Dynamic regression discontinuity under treatment effect heterogeneity

Hsu, Yu-Chin; Shen, Shu Article Dynamic regression discontinuity under treatment effect heterogeneity Quantitative Economics Provided in Cooperation with: The Econometric Society Suggested Citation: Hsu, Yu-Chin; Shen, Shu (2024) : Dynamic regression discontinuity under treatment effect heterogeneity, Quantitative Economics, ISSN 1759-7331, The Econometric Society, New Haven, CT, Vol. 15, Iss. 4, pp. 1035-1064, https://doi.org/10.3982/QE2150 This Version is available at: https://hdl.handle.net/10419/320321 Standard-Nutzungsbedingungen: Die Dokumente auf EconStor dürfen zu eigenen wissenschaftlichen Zwecken und zum Privatgebrauch gespeichert und kopiert werden. Sie dürfen die Dokumente nicht für öffentliche oder kommerzielle Zwecke vervielfältigen, öffentlich ausstellen, öffentlich zugänglich machen, vertreiben oder anderweitig nutzen. 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If the documents have been made available under an Open Content Licence (especially Creative Commons Licences), you may exercise further usage rights as specified in the indicated licence. https://creativecommons.org/licenses/by-nc/4.0/ Quantitative Economics 15 (2024), 1035–1064 1759-7331/20241035 Dynamic regression discontinuity under treatment effect heterogeneity Yu-Chin Hsu Institute of Economics, Academia Sinica, Department of Finance, National Central University, Department of Economics, National Chengchi University, and CRETA, National Taiwan University Shu Shen Department of Economics, University of California Regression discontinuity is a populartool for analyzing economic policies or treatment interventions. This research extends the classic static RD model to a dynamic framework, where observations are eligible for repeated RD events and, therefore, treatments. Such dynamics often complicate the identification and estimation of long-term average treatment effects. Empirical papers with such designs have so far ignored the dynamics or adopted restrictive identifying assumptions. This paper presents identification strategies under various sets of weaker identifying assumptions and proposes associated estimation and inference methods. The proposed methods are applied to revisit the seminal study of Cellini, Ferreira, and Rothstein (2010) on long-term effects of California local school bonds. Keywords. Long-term treatment effects, dynamic regression discontinuity, semiparametric, varying coefficient logit. JEL classification. C31. 1. Introduction Regression discontinuity (RD) models, which can be traced back to Thistlethwaite and Campbell (1960), are popular in policy evaluations or other settings of treatment effect analysis. The set-up exploits discontinuity in the design of many policies to nonparametrically identify treatment effects for observations near the eligibility cutoff. Classic Yu-Chin Hsu: [email protected] Shu Shen: [email protected] This paper was first presented at a University of California, Berkeley, causal inference group seminar in March 2020 under the title of “Dynamic Regression Discontinuity.” The authors are grateful to three anonymous referees for valuable comments and suggestions on previous versions of the paper. The authors also thank seminar participants from University of California, Berkeley, University of California, Irvine, University of Nevada, Reno, University of Chicago, and Chamberlain Seminar for helpful comments. Yu-Chin Hsu gratefully acknowledges the research support from Ministry of Science and Technology of Taiwan (MOST107-2410-H-001-034-MY3, MOST110-2634-F-002-045), National Science and Technology Council of Taiwan (NSTC 112-2628-H-001-001), Academia Sinica Investigator Award of Academia Sinica (AS-IA-110H01), and Center for Research in Econometric Theory and Applications (113L8601) from the Featured Areas Research Center Program within the framework of the Higher Education Sprout Project by the Ministry of Education of Taiwan. Shu Shen gratefully acknowledges the research support from UC Davis Small Grants in Aid of Research, Creative Activities, and Scholarship. ©2024 The Authors. Licensed under the Creative Commons Attribution-NonCommercial License 4.0. Available at http://qeconomics.org.https://doi.org/10.3982/QE2150 1036 Hsu and Shen Quantitative Economics 15 (2024) studies of RD identification, estimation, and inference include Hahn, Todd, and van der Klaauw (2001), Porter (2003), Lee (2008), Imbens and Lemieux (2008), Calonico, Cattaneo, and Titiunik (2014), and Calonico, Cattaneo, Farrell, and Titiunik (2019), among many others. Cattaneo and Titiunik (2022) provide a comprehensive literature review. While the classic RD set-up, either sharp or fuzzy, is static in empirical applications we often see situations where each individual faces multiple rounds of RD and, therefore, could potentially receive repeated treatments. For example, voter-approved measures such as unionization (e.g., DiNardo and Lee (2004), Lee and Mas (2012)) or local school bonds (e.g., Cellini, Ferreira, and Rothstein (2010)) could be put in front of voters recurrently. A large body of literature in political science and economics (e.g., Lee (2008), Pettersson-Lidbom (2008), Ferreira and Gyourko (2009), Colonnelli, Prem, and Teso (2020)) uses RD to study the effect of political races that happen on a regular basis. Dube, Giuliano, and Leonard (2019)andJohnson (2020) examine the peer effect of RD treatments. Their setting is repeated as well because the same individual can be exposed to different peer treatments at different points of time. The repeated treatment design brings complications to identifying long-term effects in the RD setting just as in other non-RD settings. As Heckman, Humphries, and Veramendi (2016) discuss, in repeated/sequential treatment settings reduced-form analysis can only identify a mixed bag of effects, called the long-term total effect. For policy analysis, researchers often want to distinguish a long-term direct effect, or