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1 See Hsiao, Ching, and Wan (2012) and Angrist, Jord, and Kuersteiner (2013) for alternative matching methods along this line of thought.

2 To gauge the uncertainty of the estimated treatment effect, the synthetic control method compares the estimated treatment effect with the “effects” estimated from placebo tests in which the treatment is randomly assigned to a control unit.

3 See Campbell, Lo, and MacKinlay (1997) for applications of factor models in finance.

4 For more empirical applications of the IFE estimator, see Kim and Oka (2014) and Gaibulloev, Sandler, and Sul (2014).

5 When the treatment effect is heterogeneous (as it is almost always the case), an IFE model that imposes a constant treatment effect assumption gives biased estimates of the average treatment effect because the estimation of the factor space is affected by the heterogeneity in the treatment effect.

6 For example, Acemoglu *et al.* (2016), who estimate the effect of Tim Geithner connections on stock market returns, conduct the synthetic control method repeatedly for each connected (treated) firm; Dube and Zipperer (2015) estimate the effect of minimum wage policies on wage and employment by conducting the method for each of the 29 policy changes. The latter also extend Abadie, Diamond, and Hainmueller (2010)’s original inferential method to the case of multiple treated units using the mean percentile ranks of the estimated effects.

7 Cases in which the treatment switches on and off (or “multiple-treatment-time”) can be easily incorporated in this framework as long as we impose assumptions on how the treatment affects current and future outcomes. For example, one can assume that the treatment only affect the current outcome but not future outcomes (no carryover effect), as fixed effects models often do. In this paper, we do not impose such assumptions. See Imai and Kim (2016) for a thorough discussion.

8
$\unicode[STIX]{x1D6FD}$
is assumed to be constant across space and time mainly for the purpose of fast computation in the frequentist framework. It is a limitation compared with more flexible and increasingly popular random coefficient models in Bayesian multi-level analysis.

9 For this reason, additive unit and time fixed effects are not explicitly assumed in the model. An extended model that directly imposes additive two-way fixed effects is discussed in the next section.

12 For a clear and detailed explanation of quantities of interest in TSCS analysis, see Blackwell and Glynn (2015). Using their terminology, this paper intends to estimate the Average Treatment History Effect on the Treated given two specific treatment histories:
$\mathbb{E}[Y_{it}(\text{}\underline{a}_{t}^{1})-Y_{it}(\text{}\underline{a}_{t}^{0})|\text{}\underline{D}_{i,t-1}=\text{}\underline{a}_{t-1}^{1}]$
in which
$\text{}\underline{a}_{t}^{0}=(0,\ldots ,0)$
,
$\text{}\underline{a}_{t}^{1}=(0,\ldots ,0,1,\ldots ,1)$
with
$T_{0}$
zeros and
$(t-T_{0})$
ones indicate the histories of treatment statuses. We keep the current notation for simplicity.

13 We attempt to make inference about the ATT in the sample we draw, not the ATT of the population. In other words, we do not incorporate uncertainty of the treatment effects
$\unicode[STIX]{x1D6FF}_{it}$
.

14 The idea of predicting treated counterfactuals in a DID setup is also explored by Brodersen *et al.* (2014) using a structural Bayesian time-series approach.

18 The DGP specified here is modified based on Bai (2009) and Gobillon and Magnac (2016).

20 In the Online Appendix, we list the years during which EDR laws were enacted and first took effect in presidential elections.

21 See Wolfinger and Rosenstone (1980), Mitchell and Wlezien (1995), Rhine (1992), Highton (1997), Timpone (1998), Timpone (2002), Huang and Shields (2000), Alvarez, Ansolabehere, and Wilson (2002), Brians and Grofman (2001), Hanmer (2009), Burden *et al.* (2009), Cain, Donovan, and Tolbert (2011), Teixeira (2011) for examples. The results are especially consistent for the three early adopters, Maine, Minnesota, and Wisconsin.

22 See, for example, Fenster (1994), King and Wambeam (1995), Knack and White (2000), Knack (2001), Neiheisel and Burden (2012), Springer (2014).

23 The data from 1920 to 2000 are from Springer (2014). The data from 2004 to 2012 are from The United States Election Project, http://www.electproject.org/. Indicators of other registration laws, including universal mail-in registration and motor voter registration, also come from Springer (2014), with a few supplements. Replication files can be found in Xu (2016).

24 We do not use the voting-eligible population (VEP) as the denominator because they are not available in early years.

25 As is shown in the figure and has been pointed out by many, turnout rates are in general higher in states that have EDR laws than states that have not, but this does not necessarily imply a causal relationship between EDR laws and voter turnout.

26 Note that although the estimated ATT of EDR on voter turnout is presented in the same row as the coefficient of EDR using the FE model, the GSC method does not assume the treatment effect to be constant. In fact, it allows the treatment effect to be different both across states and over time. Predicted counterfactuals and individual treatment effect for each of the nine treated states are shown in the Online Appendix.

27 The results are similar if additive state and year fixed effects are not directly imposed, though not surprisingly, the algorithm includes an additional factor.

28 Although it is not guaranteed, this is not surprising since the GSC method uses information of all past outcomes and minimizes gaps between actual and predicted turnout rates in pretreatment periods.

29 The results are essentially the same with or without controlling for the other two registration reforms.

30 Although we can control for indicators of Jim Crow laws in the model, such indicators may not be able to capture the heterogeneous impacts of these laws on voter turnout in each state.

31 In the Online Appendix, we show that the treatment effects are positive (and relatively large) for all three early adopting states, Maine, Minnesota, and Wisconsin. Using a fuzzy regression discontinuity design, Keele and Minozzi (2013) show that EDR has almost no effect on the turnout in Wisconsin. The discrepancy with this paper could be mainly due to the difference in the estimands. Two biggest cities in Wisconsin, Milwaukee and Madison constitute a major part of Wisconsin’s constituency but have neglectable influence to their local estimates. One advantage of Keele and Minozzi (2013)’s approach over ours is the use of fine-grained municipal level data.

32 Glynn and Quinn (2011) argue that traditional cross-sectional methods in general overestimate the effect of EDR laws on voter turnout and suggest that EDR laws are likely to have minimum effect on turnout in non-EDR states (the ATC). In this paper, we focus on the effect of EDR in EDR states (the ATT) instead.