They consider difference-indifferences, and use control units to form the null distribution of the statistic. In this particular setting with only a few treated units, difference-in-difference estimator can be treated as a speical case of the SCM with equal weights. In Ferman and Pinto (2017) and Hahn and Shi (2017), similar ideas are used to conduct placebo tests which permute across observed units. Among all, Chernozhukov et al. (2017) is the most related to our work, since they also use outcomes across periods rather than across units like the above citations. Li (2019) proposes a testing procedure that is based on the idea of projection onto convex sets and results in Fang and Santos (2018). However, none of the papers mentioned above allows for the existence of spillover effects. Our methods provide formal statistical results in this setting, without assuming SUTVA. Furthermore, our estimation and testing procedure applies to factor models with cointegrated common factors, which is of special interest even in cases without spillover effects.
We also contribute to the literature on spillover effects. This fast-growing literature looks into both estimation of treatment effects in the presence of spillover effects, as well as estimation of spillover effects themselves. For example, Vazquez-Bare (2017) consider a framework where observations are grouped into clusters, and spillover effects are allowed within a cluster, but not across clusters. It discusses estimation of heterogeneous treatment effects as a function of the number of treated units within the same cluster, and spillover effects as a function of whether the unit is treated, and number of treated units within the same cluster. Basse et al. (2017) and Rosenbaum (2007) use randomization test for inference in the presence of spillover effects. Also see Basse et al. (2017) and Vazquez-Bare (2017) for a literature review on spillover effects. However, this literature seldom looks at the panel data setting with only a few treated units and short post-treatment periods. This limitation is in part because we usually do not have enough information about the spillover effects in this particular setting. We overcome this problem by requiring a potentially weak assumption that the spillover structures be pre-specified and follow a pattern that is linear in some underlying parameters. With that specification, we can estimate the spillover effects and perform statistical tests on the spillovers. Third, our results extend the literature on Andrews (2003)'s end-of-sample instability tests. Andrews (2003) uses data across time periods to approximate the null distribution of the test statistic, and apply this idea to OLS, IV, and GMM. Chernozhukov et al. (2017) propose a permutation test that is more general, but similar in cases where serial correlation matters. We extend this idea to the the SCM case, and further to more complicated cases with spillover effects. As Andrews and Kim (2006) extends Andrews (2003)'s results to the cointegrated cases, we also show that our method is still valid for a cointegrated factor model.

A Rubin Model with spillover effects
We consider Rubin's potential outcome model. In Rubin's model with violation of SUTVA, the potential outcomes are functions of treatment assignments on all units. Namely, the outcome of unit i at time t is where dt = (d1,t, . . . , dN,t) and di,t = 1 if unit i has been treated at time t.
We consider a standard synthetic control setting where only one unit is treated and only one period is available after the treatment is implemented. We consider cases with multiple treated units and multiple post-treatment periods in Section 4. Let unit 1 be treated between time T and T + 1, and there be another N − 1 units that are not directly treated by the policy. Thus, we observe an N × (T + 1) panel as shown in Figure 1.
In case studies, we are often interested in estimating the treatment effect α1. For example, Abadie et al. (2010) consider the direct treatment effect on California of the tobacco control policy implemented in the state. A common choice is the synthetic control estimator. Namely, we obtain the synthetic control weights by solving the optimization problem where Yt = (y1,t, . . . , yN,t) and W (1) = {(w1, . . . , wN ) ∈ R N + : w1 = 0, N j=2 wj = 1}. An estimator of the treatment effect α1 is given by i.e., the counter-factual value y1,T +1(0) is approximated by a+Y T +1 b. For this paper we use an constraint set as in the demeaned synthetic control method (Ferman and Pinto, 2019). That is, we do not restrict the intercept but require the other coefficients to be positive and sum up to one. 1