the “clean” long-term effect of an earlier treatment with no subsequent treatments (Heckman, Humphries, and Veramendi (2016)), from the mixed bag. In the California education bond example studied by Cellini, Ferreira, and Rothstein (2010) (CFR), for example, policymakers are interested in identifying the long-run effect of passing a local education bond on education expenditure, test scores, and local house prices. For the purpose of identification, one wishes that the education bond voting would only take place once. Then, comparing long-run outcomes between school districts that barely pass and barely miss the vote share cutoff, would give average longterm direct effects of interests (for those school districts at the vote share cutoff). In reality, education bond measures can be put forward repeatedly. As is discussed in CFR, the difference in observed long-run outcomes at the RD cutoff only captures an average total effect that is also influenced by subsequent bond authorizations. For example, school districts failing to pass the initial bond measure are more likely to put forward another bond measure in later periods (Cellini, Ferreira, and Rothstein (2010)). Among the empirical literature on repeated RD settings, CFR and subsequent studies adopting their methods (e.g., Darolia (2013), Abott, Kogan, Lavertu, and Peskowitz (2020)) are the only ones, as far as the authors know, that seek proper identification of average long-term direct effects. Other empirical studies either ignore the repeated design or opt to only study immediate effects and/or long-term total effects. CFR proposes to identify average long-term direct effects from total effects with a recursive RD strategy and a more parametric event study strategy. Recently, Gallen, Joensen, Johansen, and Veramendi (2023) extend CFR’s recursive identification strategy to a non-RD IV setting. This paper formalizes the repeated RD design under the potential outcome framework. We find that, under treatment effect heterogeneity, preserving the recursive CFR Quantitative Economics 15 (2024) Dynamic regression discontinuity 1037 strategy to identify long-term average direct effects requires strong assumptions. In the California education bond application, for example, using the recursive CFR strategy requires the decision of putting forward other bond measures after the focal round to be exogeneous, among other identifying conditions such as path-independency and homogeneity in bond effects. As Dong (2019) points out in a study of RD design with sample selection, although RD models could be regarded as local random experiments, such randomness around running variable cutoffs could not be used to argue for the ignorance of endogenous selection into RD events. In the dynamic RD design, random participation in subsequent rounds of RD is rarely plausible. Homogeneity in average effects across different RD rounds and regardless of past treatment paths is also very strong. Given the aforementioned considerations, the main contribution of this paper is to propose a new identification strategy for long-term average direct effects. In contrast to recursive CFR, our proposed identification strategy does not impose any restriction on potentially endogenous RD participation decisions. Our strategy also allows treatment effects to depend on last period’s treatment take-up. Our key identification restriction is a conditional mean independence assumption (CIA) that requires mean independence between the second-round running variable and the second-round potential outcomes without the second-round treatment, conditional on RD participation. For tractability in longer-term effect identification, we also impose a Markovian-type assumption to simplify the path-dependency structure of average treatment effects. Besides point identification, we provide partial identification results in the Supplemental Appendix (Hsu and Shen (2024)) under Manski-type (e.g., Manski and Pepper (2000)) monotonicity conditions. Our paper relates to the dynamic treatment effect literature outside the RD setting. As Han (2021) discusses, the biostatistics literature (e.g., Robins (1986,1987), Murphy, van der Laan, Robins, and C. P. P. R. Group (2001), Murphy (2003), Chakraborty and Murphy (2014)) has a long history of studying dynamic causal effects under the assumption of sequential randomization. As we shall explain in the paper, although sharp RD designs are often understood as local random experiments, the dynamic RD set-up does not enjoy sequential randomization by design. In addition, imposing sequential randomization or ignorability (e.g., Blackwell (2013), Imai and Ratkovic (2015), Imbens and Lemieux (2008), Bojinov, Rambachan, and Shephard (2021)) on treatments as an identification condition can be undesirable in empirical RD studies. Our paper relates to Heckman, Humphries, and Veramendi (2016) who evaluate treatment effects in ordered and unordered multistage decision problems with an instrumental variable approach, to Sun and Abraham (2021), Callaway and Sant’Anna (2021), and Athey and Imbens (2022) who examine treatment effects in panel event studies with one single irreversible treatment, to De Chaisemartin and d’Haultfoeuille (2020) who study linear two-way fixed-effect regressions for panel data models with treatment effect heterogeneity across groups or over time, and to De Chaisemartin and d’Haultfoeuille (2024) who investigate path-specific long-term average treatment effects using the parallel trend condition. All aforementioned papers have different model set-ups and identifying assumptions than ours. Han (2021) proposes to identify path-specific 1038 Hsu and Shen Quantitative Economics 15 (2024) ATEs using a sequence of dynamic treatment selection equations and excluded instruments. We do not have natural instruments in the repeated RD setting. Our dynamic RD model also relates to RD models with repeated designs or multiple scores/cutoffs, including Grembi, Nannicini, and Troiano (2016) who propose