RACIAL AND GENDER DIVERSITY ON THE FEDERAL BENCH

Historically, the federal judiciary has been composed of mostly white men. In fact, the first woman was not appointed to a federal Article III court until 1934 (Florence E. Allen), and the first Black judge was not named until 1950 (William Henry Hastie). Since the Carter administration, presidents have made concerted efforts to appoint more women and judges of color. We show these trends in Figure 1.

Figure 1.

Federal Article III Judges, 1977–2021

Note: Each panel plots a bar chart showing the total number of active and senior Article III federal judges serving on January 1 of each year, broken down by the party of the appointing president as well as the race and gender of the judges.

What role do the racial or gender identities of judges play in how cases get resolved? Examining a wide range of civil cases heard in the federal courts of appeals, studies have coalesced around the notion that—after controlling for some other observable judicial characteristics—a judge’s gender and race are associated with different outcomes in cases related to “racialized” or “gendered” issues, like employment discrimination (Farhang and Wawro Reference Farhang and Wawro2004; Morin Reference Morin2014; Songer, Davis, and Haire Reference Songer, Davis and Haire1994), affirmative action (Kastellec Reference Kastellec2013), and sex discrimination (Boyd, Epstein, and Martin Reference Boyd, Epstein and Martin2010).Footnote ⁶ These studies are unified by their common conclusion that women or racial minorities induce more liberal (pro-plaintiff) outcomes, but there are a few exceptions (e.g., Morin Reference Morin2014 on Latino judges in employment discrimination cases, and Songer, Davis, and Haire Reference Songer, Davis and Haire1994 on female judges in obscenity and search and seizure cases).

At the trial court level, an early contribution by Ashenfelter, Eisenberg, and Schwab (Reference Ashenfelter, Eisenberg and Schwab1995) did not find evidence that, controlling for a host of other factors, women resolve civil rights cases differently than men. Most recently, studies have concluded that cases assigned to women in the district courts are—adjusting for many other factors—more likely to result in pro-plaintiff outcomes in sex/pregnancy discrimination cases (Boyd Reference Boyd2016) and settled more frequently in civil rights cases (Boyd Reference Boyd2013). Controlling for other factors, Black judges increase pro-plaintiff outcomes in race discrimination suits (Boyd Reference Boyd2016), and judges of color are more likely than white judges to produce pro-claimant outcomes in Social Security disability cases (Boyd and Rutkowski Reference Boyd and Rutkowski2020).

Why might the races or genders of judges affect case outcomes?Footnote ⁷ Scholars have focused on three main theories. The first posits that women and people of color have “different voices” they bring to the bench, leading them to resolve cases differently. The second theory holds that women and people of color—due to their different experiences in life—bring different information to judging. Finally, the third theory says that female judges and judges of color will act as substantive representatives of women and people of color, respectively, advocating for those groups’ interests in their judicial decision-making. These theories are summarized in several recent papers, so we refer readers to those for more detailed descriptions (Boyd Reference Boyd2016; Boyd, Epstein, and Martin Reference Boyd, Epstein and Martin2010; Harris and Sen Reference Harris and Sen2019).

This literature has provided a large set of influential empirical findings. But it has some limitations. In addition to a relative lack of focus on the district courts, prior studies use research designs that are vulnerable to posttreatment statistical bias and that may partly obscure differences between judges of different races and genders. They also limit researchers’ ability to detect selection effects.

Trying to “Isolate” the Effect of Judges’ Identity Features Hides Important Selection Effects

Most quantitative studies of diversity in judging are framed around theories of judicial behavior that seek to explain why men and women, as well as white judges and judges of color, might generate different case outcomes. We briefly described these above. A common goal of these studies is to address potential confounding caused by other judge characteristics (like judges’ political ideologies). To do so, they typically include sets of judge-level control variables in their statistical analyses in order to “isolate” the specific effect of judges’ races or genders on case outcomes. In our review of prior studies, nearly all of them include judge-level control variables.Footnote ⁸