spillover structure
Throughout the paper, we assume some knowledge about the spillover effects is known. Namely, assume that the full effect vector α is a linear transformation of some unknown parameter γ ∈ R k , i.e. α = Aγ.
Typically, γ has less dimensions than α does. Here are some examples that fit in this framework.
Example 1. Assume a subset of control units, but not all of them, are equally affected by the spillover effects, i.e.  Doudchenko and Imbens (2016) for a discussion of other restriction sets.
Example 2. Assume the spillover effect shrinks as the geometric distance goes up. For i = 2, . . . , N , where di is the distance between unit 1 and unit i and b is some unknown parameter of interest. Then, we have Example 3. Assume the spillover effect is likely to take place at some known locations, but not at other locations, while the sizes of spillover effects are allowed to vary across those units. For example, assume there are potential spillovers at locations whose distance to unit 1 is less thand. Then, the treatment and spillover effect vector can also be represented by Aγ. WLOG order the units by increasing distance from unit 1, and let p the number of units experiencing spillovers. Then Thus the units indexed 2, ..., (p + 1) each experience their own size spillover effect.
The assumptions in Example 3 are often plausible. We give an empirical example in Section 6. If misspecification of the spillover structure is a concern, one can always choose an A matrix that incorporates more potential spillovers, i.e., a bigger p.

invertibility assumption
In order to back out the spillover effects, we proceed as follows. We first define the individual synthetic control weights and their limits. Namely, let where W (i) = {(w1, . . . , wN ) ∈ R N + : wi = 0, N j=1 wj = 1}. Then, let ai = plim ai, bi = plim bi, and we only consider cases where they are well-defined. We show later by Lemma 1 that ai and bi exist for each i in factor models with stationary or cointegrated common factors. In general, ai and bi do not coincide with the weights that reconstruct the factor loadings (Ferman and Pinto, 2019). where and ut = (u1,t, . . . , uN,t) . For t = T + 1, this becomes where YT +1 = (y1,T +1, . . . , yN,T +1) . We will use this equation to estimate the spillover effect.
Defining M = (I − B) (I − B), we introduce the following invertibility assumption: First note Condition IN is testable in principle. We can consistently estimate B so the data informs us of the validity of this assumption. To understand this assumption better, we replace α by Aγ in Equation (4) and have Equation (5) is the key to learning α. Under mild regularity conditions, a and B are identified from the model and learned by the synthetic control method. We do not observe uT +1, but the distribution of uT +1 can be learned using pre-treatment data under stationarity of {ut} t≥1 . Therefore, if A M A is non-singular, or equivalently, (I − B)A has full rank, we can form an estimator of γ whose limiting distribution is identified by multiplying both sides of Equation (5) . Note that we do not identify γ or α. This is because we have only one observation of the outcome in post-treatment periods.
We illustrate Condition IN in the following toy example.
Example 4. Assume there are 3 units in total, where unit 1 is treated. Let the synthetic control weight Suppose the researcher first assumes unit 2 and 3 are equally exposed to the spillover effects. That is, Then, Condition IN does not hold, because If they instead assumes only one of the controls is exposed to the spillover effects, Condition IN is satisfied in general. In this case, It can be shown that (I − B)A2 always has full rank for (w1, w2, w3) ∈ [0, 1] 3 .
This applies to more general settings. That is, if all controls are equally hit by the spillover effects, then (I − B)A does not have full rank and we lose Condition IN. Allowing a few units to be exempt from the spillover effects makes (I − B)A have full rank in general.
A more interesting case is Example 3, where we only restrict the range of spillover effects and allow the levels to vary. In this case, (I − B)A can be obtained by eliminating columns that correspond to units that are neither treated nor exposed to spillover effects. Again, as long as at least one control is not exposed to the spillover effects, (I − B)A has full rank in general. This assumption is more convincing if a moderate number of columns are eliminated from (I − B), i.e. only a few units are exposed to the spillover effects.

Estimation
We form estimators for (a, B) using synthetic control methods as in (2). We do that for each i = 1, . . Let an estimator of γ be such that Note that the FOC implies i.e. it requires that some weighted sum of the residuals to be zero. Under that condition, the treatment and spillover effect vector α can be estimated by α = A γ.
Note that Part (c) excludes polynomial time trends.
The structure of the limiting distribution is similar to the case as in Ferman and Pinto (2019), as it is inconsistent but asymptotically unbiased (i.e. that the difference between the estimator and the true value has zero mean). Note that consistent estimators are impossible because only one post-treatment period is available.
Moreover, we can form an estimator of α with possibly lower variance. For some positive definite . The corresponding estimator for α is αW = A γW . In the spirit of GMM with an efficient weighting matrix, let Ω = Cov[u1] and W e T be a consistent estimator of Ω −1 . Then an estimator of α with lower variance can be achieved by and G e = GW e . Then, we have the following results.
Proposition 1. Suppose Assumption 1 holds, WT is a consistent estimator for W , and W e T is a consistent estimator for W e . Then, αW T − (α + GW uT +1) →p 0, and specifically, α e − (α + G e uT +1) →p 0, as In practice, we need to estimate Ω, and for that we would need relatively large sample size (large T ) to have a good approximation.

