Data on the Relevant Institutional Features

Our standardized coding of relevant institutional features is based on the prototypical redistricting process shown in Figure 3. First, an initial map drawer proposes a plan that may be vetoed by other actors. If the plan is not vetoed, it can be challenged in court. If it is vetoed, there is another round of map drawing. If a plan is vetoed twice, or if the initial map drawer cannot agree on a plan, then a different institution (often a court) must resolve the stalemate and adopt a plan.

Figure 3.

Prototypical Game Tree Used to Model Redistricting

Note: States differ in which party, if any, controls each node, and which nodes are present in the state’s process.

Every state’s process can be described as a subset of this prototype. For example, in Michigan, a commission draws congressional districts, resolves any stalemates, and there is an explicit mechanism for state court review. Thus, Michigan’s process would be described by the “Drawer” step in Round 1 and “Stalemates” steps only in Figure 3.

For each state, we record which institutional body, if any, acts at each step and which party, if any, controls that institution. We also collected additional information relevant to modeling redistricting processes and court review, such as whether the state’s redistricting plans were subject to DOJ preclearance before 2013,Footnote ² and which institutional body ended up drawing the plan that was used in the first postcensal elections. Most procedural details are straightforward, and the information for coding is readily available in public data from each state (see, e.g., https://redistricting.lls.edu/). Furthermore, many states have similar redistricting procedures that are easily classified under the categories we defined earlier.

Section S1 of the Supplementary Material explains in detail how each of these variables was coded and describes special cases. Figure 2 of the previous section graphically summarizes this dataset for 2020 while Table S1.1 in the Supplementary Material presents all the variables across states in both 2010 and 2020.

The Redistricting Game

Coding the details of each state’s redistricting process preserves important procedural information, compared to categorizing each state into a small number of groups, such as “legislature-controlled” and “independent commission.” However, the detailed coding presents a challenge for causal inference, since the treatment—a state’s redistricting process—is now high dimensional. Out of the 87 state-decade processes we code,Footnote ³ there are 58 distinct combinations of procedural variables, 41 of which are completely unique.

The combination of high-dimensional treatment and a limited sample size means that there may not be enough information to estimate the causal effect of changing from one specific configuration of procedural variables to another, without further assumptions.

We address this methodological challenge by leveraging two basic substantive assumptions about the redistricting process. First, each party aims to draw a map that favors it as much as possible, and second, the parties are constrained by statutory and constitutional rules in doing so. Specifically, we treat the redistricting process depicted in Figure 3 as a sequential zero-sum gameFootnote ⁴ with two players—the Democratic and Republican parties—each trying to maximize the degree to which the drawn plan favors their party.

In each state, the nodes in the game tree can be controlled by different parties, or by neither party (e.g., when a supermajority is required to adopt a plan and neither party has supermajority control). Any split-control nodes, as well as a node for state court action, are considered moves by nature. Moves at one node do not affect the set of actions available at other nodes. Some nodes involve discrete choices, such as whether to veto a plan or not, others are labeled “choose bias,” meaning that the player at that node draws a plan with a chosen amount of partisan bias favoring either party. This bias is exactly the utility for the party of the chosen plan: a plan with bias x is worth x to the Republicans and $ -x $ to the Democrats. We need not quantify exactly what the utility measure is as a function of a specific plan chosen; it suffices to let the parties try to maximize an abstract univariate measure of partisan bias. We let the bias score range from $ -4 $ , indicating a maximum Democratic advantage, to $ +4 $ , indicating a maximum Republican advantage.

For concreteness, consider the case of redistricting in Oregon. In 2020, the first move belonged to the Democratic controlled legislature. It has to pick the amount of partisan bias $ -4<x<4 $ in the plan that it adopts. If this plan is ultimately the final enacted plan, Republicans receive utility x and Democrats receive utility $ -x $ . If the legislature fails to adopt a plan, the first stalemate move in Oregon belongs to a nonpartisan commission.

If a plan is adopted in the first round in Oregon, it proceeds to face a potential veto by the Democratic governor or a possible court review. The court may decide to accept a legal challenge, decide in favor of the plaintiffs, and redraw the map; this choice is considered a move by nature. If the court review results in a redrawn map with partisan bias $ {x}^{\prime } $ , then the Republicans receive utility $ {x}^{\prime } $ and the Democrats receive utility $ -{x}^{\prime } $ . In Oregon, court review is explicitly allowed on partisan grounds and challenges under the federal Voting Rights Act are possible, so there is moderate probability that the commission-adopted plan will be overturned. If no plan is enacted by the commission in the first round, the commission is again tasked with drawing a plan. If the commission fails to enact a plan again, courts must step in and redraw district lines to ensure compliance with federal constitutional “one person, one vote” apportionment requirements. This is also considered a move by nature.

To complete the description of the game, we must specify the rules for determining the expected outcomes for moves by nature. There are two kinds of moves by nature: map drawers controlled by neither party exclusively, and the results of court challenges. The full specification of these moves can be found in Section S2 of the Supplementary Material, but we briefly summarize them here. We make three assumptions: (1) nonpartisan map-drawers whose choices are subject to veto will generate maps which favor the party controlling the veto after a first veto has been made, (2) stalemate map-drawing will produce a map that is moderately balanced but tends to be influenced by any biases present in the most recent redistricting proposal, and (3) split-control map-drawers will stalemate with some probability and produce similar results to nonpartisan map-drawers the rest of the time. Similar assumptions about partisan map-drawers are not needed, since partisan drawers are assumed to act strategically within the game.