There are several problems with this. First, there is a standard selection on observables critique one could make about studies that control for specific judge-level characteristics. It is very difficult, if not impossible, to estimate an unbiased effect of a specific characteristic that is likely to be jointly determined with many other unobserved characteristics. We do not explore this critique in detail here, since there is a robust methodological literature on the topic (see Greiner and Rubin Reference Greiner and Rubin2011; Sen and Wasow Reference Sen and Wasow2016).Footnote ⁹ Moreover, since different studies control for different judge-level variables—usually some combination of a judge’s race, gender, age, ideology, tenure, prosecutorial experience, law school, religion, and prior judicial experience—it is unclear how to compare effects across studies.

There is another problem: reporting conditional effects can conceal insights about the overall impact of diversity on the bench. Consider a hypothetical dataset that generates the summary statistics presented in Table 1. A researcher is interested in seeing whether men or women are more favorable to plaintiffs, but she also has an intuition (based on theory) that ideologically liberal judges tend to rule for plaintiffs more often than ideologically conservative judges. She accordingly decides any regression looking at the effect of judge gender on case outcomes should include a control variable for judges’ ideologies.

Table 1.

A Hypothetical Dataset

Note: Each cell contains the proportion of pro-plaintiff decisions for each combination of the two judge-level characteristics in a hypothetical dataset.

An analysis like that would find that women are 5 percentage points more likely to rule for plaintiffs than men, holding constant judges’ ideologies. With this finding in hand, suppose that a hypothetical paper’s abstract reports: “Assignment of cases to women causes those cases to end in a pro-plaintiff way more often than assignment to men.” However, this statement may be misleading. Suppose now that the women in this dataset are more likely to be ideologically conservative than men in this dataset. Depending on how different the pools of men and women are, it is possible that the assignment of cases to women actually decreases the rate of pro-plaintiff decisions!Footnote ¹⁰

This is an example of Simpson’s Paradox, and it highlights the pitfalls of making claims about overall effects based on conditional estimates. This is substantively meaningful in our context: to know whether diversity on the federal bench affects case outcomes one would, at a minimum, want to know the overall effect. Yet the overall effect may be different in magnitude (or even direction) than a conditional effect. This is because differences in other judge characteristics might be an important consequence of diversifying the bench. Indeed, our own analysis demonstrates that nontraditional Republican appointees generate more conservative case outcomes than traditional Republican appointees, teaching us something important about the kinds of judges Republican presidents have put on the bench. Had we controlled for judges’ ideologies, we may have inadvertently hidden this finding.

An important clarification is necessary: controlling for judge characteristics is not the same thing as looking at treatment effects among subsets of judges.Footnote ¹¹ For example, since politicians from the two parties seem to approach the issue of diversity on the bench differently, there is a clear conceptual rationale for performing within-party analyses by comparing nontraditional appointees with the white men appointed by presidents of the same party. This is what we do in our analysis. We are examining conceptually grounded heterogeneous treatment effects, not trying to “control for” a judge’s political ideology, as is the standard rationale for including this variable in other judicial politics research.

Prior research studies often include judge-level control variables in order to test various hypotheses derived from theories of judicial behavior, and especially theories of race and gender in judging. Our focus is different since we seek to better understand whether the creation of a more diverse judiciary has affected case outcomes. As a result, we have no clear reason to include judge-level controls in our statistical models. But even if we were examining such theories of judicial behavior in this article, our core point still applies: including judge-level controls would weaken our ability to make accurate causal claims about the impact of diversity on the bench. When one includes judge-level controls in their main analyses, this is akin to skipping past the question “Do these judges have an effect?” and jumping straight to the question “Why do these judges have an effect?”Footnote ¹² We think it is important to convincingly estimate unbiased effects before exploring the mechanisms driving those effects (see also page 173 of Friedman et al. Reference Friedman, Lemos, Martin, Clark, Larsen and Harvey2020).