The factor model as an example
Factor models are often used to justify the usage of synthetic control methods. Here we show that our assumptions are satisfied by factor models with stationary and cointegrated common factors. We follow Ferman and Pinto (2019) and consider a factor model such that for i = 1, . . . , N and t = 1, . . . , T + 1, where λt is F -dimensional common factors, and i,t is noise that is uncorrelated with λt. For notation simplicity, we write Yt(0) = (y1,t(0), . . . , yn,t(0)) , Yt = (y1,t, . . . , yn,t) , and t = ( 1,t, . . . , n,t) .
We focus on two sets of conditions in our discussion.
Remarks: 1. We show in the proof of Lemma 1 that in this case bi = arg min where ei is a unit vector with one at the i-th entry and zeros everywhere else, and W (i) = {(w1, . . . , wN ) ∈ R N + : wi = 0, j =i wj = 1}. Note that in general bi does not recover the factor structure, because µi = (µ1, . . . , µN )bi in general.
2. We do not impose any restriction on the factor loadings {µi} N i=1 except for Ωy being positive definite. In the stationary case, the key for the treatment estimator to be asymptotically unbiased and the test proposed below to be valid is to include an intercept in the optimization problem (2).
Condition CO (model with cointegrated I(1) common factors). Rewrite Equation (7) as and ηt can be either in λ 1 t or λ 0 t . Assume {(λ 0 t , t)}t≥1 is stationary, ergodic for the first and second moments, and has finite 4-th moment. Without loss of generality, Further assume for each i, yi,t(0) is such that weak convergence holds for T −1/2 y i, [rT ] (0) ⇒ νi(r), where ⇒ is weak convergence and process νi(r) is defined on [0, 1] and has bounded continuous sample path

cointegrating vector for
Yt (0), where ei is a unit vector with i-th entry being one and zeros everywhere else.
Note that Condition CO puts restrictions on the factor loadings. The restrictions are similar to those in Ferman and Pinto (2019).
The relevance of the factor model is given by the following lemma: Lemma 1. Under Condition IN, either Condition ST or Condition CO implies Assumption 1.
Thus, results derived in Thereom 1 apply to factors models with Condition ST or Condtion CO.

Inference
In this section, we discuss formal results on inference. At a high level, our test uses pre-treatment data to form the null distribution of a pre-specified post-treatment quantity. Flexibility in defining that quantity leads to a variety of hypotheses. In Section 3.1, we consider the case without spillover effects, and state the assumptions under which Andrews' P test (Andrews, 2003) is valid. In Section 3.2, we generalize P test to cases where spillover effects cannot be ignored.

Cases without spillover effects
Suppose for now there are no spillover effects, i.e. α2 = · · · = αN = 0. We want to test for the existence of treatment effect on unit 1. The null and alternative hypotheses of interest are The test procedure we consider here is the end-of-sample instability test (P -test) in Andrews (2003). The usage of Andrews' test in the context of synthetic control methods is mentioned in Ferman and Pinto (2018), where they focus on the difference-in-differences estimator. We formalize this idea and derive conditions under which Andrews' test delivers valid inference results.
We assume the α1 is independent of T under H1. That is, we consider fixed, not local, alternatives, as in Andrews (2003) and Andrews and Kim (2006). Specifically, α1 does not change as T grows, which facilitates our analysis of the test statistic under H1.
Now we translate our hypothesis into the linear formulation considered in Abadie and Gardeazabal (2003). Namely, we have A non-zero treatment effect is equivalent to a shift in the intercept a1 (or equivalently, change of the distribution of u1,t, at t = T + 1). The null and alternative hypothesis become Let the synthetic control regression residuals be The test statistic is defined by For notational simplicity, let β1 = ( a1, b 1 ) and Let P∞ be a random variable with the same distribution as and qP,1−τ be the (1 − τ )-quantile of P1(β1). The assumptions and validity of the testing procedure are established as follows.
Theorem 2. Suppose Assumption 2 holds. Then, as T → ∞, for all x in a neighborhood of qP,1−τ under H0 and H1, (c) qP,1−τ →p qP,1−τ under H0 and H1, In addition, we show the relevance of the factor model in this context by the following lemma: Lemma 2. Suppose the distribution function of P1(β1) is continuous and increasing at its (1−τ )-quantile.

