Political Ideology and the Law Review Selection Process

Political Ideology and the Law Review Selection Process Abstract We investigate the role that political ideology plays in the selection process for articles in law reviews. To do so, we match data on the political ideology of student editors from 15 top law reviews from 1990 to 2005 to data on the political ideology of the authors of accepted articles. We find that law reviews with a higher share of conservative editors accept a higher share of articles written by conservative authors. We then investigate potential explanations for this pattern. One possibility is that editors have a preference for publishing articles written by authors that share their ideology. Another possibility is that editors are objectively better at assessing the contribution of articles written by authors that share their ideology. We find evidence that the latter explanation drives the relationship between editor and author ideology. 1. Introduction Law reviews are the main outlet for legal scholarship. They are journals run by groups of law students who select which articles to publish. These publication decisions are shrouded in mystery, and little is known about the factors that affect them. In this article, we investigate one potentially important factor: political ideology. To study the role that political ideology plays in the law review selection process, we collect data on articles published at 15 of the top law reviews from 1990 to 2005. Next, we obtain the identities of editors from yearly mastheads of the editorial boards. Finally, we match editors and authors to a measure of their political ideology based on their political donations. Using these data, we find that the number of accepted articles written by conservative authors is increasing in the conservativeness of a law review’s editorial board. Our estimates suggest that an editorial board with 1 percentage point more conservative editors accept 0.6% more articles written by conservative authors. To interpret the magnitude of this estimate, consider the ideological differences between law reviews’ least and most conservative boards. On average across the 15 law reviews in our dataset, a law review’s most conservative board has 72 percentage points more conservatives than their most liberal board. Therefore, our estimates suggest that a law review would accept 43% more articles written by conservative authors in a year with their most conservative board compared to a year with their most liberal board. Next, we investigate two potential explanations for this pattern. One possible explanation is that the relationship stems from editor favoritism toward authors with shared ideology or from a desire to publish articles that promote editors’ preferred political agendas. Another possible explanation is that the relationship stems from editors being better able to screen articles with shared ideology, which can be driven by higher levels of relevant knowledge or expertise. For example, if conservative editors have more expertise in the legal methodology of originalism, they might have a greater ability than liberal editors to distinguish articles that will be widely cited that utilize this predominantly conservative approach. Studies have demonstrated that a similar explanation drives disparities in other contexts. For example, evaluators of grant proposals are better able to distinguish the quality of grant proposals in their particular field of expertise (Li, 2017). Although both explanations would predict that editors would accept more articles written by authors that share their ideology, the explanations generate conflicting predictions about the future citations of articles written by authors with and without shared ideology. On the one hand, if editors accept articles on the basis of ideology because of a preference to promote their ideology, a standard result is that the average article citations would be lower for articles written by authors with shared ideology and higher for articles written by authors without shared ideology (Becker, 1957; Knowles et al., 2001). On the other hand, if editors accept articles on the basis of ideology because they are better at screening articles written by authors with shared ideology, it is possible that the average citations would be higher for articles written by authors with shared ideology and lower for articles written by authors without shared ideology (Aigner and Cain, 1977). We test these predictions and find that articles written by authors with shared ideology are cited more often than articles written by authors without shared ideology. These findings are inconsistent with the preference explanation and consistent with the screening explanation of why editors select more articles written by authors with shared ideology. The results shed light on important debates in the legal academy. First, the results highlight a potential mechanism influencing the ideological diversity of law professors. Because the number of articles published by conservative authors depends on both the supply of articles from conservative authors and the demand for articles by editors, the relationship between editor and author ideology implies that changes in the ideology of student editors can change the career opportunities available to conservative law professors. However, the direction of the effects for academics during our time period is ambiguous because student editors at elite law schools tend to be liberal but are nonetheless relatively more conservative than law professors. Second, the results are relevant to the “common criticism . . . that law students lack the experience or training to effectively evaluate legal scholarship” (Posner, 1995). Although the results do not allow us to directly comment on the debate over whether selecting articles through a peer-review process would be superior to a student-run process (see, e.g., Friedman, 2018), they suggest that students may be relatively better at selecting articles over which they have some prior knowledge or expertise. The results also have potentially important welfare implications. If articles published in higher-ranked law reviews are more likely to influence judges or policymakers, the role of ideology in the article selection process could alter judicial and policy outcomes. In addition, the fact that author ideology matters in the article selection process means that it can influence hiring decisions on the entry-level and lateral legal academic markets. And given the conventional wisdom among law professors that past article placements influence student editors’ publication decisions, any disparities created by shared ideologies between editors and authors could compound over time. This article proceeds as follows. Section 2 discusses the institutional setting. Section 3 describes the data and reports descriptive statistics. Sections 4 and 5 present the identification strategy and report the results. Section 6 explores whether limitations of our ideology data could influence the results. Section 7 concludes. 2. Institutional Setting A large social science literature finds that political ideology plays an important role in decision-making (e.g., Martin et al., 2004). Although there has been some research documenting the political diversity of the academic profession (e.g., Gross, 2013; Bonica et al., 2018) and the role of ideology in the production of academic research (e.g., Jelveh and Kogut, 2014; Chilton and Posner, 2015; Jelveh et al., 2017), there is no research investigating whether political ideology influences the article selection process. However, there is a literature on the influence of other factors on the article selection process across a wide range of fields, including biology (Borsuk et al., 2009), computer science (Tomkins et al., 2017), ecology (Budden et al., 2008), economics (Blank, 1991; Smart and Waldfogel, 1996), medicine (Gilbert et al., 1994), and psychology (Lloyd, 1990). Most of this literature studies whether referees give more favorable recommendations to some authors, but some addresses whether journal editors favor some authors (e.g., Laband and Piette, 1994). These studies usually find no evidence of referee favoritism, but there are exceptions. Notably, Hengel (2016) finds evidence that women authors are held to higher writing standards than men, and Tomkins et al. (2017) finds evidence that articles written by famous authors are more likely to be published after a single-blind review than after a double-blind review. Most of this research assesses differences in outcomes by the characteristics of an identifiable group of authors without regard to the characteristics of the editors or referees (e.g., Ayres and Vars, 2000). However, three articles investigate whether publication outcomes vary by shared attributes of authors and either editors or referees. Abrevaya and Hamermesh (2012) find no evidence that referees’ recommendations differ if the referee and author share a gender. Colussi (2018) finds evidence that an author’s social connections to the editor improves publication outcomes. Yoon (2013) finds evidence that law professors are more likely to publish in the law review of their home law school and that those in-home articles are cited less frequently than publications by outside faculty in the same law review. This article investigates the influence of political ideology in the selection process of law review articles. Student editors review submitted manuscripts and make acceptance decisions, generally without seeking expert review.1 Student editors have long been criticized for a lack of expertise (see, e.g., Friedman, 2018). Scholars have suggested that student editors rely on a set of proxies when choosing which articles to publish. Quantitative and qualitative evidence suggests that factors not directly related to article quality influence student’s acceptance decisions: the author’s credentials and reputation, the author’s previous publication record, the author’s connections to the publishing institution, the subject matter (with a preference for hot topics), and the author’s race and gender.2 Although there have been some suggestions of an effect of ideology in law review selection decisions (including an offhanded comment in Posner, 1995),3 the question has not been studied empirically. There are six features of the law review publication process that make the institutional setting well suited for studying the relationship between ideology and article selection. First, unlike editors of peer-reviewed journals, law review