DATA AND RESEARCH DESIGN

We constructed an original dataset of civil rights cases filed in 20 federal district courts. For most of these courts, our dataset includes all civil rights cases either filed between 1995 and 2016, or filed between 1995 and 2020. However, for three of the smaller courts, our dataset spans fewer years. Because our identification strategy requires us to estimate effects within district and within year, the slight differences in year coverage across the courts in our dataset do not create methodological problems. In Figure 2, we show the composition of our dataset.

Figure 2.

Courts and Years in Our Dataset of Civil Rights Cases

Note: We show the number and percentage of cases in our dataset drawn from each of the 20 courts included in our analysis. For each court, we also use color shading to indicate the year range for which we have data from that court.

Our dataset contains information about each case’s characteristics as well as the presiding judge. Most of our case-level variables are drawn from the publicly available version of the Federal Judicial Center’s Integrated Database (known as the “IDB” and available at https://www.fjc.gov/research/idb). We identified civil rights cases using the nature of suit (NOS) code variable in this dataset (i.e., those with NOS codes beginning with 44). In Appendix A of the Supplementary Material, we provide additional information about these cases, both from the IDB and from a hand-coded random sample of cases in our dataset.

The publicly available version of the IDB redacts the judge name from each case and only contains rudimentary information about each case’s litigants. We add information about each case’s litigants and presiding judge from an original database of docket sheets that we collected from the federal courts’ fee-based online records system (called PACER) in connection with our ongoing research on judicial decision making. Twenty district courts from six different circuits and in four different regions of the United States issued us fee waivers that enabled us to access PACER for free. After more than a year of data collection and data cleaning, we were able to link judge-identifying information from these court records to the IDB.

Biographical data for each judge appearing in our dataset—and most importantly, each judge’s race and gender—are drawn from the FJC’s Biographical Directory of Article III Federal Judges (https://www.fjc.gov/history/judges). We follow prior research on federal judges and take the FJC’s Biographical Directory as an authoritative source of information about each judge’s racial and gender identity. We merge our three data sources together using both case numbers and judge names.

We supplement our main analysis with an analysis of a second dataset that contains all civil rights cases filed in every federal district court in 2016 and 2017. The docket sheets for this dataset were graciously provided by the Systematic Content Analysis of Litigation EventS (SCALES) Open Knowledge Network, which is working to build a platform that will provide open access to federal court data. We constructed this second dataset, which we call the SCALES dataset, using the same steps as we took for our main dataset.

Our statistical analyses focus on estimating the effect that assigning cases to nontraditional appointees instead of traditional appointees has on the outcomes of civil rights cases. Because our research design allows us to approximate a randomized experiment, we often describe the assignment of cases to nontraditional appointees as the “treatment” and the assignment of cases to traditional appointees as the “control.” We also decompose this treatment variable and show separate estimates for several subgroups of nontraditional appointees. Our choice to define “treatment” and “control” in this way is simply a matter of labeling; our results would be identical (but with the opposite sign) if we reversed this. In Figure 3, we provide more detail about the racial and gender breakdown of the judges in our main dataset. In Appendix A of the Supplementary Material, we provide this same information for the SCALES dataset.

Figure 3.

Races and Genders of the Judges in Our Dataset

Note: We plot the number of judges in our main dataset, broken down by judges’ races, genders, and partisanship.

District court cases can end in many different ways. In our analysis, we focus on the two most prevalent case outcomes in our dataset: settlements (45% of cases) and defendant wins (i.e., both involuntary dismissals and judgments favoring the defendant, together comprising 33% of cases). We code these case outcomes using both the IDB and our database of docket sheets. Appendix A of the Supplementary Material provides additional descriptions of these outcomes and additional details about our coding process.Footnote ¹³

Civil rights cases have a relatively clear political directionality to them (at least on average) since they almost always involve a plaintiff alleging a civil rights violation by a defendant.Footnote ¹⁴ We manually reviewed a random sample of cases and found that in only 3% of them could the plaintiff’s legal claims plausibly be classified as ideologically conservative (e.g., a claim that an employee was discriminated against on the basis of being white). As a result, we interpret defendant wins as more “conservative.” We interpret settlements as more “liberal” relative to defendant wins.Footnote ¹⁵

In order to provide unbiased estimates of the effect of assigning nontraditional appointees to cases, we rely on the assumption that judges are randomly assigned to cases. However, for this to be a reasonable assumption, we take several steps that we outline in detail in Appendix B of the Supplementary Material. In brief, we first drop subsets of cases (based on pretreatment characteristics) that we suspect are not randomly assigned, and then we perform an aggressive statistical test of case randomization.