a difference-in-discontinuities strategy to partial out the effect of a confounding policy, Lv,Sun,Lu,andLi(2019) who consider RD survival analysis where individual treatments are allowed to be allocated at different pre-treatment duration, multiscore models studied by Papay, Willett, and Murnane (2011), Reardon and Robinson (2012), and Wong, Steiner, and Cook (2013), and the multicutoff RD model of Cattaneo, Keele, Titiunik, and Vazquez-Bare (2016). Given our focus on long-term direct effects, this paper is significantly different from the others. Aside from identification, our paper contributes to the literature by designing a new two-step semiparametric boundary estimation procedure. Specifically, our identified long-term effects has a form of inverse propensity score weighting (IPW), and so the estimation follows two steps. In the first step, we model the propensity score function semiparametrically and estimate it with the local MLE approach in Cai, Fan, and Li (2000). In the second step, we plug in estimated propensity scores to local-linear regressions. Our proposed first-step local MLE algorithm is particularly suitable for the RD setting, because it allows the propensity score estimator to stay local to the RD cutoff along the dimension of the running variable (cf. Gelman and Imbens (2019)) while not overburdening the final two-step estimator with the “curse of dimensionality.” In terms of inference, our paper is the first to apply the weighted bootstrap designed in Ma and Kosorok (2005) to kernel-based boundary estimation, which is the main workhorse of the RD literature. The weighted bootstrap method has also been adopted by Chen and Pouzo (2009), Chernozhukov, Fernández-Val, Hoderlein, Holzmann, and Newey (2015), Chernozhukov, Fernández-Val, and Kowalski (2015), and Fernández-Val, van Vuuren, and Vella (2021), among others, in other estimation settings. The rest of the paper is organized as follows. Section 2starts with a simple twoperiod dynamic RD model, explaining why long-term direct effects are important policy parameters and why their identification cannot be obtained directly from the RD design. Section 2.2 formalizes the recursive CFR identification strategy under treatment effect heterogeneity and discuss its limitations. Sections 2.3 and 2.4 present a new identification and estimation strategy for the one-period-after average direct effect in the benchmark two-period model. Section 3presents the general multiperiod dynamic RD model and the identification of longer-term average direct effects. Section 4studies estimation and inference of the general model. Section 5revisits the empirical study of California education bonds using CFR’s published data set. Section 6concludes. Monte Carlo simulations and proofs are provided in the Supplemental Appendix, which also includes partial identification results and several empirical-relevant special cases. 2. A benchmark two-period model In this section, we use a simple two-period model to define the dynamic RD design under the potential outcome framework. We take the simple model to point out complications brought by having a repetition in the RD design, as well as the differences between Quantitative Economics 15 (2024) Dynamic regression discontinuity 1039 dynamic RD models and other non-RD dynamic models previously studied in the literature. We propose a novel identification strategy in this two-period model and discuss its advantages compared to previous methods. Before we begin, it is important to point out that the simple two-period model defined in this section is only a starting point. Some important identification results provided in this paper are only relevant for the general case presented in Section 3. 2.1 The classic potential outcome framework Consider a repeated RD setting, where the RD event (e.g., election, testing, etc.) takes place at the beginning of each period, and the treatment is administrated immediately following the event for participants who pass a running variable threshold. An outcome is observed at the end of each period. In period one, we assume for now that everyone takes part in the RD event, so the observed treatment Di1and outcome Yi1of individual isatisfy Di1=1(Zi1≥0),Yi1=Yi1(0)·(1−Di1)+Yi1(1)·Di1, where Zi1is the first-round running variable and Yi1(d1)is the potential first-period outcome with Di1=d1,ford1=0, 1. Without loss of generality, all RD cutoffs in this paper are normalized to zero. In period two, the potential outcome framework gives Di2=Di2(0)·(1−Di1)+Di2(1)·Di1,and Yi2=Yi2(0, 0)·(1−Di1)·1−Di2(0)+Yi2(0, 1)·(1−Di1)·Di2(0) +Yi2(1, 0)·Di1·1−Di2(1)+Yi2(1, 1)·Di1·Di2(1) ≡ 2∈L2 Yi22·Di2,L2=(0, 0),(0, 1),(1, 0),(1, 1), where Di2and Yi2are observed treatment decisions and outcomes, while Di2(d1)and Yi2(d1,d2),d1,d2=0, 1, are their potential counterparts. Di(.)is the path indicator of individual iand L2is the set of all possible treatment paths in two periods. This dynamic potential outcome framework is common in dynamic causal effect settings outside RD. See, for example, Section III of the biostatistics textbook Hernán and Robins (2023)and previous work in econometrics, including Hahn, Todd, and van der Klaauw (2001)and Bojinov, Rambachan, and Shephard (2021). The RD setting also brings special features to the dynamic model. Specifically, the second-period treatment decision Di2(d1)is determined by a potentially endogenous RD participation indicator Si2(d1)and a potentially endogenous second-round running variable Zi2(d1)such that Di2(d1)=Si2(d1)·1(Zi2(d1)≥0). The second-period observed participation decision and treatment decision satisfy Si2=Si2(0)·(1−Di1)+Si2(1)·Di1, Di2=Si2(0)·1Zi2(0)≥0·(1−Di1)+Si2(1)·1Zi2(1)≥0·Di1. 