Finally, we decompose the court challenge process into five components: the probability that a legal challenge is possible, the probability that a challenge is made when possible, the probability that a court sides with plaintiffs, the expected remedy a court orders in those cases, and the probability and expected effect of a challenge based on the federal VRA. The latter applies only to states previously subject to DOJ preclearance. Each of these five components has a parametric specification, detailed in Section S2 of the Supplementary Material. The partisan control of state courts is accounted for in the specification of these various components, thus allowing judicial polarization to enter the picture without assuming absolute strategic coordination between the state party and its allies in the judiciary. Overall, the court challenge process is not modeled strategically, since non-party actors are more often than not the ones that initiate litigation and have different incentives than the party actors.

All in all, the game specification depends on 19 parameters which govern the moves by nature, with most of these parameters relating to the court challenge process. Rather than fix these parameters to arbitrary constants, we place a prior distribution on each parameter over a range of probable values. We simulate 200 different draws from this joint prior distribution; each draw generates a slightly different game specification. We then average our results across the random draws.Footnote ⁵

Equilibrium Solution as a Treatment Variable

To effectively summarize a high-dimensional treatment, we use the subgame perfect Nash equilibrium of the redistricting game. The utility of the equilibrium solution captures the expected partisan bias of plans that arise out of a state’s redistricting process, under the current party control of the state’s institutions. All of the multistep institutional interactions and negotiations that might happen as part of the redistricting process are thus reduced to a univariate score. The upshot is that the 14 procedural variables can be reduced into a single variable that measures the leeway political actors have over the partisan lean of the final redistricting plan.

To calculate the equilibrium itself, we numerically solve the game via backward induction. This requires up to four levels of nested optimization in some states. A later section describes a full example of this process for Michigan, and Section S2.5 of the Supplementary Material walks through a more complex, multistep example for Alabama. This solution process is automated across all of the states and is carried out on each of the 200 different draws from the prior on the game’s parameters. This process requires the use of several tuning parameters described at length when we present the full details of the game in Section S2 of the Supplementary Material. Further, Section S8 of the Supplementary Material shows that the values of our calculated equilibria are not sensitive to the choice of initial values for these tuning parameters.

For our causal analysis, we use three treatment measures. The first treatment measure is exactly the game’s Nash equilibrium, averaged across the prior. This measure depends on which parties control each node in the game tree. In our analysis of nonpartisan outcomes, we also use the absolute value of the equilibrium to capture the magnitude but not the sign of the expected bias. Finally, we also generate a third treatment measure that does not depend on the current party control. This is calculated by assigning a single party (here, the DemocratsFootnote ⁶) to control each node in the game tree that belongs to a partisan actor—legislature, governor, or partisan commission—and then recalculating the average Nash equilibrium. We refer to this equilibrium as the maximum leeway of a state’s redistricting process, since it captures the expected bias under a worst-case partisan outcome where all of the levers of state government are controlled by one party. The first and second treatment measures we refer to as the realized leeway and absolute realized leeway, since they depend on the realized values of the party control for each state institution.

Realized and Maximum Leeway Scores

Figure 4 visualizes these treatment measures for all the states we study; an arrow indicates a change in the treatment value from 2010 to 2020. The realized leeway scores (game equilibria) cover the entire range of possible partisan biases, from West Virginia in 2010 with complete Democratic control of state government, to Wisconsin, Iowa, Kansas, Utah, and Nebraska, where Republican trifectas were unconstrained by Democrats or by the VRA in both cycles. The maximum leeway scores likewise span the range of possible bias, but take on fewer values, since the various actual combinations of partisan control of state institutions are no longer considered.

Figure 4.

Summary of Treatment Values for All States

Note: Treatment values for each state in 2010, with values for 2020 indicated by arrows, where different. States in orange are those which experienced a reform to their redistricting procedures, either by legislation, constitutional amendment, or a court ruling that allowed for state court review of alleged partisan gerrymanders.

Intuitively, states introducing a commission (e.g., New York, Virginia, or Colorado) drastically reduced their leeway to match states with similar sets of rules in 2020. States that had intervening litigation to clarify the interpretation of state redistricting rules (e.g., New Mexico, North Carolina, or Pennsylvania) see appropriate changes in leeway, even absent a commission. Further, in our party-signed treatment, states that had a flip in party control of the whole system see large changes in leeway in the correct direction (e.g., West Virginia). Finally, states with minor changes to the total control of state institutions see minor changes in leeway (e.g., North Carolina).

Full Process Example: Michigan

Here, we build further intuition for our approach by summarizing each step described above for Michigan, a state that experienced a large change in leeway from 2010 to 2020 by adopting an independent commission. Section S2.5 of the Supplementary Material walks through a more complex example for this process in Alabama.

First, we outline the institutional structure of the redistricting process to establish the steps in the game. In Michigan, an independent commission drew the initial map in 2020. See Section S1 of the Supplementary Material for details on all steps for each state. Michigan’s commission makes the first move, which is to pick the amount of partisan bias $ -4<x<4 $ in the plan that it adopts. As above, the bias in this plan translates into partisan utility—if this proposal is adopted, Republicans receive utility x and Democrats receive utility $ -x $ .

The following steps also depend on the state’s specific institutional structure. In Michigan, if this initial proposal is adopted, the plan faces potential court review. Alternatively, if the commission’s first proposal fails, the stalemate move also belongs to the commission (see Section S1 of the Supplementary Material). While Michigan has no partisan veto points, plans in other states could also face potential vetoes at this point (or, in states like Iowa, could even face vetoes from two sources).

With this game structure established, we solve the equilibrium as above using backward induction. Michigan’s redistricting process requires one optimization step due to its lack of partisan veto points, though see Section S2.5 of the Supplementary Material for a more complex example with multiple subgames. This means that the last partisan move in the game is the initial (Round 1) commission proposal described above.