After this data cleaning, our randomization test provides convincing statistical evidence that the remaining cases in our dataset were randomly assigned to judges within each district’s division and year. We can thus conceptualize our research design as a blocked (natural) experiment with as-if random treatment assignment within district-division-year randomization blocks. We use regression adjustment to account for the district-division-year randomization blocks, using the strategy described in Lin (Reference Lin2013) and research design recommendations provided in Lin, Green, and Coppock (Reference Lin, Green and Coppock2016).

Because our effects are only causally identified within each randomization block, we can only include randomization blocks that have sufficient variation in the treatment and control variables. This means our sample size varies across our analyses. We conduct our main analysis on 264,889 civil rights cases heard by 250 nontraditional appointees (164 appointed by Democratic presidents and 86 appointed by Republican presidents) and 295 traditional appointees (131 appointed by Democratic presidents and 164 appointed by Republican presidents). In all our figures, we include the sample size and number of judges for each analysis. We limit our analysis to cases assigned to judges appointed by Presidents Carter through Obama.

This estimation strategy allows us to recover credible causal estimates of the effect of assigning cases to nontraditional appointees, relative to assigning cases to white men. As we note above, we estimate effects separately for Democratic and Republican appointees to allow for the possibility that the effect of the assigned judge’s race or gender on case outcomes matters differently depending on whether he or she is a Democratic or Republican appointee.

The regression model we use for each of our analyses is

$$ \begin{array}{l}{Y}_i^p={\alpha}^p+{\beta}^p\cdot {N}_i^p\\ {}\hskip2em +{\displaystyle \sum_{dy}}\left\{{\phi}_{dy}^p\cdot {X}_{idy}^p+{\gamma}_{dy}^p\cdot {N}_i^p\cdot ({X}_{idy}^p-{\overline{X}}_{dy}^p)\right\}+{\varepsilon}_i^p,& & \end{array} $$

where i indexes cases, $ dy $ indexes a court division and case filing year (i.e., a randomization block), and p indexes the party of the appointing president. The variable $ {N}_i^p $ takes a value of 1 if case i is assigned to a nontraditional appointee and 0 if it is assigned to a traditional appointee. $ {X}_{idy}^p $ is a dummy variable indicating whether case i is in randomization block $ dy $ , and $ {\overline{X}}_{dy}^p $ is the proportion of cases in our sample heard within randomization block $ dy $ .

Our main estimate of interest for each analysis is the estimate for $ {\beta}^p $ , which gives the average treatment effect of a case being assigned to a nontraditional appointee of party p. We cluster standard errors at the judge level. We use the estimatr library for the R statistical programming language to estimate effects and standard errors (Blair et al. Reference Blair, Cooper, Coppock, Humphreys, Sonnet and Fultz2015).

DOES DIVERSITY ON THE BENCH BENEFIT CIVIL RIGHTS PLAINTIFFS?

We begin our analysis by estimating whether nontraditional appointees cause different case outcomes than traditional appointees. We plot these effects in the two left panels in Figure 4. Among Democratic appointees, there is no statistically significant difference in the average outcomes of the civil rights cases assigned to nontraditional appointees versus those assigned to traditional appointees. However, among Republican appointees, civil rights cases are less likely to end in settlements and more likely to end in wins for the defendant when assigned to a nontraditional appointee instead of a traditional appointee. Specifically, when a case is assigned to a nontraditional Republican appointee instead of a traditional Republican appointee, the case is 2.2 percentage points less likely to settle (p-value < 0.01) and 1.2 percentage points more likely to end in a judgment for the defendant (p-value < 0.05).

Figure 4.