1040 Hsu and Shen Quantitative Economics 15 (2024) The second-round running variable Zi2=Zi2(0)·(1−Di1)+Zi2(1)·Di1is only observed given RD participation, that is, Si2=1. Example (California Education Bonds). In the California education bond example studied in CFR, outcome measures include local education expenditures, house prices, student achievements, etc. A bond measure is approved if its vote share exceeds the legislative cutoff (normalized to (0). No matter whether a school district gets its bond approved in the first round (Di1) or not, it could choose to initiate a new bond measure in the next election year (Si2=1) and choose how much campaign efforts to put into the new measure to improve its vote share result (Zi2(d1),ford1=0, 1). We formally define the following individual treatment effects for the two-period model: immediate effect of Di1:θi;0,1 =Yi1(1)−Yi1(0); immediate effect of Di2:θd1 i;0,2 =Yi2(d1,1)−Yi2(d1,0),for d1=0, 1; one-period-after direct effect of Di1:θi;1,1 =Yi2(1, 0)−Yi2(0, 0); one-period-after total effect of Di1:˜ θi;1,1 =˜ Yi2(1)−˜ Yi2(0), where ˜ Yi2(d1)≡Yi2d1,Di2(d1)=Yi2(d1,0)1−Di2(d1)+Yi2(d1,1)Di2(d1). Note that the immediate effect of the second-round treatment is path-dependent. Following Heckman, Humphries, and Veramendi (2016) and CFR, we define long-term direct effects by prohibiting treatment take-ups after the focal round. The total effect, on the other hand, does not limit treatment decisions after the focal round. Direct and total effects are also commonly seen in the mediation literature.1See Huber (2020)fora literature review. Assumption 2.1. There exists an >0, such that: 1. Zi1is continuous in z1∈(−,)≡Nwith P[Zi1≥0]∈(0, 1); 2. E[Yi1(d1)|Zi1=z1],E[Di2(d1)|Zi1=z1],and E[˜ Yi2(d1)|Zi1=z1]are all continuous in z1∈N,for both d1=0, 1. Assumption 2.1 imposes traditional RD smoothness conditions that provide identification for the average immediate effect E[θi;0,1|Zi1=0]and the average first-stage effect E[Di2(1)−Di2(0)|Zi1=0]. Since the random variable ˜ Yi2(d1), which takes place in the second period but only specifies the first-round treatment status, can be viewed 1In the mediation literature, θi;1,1 =Yi2(1, 0)−Yi2(0, 0)is the controlled direct effect, in contrast to the pure direct effect, which would be Yi2(1, Di2(0))−Yi2(0, Di2(0))in our notation. Flores and Flores-Lagunes (2009,2010) study the pure direct effect in the econometrics literature. As Huber (2020) discusses, the pure direct effect is not interesting in the dynamic setting. Quantitative Economics 15 (2024) Dynamic regression discontinuity 1041 as a potential outcome of the first-round treatment, smoothness conditions in Assumption 2.1 also identifies the average one-period-after total effect: E[˜ θi;1,1|Zi1=z1]=E˜ Yi2(1)−˜ Yi2(0)|Zi1=0 =lim z10E[Yi2|Zi1=z1]−lim z10E[Yi2|Zi1=z1]. (2.1) IntherestofSection2, we explore conditions that identify the average direct effect E[θi;1,1|Zi1=0], which has important policy implications as argued in Heckman and Navarro (2007) and CFR. For conciseness, we call E[θi;1,1|Zi1=0]the one-period-after ATE. It has the following relationship with the one-period-after average total effect: E[˜ θi;1,1|Zi1=0]=E[θi;1,1|Zi1=0]+Eθ1 i;0,2Di2(1)|Zi1=0 −Eθ0 i;0,2Di2(0)|Zi1=0. (2.2) Example (continued). In the California education bond example, the one-period-after ATE (E[θi;1,1|Zi1=0]) is the average effect of passing an education bond in the first period on the second-period outcome with no bond authorization after the first period, among all school districts at the first-period vote share cutoff. The one-period-after ATE influences the one-period-after average total effect (E[˜ θi;1,1|Zi1=0]), which is identified by the period two outcome discontinuity observed at the period one vote share cutoff. However, the one-period-after total effect is also influenced by the fact that school districts can pass new bond measures in the second period, and hence receive immediate effects from those additional treatments. 2.2 Recursive identification strategy in CFR CFR propose a recursive identification strategy for long-term direct effects based on an implicit treatment effect homogeneity assumption, which requires individual treatment effects to vary only by the number of periods between potential outcomes and the focal round of treatment.2For the two-period model, that is to require θ0≡θi,0,1 =θ0 i,0,2 =θ1 i,0,2 and θ1≡θi,1,1 for all i, (2.3) where θ0and θ1are unknown fixed parameters. The strong assumption reduces the relationship in (2.2)to E[˜ θi;1,1|Zi1=0]=θ1+θ0EDi2(1)−Di2(0)|Zi1=0. The simplification implies recursive identification of the one-period-after ATE θ1, since all other components of the equation are directly identifiable through smoothness conditions. CFR’s recursive strategy can be extended to allow for individual treatment effect heterogeneity under the potential outcome framework outlined in the previous section. 2See, for example, Section IV.B of CFR. In CFR, our direct effect is called the “treatment-on-the-treated” effect and our total effect is called the “intent-to-treat” effect. 1042 Hsu and Shen Quantitative Economics 15 (2024) Lemma 2.1. Under Assumption 2.1,the homogeneous ATE requirement: ATE0≡E[θi;0,1|Zi1=0]=Eθ1 i;0,2|Zi1=0=Eθ0 i;0,2|Zi1=0, (2.4) and the random second-round treatment selection requirement: Eθd1 i;0,2|Di2(d1),Zi1=0=Eθd1 i;0,2|Zi1=0,d1=0, 1, (2.5) the recursive identification strategy in CFR can be preserved: ATE0=lim z10E[Yi1|Zi1=z1]−lim z10E[Yi1|Zi1=z1], ATE1≡E[θi;1,1|Zi1=0]=lim z10E[Yi2|Zi1=z1]−lim z10E[Yi2|Zi1=z1] −ATE0·lim z10E[Di2|Zi1=z1]−lim z10E[Di2|Zi1=z1]. To preserve CFR’s recursive identification strategy under individual treatment effect heterogeneity, conditions (2.4)and(2.5) are required. The conditions include the strong homogeneity assumption in (2.3) as a special case.3If the homogeneity ATE condition in (2.4) is violated due to diminishing marginal returns to repeated treatments (i.e., E[θ1 i;0,2|Zi1=0]<E [θ0 i;0,2|Zi1=0]=E[θi;0,1|Zi1=0]), then ATE1identified in Lemma 2.1 is smaller than the true value of E[θi;1,1|Zi1=0]. The random treatment selection condition in (2.5) should not to be confused with the local randomness intuition of the RD design. A treatment intervention satisfying the sharp RD design is only locally random at its own running variable