Cases with spillover effects
Now we allow for non-zero spillover effects. We propose a testing procedure that is based on Andrews' P -test and accounts for the spillover effect. The null and alternative hypotheses we consider are H0 : Cα = d and H1 : Cα = d, with C and d known. For example, we want to test for the hypothesis that there is no treatment effect at the treated unit (unit 1), then we let C = (1, 0, 0, . . . , 0) ∈ R 1×N and d = 0. This effectively makes Section 3.1 a special case of our test, although Theorem 2 has slightly stronger results than Theorem 3 does. If we want to test that there is a spillover, then we can let The test statistic we consider here is P = (C α−d) WT (C α−d) for some weighting matrix WT →p W . Theorem 3. Suppose Assumption 3 holds. Then, under H0, as T → ∞, Again, we show the relevance of the factor model in this context by the following lemma: Lemma 3. Suppose the distribution function of P1(θ0) is continuous and increasing at its (1−τ )-quantile.
Then, under Condition IN, Assumption 3 is satisfied if either of these holds: (ii) Condition CO with WT = I.

Other testing procedures
When we allow for existence of non-zero spillover effects, the existing testing procedures will have poor performance. Here we intuitively explain what happens to placebo test as in Abadie and Gardeazabal (2003) and Andrews' test as in Andrews (2003) in the presence of spillover effects.
Suppose we want to test for the treatment effect being zero and are not aware of the spillover effects.
Placebo test and Andrews' test are similar in the sense that they use data to form the null distribution of u1,T +1 in order to perform hypothesis testing. The difference is that the placebo test exploits variations We look at the placebo test first. When there is no spillover effect, the distribution of u1,T +1 and distribution of { ui,T +1} N i=2 overlap asymptotically. As shown in Figure 2 Table   3 of Section 5 the empirical sizes of placebo test for T = 50 and 200 cases are not too far away from the nominal size 0.05. In essence, the placebo test becomes much more conservative and has low power as shown in Table 4. Now we consider Andrews' test. When there is no spillover effect, the distribution of u1,T +1 and distribution of { u1,t} T t=1 overlap asymptotically. As shown in Figure 3(b), when there is positive spillover effect, we underestimate the treatment effect and the density function of u1,T +1 shifts to the left, while the density of { u1,t} T t=1 doesn't, since they are pre-treatment and the spillover only happens after the treatment. This results in an invalid test.

Multiple treated units
Our method readily extends to cases where multiple units are treated. In our setting, spillover effects are not distinguished from treatment effects, since one can think of spillover as the treatment on the units that are not directly treated. With a corrected specified structure matrix A, we can perform estimation and testing just as previous sections. For example, suppose N = 4, unit 1 and unit 2 are treated, unit 3 is affected by spillover effect, and unit 4 is neither treated nor exposed to spillover effect. Then we can , and the resulting estimator γ = ( γ1, γ2, γ3) by (6) is such that γ1 and γ2 are the treatment effect estimator for unit 1 and unit 2, respectively, and γ3 is the spillover effect estimator for unit 3. Tests can be performed accordingly. If one wants to test for the hypothesis that there are no spillover effects, the null is then H0 : Cα = d, where C = (0, 0, 1, 0) and d = 0.