Our overall equilibrium solution for Michigan’s 2020 structure is a bias of $ -0.03 $ , suggesting very little bias in favor of either party. This near-zero bias reflects the lack of partisan control in this particular structure. Because our solution approach reflects institutional designs at each time period, our equilibria estimates also capture intuitive changes in leeway over time. For example, in 2010, Michigan redistricting was entirely controlled by the legislature and governor, who were both Republican. This game structure results in the highest possible value of maximum leeway (party-blind) near 4, as a single party controls all important game steps. However, our near-zero 2020 equilibria reflects the adoption of a strong independent commission. In the new process, the commission is bound by strict criteria, the process allows for court review, and even the commissioners themselves are selected in part by a lottery system. With the reform, Michigan’s maximum leeway changed from the highest observed value to zero, meaning that partisan actors have no control over redistricting outcomes, on average.

Empirical Validation of the Proposed Treatment Variables

Building treatment variables through a game-theoretic model provides significant advantages in dimension reduction and interpretability, but it also comes with the risk that the model is misspecified. Although it is difficult to completely verify the validity of each component of the model, we take several steps toward empirically validating the model as a whole, showing that the resulting treatment variable predicts the observed outcomes well. We also later conduct a robustness analysis for model misspecification in the context of causal effect estimation (see Section S6.2 of the Supplementary Material).

The model was designed to be flexible enough to capture the actual redistricting processes in each state. Any misspecification is therefore due to how the moves by nature are specified, or in the underlying setup of two opposing partisan actors competing on a single zero-sum dimension. First, we find that the treatment values are not sensitive to specific parameter values, up to monotonic transformations. Across the 200 random draws from the prior, the average pairwise Spearman correlation between the Nash equilibria for each state is above 0.99.Footnote ⁷ This also gives us confidence that the specific choice of the prior is not influencing the results.

Second, as shown in Figure 5, there is a substantial correlation in the expected direction between the treatment values and the measures of partisan advantage. The left panel plots the expected share of seats won by Republicans versus the realized leeway measure; recall that the leeway measure is positive for plans that favor Republicans. The right panel shows the partisan bias (King and Browning Reference King and Browning1987), measured at the state’s baseline vote share, versus the realized leeway. The greater values of partisan bias correspond to plans that systematically favor one party, with positive values favoring Republicans.

Figure 5.

Treatment Values versus Measures of Partisan Advantage

Note: Measures of partisan advantage versus treatment values for states’ enacted plans for the 2010 and 2020 redistricting cycles. Points are slightly jittered to avoid overplotting.

For both outcome measures, the purely a priori model predictions of the expected partisan bias do in fact correlate with the actual partisan bias of the plans that come out of each state’s redistricting process. To what extent these correlations can tell us about the causal effects of reforms is of course another matter, and the primary question addressed in the next section.

We also compare the equilibrium path in the model with the actual institution that drew the final map in each state. Because the moves by nature in the game are random, the actual equilibrium path may be a probabilistic mixture over multiple possible paths. We average these probabilities over the 200 draws of the game to arrive at an overall probability that a legislature, commission, or court draws the final map in each state, given its procedure and party control.

Table 1 compares the most likely final map-drawer, according to these probabilities, to the actual institution that drew the final redistricting plan. The correspondence is generally excellent, considering that the predictions are made based on theory alone. There is a tendency, however, for the model to predict court-drawn maps when they are in fact drawn by legislatures. The overall likelihood of a court intervention is itself a model parameter that is varied across random draws, and as noted above the ranking of the states by leeway is basically unchanged by different parameter values. Therefore, we expect this tendency to overpredict court intervention to at most slightly understate the equilibrium value for states with court review, since a higher likelihood of intervention would tend to pull the equilibrium toward zero.

Table 1.

Accuracy of Model Predictions of Final Map-Drawers

Note: Correspondence between the institution that drew the final redistricting plan for each state and the most likely outcome based on the equilibrium path of the redistricting game.

Finally, it is natural to wonder whether a more accurate model could be obtained by estimating the model parameters from the observed data rather than specifying their prior distributions. That is, one could find the parameter values that maximize the correlation between the treatment and the outcome. We do not take this approach to cleanly separate the estimation of causal effects from the construction of a treatment variable (Rubin Reference Rubin2008). This enables us to employ a causal identification strategy that does not assume the correct specification of the game-theoretic model. Instead, we use the model to summarize a high-dimensional treatment variable in a theoretically informed way without looking at the outcome variable.Footnote ⁸

Difference-in-Differences Design

To estimate the causal effects of changes in leeway on redistricting outcomes, we use a DiD design with a continuous treatment variable. This strategy addresses potential confounding by comparing changes in states that have enacted reforms to changes in similar states that have not modified their redistricting process across the 2010 and 2020 redistricting cycles. We assume that, in the absence of reforms, the states with institutional changes would have experienced the same trend in outcome variables as those states without reforms.

Formally, let $ {\mathbf{Z}}_{it} $ be the 14-dimensional vector of institutional features for state i at time t discussed in the data section above. We use $ t=0 $ and $ t=1 $ to denote 2010 and 2020 redistricting cycles, respectively. Let $ {u}^{*}(\mathbf{z}) $ represent the equilibrium outcome (game utility) for the average Nash equilibrium of the redistricting game described by the process $ \mathbf{z} $ . Then, we can define a univariate treatment variable $ {D}_{it}={u}^{*}({\mathbf{Z}}_{it}) $ for each state-decade, which represents the “dose” of institutional leeway given to political actors.