boards turn over each year. This means there is year-to-year variation in the individuals involved in the article selection process. Second, we are able to compare the outcomes of multiple articles for the same editors. In the peer review process, this may not be possible because rarely will the same editor and referee be observed. Third, there are not multiple sources of influence in the law review selection process. One identification challenge when studying influences in peer review journals is that there could be both editorial and referee influences acting simultaneously, making it difficult to disentangle their effects. For example, there could be three-way interactions between authors, editors, and referees. With law reviews, that is generally not the case. Fourth, the same pool of articles are considered by each law review board. Most academic journals outside of law reviews restrict authors from submitting to other journals simultaneously, which might lead authors to self-select into submitting to different journals. The result is that different journals may have dramatically different pools of articles to select from. This is not true of law reviews. Twice per year (roughly February and August), authors who submit to one top law review almost exhaustively submit to all top law reviews. This simultaneous submission setting overcomes concerns of selection into journals on the basis of ideology. Fifth, student editors have very few social ties with law professors, particularly law professors from other schools. In many peer-reviewed journals, the editors and potential authors can share professional connections. The result is that conservative (liberal) editors may be more likely to accept articles from conservative (liberal) authors simply because they have more professional and personal ties (Colussi, 2018). Finally, the law review setting allows us to match student editors to a measure of their ideology. Linking individuals to common measures of political ideology based on political donations requires enough information on the individual to distinguish between individuals with the same name in the United States. However, data used in most studies of the peer review process only contain the first name of the reviewer (e.g., Abrevaya and Hamermesh, 2012). Unlike the single or double blind process in peer review journals, the first and last names of student editors are available on mastheads for each volume.4 3. Data and Descriptive Statistics We built a dataset that contains an estimate of the ideologies of both student editors and the authors of the articles they accept, as well as the citations to each article. Our sample includes 15 law reviews: California Law Review, Columbia Law Review, Cornell Law Review, Duke Law Journal, Georgetown Law Journal, Michigan Law Review, Northwestern University Law Review, Stanford Law Review, Texas Law Review, UCLA Law Review, University of Chicago Law Review, University of Pennsylvania Law Review, Vanderbilt Law Review, Virginia Law Review, and Yale Law Journal. The law reviews at Harvard and New York University are not included in the sample because of an inability to link voting boards to the articles they accepted.5 We use articles from these 15 law reviews from 1990 to 2005.6 3.1. Voting Members on Law Review Each law review allows different board positions to vote on which articles to accept, but the board positions with voting rights differ between law reviews and changes over time. To determine the positions with voting rights, we surveyed the editor-in-chief of every volume in our sample. Supplementary Appendix A provides details about the survey. Although technically only the voting members of a law review ultimately vote on whether to accept an article, it is likely that high-ranking members without voting rights also influence which articles are accepted. This may be through control of the agenda: most articles are rejected before the board holds a vote, and the editor-in-chief and other high-ranking members of a law review may have the ability to influence which articles are put up for a vote. We therefore identify high ranking members as voting members even if they do not technically vote7 but the results are consistent if we define the voting board to include only voting members. 3.2. Mapping Editorial Boards to Selected Articles The editorial board at the time an article is published may not have initially selected the article. For example, an article published in Volume 100 of a law review may have been selected for publication by the articles committee of Volume 99. We thus needed to link articles to the board that actually selected them. To do so, the survey asked the editor-in-chiefs what volumes published the articles they accepted. We then used this information, and additional information from follow-up correspondence, to map published articles to the board members that selected them. 3.3. Student Editor Identities from Masthead Each volume of a law review contains a masthead page which lists each editor and their position. We obtained the mastheads for each volume in our sample. From the mastheads, we hand-coded the name of each voting member. In total, we coded the identities of 1,988 editors. The mean and median number of relevant members per journal in our sample is 8.8 3.4. Estimating Gender and Race We use editors’ names to recover an estimate of their gender and race. To estimate gender, we use the website “Genderize.”9 To estimate race, we use the python package “ethnicolr.”10 Ethnicolr “exploit[s] the U.S. census data, the Florida voting registration data, and the Wikipedia data collected by Skiena and colleagues, to predict race and ethnicity based on first and last name or just the last name.” We code someone as non-white if they are predicted to be non-white in any of the datasets. 3.5. Published Articles and Their Citations Heinonline is a website that contains information about law review publications. We gathered information from Heinonline about each publication between 1990 and 2005 in the 15 law reviews in our sample. This includes the title, identity of each author, volume, issue, and number of citations of that article. We make three sample restrictions. First, each volume of a law review usually contains multiple pieces not selected through the same mechanism as typical articles, including comments, notes, and book reviews. We exclude these non-article publications. Second, articles that are published as part of a symposium are typically solicited and do not go through the same selection process. We exclude symposium articles, but the results are similar if we include them. Third, there is evidence that student editors do not evaluate all authors in the same way, with law reviews publishing more articles written by faculty at their own institution (Yoon, 2013). We exclude home school authors because one might expect ideology to play a different role during article selection for them,11 but the results are consistent if we include them.12 After these restrictions, the final sample is 1,573 articles. 3.6. Measure of Political Ideology Our measure of political ideology is based on the political donations of the student editors and authors. The specific measure we use is called the Campaign Finance score (“CFscore”) and is drawn from the Database on Ideology, Money in Politics, and Elections (DIME) (Bonica, 2014). A growing literature uses and validates CFscores (Bonica, 2014; Thomsen, 2014; Chilton and Posner, 2015; Bonica and Rosenthal, 2016; Wood and Spencer, 2016; Bonica and Sen, 2017; Bonica et al., 2019).13 DIME is a database of campaign contributions made from 1979 to 2016. This comprises more than 250 million donations made by more than 20 million unique donors. Supplementary Appendix C describes the process of matching our sample to DIME. To calculate the CFscores from raw donations data, DIME first assigns political candidates unidimensional ideological scores based on their common donors. The scale is normalized to the population of U.S. donors such that the mean is zero and the standard deviation is one. For instance, Bernie Sanders has a CFscore of -1.89, Barak Obama has a CFscore of -1.16, Hillary Clinton has a CFscore of -1.10, Mitt Romney has a CFscore of 0.90, and Donald Trump has a CFscore of 1.29. Individual donors are then assigned ideological scores on the same unidimensional scale based upon a weighted average of the amount of donations they have made and the CFscore of the candidate to whom they gave. For instance, if an individual’s only political contribution was to Mitt Romney, her CFscore would match Romney’s CFscore (0.90). If an individual donated $$1{,}000$$ to Barack Obama and $$2{,}000$$ to Bernie Sanders, her CFscore would be the sum of 1/3 of Obama’s score and 2/3 of Sanders’ score (-1.65). A number of concerns arise with the use of the CFscore for measuring editor and author ideology. For instance, CFscores are based on lifetime donations, and not all people donate to campaigns and thus do not have a CFscore. In Section 6, we explore the extent to which the drawbacks of the CFscore are likely to affect the results. 3.7. Descriptive Statistics Table 1 provides descriptive statistics. Panel A describes the full sample of editors, and Panel B describes the full sample of authors. For editors, our measure of board ideology is at the journal-year level. For authors, we define an article as conservative if at least one author is conservative. This approach is motivated by Colussi (2018), who defines an article authored by more than one author as having a social connection with the editor if at least one author is has a social connection with an editor. However, the results are consistent when using alternative ways of classifying co-authored articles.14 Table 1. Descriptive Statistics A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 Open in new tab Table 1. Descriptive Statistics A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 Open in new tab Figure 1 plots the percent of editors and authors with political donations over time.15 Over the sample as a whole, we matched 34% of editors and 58% of authors to donations. We classify individual donors as “conservative” if their CFscore places them at or above the average American donor (CFscore $$\geq$$ 0) and “liberal” if their CFscore places them below the average American donor (CFscore $$<$$ 0). Using this definition, 21% of editors and 15% of authors are conservative. Figure 2 provides the distributions of the percent of conservative editors and authors per volume.16 The ideology of editors and authors is consistent with previous research (see, e.g., Bonica et al., 2016, 2018). Figure 1. Open in new tabDownload slide Editors and Authors with Political Donations over Time. Figure 1. Open in new tabDownload slide Editors and Authors with Political Donations over Time. Figure 2. Open in new tabDownload slide Distribution of Author and Editor Ideology. Figure 2. Open in new tabDownload slide Distribution of Author and Editor Ideology. Panel C of Table 1 provides descriptive statistics of the final sample used in the empirical analysis. The main analysis is at the journal-year level. The average number of articles per journal-year in the final sample is 7, with 10% having more than 10 articles. 