Multiple post-treatment time periods
Suppose now we have observations of {yi,t} for i = 1, . . . , N and t = 1, . . . , T + m. Treatment is received at t = T + 1. The model becomes Note that we do not allow for spillovers in time. That is, the treatment effect or spillover effects cannot affect future selves. For each t = T + 1, . . . , T + m, we need to specify the spillover structure matrix At.
Then, an estimator of αt is That is, we treat T +s period as T +1 and do the same procedure as before. For each t = T +1, . . . , T +m, we can perform separate tests as introduced in previous sections.
To answer simultaneous questions such as whether there is spillover effect at all, we can extend the P -test discussed above. Consider the null hypothesis H0 : Ctαt = dt for t = T + 1, . . . , T + m. Let Pt be constructed as in Section 3.2 for t = 1, . . . , T . For t = T +1, . . . , T +m, let Pt = (Ct αt−dt) WT (Ct αt−dt).
We can now form Pt+s for t = 1, . . . , T + 1. The test statistic is then P (T +1) , and we use {P (t) } T t=1 to form its null distribution.

Including covariates
Many empirical researchers are interested including extra covariates when using synthetic control methods. Our framework can be readily adapted to settings with covaraites. Suppose we have a vector of observable variables zi,t and want to estimate the treatment effects, while being worried about spillover effects. Following Li (2019), we estimate the least square coefficients for the model with the simplex constraints on bi,j and obtain coefficient estimates ( ai, bi, πi). This is done for each i.
Let gt = (z 1,t πi, . . . , z N,t πN ) . Under appropriate regularity conditions, the results of the paper apply when the intercept estimator a is replaced by a + gt at time t. For example, the treatment effects estimator now becomes

Simulation
We present Monte Carlo simulation results in this section. For each case considered, we use 1000 simulation repetitions.

Estimation with spillover effects
In this subsection we examine the finite sample performance of our estimation procedure proposed in Section 2.2. The model considered here is similar to Li (2019), where yi,t(0) follows a factor model structure. We show both stationary and I(1) case.

Stationary case
The underlying factor model is where λt = (λ1,t, λ2,t, λ3,t) , ηt = 1 + 0.5δt−1 + ν0,t, λ1,t = 0.5λ1,t−1 + ν1,t, λ2,t = 1 + ν2,t + 0.5ν2,t−1, λ3,t = 0.5λ3,t−1 + ν3,t + 0.5ν3,t−1, and i,t and νj,s is i.i.d. N (0, 1) for each (i, j, s, t). Each entry of µi is drawn from an independent uniform distribution on [0, 1] and fixed for each repetition. At t = T + 1, the observed outcome is yi,T +1 = yi,T +1(0) + αi, where αi is either treatment effect or spillover effect and is specified below. The treatment effect is set to 5 and the spillover effect is 3. Notes: The numbers without parentheses are empirical bias in simulation. The ones with parentheses are empirical variance. SCM is the standard synthetic control method assuming no spillover effects. SP is the estimation procedure proposed in this paper that takes spillover effects into account. No spillover effects stands for the cases where the true DGP has no spillover effects. Concentrated spillover effects is the case where 1/3 of the control units receive a spillover effect. Spreadout spillover effects is the case where 2/3 of the control units receive a spillover effect of the same level.
The empirical bias and variance (in parentheses) of the treatment effect estimator using two methods are shown in Table 1. We consider three spillover patterns. No spillover effects is the case where unit 1 receives a treatment effect of 5 at t = T + 1 and other units are not affected. Concentrated spillover effects is the case where 1/3 of the control units receive a spillover effect of 3. Spreadout spillover effects is the case where 2/3 of the control units receive a spillover effect of 3. SCM is the original synthetic control method, and SP is the corrected synthetic control method proposed in Section 2.3. Throughout the simulations we assume the coverage of spillover effect is known, but not other information, so A is constructed as in Example 3. For No spillover effects, we are being conservative in our use of the SP estimator and run it as if 1/3 of the control units are exposed to spillover effects.
To better compare results, we fit the simulation results using kernel density for the (N, T ) = (10, 50) case with concentrated spillover effects and plot it in Figure 4. The true treatment effect is 5. SCM is using the standard synthetic control method assuming no spillover effects. SP is the estimation procedure proposed in this paper that takes spillover effects into account. Estimates are fitted using kernel density.