Main Average Treatment Effects

Note: Each point plots an average treatment effect on a specific case outcome (depicted on the x-axis), along with a 95% confidence interval using judge-clustered standard errors. In the left two panels, we plot our main effects. In the right panel, we plot the average treatment effect of assigning Republican appointees to cases (instead of Democratic appointees), which we provide for comparison. For each estimate, we present the number of cases in the analysis (top number) and the number of treatment/control judges (bottom number). Full results for this plot are available in Table E.1 in Appendix E of the Supplementary Material.

To place these effect sizes in substantive context, we also estimate partisan differences in case outcomes. Specifically, for each of the two outcomes, we estimate the average treatment effect of assigning cases to Republican appointees instead of Democratic appointees using the same estimation strategy as described above. In the right panel of Figure 4, we plot the estimates for these partisan effects. Assignment to a Republican appointee instead of a Democratic appointee decreases the probability of settlement by 1.6 percentage points and increases the probability of a defendant win by 0.9 percentage points (although the latter effect is not statistically significant at the 0.05 level). Our effects for nontraditional Republican appointees are both in the same direction and similar in magnitude to the effects for assignment to Republican appointees rather than Democratic appointees. This gives us further confidence that settlements can roughly be interpreted as more liberal outcomes in civil rights cases and defendant wins can roughly be interpreted as more conservative outcomes in civil rights cases.

While these effect sizes may seem small in magnitude, it is well known that many cases filed in federal district courts are frivolous. Effects are likely to be concentrated in the cases that are not frivolous, but identifying those cases with existing datasets and without introducing posttreatment bias is a challenge.Footnote ¹⁶

Though our main dataset is expansive (covering 40% of the U.S. population), it is not a national sample. In order to mitigate concerns about generalizability, we supplement our main analysis with an analysis of the SCALES dataset, a smaller dataset but one that covers the population of civil rights cases filed in 2016 and 2017. Figure 5 displays the results, which support our previous findings: nontraditional Republican appointees cause fewer settlements and issue more decisions favoring defendants than traditional Republican appointees, while there is no difference among Democratic appointees.

Figure 5.

Average Treatment Effects in the SCALES Dataset

Note: Each point plots an average treatment effect on a specific case outcome (depicted on the x-axis), along with a 95% confidence interval using judge-clustered standard errors. These analyses use the SCALES dataset. Full results for this plot are available in Table E.2 in Appendix E of the Supplementary Material.

So far, we have only discussed whether cases end differently depending on whether they are assigned to nontraditional appointees or traditional appointees. However, we can also examine how the effects depend on which kind of nontraditional appointees are assigned to cases. In Figure 6, we show the effects on case outcomes for various subsets of nontraditional appointees. Each estimate is depicted with a circle and continues to use traditional appointees (i.e., white men) as the reference category. We restrict our analysis to only one outcome variable—settlements—but present analysis for defendant wins in Figure C.1 in Appendix C of the Supplementary Material. Note that we only present estimates when we have at least 20 judges in the treatment group.

Figure 6.

Average Treatment Effects for Subgroups of Judges

Note: Each point plots an average treatment effect on settlement, along with a 95% confidence interval using judge-clustered standard errors (the smaller bars present adjustments for multiple hypothesis testing using the Bonferroni method, with the number of independent tests estimated). Each estimate shows the estimated effect of assigning cases to judges with specific racial and/or gender characteristics, relative to traditional appointees. Full results for this plot are available in Table E.3 in Appendix E of the Supplementary Material.

There is little evidence of effect heterogeneity by subgroup. Because of the large number of statistical tests we are conducting, we focus on the thinner, longer confidence intervals reported in the figure, which have been adjusted for multiple hypothesis testing.Footnote ¹⁷ We find a statistically significant effect only for Republican white women and men of color. Despite those significant effects, it is important to note that there are generally no substantial differences between subgroups of nontraditional appointees. As is apparent from the figure, the confidence intervals across the subgroups are largely overlapping, with most point estimates being covered. Moreover, if one wanted to explicitly compare these effects to one another (e.g., comparing the effect for women of color to the effect for white women), even the adjustments we make to the confidence intervals are not aggressive enough since they only account for each test independently. We would need to adjust for the many additional hypothesis tests that are implied by comparing the estimates with one another. We thus cannot conclude that the overall effects of nontraditional appointees are driven by a particular subset of those judges.