4. Relationship Between Editor and Author Ideology 4.1. Research Design Suppose article $$i$$ has a set of attributes, including quality $$q_{i}$$ ⁠, political ideology as proxied by the author’s ideology $$a_{i}$$ ⁠,17 author gender $$g_{i}$$ ⁠, and author race $$r_{i}$$ ⁠. Suppose the editors of law review $$j$$ in year $$t$$ have a set of attributes, including political ideology $$e_{jt}$$ ⁠, gender $$g_{jt}$$ ⁠, and race $$r_{jt}$$ ⁠. Further suppose the editors have three preferences over articles. First, editors prefer articles with higher quality $$q_{i}$$ ⁠. Second, editors prefer to select articles from authors with shared gender and race denoted $$G_{ijt}$$ and $$R_{ijt}$$ ⁠. Third, editors prefer to select articles with an ideology close to their own ideology. In particular, let $$P_{ijt}$$ be the ideological distance between editors $$j$$ and article $$i$$ ⁠. Let $$y_{ijt}$$ be an indicator variable for whether editors from law review $$j$$ accept article $$i$$ in year $$t$$ ⁠. To estimate the relationship between editor and article ideology, we would ideally estimate: \begin{align*} y_{ijt}=\hat{\alpha}+\hat{\gamma}q_{ijt}+\hat{\beta}P_{ijt}+\hat{\sigma}G_{ijt }+\hat{\theta}R_{ijt}+\varepsilon_{it}, \end{align*} where $$\hat{\beta}$$ estimates the relationship between editor and article ideology. The problem is that estimating the above equation requires the full set of articles considered by the editors—that is, both the articles they published and the articles they did not publish. We do not observe the full set of articles submitted to editors. Rather, we only observe the set of accepted articles. Given the set of accepted articles, one potential option is to regress author ideology on editor ideology. The problem with such an approach is that, because gender and race are correlated with ideology, any preferences for shared gender or race would create omitted variables bias.18 To account for the possibility of gender and racial preferences, we control for editor gender and race. We estimate Equation 1 at the journal-year level. \begin{align} a_{jt}=\alpha+\beta e_{jt}+\gamma g_{jt}+\theta r_{jt}+\phi_{t}+ \eta_{j}+\epsilon_{jt} . \end{align}(1) The primary dependent variable $$a_{jt}$$ is the percent of articles with at least one conservative author. One advantage of this measure is that it lends itself to easy substantive interpretation. It is also possible that the students selecting articles are aware of whether an author is conservative or liberal but unaware of the degree to which an author is conservative or liberal. One disadvantage of this measure is that it discards information that is contained within the continuous measure of ideology. Therefore, we also use the mean CFscore of the authors of each accepted article as a second dependent variable. The independent variable of interest $$e_{jt}$$ is either the percent of donating editors who are conservative or the mean CFscore of the donating editors. In the preferred specification, we include year fixed effects $$\phi_{t}$$ ⁠, journal fixed effects $$\eta_{j}$$ ⁠, and controls for editor gender and race (⁠ $$g_{jt}$$ and $$r_{jt}$$ ⁠). For the gender and race controls, we use the percent of female editors and the percent of non-white editors. The coefficient of interest is $$\beta$$ ⁠. It asks, for a given mix of editors in terms of gender and race, is within-journal variation in the ideology of the editors associated with a different likelihood of publishing articles written by conservative authors? The articles selected by one law review in a given year are not independent of the articles selected at other journals in the year, which can create mutual dependence in the error terms within a year. In the main results, we thus cluster standard errors at the year level. Below, we find that the size of the standard errors are similar using different levels of clustering. 4.2. Results Panel A of Table 2 reports the results of regressing the percent of conservative authors on the percent of conservative editors. Column 1 includes year fixed effects, Column 2 adds law review fixed effects, Column 3 adds controls for gender and race, and Column 4 adds journal time trends. Column 3 reports the results from estimating Equation 1 and is our preferred specification. The estimate indicates that a board with 1 percentage point more conservative editors accept 0.6% more articles written by conservative authors (0.0093 percentage points from a baseline of 0.148).19 To interpret the magnitude of the effect, first consider that the within-journal standard deviation of editor ideology is 24% of conservative editors on average across the journals. Therefore, the estimate suggests that a 1 standard deviation conservative shift in a board’s ideology is associated with a 14% increase in the number of articles published by conservative authors. As another way to interpret the magnitude of the effect, consider that across the law reviews, on average a law review’s least conservative board has 72% fewer conservatives than the law reviews most conservative board. Therefore, the estimate suggests that a law review would accept 43% more articles written by conservative authors in a year with their most conservative editors compared to a year with their most liberal editors.20 Table 2. Relationship Between Editor Ideology on Author Ideology . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 Note: The regressions are at the journal-year level. Standard errors clustered by year in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. Open in new tab Table 2. Relationship Between Editor Ideology on Author Ideology . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 Note: The regressions are at the journal-year level. Standard errors clustered by year in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. Open in new tab Panel B reports the results of regressing the mean CFscore of authors on the mean CFscore of editors. Although the results are not statistically significant at conventional levels in all specifications, they are consistent with the estimates in Panel A. The results in Column 3 indicate that a 1 CFscore point more conservative board accepts articles written by authors that are 0.083 CFscore points more conservative. Figure 3 assesses the sensitivity of the results to alternative modeling choices while using the same specifications as in Table 2. First, we assess the sensitivity of the results to different levels of analysis. The main specification was at the journal-year level, but we also estimate these same specifications at the article level, as indicated on the left-hand side of the figure. This means that the ideology of authors varies within a journal-year, but the ideology of editors is constant within the journal-year. The dependent variable is either an indicator variable for whether there is at least one conservative author for a given article or the author CFscore (if there are multiple authors, the mean CFscore). Second, we assess the possibility that the specification did not properly account for trends by estimating a first-difference specification, as indicated on the left hand side of the figure. The dependent variable is the change in the percent conservative authors (mean author CFscore) from one year to the next, and the independent variable is the change in the percent conservative editors (mean editor CFscore) from one year to the next. Finally, we assess the sensitivity of the results to different levels of clustering. For each combination of control variables and level of analysis, we estimate the specification without a clustering adjustment (as indicated by “No”), clustering by journal (as indicated by “Journal”), and clustering by year (as indicated by “Year”). Figure 3. Open in new tabDownload slide Sensitivity Tests to Controls and Clustering. Note: The Figure reports the point estimate and 90 percent confidence interval for a series of regressions. The left panel reports the results of regressing the percent of conservative authors on the percent of conservative editors. The right panel reports the results of regressing the mean CFscore of authors on the mean CFscore of editors. As indicated on the left hand side of the figure, the top section estimates the specifications at the article level, the middle section estimates the specifications at the journal-year level, and the bottom section estimates a first-difference specification at the journal-year level. Within a section, the controls correspond to the specifications in Table 2. For each combination of controls and level of analysis, the figure reports regressions without a clustering adjustment (as indicated by “No”), clustering by journal (as indicated by “Journal”), and clustering by year (as indicated by “Year”). Figure 3. Open in new tabDownload slide Sensitivity Tests to Controls and Clustering. Note: The Figure reports the point estimate and 90 percent confidence interval for a series of regressions. The left panel reports the results of regressing the percent of conservative authors on the percent of conservative editors. The right panel reports the results of regressing the mean CFscore of authors on the mean CFscore of editors. As indicated on the left hand side of the figure, the top section estimates the specifications at the article level, the middle section estimates the specifications at the journal-year level, and the bottom section estimates a first-difference specification at the journal-year level. Within a section, the controls correspond to the specifications in Table 2. For each combination of controls and level of analysis, the figure reports regressions without a clustering adjustment (as indicated by “No”), clustering by journal (as indicated by “Journal”), and clustering by year (as indicated by “Year”). Figure 3 reports the point estimates and 90% confidence intervals for these regressions. These results show that the size of the point estimates and the standard errors are not highly sensitive to the level of analysis, the way trends are accounted for, and the level of clustering. Overall, although the estimates in some specifications do not quite reach statistical significance, the results are consistent across the specifications. 