I(1) case
For the I(1) case, the underlying factor model follows where λt = (λ1,t, λ2,t, λ3,t) , λ3,t = 0.5λ3,t−1 + ν3,t, and i,t and νj,s follows i.i.d. N (0, 1) for each (i, j, s, t). The factor loadings are constructed such that condition CO is satisfied. Namely, we let µ1 = (1, 0, 0) , µ2 = (0, 1, 0) , µ3 = (1, 0, 0) , µ4 = (0, 1, 0) , and for µj with j = 5, . . . , N , we draw independent uniform distribution on [0, 1] for each entry and then normalize each loading vector such that three entries of each µj sum up to one. The constructed factor loadings are fixed for each repetition while other settings are same as the stationary case. The results are shown in Table 2. Notes: The numbers without parentheses are empirical bias in simulation. The ones with parentheses are empirical variance. SCM is the standard synthetic control method assuming no spillover effects. SP is the estimation procedure proposed in this paper that takes spillover effects into account. No spillover effects stands for the cases where the true DGP has no spillover effects. Concentrated spillover effects is the case where 1/3 of the control units receive a spillover effect. Spreadout spillover effects is the case where 2/3 of the control units receive a spillover effect of the same level.

Test for treatment effects
In this section we compare test procedures against the null hypothesis H0 : α1 = 0, i.e. the treatment effect is zero. The results are shown in Table 3 and Table 4. The DGP is exactly the same as in Section 5.1.1 (the stationary case), except that α1 = 0 (the null) for Table 3 and α1 = 5 (the alternative) for Table 4. Placebo test is as in Abadie and Gardeazabal (2003) and Hahn and Shi (2017). Andrews' test is as in Andrews (2003). SP is the spillover-adjust test proposed in Section 3.2.
Among the three testing procedures, SP test has correct sizes and outperforms the other two methods in power. Placebo test has correct sizes in some cases but has lower power, and Andrews' test over-rejects under null. The reasons are discussed in Section 3.3. Notes: SP is the estimation procedure proposed in this paper that takes spillover effects into account. No spillover effects stands for the cases where the true DGP has no spillover effects. Concentrated spillover effects is the case where 1/3 of the control units receive a spillover effect. Spreadout spillover effects is the case where 2/3 of the control units receive a spillover effect of the same level.

Test for existence of spillover effects
In this section we examine the power of the proposed test against the null hypothesis that there are no spillover effects. We also look into its behavior when the range of the spillover effect is not correctly specified. In this set of experiments, the level of spillover effects varies from 0 to 2, corresponding to the strength of alternative hypotheses. We set (N, T ) = (20, 50) and α1 = 5. There are 9 units that are affected by spillover effects. Other settings follow exactly as in Section 5.1.1 (the stationary case). The model for the range of spillover is as in Example 3.
The empirical rejection rates against various levels of spillover effects using our method proposed in Section 3.2 are plotted in Figure 5. Here Include too few misses half of the units that are actually affected by the treatment (assuming that unit 1 as well as four other units are affected), Correct specification assumes we know exactly which units are affected, and Include too many assumes 15 units are affected in estimation, 5 of which are actually not affected by spillover effects.
The simulation results show that the proposed test is quite robust to model misspecification. Among the three cases, Include too many is still a correct specification but is supposed to be more conservative, so it has less power than Correct specification does. The range of spillover effects is misspecified in Include Notes: SP is the estimation procedure proposed in this paper that takes spillover effects into account. No spillover effects stands for the cases where the true DGP has no spillover effects. Concentrated spillover effects is the case where 1/3 of the control units receive a spillover effect. Spreadout spillover effects is the case where 2/3 of the control units receive a spillover effect of the same level.
too few, but the test is still correctly sized under the null 4 and has reasonable power under alternatives.