cutoff. In other words, the RD design associated with Di2(d1)only indicates local randomness among individuals at Zi2(d1)=0, for d1=0, 1. Equation (2.5) is different. It is not implied by the RD design and is a strong condition used to obtain the recursive identification result. Example (continued). In the California education bond example, data reveal that school districts barely passing their educationbond in the first round do not put forward another bond in the second period (i.e., E[Si2(1)|Zi1=0]=limz10E[Si2|Zi1=z1]=0). Therefore, equation (2.5) essentially restricts that, for a school district ithat marginally failed the first-round voting, the decision of putting forward another measure in the next election cycle (Si2(0)) is not related to the immediate treatment effect of the new 3A more general multiperiod version of the lemma is discussed in the Supplemental Appendix, where we also extend Lemma 2.1 to include conditioning covariates Xi∈X. The extension replaces the homogeneous ATE assumption in (2.4) and the random treatment selection assumption in (2.5)with Eθd1 i;0,2|Di2(d1),Xi=x,Zi1=0=Eθd1 i;0,2|Xi=x,Zi1=0, and (2.6) CATE0(x)=E[θi;0,1|Xi=x,Zi1=0] =Eθd1 i;0,2|Xi=x,Zi1=0,∀d1=0, 1, x∈X. (2.7) Quantitative Economics 15 (2024) Dynamic regression discontinuity 1049 The decomposition is new to the literature, as far as the authors know. It is different from the decomposition used behind the recursive CFR identification strategy, where the long-term total effect is decomposed to its corresponding direct effect plus a sum of various shorter-term direct effects adjusted by first-stage treatment decisions.6In the rest of the section, we use equation (3.1) to develop an identification strategy because the new decomposition involves much fewer path-dependent treatment effects in its formulation. Aside from utilizing the new decomposition result, we impose a Markovian-type condition to further reduce the number of path-dependent treatment effect parameters involved in identification. Let ηi;0,1,ηk−1 i;0,k,ηi;τ,1,ηk−1 i;τ,k,˜ηi;τ,1,and ˜ηk−1 i;τ,kbe firststage counterparts of immediate effects θi;0,1 and θk−1 i;0,k, direct effects θi;τ,1 and θk−1 i;τ,k, and total effects ˜ θi;τ,1 and ˜ θk−1 i;τ,k, respectively.7The following assumption summarizes the identifying restrictions used in the general multiperiod dynamic RD model. Assumption 3.1 (Longer-term ATEs). There exists >0such that for all z1∈N,we have: 1. (Markovian)for any k=3, 4, ,K,k−2∈Lk−2,and d=0, 1, immediate effects and τ-period-after total effects satisfy that E[θ(k−2,d) i;0,k|Dik(k−2,d)=1, Zi1=z1]= E[θd i;0,2|Di2(d)=1, Zi1=z1]≡μd 0and E[˜ θ(k−2,d) i;τ,k|Dik(k−2,d)=1, Zi1=z1]= E[˜ θd i;τ,2|Di2(d)=1, Zi1=z1]≡˜μd τ,for all τ=1, ,K−k;similar conditions also hold for immediate and long-term first-stage effects; 2. (CIA:multiperiod)for any d1=0, 1, z2∈R,and x∈X,E[Mi(d1,0)|Xi=x,Zi2(d1)= z2,Si2(d1)=1, Zi1=z1]=E[Mi(d1,0)|Xi=x,Si2(d1)=1, Zi1=z1],where the random variable Mi(d1,0)can be Di3(d1,0),˜ Yi(2+τ)(d1,0)for all τ=1, ,K−2, or ˜ Di(3+τ)(d1,0)for all τ=1, ,K−3; 3. (Smoothness:multiperiod)for all d1,d2=0, 1, and x∈X,E[Mi(d1,d2)|Xi= x,Di2(d1)=d2,Zi1=z1]is continuous in z1,where the random variable Mi(d1,d2) can be Di3(d1,d2),˜ Yi(2+τ)(d1,d2)for all τ=1, ,K−2, or ˜ Di(3+τ)(d1,d2)for all τ=1, ,K−3; The second and third parts of Assumption 3.1 are vanilla extensions of Assumption 2.2 viewing Di3(d1,d2),˜ Yi(2+τ)(d1,d2),and ˜ Di(2+τ)(d1,d2)as potential outcomes associated with the first two treatments but taking place in a later period. The key new 6When τ=2, for example, the decomposition underlying the recursive CFR identification strategy is ˜ θi;2,1 =θi;2,1 +θ1 i;1,2Di2(1)+θ(1,0) i;0,3(1−Di2(1))Di3(1, 0)+θ(1,1) i;0,3Di2(1)Di3(1, 1)−θ0 i;1,2Di2(0)−θ(0,0) i;0,3(1− Di2(0))Di3(0, 0)+θ(0,1) i;0,3Di2(0)Di3(0, 1). 7Let ˜ Di(k+1+τ)(k)be the (k+1+τ)-th period quasi-potential treatment decision with only the first krounds of previous treatment status specified, for any τ≥1 and k≥1. Then ηi;0,1 =Di2(1)−Di2(0), ηi;τ,1 =Di(2+τ)(1, 0τ)−Di(2+τ)(0, 0τ), and ˜ηi;τ,1 =˜ Di(2+τ)(1)−˜ Di(2+τ)(0)for all τ≥1. For all k≥ 2, ηk−1 i;0,k=Di(k+1)(k−1,1)−Di(k+1)(k−1,0),ηk−1 i;τ,k=Di(k+1+τ)(k−1,1,0τ)−Di(k+1+τ)(k−1,0,0τ), and ˜ηk−1 i;τ,k=˜ Di(k+1+τ)(k−1,1)−˜ Di(k+1+τ)(k−1,0)for all τ≥1. 1050 Hsu and Shen Quantitative Economics 15 (2024) condition in Assumption 3.1 is the Markovian restriction. In the California education bond application, the Markovian restriction allows an education bond’s various immediate and long-term average effects to depend arbitrarily on last election cycle’s bond authorization but not any other bond authorizations further in the past. Although nontrivial, the Markovian condition is much less restrictive than the homogeneous ATE condition used in Lemma 2.1 (or Lemma A.1) for the recursive CFR identification strategy. Similar Markovian-type restrictions are also used in De Chaisemartin and d’Haultfoeuille (2024)andImai, Kim, and Wang (2023) for non-RD dynamic treatment effect settings. When τ=2, the Markovian assumption together with the decomposition in (3.2) imply that E[˜ θi;2,1|Zi1=0]=E[θi;2,1|Zi1=0]+˜μ1 1·EDi2(1)|Zi1=0−˜μ0 1·EDi2(0)|Zi1=0 +μ0 0·E[ηi;1,1|Zi1=0]. Lemma 3.2. Under the assumptions used in Lemma 2.2,Assumption A.1 for identifying long-term average total effects,and Assumption 3.1,we have that for τ=2, ,K−1, E[θi;τ,1|Zi1=0]=lim z10E[Yi(τ+1)|Zi1=z1]−lim z10E[Yi(τ+1)|Zi1=z1] −˜μ1 τ−1·lim z10E[Di2|Zi1=z1]+˜μ0 τ−1·lim z10E[Di2|Zi1=z1] − τ−2  s=1˜μ0 s·E[ηi;τ−1−s,1|Zi1=0]−μ0 0·E[ηi;τ−1,1|Zi1=0], (3.3) where μ0 0=lim z10EYi2Si2Di2−λ0(Xi) 1−λ0(Xi)E[Di2|Zi1=z1]Zi1=z1, ˜μ0 s=lim z10EYi(2+s)Si2Di2−λ0(Xi) 1−λ0(Xi)E[Di2|Zi1=z1]Zi1=z1,and ˜μ1 s=lim z10EYi(2+s)Si2Di2−λ1(Xi) 1−λ1(Xi)E[Di2|Zi1=z1]Zi1=z1, for all s≥1. In addition,treating first-stage decisions as outcomes,E[ηi;1,1|Z1=0]is identified by Lemma 2.2 and E[ηi;k,1|Z1=0]for all k=2, ,τ−1is identified by (3.3) recursively. The proof is given in the Supplemental Appendix. In Section A.4 of the Supplemental Appendix, we also discuss several important special cases of the dynamic RD model, including having an absorbing state treatment and not observing some initial rounds of RD data. Quantitative Economics 15 (2024) Dynamic regression discontinuity 1051 4. Estimation and inference Estimation of the one-period-after ATE is discussed in Section 2.4 for the benchmark two-period model. In the next, we first study inference of the proposed one-period-after ATE estimator. Then we extend the two-period estimation and inference strategy to the general multiperiod setting introduced in Section 3. 