5. Mechanisms There are two main potential explanations for the positive relationship between editor and author political ideology. First, editors could have a preference for accepting or rejecting articles on the basis of ideology (Becker, 1957). Second, editors could attempt to choose the articles that will be most cited, observe noisy signals of quality, and are better at screening articles written by authors with shared ideology (Phelps, 1972 Arrow, 1973; Aigner and Cain, 1977). Although both of these explanations predict that editors will accept more articles written by authors with shared ideology (which we refer to as “likeminded articles”), the explanations have conflicting predictions about the citations of likeminded articles and non-likeminded articles. If likeminded articles are selected more often because of a preference, the likeminded articles will have fewer citations. This is a standard prediction from Becker (1957).21 Therefore, if likeminded articles have more citations, it cannot be the case that a taste for selecting likeminded articles is driving the relationship between editor and author political ideology.22 To test between these explanations, we generate a dataset at the journal-year-author ideology level. That is, for each journal-year, there are two observations: the average number of citations for liberal authors and the average number of citations for conservative authors. Let $$c_{jt}$$ be an indicator variable for conservative author. We estimate Equation 2. \begin{align} \ln(\text{citations}_{jtc})=\alpha+\beta p_{jt}\times c_{jt}+ \sigma c_{jt}+\phi_{jt}+\epsilon_{jt} , \end{align}(2) where $$\ln(\text{citations}_{jtc})$$ is the natural log of the average article citations published in journal $$j$$ in year $$t$$ of author of ideology $$c_{jt}$$ ⁠, $$p_{jt}$$ is the percent of donating editors that are conservative, and $$\phi_{jt}$$ are journal-year fixed effects.23 The coefficient $$\beta$$ on the interaction term captures the differential effect of the conservativeness of the editorial board on citations of articles written by conservative authors. Equation 2 produces an unbiased estimate for $$\beta$$ under two assumptions. The first assumption is that student editor feedback in the editing process changes citations to a likeminded article the same as a non-likeminded article. Although we have no support for the assumption, we are skeptical that differential effort that students put into editing articles because of ideology can be material in changing citations to the article. The second assumption is that the additional likeminded articles that are accepted are not more likely to be drawn from highly cited fields. This assumption would be violated if, for example, a board decides to publish one more likeminded article from a high citation field (e.g., constitutional law) instead of a non-likeminded article from a low citation field (e.g., tax law).24 In Table 3, Column 1 includes the main effect on percent conservative editors, the main effect on conservative author, year fixed effects, and journal fixed effects. Column 2 adds the interaction term, Column 3 adds the controls for gender and race, and Column 4 adds journal time trends. Column 5 estimates Equation 2 by replacing the journal time trends with journal-year fixed effects, which allows for a comparison of the citations of articles written by liberal and conservative authors within a journal-year. Because there is no variation in editor ideology within a journal-year, the main effect on percent conservative editors and the controls for race and gender drop out of the regression with journal-year fixed effects. In Columns 2–4, the main effect on percent conservative editors is negative, suggesting that more conservative editors accept liberal articles that are cited less. The estimate on the interaction term is positive, statistically significant, and stable across the specifications. The point estimates for Columns 2–5 indicate that moving from 0% conservative editors to 100% conservative editors is associated with a 55% increase in citations for articles written by conservative authors. To interpret the estimate, note again that the within-journal standard deviation of editor ideology is 24% of conservative editors on average across the journals. This means that a 1 standard deviation shift in a board’s ideology is associated with a 13% change in citations for articles written by conservative authors. Table 3 thus provides no evidence that the relationship between editor and author ideology is driven by a preference for selecting articles on the basis of ideology. Table 3. Relationship Between Editor–Author Ideology and Citations . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 Note: The regressions are at the journal-year-ideology level. Standard errors clustered by year are in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. The sample is restricted to journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author, so the sample size is lower than in Table 2. See text for details. Regressions are weighted by the number of articles. The main effect on “Conservative author” is included in the specifications but is not reported. Open in new tab Table 3. Relationship Between Editor–Author Ideology and Citations . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 Note: The regressions are at the journal-year-ideology level. Standard errors clustered by year are in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. The sample is restricted to journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author, so the sample size is lower than in Table 2. See text for details. Regressions are weighted by the number of articles. The main effect on “Conservative author” is included in the specifications but is not reported. Open in new tab To further investigate the relationship, Figure 4 reports a binned scatterplot and a line of best fit of the relationship of interest. The y-axis is the difference between the natural log of the mean citations of articles written by conservative authors in a journal-year and the natural log of the mean citations of articles written by liberal authors in the same journal-year. A positive number indicates that the articles written by conservative authors were cited more on average than the articles written by liberal authors. The x-axis is the percent of donating editors that are conservative. The positive and statistically significant relationship indicates that more conservative boards accept articles written by conservative authors that are cited more than the articles written by liberal authors that they accept. Figure 4. Open in new tabDownload slide Relationship between Editor Political Ideology and Difference in Citations to Articles from Liberal and Conservative Authors. Note: The figure reports a binned scatterplot and a line of best fit of the relationship of interest. The $$y$$ -axis is the difference between the natural log of the mean citations of articles written by conservative authors in a journal-year and the natural log of the mean citations of articles written by liberal authors in the same journal-year, where a positive number indicates that the articles written by conservative authors were cited more on average than the articles written by liberal authors. The $$x$$-axis is the percent of donating editors who are conservative. Figure 4. Open in new tabDownload slide Relationship between Editor Political Ideology and Difference in Citations to Articles from Liberal and Conservative Authors. Note: The figure reports a binned scatterplot and a line of best fit of the relationship of interest. The $$y$$ -axis is the difference between the natural log of the mean citations of articles written by conservative authors in a journal-year and the natural log of the mean citations of articles written by liberal authors in the same journal-year, where a positive number indicates that the articles written by conservative authors were cited more on average than the articles written by liberal authors. The $$x$$-axis is the percent of donating editors who are conservative. 6. Using Political Donations to Measure Ideology Measures of ideology based on political donations are increasingly used in social science research (e.g., Bonica et al., 2017a), but there are potentially important limitations with the approach.25 We assess whether two limitations of using CFscores to measure ideology—that they are based on lifetime donations and that they are not available for all authors and editors—are likely to bias the results. 6.1. Lifetime Measure of Ideology One concern with using CFscores as a measure of ideology is that they are based on lifetime donations. There are three reasons to believe that this approach does not raise identification concerns for the analysis. First, ideology of adults has been shown to be stable (e.g., Bonica, 2014), and research suggests that typically only major life changes are likely to alter ideology (Green et al., 2004). To put the stability of ideology in context, some evidence suggests that Americans are more likely to change their religion than their political party.26 Although many of the editors may have gone through these kind of major life changes, we think it is unlikely that this would occur in a systematic way that would drive correlations between average board ideologies and the articles that are accepted. Second, if editors’ ideology changes after law school and before subsequent political donations are made, this approach would likely introduce measurement error rather than create any bias in the estimates. Finally, the main concern for identification would be if the process of reviewing articles caused editors’ ideologies to change (i.e., reverse causation). For the results to be driven by reverse causation, editing one and a half more conservative articles would have to lead to a one standard deviation change in ideology of the entire editorial board. That is, for the combined group of editors, editing the article would need to have an effect on each editor’s ideology dramatically bigger than the demonstrated effect from profound life events, such as large changes in wealth (Bonica and Rosenthal, 2016). Although the students who spent the