Empirical Example
To demonstrate our method, we use it on the classic SCM example from Abadie et al. (2010) (ADH), which looks at the effect of Proposition 99 on California cigarette consumption. In this section, we will walk through the results from our method, with interruptions to point out key features and issues.
Proposition 99 intended to disincentivize smoking, which was primarily achieved by introducing a $0.25 tax on each pack of cigarettes. By measuring sales in California, ADH and others have attempted to determine the effect of the policy on smoking rates. However, traditional SCM is not guaranteed to produce an unbiased treatment effect estimator in the presence of spillover effects. In this tobacco control program example, we are concerned about two kinds of spillover effects. The first spillover is based on concerns about "leakage". A common problem with cigarette taxes is that measured local consumption might fall as people move their purchasing behavior across legal boundaries. In order to accommodate this, we allowed for a spillover affecting states neighboring California and a spillover affecting states which a state away from California. The second spillover type we considered was a cultural change. If tobacco is discouraged in California, it might reduce the cultural appeal of smoking. Reasoning that the northeast is culturally close to the west coast, we allowed for the northeastern states to experience this cultural spillover.
One might also think that there could be a policy contamination whereby culturally close states also enact policies with similar targets. Our method can allow for this kind of spillover in our estimation.
However, the initial paper took that type of problem into account, and 12 states which experienced legislative changes in the ensuing years were removed in that paper (and thus in our data).
The data used is per capita cigarette consumption in 38 of the 50 states running from 1970 to 2000.
Twelve states were removed from the data because of concerns that they were either contaminated, or received treatment later on. In 1989 California enacted Proposition 99, so all periods from 1989 onwards are considered post-treatment periods. We replicate this program evaluation using the method introduced in previous sections, allowing for possible spillover effects. We use the spillover structure as in Example 3. That is, we allow for arbitrary spillover effects in those geographically close and culturally similar states as described in the last paragraph, but not the others. We also perform hypothesis testing on both treatment effects and spillover effects. California. SP synthetic California is using our estimation procedure, which accounts for spillover effects. The vertical line indicates the start of treatment.
The results are shown in Figure 6 and Figure 7. The method in Abadie et al. (2010) is indexed by SCM and our method is SP. Figure 6 shows the "synthetic California" and Figure 7 elaborates on this by specifically looking at the estimated treatment effects. The error bars are built using the methods described in this paper, at a significance level of 90%. We do not use a 95% significance level because there are only 19 pre-treatment periods.
As Figure 6 shows, our estimated consumption in the "synthetic California" does not differ qualitatively from what a standard SCM would predict. Quantitatively, Figure 7 shows that our results are more consistent with an addiction story, that tobacco consumption is addictive and should not fall immediately after the policy. From the tests of spillover effects (shaded area of Figure 7), we see that likely there were substantial spillover effects, which in some periods lead to statistically significant changes in the treatment effect estimates. For example, the SCM estimate of year 1990 lies outside our confidence interval, which potentially results from the over-estimation of scale of the treatment effects in the presence of spillover effects. 99 1970 1975 1980 1985 1990 1995 2000 year -25

Passage of Proposition
-20 confidence interval). The lines to the right of passage of Proposition 99 are treatment effect estimates. SCM is obtained by using standard synthetic control method. SP is using our estimation procedure, which accounts for spillover effects. Shaded area denotes our test rejects there is no spillover effects in those years.