The key assumption made by our use of the Nash equilibria as the treatment variable is that the institutional features affect the outcome only through this treatment variable, that is,

$$ \begin{array}{rll}{Y}_{it}(\mathbf{z})={Y}_{it}({\mathbf{z}}^{\prime })\hskip0.35em \mathrm{for}\ \mathrm{any}\hskip0.35em \mathbf{z},{\mathbf{z}}^{\prime}\hskip0.3em \mathrm{with}\hskip0.3em {u}^{*}(\mathbf{z})={u}^{*}({\mathbf{z}}^{\prime }),& & \end{array} $$

where $ {Y}_{it}(\mathbf{z}) $ denotes a generic potential outcome variable for state i at time t with institutional features $ \mathbf{z} $ .Footnote ⁹ Under this sufficiency assumption, we can simply write the potential outcomes as $ {Y}_{it}(d)={Y}_{it}({u}^{*}(\mathbf{z})) $ for the treatment dose $ d={u}^{*}(\mathbf{z}) $ . While the assumption is not directly testable with the data we have, we evaluate robustness to its violations in Section S6.2 of the Supplementary Material by additionally controlling for $ \mathbf{z} $ in effect estimation; the resulting estimates are not statistically distinguishable from the main specification’s estimates.Footnote ¹⁰

Our target estimand is the conditional average treatment effect (CATE) for a change from the treatment level d to $ {d}^{\prime } $ given a set of covariates $ {\mathbf{X}}_i $ that are not affected by the treatment. The CATE is defined as

$$ \begin{array}{rll}{\mathrm{CATE}}_{\mathbf{x}}({d}^{\prime },d)=\unicode{x1D53C}[{Y}_{i1}({d}^{\prime })-{Y}_{i1}(d)\mid {\mathbf{X}}_i=\mathbf{x}].& & \end{array} $$

Estimating $ {\mathrm{CATE}}_{\mathbf{x}}({d}^{\prime },d) $ for any pair of values $ {d}^{\prime },d $ and covariate values $ \mathbf{x} $ requires the identification of a full dose–response curve. Our identification approach relies on a strong conditional parallel trends assumption introduced by Callaway, Goodman-Bacon, and Sant’Anna (Reference Callaway, Goodman-Bacon and Sant’Anna2024). Specifically, we assume that the average change in outcomes for states experiencing a change in treatment dosage from d to $ {d}^{\prime } $ depends only on the observed covariates, and not the observed dosage value.

Our covariates include a range of variables that existing work in the redistricting literature identifies as predicting redistricting outcomes and are not affected by redistricting reforms. We include (pretreatment) 2008 Democratic presidential vote share, an indicator for being in the South,Footnote ¹¹ the logarithm of the number of districts in 2020, the change in the number of districts between 2010 and 2020, the logarithm of the average number of state corruption convictions by year between 2000 and 2010, and an indicator for whether states allow ballot initiatives. For the maximum leeway treatment, which uses no information about partisan control of state institutions, we also control for changes in partisan control of the map-drawing body and of the state supreme court.

Formally, we require the following conditional parallel trends assumption for all $ d,{d}^{\prime } $ :

$$ \begin{array}{rll}\unicode{x1D53C}[{Y}_{i1}({d}^{\prime })-{Y}_{i0}(d)\mid {\mathbf{X}}_i=\mathbf{x}]=\unicode{x1D53C}[{Y}_{i1}({d}^{\prime })-{Y}_{i0}(d)\mid {\mathbf{X}}_i=\mathbf{x},{D}_{i0}=d,{D}_{i1}={d}^{\prime }].& & \end{array} $$

This assumption is analogous to the parallel trends assumption in the traditional binary DiD design, but differs in that it refers to changes in dosage across a continuous measure, rather than a single level change from zero. Compared to a traditional selection-on-observables assumption, the conditional parallel trends does not rule out confounding factors that are constant over time. With this assumption, we can identify our estimand as

$$ \begin{array}{r}{\mathrm{CATE}}_x(d,{d}^{\prime })=\unicode{x1D53C}[{Y}_{i1}-{Y}_{i0}\mid {\mathbf{X}}_i=\mathbf{x},{D}_{i0}=d,{D}_{i1}={d}^{\prime }]\\ {}-\unicode{x1D53C}[{Y}_{i1}-{Y}_{i0}\mid {\mathbf{X}}_i=\mathbf{x},{D}_{i0}=d,{D}_{i1}=d],& & \end{array} $$

where $ {Y}_{it}={Y}_{it}({D}_{it}) $ is the observed outcome. Averaging over the marginal distribution of $ {\mathbf{X}}_i $ , we can also estimate the average treatment effect (ATE).

Evaluating the plausibility of the parallel trends assumption here is complicated by a lack of public data on precinct-level election returns for the 2000 redistricting cycle or earlier cycles. Without these data, we cannot generate simulated districts for decades before 2010, which prevents us from conducting placebo checks using the pre-trends, a common practice for DiD studies. We are able, however, to conduct a placebo check using an outcome that should be unaffected by redistricting reform, as we discuss below.

Thus, at least partially, we are left to justify the assumption based on substantive grounds. To violate the conditional parallel trends assumption, the change in outcomes (such as Democratic seats) that would have been observed in Michigan, had it not adopted reforms, would have to systematically differ from the corresponding change in other non-reform states like Wisconsin, after controlling for covariates. The covariates we include are some of the strongest predictors of treatment adoption and redistricting outcomes, which substantially increases the plausibility of this assumption.

Second, aspects of the treatment and outcome themselves weigh against the possibility of a violation. Changes in redistricting procedure are usually advanced outside of legislatures, often via citizen referenda funded by nonpartisan good-governance groups who are not responsible for map-drawing. The political parties also coordinate redistricting strategy at a national level. Further, state legislatures and other map-drawing bodies experience turnover between decades.

Together, these factors suggest that the change in Michigan’s outcomes would have looked much like that of a non-reform state’s, had it not adopted reforms. In the specific example of Wisconsin, political developments since 2023 further justify this conclusion. A narrow state supreme court victory by a justice who campaigned, in part, in opposition to gerrymandering, led to a successful court challenge to state legislative maps that resulted in a significant decrease in the partisan bias of those maps (on common bias metrics). Challenges to the congressional maps are currently pending.