DOES DIVERSITY ON THE BENCH BENEFIT WOMEN OR PEOPLE OF COLOR?

The significance of diversity on the bench may extend beyond its general impact on case outcomes. In particular, nontraditional appointees might improve outcomes specifically for women and people of color. As Harris and Sen (Reference Harris and Sen2019) point out, “[r]esearch suggests that more women on the courts would lead to more decisions favorable to women [and] more people of color on the courts would lead to more decisions favorable to people of color…” (243).

We use our dataset to explore this issue. First, we use standard automated methods to (1) identify which plaintiffs in our dataset are human individuals and (2) predict the race/ethnicity and gender of those individuals. We use the gender package in R to predict each plaintiff’s gender and the wru package in R to predict each plaintiff’s race or ethnicity.Footnote ¹⁸ Given that data on the racial and gender identities of civil plaintiffs are not typically collected by federal courts, researchers must rely on these cutting-edge tools to predict these characteristics based on available data. These tools are now commonly used in political science (e.g., Grumbach and Sahn Reference Grumbach and Sahn2020; Grumbach, Sahn, and Staszak Reference Grumbach, Sahn and Staszak2022). We discuss our data coding process in more detail in Appendix A of the Supplementary Material. Using our predictions, we identify cases where we predict that all plaintiffs were people of color or white and cases where we predict that all plaintiffs were women or men. In the subsets of cases filed by plaintiffs of color and white plaintiffs (of any gender), we test if judges of color cause different outcomes than traditional appointees. In the subsets of cases filed by women and men (of any race), we test if female judges cause different outcomes than traditional appointees.

We only examine whether our effects vary by the identity of plaintiffs. In the context of Israeli small claims courts, Shayo and Zussman (Reference Shayo and Zussman2011) show that defendant identity also affects case outcomes. This is a less salient issue in our setting since the majority of the defendants in our dataset are organizations and governments. Indeed, only a small subset of the cases in our dataset (around 7%) feature individual (human) plaintiff(s) suing individual (human) defendant(s).

In this analysis, of the judges included in the “judges of color” category for Democratic appointees, 56% are Black, 30% are Latino, and 16% are Asian American.Footnote ¹⁹ Of the judges included in the “judges of color” category for Republican appointees, 43% are Black, 49% are Latino, and 8% are Asian American. Among the cases filed by plaintiffs of color who were heard by judges of color, 46% were filed by plaintiffs of the same race as the judge. Among the cases filed by women who were heard by female judges, 44% were filed by plaintiffs of the same race as the judge.

We plot the results of these analyses in Figure 7. First, we do not find evidence of any benefit to plaintiffs of color for having their cases assigned to a judge of color instead of a traditional appointee, nor do we find any benefit to female plaintiffs for having their cases assigned to a woman instead of a traditional appointee (the square shaped point estimates in the figure). Second, we do not find any evidence that the treatment effect for judges of color varies by whether the plaintiffs are people of color or white; nor do we find any evidence that the treatment effect for women appointees varies by whether the plaintiffs are women or men (comparing the square shaped point estimates with the diamond shaped point estimates).

Figure 7.

Average Treatment Effects in Subsets of Cases

Note: Each point plots an average treatment effect on settlement, along with a 95% confidence interval using judge-clustered standard errors. The squares show the effect of assigning cases to judges with specific racial and/or gender characteristics in cases where the plaintiffs share the identity of the treatment group appointees. The diamonds show the effect of assigning cases to judges with specific racial and/or gender characteristics in cases where the plaintiffs do not share the identity of the treatment group appointees. Full results for this plot are available in Table E.4 in Appendix E of the Supplementary Material.