most time editing the additional conservative article may have had a deep enough level of intellectual engagement to change their ideology, such a change is unlikely to occur for the board overall in a given year. 6.2. Missing Ideology Data Our measure of ideology is based on political donations, and editors and authors that have not made a donation thus have missing ideology. For authors, missing ideology does not create any identification concerns. Because our sample of articles is restricted to those with at least one donating author, missing author ideologies changes the sample of articles. It therefore only changes the interpretation of the results. For editors, however, missing ideology creates potential identification concerns. Because we define a board’s conservativeness based on the ideology of the donating editors, missing editor ideology may bias the results.27 We investigate whether missing data may be driving the results under three different assumptions.28 First, it is possible that editors’ propensity to donate is uncorrelated with their ideology. If so, missing editor ideologies would be drawn from the same ideological distribution as the editors in our sample who have donated, implying that editors are effectively missing at random. If so, missing ideology would introduce only classical measurement error, which would attenuate the estimated coefficients towards zero but would not bias the estimated coefficients. If missing editor ideologies are random and introduce measurement error, restricting the sample to one in which we observe relatively more editor ideologies would decrease measurement error, leading to larger point estimates and more precision. We tested this possibility by restricting our sample to boards with at least three editors with donations and to years when there were relatively more editors donating (1990 to 2000).29 We find that that the size of the point estimates increase, suggesting that measurement error for missing editor ideology was driving down the size of the estimates in Table 2. Second, it is possible that missing editors have similar ideologies to their fellow law school classmates. To test how this possibility would change the results, we use data on the percentage of conservative graduates from each law school-year from Bonica et al. (2016). We then assume that editors with missing ideology are ideologically represented by the alumni of their law school in the 5 years around when they graduated and calculate the percent conservative editors for all the board—editors that made and have not made donations—after filling in the missing editor ideologies with this average conservativeness. Unlike the last tests that reduced measurement error by restricting the sample, this approach introduces measurement error into our measure of editor ideology. As expected, we find that the standard errors increase (more than doubling in some specifications) when using this approach. Although the estimates are not statistically significant in most specifications, the point estimates remain positive in each of them. This provides some evidence that observing the missing editor ideologies would not change the direction of the point estimates. Third, it is possible that donating editors have systematically different ideologies from non-donating editors.30 If donors have different ideological preferences than non-donors, it could systematically bias the estimates. We investigate how the results would change if missing editors have less intense ideological preferences than donating editors. To do so, we follow Bonica et al. (2019) and use a back-of-the-envelope adjustment to correct for missing data. Assume that in a journal-year the mean ideology of missing editors is equal to $$\rho$$ times the mean ideology of the non-missing editors: \begin{align*} e_{jt}^{M}=\rho\,e_{jt},\end{align*} where $$e_{jt}^{M}$$ is the ideology of missing editors and $$\rho < 1$$ corresponds to the case in which editors with more intense ideological preferences are more likely to donate. In this case, the true ideology of editors, $$e_{jt}^{*}$$ ⁠, is: \begin{align*} e_{jt}^{*}=(1-\mu)e_{jt}+\mu e_{jt}^{M}, \end{align*} where $$\mu$$ is the proportion of missing editors. In this setting, Bonica et al. (2019) show that obtaining the true effect of ideology requires scaling the coefficient estimated from the sample of donors by a factor of $$\frac{1}{1-\mu(1-\rho)}$$ ⁠.31 Given that we observe 34 percent of editors donations (⁠ $$\mu=0.66)$$ ⁠, the point estimate in Table 2, Panel B, Column 3 of $$\hat{\beta}=0.093$$ implies that the true coefficient is $$\beta=\frac{0.093}{0.34+.66*\rho}$$ ⁠. Because $$\rho$$ is between 0 and 1, the true value of $$\beta$$ under these assumptions is between $$0.093$$ and $$0.273$$ ⁠. As the extent to which donors have stronger ideological views relative to non-donors increases, the true coefficient increases. Because it is unlikely to be the case that editors with missing ideology actually have more intense preferences than those whose ideology we observe, the estimates likely provide a lower bound for the true effect. Taken together, these results suggest that missing editor ideology may be moderately biasing the size of the estimated coefficients toward zero, but they do not suggest that missing editor ideology is driving our finding of a non-zero effect. 7. Conclusion This article studied the role that political ideology plays in the selection process for law review articles. We matched the identities of student editors and authors of accepted articles to a measure of political ideology based on political donations. We find that the number of accepted articles written by conservative authors is increasing in the conservativeness of a law review’s editorial board. This finding contributes to the literature on disparate outcomes in the article selection process (e.g., Blank, 1991; Abrevaya and Hamermesh, 2012; Hengel, 2016; Colussi, 2018) by examining both a new setting (the legal academy) and a new dimension along which disparate outcomes can occur (political ideology). We then investigated whether this relationship was driven by student editors having a preference for publishing articles that promote their political ideology or by student editors being objectively better at assessing the contribution of articles written by authors with shared ideology. To do so, we assessed whether articles whose authors and editors share an ideology are cited more than articles whose authors and editors have different ideologies. We found evidence inconsistent with the preference explanation and consistent with the screening explanation. This second finding contributes to the literature exploring the underlying causes of disparate outcomes (e.g., Levitt, 2004; Antonovics and Knight, 2009; Ewens et al., 2014). The results shed light on important debates in the legal academy. Academic careers are based on publishing (Frey and Rost, 2010), and the journal in which a scholar publishes exerts a strong influence on that individual’s job opportunities (Diamond, 1986). Moreover, academic articles published in journals remain the primary mechanism for disseminating research, so the journal in which an article is published affects the article’s reach and influence. The fact that ideology plays a role the selection process for law review articles thus has ramifications for both career trajectories and the dissemination of knowledge. Acknowledgement We thank Thomas Drueke for help constructing the data and Kimberly Rubin for excellent research assistance. For helpful comments, we are grateful to Adam Bonica, Michael Frakes, Erik Hovenkamp, William Hubbard, J.J. Prescott, Maya Sen, and participants at the 2018 American Law and Economics Association Annual Meeting. Footnotes 1. " A few law reviews (e.g., Harvard Law Review, University of Chicago Law Review, and the Yale Law Journal) have recently begun to send some articles out to expert faculty referees. During our sample period (1990 – 2005), expert reviews in law review article selection were very uncommon. If we exclude the few journals that might have sent articles out for review during our sample period, the results are largely unchanged in both an economic and statistical sense. 2. " See, e.g., Ellman (1983), Leibman and White (1989), Merritt (1998), Christensen and Oseid (2007), Nance and Steinberg (2009), and Higdon (2016). Recent lawsuits have been filed challenging the use of race and gender in law review article selection decisions (Van Voris, 2018). 3. " See Posner (1995) at 1133 (“The change in the character of legal scholarship has been accompanied by a collapse of political consensus among legal scholars and by a vast expansion in constitutional law, which is the most political field of law as a consequence of the nature of the issues it addresses, the remoteness of the governing text, and the field’s domination by a court (the Supreme Court) from which there is no possibility of appeal to a still higher court to keep the judges in line. Legal scholarship became more political at the same time that it was becoming more centrifugal. These developments beached not only a number of doctrinal scholars but also most student editors. They were now dealing with a scholarly enterprise vast reaches of which they could barely comprehend, and they were being tempted by the increasing politicization of the enterprise to employ political criteria in their editorial decisions.”). 4. " It is worth emphasizing that because law students make publication decisions, the article selection process for law reviews is probably unlike other article selection processes. Any findings of a relationship between political ideology and article selection for laws reviews thus might not be generalizable to the article selection process in other disciplines, and any findings of a relationship between political ideology and article selection in other disciplines might not be generalizable to the article selection process in law reviews. 5. " We do not include the Harvard Law Review in our sample because the masthead does not distinguish between editorial positions and allow all editors to vote on which articles to accept. The large number of editors thus implies that there would be almost no year-to-year variation in the ideology of the board. We do not include New York University Law Review because there is not a one-to-one correspondence between boards and volumes. As a result, we cannot identify precisely which boards chose which articles. Nonetheless, we reran the analysis with New York University in the sample while coding students as accepting articles with a publication date in the year they have a board position on the masthead, and the results are consistent. 