Adjusting for Political Geography

To further increase the credibility of the conditional parallel trends assumption above, we adjust for the changes in political geography between the two redistricting cycles. Partisan preferences and the geographic distribution of voters can change in different ways within each state over time. For example, Michigan, which experienced reform, became more Republican during our sample period, while Georgia, which did not, became more Democratic. Without this adjustment, an estimated effect of the Michigan reform would be biased by the differential change in the states’ political geographies.

To make the adjustment, we use representative sets of nonpartisan redistricting plans within each state that respect each state’s specific redistricting rules. These simulation samples were separately generated for 2020 (McCartan et al. Reference McCartan, Kenny, Simko, Garcia, Wang, Wu and Kuriwaki2022) and 2010 (Kenny et al. Reference Kenny, Simko, McCartan, Ebowe, O’Sullivan, Arora and Samarth2024) using the algorithm of McCartan and Imai (Reference McCartan and Imai2023). A detailed discussion of these simulations and their limitations may be found in Section S3 of the Supplementary Material. We subtract the mean outcome in each state’s simulated sample, denoted by $ {\overset{\sim }{Y}}_{it} $ , from the observed outcome $ {Y}_{it} $ before estimating the causal effects under the DiD design. We argue that this subtraction of the outcomes based on simulated baseline plans from the observed outcomes accounts for the change in political geography in each state.

One limitation of basing simulations off of each state’s rules is that any changes in outcome variables from 2010 to 2020 that are due to changes in rules would be subtracted away. Since redistricting rules are sometimes changed as part of larger reform efforts, part of the overall effect of redistricting reform would not be included in the measured effect, attenuating the overall estimated effects. However, these rules changes occurred in only a few states, and their effect on partisan outcomes was measured by Kenny et al. (Reference Kenny, McCartan, Simko, Kuriwaki and Imai2023) and found to be minimal.

Thus, we assume that once we adjust for the state-specific change in political geography, states with different changes in institutional features have parallel trends in the potential outcomes. Formally, if we denote the difference between the potential outcome and the simulated outcome as $ \Delta {Y}_{it}(d)={Y}_{it}(d)-{\overset{\sim }{Y}}_{it} $ , our conditional parallel trends assumption becomes

$$ \begin{array}{rll}\unicode{x1D53C}[\Delta {Y}_{i1}({d}^{\prime })-\Delta {Y}_{i0}(d)\mid {\mathbf{X}}_i=\mathbf{x}]=\unicode{x1D53C}[\Delta {Y}_{i1}({d}^{\prime })-\Delta {Y}_{i0}(d)\mid {\mathbf{X}}_i=\mathbf{x},{D}_{i0}=d,{D}_{i1}={d}^{\prime }]& & \end{array} $$

for all $ d,{d}^{\prime } $ . Then, as above, the CATE is identified as

$$ \begin{array}{r}{\mathrm{CATE}}_{\mathbf{x}}(d,{d}^{\prime })=\unicode{x1D53C}[\Delta {Y}_{i1}-\Delta {Y}_{i0}\mid {\mathbf{X}}_i=\mathbf{x},{D}_{i0}=d,{D}_{i1}={d}^{\prime }]\\ {}-\unicode{x1D53C}[\Delta {Y}_{i1}-\Delta {Y}_{i0}\mid {\mathbf{X}}_i=\mathbf{x},{D}_{i0}=d,{D}_{i1}=d],& & \end{array} $$

where $ \Delta {Y}_{it}={Y}_{it}-{\overset{\sim }{Y}}_{it} $ .

Estimation of Causal Effects

We estimate this causal estimand with a Bayesian linear regression model, where the response is the change in each simulation-adjusted outcome between 2010 and 2020, $ \Delta {Y}_{i1}-\Delta {Y}_{i0} $ (Section S7 of the Supplementary Material for the descriptive analysis of raw changes). The predictors are the change in treatment level $ {D}_{i1}-{D}_{i0} $ , the baseline treatment level $ {D}_{i0} $ , the covariates $ {\mathbf{X}}_i $ , and the interaction of the treatment change with baseline treatment and with each of the covariates. This is a regression-adjusted DiD estimator (Heckman, Ichimura, and Todd Reference Heckman, Ichimura and Todd1997). In contrast to the common two-way fixed effects estimator, this approach allows for heterogeneous treatment effects. The difference from most regression-adjusted estimators is the continuous treatment, which necessitates a modeling choice on the form of the dose–response curve (Callaway, Goodman-Bacon, and Sant’Anna Reference Callaway, Goodman-Bacon and Sant’Anna2024).

Given the small sample size ( $ n=87 $ ), the moderate number of covariates ( $ p=15 $ with interactions for the modal specification), and the high noise level, we believe that the linear specification and Bayesian estimation are appropriate. The coefficient priors help avoid overfitting to a few samples, and uncertainty in the ATE is automatically quantified; details on these priors are included in Section S5 of the Supplementary Material. A more flexible regression model beyond linear would be unlikely to increase predictive power, given the small sample size, and would further risk overfitting. However, as a robustness check, we also fit a nonparametric Bayesian Additive Regression Trees (BART) model (Chipman, George, and McCulloch Reference Chipman, George and McCulloch2010) and include those results in Section S6.1 of the Supplementary Material. The results are qualitatively the same, but the estimated effect magnitudes are attenuated.

Outcome Measures

Our measures can be divided into two buckets: nonpartisan outcomes that quantify how much gerrymandering is present or how responsive a districting plan is to shifts in public opinion, and partisan outcomes that capture which party is advantaged by a districting plan. For the nonpartisan outcomes, we also use the absolute value of the realized leeway as an additional treatment variable so that neither treatment nor outcome considers the partisan direction.