4.1 Inference in the benchmark two-period setting The inference procedure proposed in this section for the one-period-after ATE estimator defined in Section 2.4 adapts the weighted bootstrap procedure following Ma and Kosorok (2005). The procedure is tractable in empirical applications as it keeps estimation and inference of different long-term ATEs within a uniform format. The procedure does not pursue bandwidth choice optimality in the sense of asymptotic mean squared errors (AMSE), however. In the Supplemental Appendix, we discuss an alternative AMSE-optimal estimation and inference procedure for the one-period-after ATE based on Calonico, Cattaneo, and Titiunik (2014), Calonico, Cattaneo, and Farrell (2018, 2020,2022).8The weighted bootstrap procedure discussed in this section could also be adapted for recursive CFR estimators. 4.1.1 Assumptions and asymptotic properties Let φγ1,ni(D2i,S2i,Z1i,Xi)and φγ0,ni(D2i,S2i,Z1i,Xi)be influence functions of estimators ˆγ1and ˆγ0defined in Section 2.4, respectively, such that √nhˆγ1−γ1=1 √nh n  i=1 φγ1,ni(D2i,S2i,Z1i,Xi)+op(1), √nhˆγ0−γ0=1 √nh n  i=1 φγ0,ni(D2i,S2i,Z1i,Xi)+op(1). Let ˜ φα1,ni(Y2i,D2i,S2i,Z1i,Xi)and ˜ φα0,ni(Y2i,D2i,S2i,Z1i,Xi)be influence functions of infeasible estimators ˜α1and ˜α0defined by the following: ˜α1,˜ β1=argmin α,β n  i=1 1(Z1i≥0)KZ1i hAiα,β;γ12, ˜α0,˜ β0=argmin α,β n  i=1 1(Z1i<0)KZ1i hAiα,β;γ02. The infeasible estimators are generated by the same local linear regressions as used in Section 2.4 for estimators ˆα1and ˆα0, but assuming known first-step propensity scores. 8Extending the robust inference procedure to longer-term ATE estimators could be realized through calculating first-order linear approximations of each τ-period-after estimator (e.g., Sections 4.1 and 4.2 of Calonico, Cattaneo, and Titiunik (2014)) for bias correction and optimal bandwidth choice calculation. It would be an interesting topic for future research. 1052 Hsu and Shen Quantitative Economics 15 (2024) Define gradient terms 1 γ=limz10E[∇γ[Y2S2(D2−p(X,γ)) 1−p(X,γ)]|γ=γ1|Z1=z1]and 0 γ= limz10E[∇γ[Y2S2(D2−p(X,γ)) 1−p(X,γ)]|γ=γ0|Z1=z1]. By the delta method, we obtain the following influence function representation of ˆα0and ˆα1such that for d1=0, 1, we have √nhˆαd1−αd1 =1 √nh n  i=1˜ φαd1,ni(Y2i,S2i,D2i,Z1i,Xi)−d1 γ·φγd1,ni(D2i,S2i,Z1i,Xi)+op(1) ≡1 √nh n  i=1 φαd1,ni(Y2i,S2i,D2i,Z1i,Xi)+op(1). (4.1) The representation implies that the asymptotic variance of ˆ ¯ θ1,1 could be estimated by ˆ V11 =1 nh n  i=1ˆ φα1,ni(Y2i,D2i,S2i,Z1i,Xi)2+ˆ φα0,ni(Y2i,D2i,S2i,Z1i,Xi)2, where ˆ φαd1,ni(Y2i,D2i,S2i,Z1i,Xi)is the estimated version of φαd1,ni(Y2i,D2i,S2i,Z1i, Xi)with all unknown parameters replaced with corresponding estimators; d1=0, 1. We next provide detailed assumptions and asymptotic properties of the proposed two-step estimator with respect to a varying coefficient logit first stage. For notational simplicity, we assume for the rest of the paper that the Xivector includes a constant. Then a varying coefficient logit first-stage model is formulated as p(x,γ)=L(xγ)with L(a)=exp(a)/(1+exp(a)). Assumption 4.1. λ(x;z1)=L(xγ(z1)) is the correct specification on z1∈Nfor some >0. Assumption 4.2. Density fz1(z1)is twice continuously differentiable in z1on N,and fz1(z1)is bounded away from zero on Nfor some >0. Assumption 4.3. Assume that: 1. The kernel function K(·)is a nonnegative symmetric bounded kernel with support [−1, 1];K(u)du =1. 2. The bandwidth satisfies that h→0, nh3→∞,and nh5→0as n→∞. Assumption 4.1 requires that the varying coefficient logit model is correctly specified. Assumption 4.2 imposes standard smoothness conditions on the density of the running variable. Assumption 4.3 imposes standard conditions on the kernel function and undersmoothed bandwidth. Undersmoothing is required such that the bias of kernel estimators becomes asymptotically negligible. In practice, we recommend using the triangular kernel (i.e., K(x)=|x|·1(|x|<1)) and undersmoothing the robust RD bandwidth introduced in Calonico, Cattaneo, and Titiunik (2014) (CCT), which is of order n1/5. As discussed earlier, undersmoothing is not AMSE optimal. In the Supplemental Quantitative Economics 15 (2024) Dynamic regression discontinuity 1053 Appendix, we propose an alternative procedure that uses bias correction and AMSEoptimal bandwidth in the second step. The alternative procedure also requires a higherorder local polynomial and a larger bandwidth in the first step such that estimation errors from the first step do not affect AMSE of the final estimator. The following lemma provides asymptotic properties of the first-step varying coefficient logit estimators. Similar results could be derived if the propensity score function λ(.; .)follows other semiparametric models such as varying coefficient Probit. Lemma 4.1. Suppose that Assumptions 4.1–4.3 and B.1–B.2 hold.Then for d=0, 1, we have √nhˆγd−γd hˆ βd FS −hβd=1 √nh n  i=1d−1S2i·1(Z1i≥0)d·1(Z1i<0)1−d ·K(Z1i/h)D2i−LX iγd+βdZ1iXi Z1iXi/h+op(1), where disgiveninequation(D.2) in the Supplemental Appendix.In addition,for d= 0, 1, we have √nhˆγd−γd hˆ βd FS −hβd⇒N0, d−1dd−1, where disgiveninequation(D.3) in the Supplemental Appendix. Aside from assumptions stated earlier, the lemma also requires Assumptions B.1 and B.2 in the Supplemental Appendix. The former imposes smoothness conditions on the varying coefficient in neighborhoods right above and below the RD cutoff. The latter imposes moment conditions on the conditioning covariates. For asymptotic properties of ˆα0and ˆα1, we impose additional Assumptions B.1 and B.4, stated in the Supplemental Appendix. The former includes smoothness conditions for the infeasible estimators ˜α0and ˜α1using true values of first-step propensity score functions. The latter imposes conditions that control the impact of first-step estimation errors on the asymptotic properties of feasible two-step estimators ˆα0and ˆα1.Giventhe assumptions, √nh(ˆαd1−αd1),ford1=0, 1, has linear representation as in (4.1)with ˜ φαd1,ni(Y2i,D2i,S2i,Z1i,Xi) =(10)·−1 z·1(Z1i≥0)d1·1(Z1i<0)1−d·K(Z1i/h) ·Y2i−E[Y2i|Z1i]−Y2iS2iD2i−LX iγd1 1−LX iγd1+EY2iS2iD2i−LX iγd1 1−LX iγd1Z1i ·1 Z1i/h, where z=fz1(0)·μz,0 μz,1 μz,1 μz,2 ,andμz,j=u≥0ujK(u)du for j=1, 2, . The influence function representation then implies the following asymptotic results. 