6. " An earlier version of this article used more years of data. At the advice of a referee, we use 2005 as the end year because the percent of editors making political donations noticeably decreased in the later years of the sample. 7. " Mastheads are usually structured with the highest ranking position on the top (editor-in-chief) and positions listed in decreasing rank down the page of the masthead. We hand-coded all positions that are at or near the same level as the lowest ranking title that has voting rights. We exclude editors in charge of comments and book reviews as non-voting even if they are at or above the lowest voting member on the masthead. 8. " Supplementary Appendix B reports the distribution of the overall number of members per journal-year and the number of donating members per journal-year. Of the members who have made donations, the mean and median number per journal-year in our sample is 3, with 75% having at least 2 members. 9. " https://genderize.io/ 10. " https://github.com/appeler/ethnicolr 11. " An earlier version of this article included home school authors in the main sample. We excluded home school authors from the main sample at the advice of a referee. 12. " Nance and Steinberg (2008) find that editors make decisions in part because of the prestige of the author or their institution. As a robustness check, we estimated the relationship between editor on author ideology after excluding authors from the top 15 law schools, and the results are consistent. 13. " For example, Bonica (2019) validates CFscores against a battery of policy items and finds that they are “powerful predictors of policy preferences for a wide range of issues and successfully discriminate between donors from the same party.” 14. " The results are consistent under four alternative ways of handling co-authored articles: (1) making the unit of observation the donating author rather than the article; (2) defining an article as conservative only if there is at least one conservative author and no liberal authors; (3) using the most liberal or conservative author’s CFscore rather than the mean of the author’s CFscores; and (4) dropping all coauthored articles. 15. " Figure 1 reports the mean donation rates across articles rather than at the individual level. The fact that the same author publishes multiple articles explains why the percent of authors with donations averaged over articles is roughly the same as the percent of authors who have had a donations in the matched sample. 16. " Table D1 in the Supplementary Appendix reports the mean and standard deviation of the percent conservative editors by journal, and shows that there is considerable variation of editor ideology within a journal over time. Across the journals, the average and standard deviation percent conservative editors is 20 and 24, respectively. 17. " Chilton and Posner (2015) find that the substance of articles partly reflects the ideology of their authors. 18. " For discussions of race and omitted variable bias, see Clarke and Rothenberg (2018), Liscow and Woolston (2018), and Miller (2019). 19. " In Panel A of Table 2, the dependent variable takes the value of 0 if there are no conservative authors and the value of 1 if 100% of the authors are conservative, and the independent variable takes the value of 0 if there are no conservative editors and the value of 1 if 100% of the editors are conservative. As such, the point estimate of 0.093 indicates that moving from a board with 0% conservatives to 100 percent conservatives increases the probability of selecting a conservative author by 9.3 percentage points. To interpret the coefficient as a 1 percentage point increase in the percent conservative editors, the point estimate is divided by 100. 20. " Imagine if student editors matched the ideology of the public. In our sample, 21% of editors are conservative, but 50% of the donating public are conservative. If student editors had matched the ideology of the public, the estimate suggests that the 15 law reviews would have accepted 17% more conservative articles. 21. " See Mungan (2018) for a review of this literature. 22. " Screening could lead to more likeminded articles being accepted, and the additional articles could be less likely to be cited on the whole. As a result, it is not necessarily the case that differential screening ability would lead to higher citations for the average likeminded article. Nonetheless, if we observe that likeminded articles are more highly cited than we would expect, this would suggest that the increase in citations of likeminded articles resulting from greater screening ability first order dominates any decrease in citations from the additional likeminded articles being published. 23. " With journal-year fixed effects, the regression is estimated using journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author. For the specifications without journal-year fixed effects, we restrict the sample to the same journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author in order to assess differences in impact between author ideology within an editorial board. This means that the sample size is not double the sample size in Table 2. 24. " We have been unable to obtain data on the subject matter of articles. If we had data on the subject matter of articles, we would include subject matter fixed effects. 25. " For a general discussion of uncertainty when measuring ideology, see Bailey and Spitzer (2018). 26. " As discussed in The Economist (2018), “datasets do not line up in a way that makes the conjecture possible to prove, but it is a fair bet that, at least among those most engaged in politics, Americans are more likely to change their religion than to change their party.” 27. " See Lee (2017) for an example of law and economics research confronting classical measurement error. 28. " This discussion and analysis follows Bonica et al. (2019). These results are omitted for brevity, but they are available in the working paper version of this article. 29. " The results tell the same story using different thresholds. 30. " We are unaware of any reason to think that the ideologies of non-donors are meaningfully different from the ideologies of donors. Prior research using surveys and using CFscores has produced consistent estimates of the ideologies of lawyers. For instance, Peppers and Zorn (2008) surveyed Supreme Court clerks and found that 75% were democrats and 25% were republicans; when analyzing the same population using the CFscore, Bonica et al. (2017b) found the exact same breakdown to the percent. 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For permissions, please e-mail: journals.permissions@oup.com This article is published and distributed under the terms of the Oxford University Press, Standard Journals Publication Model (https://academic.oup.com/journals/pages/open_access/funder_policies/chorus/standard_publication_model) http://www.deepdyve.com/assets/images/DeepDyve-Logo-lg.png American Law and Economics Review Oxford University Press

Political Ideology and the Law Review Selection Process

, Volume 22 (1) – Apr 1, 2020
30 pages

/lp/oxford-university-press/political-ideology-and-the-law-review-selection-process-bRvY5uaHRd
Publisher
Oxford University Press
ISSN
1465-7252
eISSN
1465-7260
DOI
10.1093/aler/ahaa005
Publisher site
See Article on Publisher Site

Abstract

Abstract We investigate the role that political ideology plays in the selection process for articles in law reviews. To do so, we match data on the political ideology of student editors from 15 top law reviews from 1990 to 2005 to data on the political ideology of the authors of accepted articles. We find that law reviews with a higher share of conservative editors accept a higher share of articles written by conservative authors. We then investigate potential explanations for this pattern. One possibility is that editors have a preference for publishing articles written by authors that share their ideology. Another possibility is that editors are objectively better at assessing the contribution of articles written by authors that share their ideology. We find evidence that the latter explanation drives the relationship between editor and author ideology. 1. Introduction Law reviews are the main outlet for legal scholarship. They are journals run by groups of law students who select which articles to publish. These publication decisions are shrouded in mystery, and little is known about the factors that affect them. In this article, we investigate one potentially important factor: political ideology. To study the role that political ideology plays in the law review selection process, we collect data on articles published at 15 of the top law reviews from 1990 to 2005. Next, we obtain the identities of editors from yearly mastheads of the editorial boards. Finally, we match editors and authors to a measure of their political ideology based on their political donations. Using these data, we find that the number of accepted articles written by conservative authors is increasing in the conservativeness of a law review’s editorial board. Our estimates suggest that an editorial board with 1 percentage point more conservative editors accept 0.6% more articles written by conservative authors. To interpret the magnitude of this estimate, consider the ideological differences between law reviews’ least and most conservative boards. On average across the 15 law reviews in our dataset, a law review’s most conservative board has 72 percentage points more conservatives than their most liberal board. Therefore, our estimates suggest that a law review would accept 43% more articles written by conservative authors in a year with their most conservative board compared to a year with their most liberal board. Next, we investigate two potential explanations for this pattern. One possible explanation is that the relationship stems from editor favoritism toward authors with shared ideology or from a desire to publish articles that promote editors’ preferred political agendas. Another possible explanation is that the relationship stems from editors being better able to screen articles with shared ideology, which can be driven by higher levels of relevant knowledge or expertise. For example, if conservative editors have more expertise in the legal methodology of originalism, they might have a greater ability than liberal editors to distinguish articles that