All of these measures are calculated from district-level election results. Since there is a significant exogenous variation in election results due to swings in the national political environment, rather than using actual 2012 and 2022 House election results to evaluate districting plans, we use a statistical model to estimate the distribution of election results across future hypothetical elections. A statistical election model also allows us to apply these same measures to the simulated districting plans, under which no elections have taken place.

We adopt the model from Kenny et al. (Reference Kenny, McCartan, Simko, Kuriwaki and Imai2023), which assumes district election outcomes can be decomposed into a baseline district-level vote share plus district-specific and national swings.Footnote ¹² The model is closely related to the stochastic uniform partisan swing model of Gelman and King (Reference Gelman and King1994) and the congressional model of Ebanks, Katz, and King (Reference Ebanks, Katz and King2023). As the baseline district-level vote, we use the 2008 presidential results for the 2010 redistricting cycle and an average of the 2016 and 2020 presidential results for the 2020 cycle, each logit-shifted so that the national partisan vote is exactly 50/50 (Voting and Election Science Team 2018; 2020). As in Kenny et al. (Reference Kenny, McCartan, Simko, Kuriwaki and Imai2023), we use historical congressional election data since 1976 to estimate the variance of district and national swings. We calculate exact expectations of all of our outcome measures against the predictive distribution of the model via numerical integration.

Our primary partisan measure of districting plans is the expected number of seats won by the Republican party. As discussed in the estimation section, we subtract the average outcomes in the simulated baseline redistricting plans (Kenny et al. Reference Kenny, Simko, McCartan, Ebowe, O’Sullivan, Arora and Samarth2024; McCartan et al. Reference McCartan, Kenny, Simko, Garcia, Wang, Wu and Kuriwaki2022) from the observed outcome in the enacted plan to adjust for the state-specific change in political geography, which is a potential confounding factor (Cottrell Reference Cottrell2019). After this adjustment, the seat outcome ranges from $ -1.57 $ in Illinois in 2020 (favoring Democrats) to $ 1.78 $ in Texas in 2020 (favoring Republicans). These simulation-differenced seats can be directly interpreted as a measurement of bias due to partisan gerrymandering, with positive values indicating a Republican bias beyond what would be expected based on the state’s political geography alone.

The expected number of Republican seats is an interpretable measure, but may not be completely comparable across states. Depending on political geography and especially the total number of districts in each state, the natural variation in the number of seats outcome may vary significantly between states. To address this, we also include as an outcome measure the simulation z-score of Republican seats, which is calculated by taking the simulation-differenced seats outcome and dividing it by the standard deviation of Republican seats in the simulation set (Kenny et al. Reference Kenny, McCartan, Simko, Kuriwaki and Imai2023). This puts all the states’ outcomes on a common scale, increasing the plausibility of the parallel trends assumption and the homoskedasticity assumption of the estimation model.

For a nonpartisan outcome measure, we take the absolute value of these two partisan measures. Both the absolute difference and the absolute z-score of Republican seats measure how far the enacted plan deviate from the nonpartisan simulation baseline in terms of partisan composition.Footnote ¹³

Finally, we also measure the responsiveness of districting plans to changes in the national electoral environment. Responsiveness is measured as the rate of change in the share of Republican seats given an infinitesimal change in Republican vote share nationwide. Responsiveness is closely linked to the presence of competitive seats; the more competitive seats there are, the larger the change in seat share will be for a given shift in vote share. Indeed, electoral responsiveness is the primary motivation for the creation of competitive congressional districts.

The responsiveness measure ranges from 0.044 in Wyoming in 2020 to 7.91 in New Hampshire in 2020, with most plans’ values lying between 0.5 and 3. The interpretation of these values is as follows; in New Hampshire, a 1 pp increase in a party’s vote share leads to a 7.91 pp change in the party’s expected seat share. This relatively large increase makes sense in context—both of the state’s congressional districts have Republican vote share within a few points of 50%. As with the other measures, we subtract the mean responsiveness of the simulated plans from the enacted plan’s responsiveness when estimating causal effects.

In Section S4 of the Supplementary Material, we extend the analysis to a series of alternative measures of partisan bias, such as the efficiency gap (Stephanopoulos and McGhee Reference Stephanopoulos and McGhee2015), and find qualitatively similar results.

Empirical Findings

We first study the effects of changes in maximum leeway on Republican seats. Recall that maximum leeway represents the worst expected bias under a single-party control. The left panel of Figure 6 shows the estimated coefficients of the estimation model fit to the simulation-adjusted seats variable. All estimated coefficients for this model and all other models in the article are contained in Section S10 of the Supplementary Material. The coefficients in Figure 6 are shown on the scale of the outcome, where a positive coefficient indicates a relationship with a positive change in Republican seats from 2010 to 2020. The model $ {R}^2 $ is around 0.4, highlighting the potential for the control variables to confound any observed correlation between reform and the outcome measure.

Figure 6.

Sample Model Fit and Estimated Conditional Average Treatment Effects

Note: Fitted model coefficient estimates for the Republican seat outcome measure (left) using the maximum leeway treatment, and estimated conditional average treatment effects for each reformed state’s covariate combination plotted against the state’s dose (right). The model-based dose–response curve is underlaid in blue. 80% and 95% credible intervals are shown throughout.