1054 Hsu and Shen Quantitative Economics 15 (2024) Theorem 4.1. Suppose that Assumptions 4.1–4.3 and B.1–B.4 hold.For d1=0, 1,we then have √nhˆαd1−αd1d →N(0, Vαd1),d1=0, 1; √nh(ˆ ¯ θ1,1 −¯ θ1,1)d →N(0, Vα1+Vα0), where Vα0=limn→∞ limz10h−1E[φ2 α0,ni(Y2i,D2i,S2i,Z1i,Xi)|Z1i=z1]and Vα1= limn→∞limz10h−1E[φ2 α1,ni(Y2i,D2i,S2i,Z1i,Xi)|Z1i=z1]. The exact expressions of Vα0and Vα1are tedious to calculate in general. In the next section, we adapt the weighted bootstrap procedure first introduced in Ma and Kosorok (2005) to simulate the limiting distribution of the proposed estimator. Studies adopting the procedure in other settings include Chen and Pouzo (2009), Chernozhukov et al. (2015), Chernozhukov, Fernández-Val, and Kowalski (2015), and Fernández-Val, van Vuuren, and Vella (2021), among many others. Our paper is the first to apply weighted bootstrap to kernel-based boundary estimation, which is the main workhorse of the RD literature. 4.1.2 Weighted bootstrap inference Let {Wi}n i=1be a sequence of pseudo-random variables independent of the sample path with unit mean and variance. Define the weighted bootstrap estimator for ¯ θ1,1 as ˆ ¯ θw 1,1 =ˆα1,w−ˆα0,w, ˆα1,w,ˆ β1,w=arg min α,β n  i=1 Wi·1(Z1i≥0)KZ1i hAiα,β;ˆγ1,w2, ˆα0,w,ˆ β0,w=arg min α,β n  i=1 Wi·1(Z1i<0)KZ1i hAiα,β;ˆγ0,w2, where ˆγ1,w,ˆ β1,w FS =argmax γ,β n  i=1 Wi·S2i1(Z1i≥0)KZ1i h ·D2ilogp(Xi,γ+βZ1i)+(1−D2i)·log1−p(Xi,γ+βZ1i), ˆγ0,w,ˆ β0,w FS =argmax γ,β n  i=1 Wi·S2i1(Z1i<0)KZ1i h ·D2ilogp(Xi,γ+βZ1i)+(1−D2i)·log1−p(Xi,γ+βZ1i). The weighted bootstrap procedure is simple to carry out. Given a simulated copy of {Wi}n i=1, weighted bootstrap repeats the original two-step kernel-based estimation procedure (i.e., first-step local MLE propensity score estimation and second-stage local linear regressions), replacing the original kernel weights K(Z1i/h)with new weights Quantitative Economics 15 (2024) Dynamic regression discontinuity 1055 Wi·K(Z1i/h). The procedure could also be easily extended to adjust for within-cluster correlations by assigning random Wiat the cluster level. Following Ma and Kosorok (2005), √nh(ˆ ¯ θw 1,1 −ˆ ¯ θ1,1)and √nh(ˆ ¯ θ1,1 −¯ θ1,1)have the same limiting distribution under suitable conditions. The next theorem formalizes the validity of the weighted bootstrap estimator given a varying coefficient logit first stage. Theorem 4.2. Suppose that Assumptions 4.1–4.3 and B.1–B.4 hold and that {Wi}n i=1is a sequence of i.i.d.pseudo-random variables independent of the sample path with E[Wi]= Var[Wi]=1for all i.We then have √nhˆ ¯ θw 1,1 −ˆ ¯ θ1,1d →N(0, Vα1+Vα0) conditional on the sample path with probability approaching one. Although Wican follow any distribution with unit mean and variance, in the simulation and empirical sessions where the first-step propensity score function is modeled with varying-coefficient logit, we use a discrete distribution where Wi=0.5 or 3 with probabilities 0.8 and 0.2, respectively. The binary random variable with positive support ensures that the weighted logit objective functions remain globally concave. 4.2 Estimation and inference in the general multiperiod setting Long-term ATEs in the multiperiod setting or E[θi;τ,1|Zi1=0]for τ≥2 are identified in Lemma 3.2. This section elaborates their estimation and inference. Let us start with case of τ=2. To estimate the two-period-after ATE, or ¯ θ2,1 ≡ E[θi;2,1|Zi1=0], one can first estimate the one-period-after average first-stage effect ¯η1,1 ≡E[ηi;1,1|Zi1=0]following the estimation procedure for one-period-after ATE, or ¯ θ1,1, described in Section 2.4, treating first-stage treatment decisions as outcomes. Then one can estimate other components of equation (3.3). Similarly, the estimation of any τ-period-after ATE for τ≥3 involves estimating the average first-stage effect ¯ηk,1 ≡E[ηi;k,1|Zi1=0]for all k=1, 2, ,τ−1, which can be done recursively following Lemma 3.2, and separate estimation of other components in equation (3.3). We formally define the estimator of ¯ θ2,1. Rewriting Lemma 3.2 with τ=2gives ¯ θ2,1 =α1 1−α0 1−˜μ0 nu/˜μde¯η1,1,where˜μ0 nu =lim z10EYi2Si2Di2−λ0(Xi) 1−λ0(Xi)Zi1=z1, ˜μde =E[Di2|Zi1=z1], α1 1=lim z10EYi3−Yi3Si2Di2−λ1(Xi) 1−λ1(Xi)Zi1=z1, α0 1=lim z10EYi3−Yi3Si2Di2−λ0(Xi) 1−λ0(Xi)Zi1=z1. Let ˆα1 1,ˆα0 1,ˆ ˜μ0 nu,ˆ ˜μde,ˆα1 fs,andˆα0 fs be estimators of α1 1,α0 1,˜μ0 nu,˜μde,α1 fs,andα0 fs, respectively. All of them can be defined using the same two-step semiparametric procedure described in Section 2.4 for the estimation of ˆα0and ˆα1, where the first-step 1056 Hsu and Shen Quantitative Economics 15 (2024) propensity estimation uses kernel-based local MLE. Let φα1 1,ni,φα0 1,ni,φ˜μ0 nu,ni,φ˜μde,ni, φα1 fs,ni,andφα0 fs,ni denote the influence functions of the estimators, respectively. Definitions of φα1 1,ni,φα0 1,ni,φ˜μ0 nu,ni,φα1 fs,ni,andφα0 fs,ni are similar to influence functions giveninequation(4.1)forˆα0and ˆα1. The influence function for ˆ ˜μde is defined as φ˜μde,ni =1 fz1(0)K(Z1i h)(D2i−E[D2i|Z1i]). Let ˆ ¯ θ2,1 =ˆα1 1−ˆα0 1−ˆ ˜μ0 nu/ˆ ˜μde(ˆα1 fs −ˆα0 fs)be the estimator of ¯ θ2,1. By the delta method, we have √nh(ˆ ¯ θ2,1 −¯ θ2,1)=1 √nh n i=1φ¯ θ2,1,ni(Y3i,Y2i,D3i,D2i,S2i,Z1i,Xi)+ op(1),whereφ¯ θ2,1,ni(Y3i,Y2i,D3i,D2i,S2i,Z1i,Xi)=φα1 1,ni −φα0 1,ni −α1 fs−α0 fs ˜μde φ˜μ0 nu,ni + ˜μ0 nu(α1 fs−α0 fs) (˜μde)2φ˜μde,ni −˜μ0 nu ˜μde (φα1 fs,ni −φα0 fs,ni ). The asymptotic normality of ˆ ¯ θ2,1 follows from the influence function representation. Given the influence function representation, it is easy to see that the weighted bootstrap procedure could be applied here, too, and in general, to the inference problem of any τ-period-after ATE with τ≥2. Monte Carlo simulations for the proposed estimation and inference procedure are summarized in the Supplemental Appendix. 