will be widely cited that utilize this predominantly conservative approach. Studies have demonstrated that a similar explanation drives disparities in other contexts. For example, evaluators of grant proposals are better able to distinguish the quality of grant proposals in their particular field of expertise (Li, 2017). Although both explanations would predict that editors would accept more articles written by authors that share their ideology, the explanations generate conflicting predictions about the future citations of articles written by authors with and without shared ideology. On the one hand, if editors accept articles on the basis of ideology because of a preference to promote their ideology, a standard result is that the average article citations would be lower for articles written by authors with shared ideology and higher for articles written by authors without shared ideology (Becker, 1957; Knowles et al., 2001). On the other hand, if editors accept articles on the basis of ideology because they are better at screening articles written by authors with shared ideology, it is possible that the average citations would be higher for articles written by authors with shared ideology and lower for articles written by authors without shared ideology (Aigner and Cain, 1977). We test these predictions and find that articles written by authors with shared ideology are cited more often than articles written by authors without shared ideology. These findings are inconsistent with the preference explanation and consistent with the screening explanation of why editors select more articles written by authors with shared ideology. The results shed light on important debates in the legal academy. First, the results highlight a potential mechanism influencing the ideological diversity of law professors. Because the number of articles published by conservative authors depends on both the supply of articles from conservative authors and the demand for articles by editors, the relationship between editor and author ideology implies that changes in the ideology of student editors can change the career opportunities available to conservative law professors. However, the direction of the effects for academics during our time period is ambiguous because student editors at elite law schools tend to be liberal but are nonetheless relatively more conservative than law professors. Second, the results are relevant to the “common criticism . . . that law students lack the experience or training to effectively evaluate legal scholarship” (Posner, 1995). Although the results do not allow us to directly comment on the debate over whether selecting articles through a peer-review process would be superior to a student-run process (see, e.g., Friedman, 2018), they suggest that students may be relatively better at selecting articles over which they have some prior knowledge or expertise. The results also have potentially important welfare implications. If articles published in higher-ranked law reviews are more likely to influence judges or policymakers, the role of ideology in the article selection process could alter judicial and policy outcomes. In addition, the fact that author ideology matters in the article selection process means that it can influence hiring decisions on the entry-level and lateral legal academic markets. And given the conventional wisdom among law professors that past article placements influence student editors’ publication decisions, any disparities created by shared ideologies between editors and authors could compound over time. This article proceeds as follows. Section 2 discusses the institutional setting. Section 3 describes the data and reports descriptive statistics. Sections 4 and 5 present the identification strategy and report the results. Section 6 explores whether limitations of our ideology data could influence the results. Section 7 concludes. 2. Institutional Setting A large social science literature finds that political ideology plays an important role in decision-making (e.g., Martin et al., 2004). Although there has been some research documenting the political diversity of the academic profession (e.g., Gross, 2013; Bonica et al., 2018) and the role of ideology in the production of academic research (e.g., Jelveh and Kogut, 2014; Chilton and Posner, 2015; Jelveh et al., 2017), there is no research investigating whether political ideology influences the article selection process. However, there is a literature on the influence of other factors on the article selection process across a wide range of fields, including biology (Borsuk et al., 2009), computer science (Tomkins et al., 2017), ecology (Budden et al., 2008), economics (Blank, 1991; Smart and Waldfogel, 1996), medicine (Gilbert et al., 1994), and psychology (Lloyd, 1990). Most of this literature studies whether referees give more favorable recommendations to some authors, but some addresses whether journal editors favor some authors (e.g., Laband and Piette, 1994). These studies usually find no evidence of referee favoritism, but there are exceptions. Notably, Hengel (2016) finds evidence that women authors are held to higher writing standards than men, and Tomkins et al. (2017) finds evidence that articles written by famous authors are more likely to be published after a single-blind review than after a double-blind review. Most of this research assesses differences in outcomes by the characteristics of an identifiable group of authors without regard to the characteristics of the editors or referees (e.g., Ayres and Vars, 2000). However, three articles investigate whether publication outcomes vary by shared attributes of authors and either editors or referees. Abrevaya and Hamermesh (2012) find no evidence that referees’ recommendations differ if the referee and author share a gender. Colussi (2018) finds evidence that an author’s social connections to the editor improves publication outcomes. Yoon (2013) finds evidence that law professors are more likely to publish in the law review of their home law school and that those in-home articles are cited less frequently than publications by outside faculty in the same law review. This article investigates the influence of political ideology in the selection process of law review articles. Student editors review submitted manuscripts and make acceptance decisions, generally without seeking expert review.1 Student editors have long been criticized for a lack of expertise (see, e.g., Friedman, 2018). Scholars have suggested that student editors rely on a set of proxies when choosing which articles to publish. Quantitative and qualitative evidence suggests that factors not directly related to article quality influence student’s acceptance decisions: the author’s credentials and reputation, the author’s previous publication record, the author’s connections to the publishing institution, the subject matter (with a preference for hot topics), and the author’s race and gender.2 Although there have been some suggestions of an effect of ideology in law review selection decisions (including an offhanded comment in Posner, 1995),3 the question has not been studied empirically. There are six features of the law review publication process that make the institutional setting well suited for studying the relationship between ideology and article selection. First, unlike editors of peer-reviewed journals, law review boards turn over each year. This means there is year-to-year variation in the individuals involved in the article selection process. Second, we are able to compare the outcomes of multiple articles for the same editors. In the peer review process, this may not be possible because rarely will the same editor and referee be observed. Third, there are not multiple sources of influence in the law review selection process. One identification challenge when studying influences in peer review journals is that there could be both editorial and referee influences acting simultaneously, making it difficult to disentangle their effects. For example, there could be three-way interactions between authors, editors, and referees. With law reviews, that is generally not the case. Fourth, the same pool of articles are considered by each law review board. Most academic journals outside of law reviews restrict authors from submitting to other journals simultaneously, which might lead authors to self-select into submitting to different journals. The result is that different journals may have dramatically different pools of articles to select from. This is not true of law reviews. Twice per year (roughly February and August), authors who submit to one top law review almost exhaustively submit to all top law reviews. This simultaneous submission setting overcomes concerns of selection into journals on the basis of ideology. Fifth, student editors have very few social ties with law professors, particularly law professors from other schools. In many peer-reviewed journals, the editors and potential authors can share professional connections. The result is that conservative (liberal) editors may be more likely to accept articles from conservative (liberal) authors simply because they have more professional and personal ties (Colussi, 2018). Finally, the law review setting allows us to match student editors to a measure of their ideology. Linking individuals to common measures of political ideology based on political donations requires enough information on the individual to distinguish between individuals with the same name in the United States. However, data used in most studies of the peer review process only contain the first name of the reviewer (e.g., Abrevaya and Hamermesh, 2012). Unlike the single or double blind process in peer review journals, the first and last names of student editors are available on mastheads for each volume.4 3. Data and Descriptive Statistics We built a dataset that contains an estimate of the ideologies of both student editors and the authors of the articles they accept, as well as the citations to each article. Our sample includes 15 law reviews: California Law Review, Columbia Law Review, Cornell Law Review, Duke Law Journal, Georgetown Law Journal, Michigan Law Review, Northwestern University Law Review, Stanford Law Review, Texas Law Review, UCLA Law Review, University of Chicago Law Review, University of Pennsylvania Law Review, Vanderbilt Law Review, Virginia Law Review, and Yale Law Journal. The law reviews at Harvard and New York University are not included in the sample because of an inability to link voting boards to the articles they accepted.5 We use articles from these 15 law reviews from 1990 to 2005.6 3.1. Voting Members on Law Review Each law review allows different board positions to vote on which articles to accept, but the board positions with voting rights differ between law reviews and changes over time. To determine the positions with voting rights, we surveyed the editor-in-chief of every volume in our sample. Supplementary Appendix A provides details about the survey. Although technically only the voting members of a law review ultimately vote on whether to accept an article, it is likely that high-ranking members without voting rights also influence which articles are accepted. This may be through control of the agenda: most articles are rejected before the board holds a vote, and the editor-in-chief and other high-ranking members of a law review may have the ability to influence which articles are put up for a vote. We therefore identify high ranking members as voting members even if they do not technically vote7 but the results are consistent if we define the voting board to include only voting members. 