Because we are subsetting to a smaller number of cases filed by specific kinds of plaintiffs, testing for more nuanced effects than what we present in Figure 7 would slice our data very thinly. (For example, there were only around 150 cases filed by Asian plaintiffs that could have been assigned to an Asian American appointee.) Our focus is on testing the more statistically tractable claim summarized in Harris and Sen (Reference Harris and Sen2019) that judges of color will produce better outcomes for plaintiffs of color and female judges will produce better outcomes for female plaintiffs. Nonetheless, for curious readers, we present additional results in Figure C.2 in Appendix C of the Supplementary Material. We do not find evidence that nontraditional appointees provide more favorable outcomes for plaintiffs who share their identities.

ARE REPUBLICANS TRADING DIVERSITY FOR IDEOLOGY?

What could explain why nontraditional Republican appointees resolve cases more conservatively, while there are apparently no differences among Democratic appointees? We argue that the asymmetry between the parties in our results, as well as the direction of those results, is broadly consistent with a strategic logic of partisan bargaining over judicial nominations in which diversity plays a role in presidents’ strategic calculations (see also Asmussen Reference Asmussen2011). This strategic logic starts with the premise that a president requires some buy-in from politicians of the opposing political party in order to successfully appoint his or her judges. This premise is reasonable in our context since a president’s judicial nominees must be confirmed by the Senate, and, for the judges appointed in our dataset, both Senate rules and political norms made confirmation difficult without some support from members of both parties.Footnote ²⁰

In Appendix D of the Supplementary Material, we analyze a simple formal model of political bargaining over judicial nominations in which two political parties have preferences over both the ideology and demographic characteristics of a judge who is nominated to fill a judicial vacancy. A key parameter in the model is $ {b}_i\in \mathbb{R} $ , which is player i’s payoff from the president appointing a nontraditional appointee instead of a traditional appointee. So, holding all else equal: $ {b}_i>0 $ implies player i prefers a nontraditional nominee, $ {b}_i<0 $ implies player i prefers a traditional nominee, and $ {b}_i=0 $ implies player i is indifferent about whether the nominee is nontraditional or not.

Importantly, the player who makes a nomination in the model (i.e., the party that holds the presidency) pays a political cost if it does not win approval from the other party.Footnote ²¹ If a nominating president wishes to avoid paying this political cost, then she must provide some concession to the opposing party. This yields the following main result. (See Appendix D of the Supplementary Material for the formal analysis and proofs.)

Assuming that our model provides a reasonable approximation of the parties’ incentives when bargaining over judicial nominees, then an empirical implication of Proposition 1 is that observed effects among one party’s appointees reveal information about the other party’s preference for (or against) the appointment of nontraditional nominees.

In light of this strategic logic, our main empirical findings provide support for the notion that Democrats place substantial weight on appointing a more inclusive federal bench, while Republicans do not. As a result, Democratic presidents cannot gain any ideological advantage by strategically choosing the identity of their nominees since Republican politicians are fairly indifferent about the identities of judicial nominees. On the other hand, Republican presidents can use Democrats’ preference for diversity to extract ideological concessions, using diversity in appointments as a tool to appoint more conservative judges who would potentially engender more opposition from Democrats were they white men. We term this phenomenon “trading diversity” since Republican presidents can trade diversity for ideology, nominating nontraditional appointees who will act more conservatively on the bench.

Is there corroborating evidence to support the idea that Democrats value diversity while Republicans do not? Recall Figure 1, which demonstrates that Democratic presidents have appointed a substantially larger percentage of traditional appointees than Republicans. Between 1977 and 2020, 48% of Democratic presidents’ appointees were women or judges of color, whereas only 26% of Republican appointees were women or judges of color.

On its face, this descriptive statistic lends support for the key implication of our trading diversity argument—that Democrats value diversity more than Republicans. However, what if these patterns in appointments are simply an artifact of differences in the pools of potential appointees available to Democratic presidents and Republican presidents? Perhaps Republican presidents value diversity just as much as Democratic presidents, but they face much higher search costs when attempting to recruit appointees from underrepresented groups.Footnote ²² However, using the logic of our theoretical model, this is unlikely. If Republican politicians placed a premium on diversity, then by Proposition 1, we would expect to see nontraditional Democratic appointees making more liberal decisions than the Democratic-appointed white men. We do not see this pattern in our data.