5. Empirical example:The effect of CA school bonds This section revisits the study of local education bonds using the data set published by CFR. As described in CFR, school districts in California became eligible for issuing general obligation bonds through Proposition 46 in 1984. CFR study the effects of bond authorization on local house prices, student achievements, and other outcomes using California data from 1987 to 2006. Due to data limitations, we study two outcome variables: total expenditure per pupil and capital loading per pupil in a school district. There are 1551 bond measures from 655 school districts with nonmissing vote share information. Although the data set starts from the first years of education bonds, the expenditure outcomes we use are not observed until 1995. Among all the bond measures, 282 are proposed after 5 or more years of inaction (no measure) and have nonmissing expenditure outcome data up to 4 periods after the measure year. We focus on long-term effects of these bond measures. Figure 1gives a visual illustration of the data. The bottom row of the figure shows immediate and long-term total first-stage effects of passing an education bond measure. No school districts that barely passed the vote share cutoff in the first trial authorized another bond the following year. The probabilities increase slightly in years 3 and 4. Around 27% of school districts that barely missed the vote share cutoff in the first trial successfully authorized their first education bond in the following year. The negative first-stage effects imply that long-term average total effects observed directly from outcome discontinuity are smaller than the long-term ATEs of policy interests. Table 1reports nonparametric estimation results of immediate and long-term average direct effects following the extended recursive CFR strategy formalized in Lemmas 2.1 and A.1. The estimated average effects for the capital outlays outcome are highly statistically significant. Effects of the total expenditures outcome are only marginally Quantitative Economics 15 (2024) Dynamic regression discontinuity 1057 Figure 1. Average total effects and histograms. Note: The data set is from Cellini, Ferreira, and Rothstein (2010). The kernel bandwidth of each row is set to the same value, which is the average of CCT bandwidths among all four RD regressions of the row. The data sample of the first two rows is a subset of that of the last row, because of missing values in the expense outcomes. significant. Estimates in Table 1are larger than those reported in Table 4 of CFR. The difference comes from two sources. First, Table 4 of CFR is estimated by pooling different rounds of RDs. Under treatment effect heterogeneity, such a pooling strategy is not ap- 1058 Hsu and Shen Quantitative Economics 15 (2024) Table 1. Average direct effects: nonparametric CFR based on Lemmas 2.1 and A.1. Immediate One-period-after Two-period-after Three-period-after k=4.25 4.5 4.25 4.5 4.25 4.5 4.25 4.5 Total expenditures per pupil 897 767 1502 1385 2101 2025 3581 3626 (664)( 601)( 885)( 826)( 1384)( 1294)( 1888)( 1775) Capital outlays per pupil 361 275 497 455 1002 977 2379 2399 (248)( 216)( 203)( 186)( 569)( 497)( 1026)( 898) Note:ThedatasetisfromCellini, Ferreira, and Rothstein (2010). Standard errors are calculated using weighted bootstrap with 1000 bootstrap repetitions. Undersmoothed CCT bandwidth is calculated following suggestions in Section E of the Supplemental Appendix, with the CCT bandwidth reported in Figure 1. propriate, because marginal individuals at different rounds of RD cutoffs have different treatment effects. Second, Table 4 of CFR is estimated parametrically with global polynomials while Table 1is estimated nonparametrically using the local linear method. Table 2reports estimation results following the proposed method. Varyingcoefficient logit is used in first-step propensity score estimation. Panel A of the table reports estimation and inference results when the CIA condition in Section 2holds without any conditioning covariate. Panel B of the table reports results when the first-period outcome is used as the first-stage conditioning covariate. The estimates are semiparametric and rely on the first-step varying-coefficient logit functional form of propensity Table 2. Average direct effects: the proposed procedure. Immediate One-period-after Two-period-after Three-period-after k=4.25 4.5 k =4.25 4.5 4.25 4.5 4.25 4.5 Panel A: Total expenditures per pupil 897 767 1070 959 1440 1266 2532 2331 (664)( 601)( 776)( 716)( 1453)( 1244)( 2874)( 1992) Capital outlays per pupil 361 275 405 398 1245 1240 2850 2884 (248)( 216)( 158)( 149)( 448)( 401)( 882)( 760) Panel B: Total expenditures per pupil 897 767 903 808 1016 863 1682 1511 (664)( 601)( 964)( 882)( 2073)( 1863)( 4684)( 3629) Capital outlays per pupil 361 275 433 416 1387 1364 3176 3195 (248)( 216)( 176)( 164)( 495)( 472)( 1156)( 1146) Note:ThedatasetisfromCellini, Ferreira, and Rothstein (2010). Standard errors are calculated using weighted bootstrap with 1000 bootstrap repetitions. Undersmoothed CCT bandwidth is calculated following suggestions in Section E of the Supplemental Appendix, with the CCT bandwidth reported in Figure 1. Panel A reports estimation results with nonparametric first-step propensity score estimators with no conditioning covariates. Panel B uses the first-period outcome as the conditioning covariate in the first-step propensity score estimation.