Conclusion
The synthetic control method is a powerful tool in treatment effect estimation in the panel data settings, but it does not work in the presence of spillover effects. In this paper, we relax this assumption and propose an estimation and testing procedure that is robust to the presence of spillover effects. Our method requires specification of the spillover structure, which can be weak (Example 3). We derive a set of conditions under which our estimators are asymptotically unbiased. We develop a testing procedure based on Andrews (2003)'s end-of-sample instability tests and show that it is asymptotically unbiased under a set of conditions. We show our conditions are satisfied by the commonly used factor models, with either stationary or cointegrated common factors. Our methods can be extended to cases with multiple treated units and multiple post-treatment periods, and with extra covariates. Simulation results certify the validity of our estimation and testing procedure in the presence of spillover effects. The simulations also indicate that our testing procedure is relatively robust to misspecification of the spillover structure.
Finally, we illustrate our method by applying it to Abadie et al. (2010)'s California tobacco control program data.  (2019), except that we do not assume that there is a set of weights that reconstruct the factor loadings and belong to the simplex.
We first show part (b). It suffices to show | ai − ai| = op(1) and bi − bi = op(1) for each i, i.e. ai and bi are well-defined. We show it for the i = 1 case and other cases follow the same strategy. Let The objective is strictly convex (with probability approaching one), so the solution is unique. Note that it implies b1 is numerically equivalent to (0, v ) , otherwise the minimization problem in forming a1 and b1 may have a lower objective evaluated at (ȳ1 − N j=2ȳ j vj, 0, v ) . Now we let Q(v) denote the objective function such that and its population analog be Let v0 be a minimizer of Q(v) in V . We verify the conditions for consistency (see Newey and McFadden, 1994, Theorem 2.1) : (i) Since Ωy is positive definite, Q(v) is strictly convex. Also, V is convex. Therefore, is continuous, since it has a quadratic form. (iv) To see uniform convergence, note where · F is the Frobenius norm. The second inequality is by ergodicity for the second moments.
Therefore, v →p v0. This implies b1 − b1 = op(1). By ergodicity, This shows part (b) and E[u1,t] = 0 by definition of ui,t. We also have that {ut} t≥1 is stationary since it is a linear combination of stationary and ergodic processes. This shows part (a) in Assumption 1.
Part (c) follows from part (b) and the stationarity of {YT +1 (0) We first show part (c). We will show YT +1(0) ( b1 − b1) = op(1) and other i's follows the same strategy. Since the synthetic control estimator can be written as a projection of the OLS estimator onto a closed convex set, we will first derive the asymptotic properties of the OLS estimator, and then use the properties of projections to obtain the desired results. For examples of this strategy, see Li (2019) and Yu et al. (2019). For some positive definite matrix D ∈ R N , let R N be a Hilbert space with the inner product ·, · D such that for θ1, θ2 ∈ R N , The norm · D is defined accordingly, i.e. θ D = √ θ Dθ, for θ ∈ R N . For a closed convex set Λ ⊂ R N , define a projection ΠD such that for each θ ∈ R N , ΠDθ = arg min θ ∈Λ θ − θ D . Zarantonello (1971) shows that for each θ, θ ∈ R N , With some abuse of notation, let xt = Yt − T −1 T s=1 Ys. Then, b1 is the synthetic control weight estimators of regressing (y1,t − T −1 T s=1 y1,s) on xt, subject to {0} × ∆N−1 with ∆N−1 being an (N − 1)-dimensional simplex. Letb1 be the OLS estimator of regressing (y1,t − T −1 T s=1 y1,s) on xt.
Appendix A.2 in Li (2019) establishes that b1 = ΠΣ Tb 1. Thus, we have where · F is the Frobenius norm of a matrix. The third equality is because b1 ∈ {0} × ∆N−1. The second inequality is by (8). To see the fifth equality, note where the second equality is standard results for I1 process (see Hamilton, 1994, part (g) and (i) of Proposition 18.1). Also, b 1 − b1 = op(T −1/2 ) is by Proposition 19.2 in Hamilton (1994). This shows (9). Apply part (a) of Proposition 18.1 in Hamilton (1994), we have (1) where ei is the unit vector with one at the i-th entry. Thus, The third equality is by (10). The fourth equality is by stationarity of {(λ 0 t , t)}t≥1 and results in part (d) of the proof. This shows part (b) of the Assumption 1 .
Combining (10) and (11), we have part (a) in Assumption 1. Part (d) is assumed by Condition
Proof of Proposition 1. The proof for the first half of the proposition is similar to the proof for
For D2,T , we have The equality is by the mean value theorem and we havePt lies between Pt( β (t) 1 ) and Pt(β1). In the inequality,k is a bound for the derivative of k. Also, note Again, the inequality is by definition of qP,1−τ , and the convergence is because of part (e) of Assumption 2 and part (b) of Theorem 2.
Proof of Lemma 3. (i) Assume Condition ST holds.
By Lemma 1, part (a) of Assumption 3 holds.
Part (b) is because ut is a linear combination of ηt, λt, t.
Also, since θ (t) = θ for each t, This concludes part (i) of Lemma 3.
(ii) Assume Condition CO holds.
The second half of Part (d) is also satisfied since θ (t) = θ for each t.
Part (e) is assumed and Part (f) is trivial for WT = I.
By Assumption 1(a), gt( T , cT , ηT ) is identically distributed across t for a fixed T .
The second equality is by Theorem 1. Since P∞ = u 1 G C W CGu1, we have P → d P∞ by stationary of {ut} t≥1 .
Part (b)-(d) can be shown using the same strategy as in the proof of Theorem 2, with gt( T , cT , ηT ) in place of gt( T , cT ), and θ in place of β, so is omitted here.