Given the fitted outcome model, we can estimate the CATE for any given starting and final value of maximum leeway and any combination of covariates. The right panel of Figure 6 plots these CATEs for each state that experienced a change in maximum leeway between 2010 and 2020, using the specific covariates of that state. There is a clear dose–response relationship between the decrease in maximum leeway and the decrease in the expected number of Republican seats.Footnote ¹⁴ A state with Michigan’s dose (nearly 4) has an estimated CATE of around $ -1.25 $ , with 95% credible interval (−2.4, 0.5), and so would be expected to gain just over one Democratic seat, on average. Similarly, a state with Ohio’s dose (just over 1) and covariates would be expected to gain about half of a Democratic seat (−0.7, −0.2). Motivated by this pattern, we also include in the right figure a dose–response curve calculated by calculating a CATE for dose level and averaging over the observed covariate distribution.Footnote ¹⁵

Since the dose–response pattern is well approximated by a linear relationship, we can summarize it by its slope, a quantity also known as the average causal response (ACR). The product of the ACR and a given dose corresponds to the estimated causal effect of that dose, averaged across states.

Figure 7 presents the ACR for Republican seats and the other outcome variables, using both the maximum and realized leeway treatment values. As mentioned above, for the nonpartisan outcomes, we also use the absolute value of the realized leeway as a treatment variable. The right side of the figure plots the ACR estimates in terms of the standard deviation of the respective outcome variable per unit change in treatment. This means that a point estimate of 0.5 is interpreted as an increase of 0.5 standard deviations of the outcome variable for a 1-unit change, or an increase of two standard deviations for a 4-unit change.

Figure 7.

Average Causal Response (ACR) of Leeway on Redistricting Outcomes

Note: The points correspond to the mean estimated ACR, while the lines represent 80% and 95% credible intervals. Intervals are colored by the treatment variable used. The numbers in the columns display the mean ACR on each outcome’s response scale. The estimates and intervals on the right are displayed in units of outcome standard deviations, to allow for comparability between outcomes. For partisan outcomes, a positive number indicates a pro-Republican effect and a negative number indicates a pro-Democratic effect for a positive dose.

Across the three nonpartisan outcomes measuring the amount of gerrymandering, we find a consistent effect of leeway. The estimated ACRs are all positive, meaning that an increase in leeway leads to a greater gap between the enacted plan and the simulated baseline. That is, states that reduce leeway through reform efforts are expected to rein in partisan gerrymandering. The magnitude of the effect is substantial: a reform effort like Michigan’s, with a decrease in the maximum leeway of four units, would be expected to reduce the difference in Republican seats from the baseline by about 0.6 seats (0.06, 1.20), or 2.6 simulation standard deviations (−1, 6)—enough to move an extreme partisan gerrymander to a fair plan. The ACRs for the absolute realized leeway are very similar to those for the maximum leeway; the ACRs for the fully signed realized leeway are positive but smaller in magnitude and have enough uncertainty that the 80% credible intervals cross zero. Thus, there is some weak evidence that giving Democrats more control of the redistricting process by increasing their leeway or reducing Republican leeway would also reduce gerrymandering.

We also find that reforms increase electoral responsiveness. The point estimates of the ACRs for both the maximum leeway and the realized leeway agree; the posterior probability that the effect is negative is more than 99% for both measures. The estimated effect for the absolute realized leeway is near zero. We estimate that a reduction in the maximum or realized leeway of four units would increase responsiveness by 1.5 (0.28, 2.67), meaning that a 1 pp increase in a party’s vote share would translate to an additional 0.6 pp in seat share on top of the average 2 pp increase in seat share across all states.

Another way to interpret the effect on responsiveness is in terms of the share of competitive seats, where a seat that is counted as competitive in proportion to how close its baseline partisanship is to 50%. This is equivalent to a linear rescaling of the responsiveness outcome.Footnote ¹⁶ In terms of competitive seats, we estimate that a reduction in leeway of four units would increase the share of competitive seats in an average state from 25% to 43% (28%, 58%).

In terms of partisan outcomes, the estimated ACRs on Republican seats are all positive, for both realized and maximum leeway. This is in line with an interpretation that increasing leeway benefits the party in control, as one might expect. Recall that the doses from Figure 4, for the realized leeway estimates, a dose of 4 represents approximately going from a Democratic legislature to an independent commission or an independent commission to a Republican legislature. For such a dose of 4, we would expect Republicans to gain around 0.75 seats (0.22, 1.27), or 8.6 simulation standard deviations (3.3, 13.5)—again, a substantial effect.

Placebo Check

As a further validation of our overall approach to estimating causal effects, we conduct a placebo check by applying the same estimation procedure to a political outcome variable that should not be affected by redistricting reform but is closely related to the outcome variable of interest. For this placebo outcome variable, we use the Democratic two-party vote share in the first presidential election following each census (2012 and 2024). As national contests, presidential elections are insulated from state-specific reform efforts. Moreover, issues like the economy, immigration, and health care dominate presidential campaigns, not state-specific governance issues such as redistricting reform. Thus, we expect there to be no effect of redistricting reforms on presidential vote share.

Figure 8 displays the estimated ACRs for the placebo outcome using each of the three treatment variables. All three estimates are nearly zero, with credible intervals that easily cover zero. If the estimates were significantly different from zero, we would suspect the validity of the sufficiency assumption, the parallel trends assumption, or the estimation method. That all placebo estimates are close to zero is therefore strong evidence of the plausibility of these assumptions and our estimation strategy overall.

Figure 8.

Average Causal Response (ACR) of Leeway on Placebo Outcome

Note: The points correspond to the mean estimated ACR, while the lines represent 80% and 95% credible intervals. Positive numbers correspond to an increase in Democratic vote share.

Analysis Procedure

To conduct the analysis, we apply fitted causal regression models based on the party-aware treatment to predict electoral outcomes under a series of hypothetical scenarios, in which every state adopts a redistricting commission with particular institutional powers, but partisan control of state institutions remains unchanged. Although each of the 15 states uses a redistricting commission with different structures and rules, our model is able to characterize these different commissions in terms of their partisan leeway and use these treatment values to predict electoral outcomes under a given commission structure.