A similar argument allows us to rule out an obvious alternative explanation for our finding that nontraditional Republican appointees make more conservative decisions: namely, that Republican presidents engage in taste-based discrimination against nontraditional appointees. Our trading diversity argument relies on Republicans being indifferent about diversity. If instead they were hostile to diversity, then this would (also) lead them to appoint especially conservative nontraditional appointees.Footnote ²³ However, this is not consistent with our other findings. If Republicans were biased against nontraditional appointees, then from Proposition 1 we would also expect that bias to result in more conservative nontraditional Democratic appointees since Democratic presidents would need to nominate more conservative nontraditional appointees in order to overcome Republicans’ racial or gender bias.

Our trading diversity argument is static and implies that appointing presidents make nominations that reflect the strategic environment at the point in time when they select judges for the bench. That said, our empirical results pool judges across time, comparing cases heard by all judges of color and women with cases heard by all white men. As is apparent from Figure 1, the bench has become more diverse as time passes. Our own dataset, for example, starts in 1995 with 36% of judges being nontraditional appointees and ends in 2020 with 55% being nontraditional appointees. There is a risk that the differences (or lack of differences) we see between traditional and nontraditional appointees in our analysis are driven simply by the fact that we are comparing nontraditional appointees disproportionately appointed more recently to traditional appointees appointed longer ago.Footnote ²⁴ If this were true, it would undermine our theoretical argument. To guard against this, we reestimate our effects from Figure 4 controlling for each presiding judge’s appointing president. Our effects are nearly identical, suggesting that our main effects are not driven by a time trend (see Figure C.3 in Appendix C of the Supplementary Material).

One final alternative explanation is that nontraditional Republican appointees may have been disproportionately appointed in times when there were fewer political constraints facing Republican presidents. If this had been the case, then Republican presidents would have been able to appoint more conservative judges (who just happened to be judges of color or women) because they faced less opposition from Democrats in the Senate. However, historical data on the partisan make-up of the Senate suggest that Republican presidents appoint nontraditional appointees when they face more of a political constraint. In our sample, nearly 51% of the white men appointed by Republican presidents were confirmed by a Republican majority in the Senate. In contrast, of the judges of color and women appointed by Republican presidents, 62% were confirmed when Republicans were in the minority in the Senate, consistent with the idea that political vulnerability encourages Republican presidents to trade diversity in order to see their judges confirmed.Footnote ²⁵

One might also take issue with the notion that presidents and senators are able to clearly discern ideological differences among those in their pool of potential nominees (see, e.g., Hofer and Achury Reference Hofer and Achury2021). For the logic of the model to work, presidents and senators must be able to predict which judges will make more or less ideological decisions. However, the logic of the model does not require that they perfectly predict this, only that these predictions are accurate on average.Footnote ²⁶ Moreover, we think our empirical analysis provides evidence that they do. Among Republican appointees, the differences in outcomes across nontraditional and traditional appointees are similar to the difference between Republican and Democratic appointees. If, as there is little doubt, presidents and senators can discern the across-party differences that affect case outcomes, then it is reasonable that they could also discern the within-party differences that yield effectively equivalent effects.

We argue that the logic of trading diversity provides a compelling explanation for our empirical results. However, our model black-boxes some potential mechanisms that are still consistent with our overall argument. For example, we do not know whether Republicans purposefully choose especially conservative women and people of color from a broad range of potential Republican appointees, or instead whether the pool of potential judges of color and women available to Republican presidents is especially conservative to begin with. Even if the pool of potential nontraditional Republican appointees is especially conservative, this is insufficient for explaining how they end up on the bench. To the extent that Democrats in the Senate have any leverage over Republican nominations, it is the Democratic preference for a more diverse judiciary that enables Republican presidents to appoint women and judges of color who make more conservative decisions.