We caution that any counterfactual policy analysis of this type involves substantial extrapolation from the observed data, and its results should therefore be interpreted as exploratory rather than confirmatory. While the regression models do allow for effect heterogeneity, the critical sufficiency assumption rules out unmodeled heterogeneity that may in practice lead to different reform effects.

We study three types of commission structures currently enacted in several states: (1) a New York-style commission with a nonpartisan map drawer and several partisan veto points; (2) an Ohio-style reform with legislature-drawn map and several partisan and bipartisan veto points and stalemate procedures, including a bipartisan commission stalemate procedure; (3) and a Michigan-style reform, with a nonpartisan commission, no partisan veto points, and the potential for court review.Footnote ¹⁸ Though each of these states has a commission of some kind, they differ in important ways—for example, Michigan’s elimination of partisan veto points removes the ability of partisan actors to veto unfavorable plans.

We visualize the impact of each reform structure using a seats–votes curve. Seats–votes curves are often used to study a measure of partisan bias, operationalized as the difference in the share of seats and votes at a given point on the curve (Katz, King, and Rosenblatt Reference Katz, King and Rosenblatt2020; King and Browning Reference King and Browning1987; Tufte Reference Tufte1973). A seats–votes curve for which a 50% vote share translates exactly to a 50% seat share represents the baseline for partisan bias. We approximate the seats–votes curve around 50% vote share as a line and estimate the effect of reforms on its slope and intercept separately. Up to a linear transformation, the slope corresponds to responsiveness and the intercept to seat share. These two outcome variables are differenced using the simulation sets, and a regression model is fit to these differenced outcomes, as discussed in the estimation section.

Findings

We find that nationwide adoption of commissions would generally reduce partisan bias, and that reforms that place additional restrictions on partisan actors (as in Michigan) are generally more effective. Figure 9 shows a seats–votes curve for each counterfactual commission scenario (the orange lines), which display the predicted number of total Democratic seats in the U.S. House (y-axis) for a given national Democratic vote share (x-axis). Figure S9.19 in the Supplementary Material presents the estimated state-level effects, which show that the reform effects in states with opposite partisan control (e.g., Texas vs. Illinois) may, in part, cancel out. The model predicts that all commission structures would reduce the existing Republican advantage in the House driven by both the inefficient geographic distribution of Democratic voters (Chen and Cottrell Reference Chen and Cottrell2016; Chen and Rodden Reference Chen and Rodden2015) and net partisan manipulation favoring Republicans (Kenny et al. Reference Kenny, McCartan, Simko, Kuriwaki and Imai2023).

Figure 9.

Predicted Seats–Votes Curves under Hypothetical Reforms

Note: The figure shows three predicted seats–votes curves if all U.S. states adopted new redistricting institutions with: (1) a New York-style commission with a nonpartisan map drawer and several partisan veto points; (2) an Ohio-style legislature-drawn map and several partisan and bipartisan veto points; and (3) a Michigan-style reform, with a nonpartisan commission, no partisan veto points, and the potential for court review. Hypothetical commission structures are plotted as orange lines (with 80% and 95% credible intervals), with reference lines for actual plans for both 2020 and 2010 in black.

We also compare these estimated relationships to the actual seats–votes curves for 2010 and 2020 (the black lines). We note that the lines for 2010 and 2020 intersect the 50% vote line below the 50% seat line, since a combination of the underlying geographic distribution of Democratic votes and gerrymandering efforts nationwide disadvantages the Democratic party. These results, however, do not necessarily imply that commissions would always advantage Democrats. For example, if political geography and electoral environments change in the future, the establishment of commissions may have different partisan impacts.

We find that New York- and Ohio-style reforms produce relatively moderate improvements in partisan bias and responsiveness. The point estimates for the number of Democratic seats gained under these reforms is 3.0 for New York-style reforms, with 95% credible interval (−0.17, 6.60), and 6.0 for Ohio-style reforms (1.8, 10.7). Responsiveness for New York- and Ohio-style reforms is also similar as for every 1 pp increase in vote share, Democrats gain an estimated 8.1 seats with New York-style reforms, and 8.3 seats with Ohio-style reforms. These responsiveness values are only slightly higher than the actual responsiveness following 2020 redistricting. Ohio-style reforms appear more effective overall, though the substantive differences are small; we are more than 99% confident that Ohio-style reforms produce a larger effect on partisan bias than New York-style reforms, and 89% confident that Ohio-style reforms increase responsiveness more than New York-style reforms do.

Further, we find that Michigan-style reforms have the greatest effects in both responsiveness and Democratic seats, since partisan actors are the most constrained by the presence of a nonpartisan commission, no partisan veto points, and the potential for court review. We estimate that the number of Democratic seats gained under Michigan-style reforms is 7.8 with 95% credible interval (2.1, 13.9), and that for every 1 pp increase in vote share, Democrats gain an estimated 8.3 seats (7.7, 8.9), an increase of 0.54 over the baseline. We are 91% confident that Michigan-style reforms have a larger effect than Ohio reforms, and more than 99% confident in a larger effect than New York-style reforms. We are also 94% confident that Michigan-style reforms increase responsiveness.

All three proposed reforms reduce the deviation from partisan symmetry. In this case, Democrats gain net seats which counteract the existing Republican advantage. However, greater effects are produced when, as in Michigan-style reforms, multiple nodes of the redistricting game constrain leeway by ensuring partisan nodes are nonpartisan, and do not precede partisan vetoes. Meanwhile, examples of New York-style and Ohio-style reforms demonstrate how constraining partisan actors at different nodes, through different reforms, may produce substantively similar effects.