3.2. Mapping Editorial Boards to Selected Articles The editorial board at the time an article is published may not have initially selected the article. For example, an article published in Volume 100 of a law review may have been selected for publication by the articles committee of Volume 99. We thus needed to link articles to the board that actually selected them. To do so, the survey asked the editor-in-chiefs what volumes published the articles they accepted. We then used this information, and additional information from follow-up correspondence, to map published articles to the board members that selected them. 3.3. Student Editor Identities from Masthead Each volume of a law review contains a masthead page which lists each editor and their position. We obtained the mastheads for each volume in our sample. From the mastheads, we hand-coded the name of each voting member. In total, we coded the identities of 1,988 editors. The mean and median number of relevant members per journal in our sample is 8.8 3.4. Estimating Gender and Race We use editors’ names to recover an estimate of their gender and race. To estimate gender, we use the website “Genderize.”9 To estimate race, we use the python package “ethnicolr.”10 Ethnicolr “exploit[s] the U.S. census data, the Florida voting registration data, and the Wikipedia data collected by Skiena and colleagues, to predict race and ethnicity based on first and last name or just the last name.” We code someone as non-white if they are predicted to be non-white in any of the datasets. 3.5. Published Articles and Their Citations Heinonline is a website that contains information about law review publications. We gathered information from Heinonline about each publication between 1990 and 2005 in the 15 law reviews in our sample. This includes the title, identity of each author, volume, issue, and number of citations of that article. We make three sample restrictions. First, each volume of a law review usually contains multiple pieces not selected through the same mechanism as typical articles, including comments, notes, and book reviews. We exclude these non-article publications. Second, articles that are published as part of a symposium are typically solicited and do not go through the same selection process. We exclude symposium articles, but the results are similar if we include them. Third, there is evidence that student editors do not evaluate all authors in the same way, with law reviews publishing more articles written by faculty at their own institution (Yoon, 2013). We exclude home school authors because one might expect ideology to play a different role during article selection for them,11 but the results are consistent if we include them.12 After these restrictions, the final sample is 1,573 articles. 3.6. Measure of Political Ideology Our measure of political ideology is based on the political donations of the student editors and authors. The specific measure we use is called the Campaign Finance score (“CFscore”) and is drawn from the Database on Ideology, Money in Politics, and Elections (DIME) (Bonica, 2014). A growing literature uses and validates CFscores (Bonica, 2014; Thomsen, 2014; Chilton and Posner, 2015; Bonica and Rosenthal, 2016; Wood and Spencer, 2016; Bonica and Sen, 2017; Bonica et al., 2019).13 DIME is a database of campaign contributions made from 1979 to 2016. This comprises more than 250 million donations made by more than 20 million unique donors. Supplementary Appendix C describes the process of matching our sample to DIME. To calculate the CFscores from raw donations data, DIME first assigns political candidates unidimensional ideological scores based on their common donors. The scale is normalized to the population of U.S. donors such that the mean is zero and the standard deviation is one. For instance, Bernie Sanders has a CFscore of -1.89, Barak Obama has a CFscore of -1.16, Hillary Clinton has a CFscore of -1.10, Mitt Romney has a CFscore of 0.90, and Donald Trump has a CFscore of 1.29. Individual donors are then assigned ideological scores on the same unidimensional scale based upon a weighted average of the amount of donations they have made and the CFscore of the candidate to whom they gave. For instance, if an individual’s only political contribution was to Mitt Romney, her CFscore would match Romney’s CFscore (0.90). If an individual donated $$1{,}000$$ to Barack Obama and $$2{,}000$$ to Bernie Sanders, her CFscore would be the sum of 1/3 of Obama’s score and 2/3 of Sanders’ score (-1.65). A number of concerns arise with the use of the CFscore for measuring editor and author ideology. For instance, CFscores are based on lifetime donations, and not all people donate to campaigns and thus do not have a CFscore. In Section 6, we explore the extent to which the drawbacks of the CFscore are likely to affect the results. 3.7. Descriptive Statistics Table 1 provides descriptive statistics. Panel A describes the full sample of editors, and Panel B describes the full sample of authors. For editors, our measure of board ideology is at the journal-year level. For authors, we define an article as conservative if at least one author is conservative. This approach is motivated by Colussi (2018), who defines an article authored by more than one author as having a social connection with the editor if at least one author is has a social connection with an editor. However, the results are consistent when using alternative ways of classifying co-authored articles.14 Table 1. Descriptive Statistics A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 Open in new tab Table 1. Descriptive Statistics A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 A. Editor information Number of editors 1,988 Percent of editors with donations (%) 34 Percent of editors with donations that are conservative (%) 21 B. Author information Number of authors 4,716 Percent of authors with donations (%) 58 Percent of authors with donations that are conservative (%) 15 C. Sample Number of journal-years 234 Number of articles 1,573 Mean percent conservative board (%) 21 At least one conservative author (%) 15 Open in new tab Figure 1 plots the percent of editors and authors with political donations over time.15 Over the sample as a whole, we matched 34% of editors and 58% of authors to donations. We classify individual donors as “conservative” if their CFscore places them at or above the average American donor (CFscore $$\geq$$ 0) and “liberal” if their CFscore places them below the average American donor (CFscore $$<$$ 0). Using this definition, 21% of editors and 15% of authors are conservative. Figure 2 provides the distributions of the percent of conservative editors and authors per volume.16 The ideology of editors and authors is consistent with previous research (see, e.g., Bonica et al., 2016, 2018). Figure 1. Open in new tabDownload slide Editors and Authors with Political Donations over Time. Figure 1. Open in new tabDownload slide Editors and Authors with Political Donations over Time. Figure 2. Open in new tabDownload slide Distribution of Author and Editor Ideology. Figure 2. Open in new tabDownload slide Distribution of Author and Editor Ideology. Panel C of Table 1 provides descriptive statistics of the final sample used in the empirical analysis. The main analysis is at the journal-year level. The average number of articles per journal-year in the final sample is 7, with 10% having more than 10 articles. 4. Relationship Between Editor and Author Ideology 4.1. Research Design Suppose article $$i$$ has a set of attributes, including quality $$q_{i}$$ ⁠, political ideology as proxied by the author’s ideology $$a_{i}$$ ⁠,17 author gender $$g_{i}$$ ⁠, and author race $$r_{i}$$ ⁠. Suppose the editors of law review $$j$$ in year $$t$$ have a set of attributes, including political ideology $$e_{jt}$$ ⁠, gender $$g_{jt}$$ ⁠, and race $$r_{jt}$$ ⁠. Further suppose the editors have three preferences over articles. First, editors prefer articles with higher quality $$q_{i}$$ ⁠. Second, editors prefer to select articles from authors with shared gender and race denoted $$G_{ijt}$$ and $$R_{ijt}$$ ⁠. Third, editors prefer to select articles with an ideology close to their own ideology. In particular, let $$P_{ijt}$$ be the ideological distance between editors $$j$$ and article $$i$$ ⁠. Let $$y_{ijt}$$ be an indicator variable for whether editors from law review $$j$$ accept article $$i$$ in year $$t$$ ⁠. To estimate the relationship between editor and article ideology, we would ideally estimate: \begin{align*} y_{ijt}=\hat{\alpha}+\hat{\gamma}q_{ijt}+\hat{\beta}P_{ijt}+\hat{\sigma}G_{ijt }+\hat{\theta}R_{ijt}+\varepsilon_{it}, \end{align*} where $$\hat{\beta}$$ estimates the relationship between editor and article ideology. The problem is that estimating the above equation requires the full set of articles considered by the editors—that is, both the articles they published and the articles they did not publish. We do not observe the full set of articles submitted to editors. Rather, we only observe the set of accepted articles. Given the set of accepted articles, one potential option is to regress author ideology on editor ideology. The problem with such an approach is that, because gender and race are correlated with ideology, any preferences for shared gender or race would create omitted variables bias.18 To account for the possibility of gender and racial preferences, we control for editor gender and race. We estimate Equation 1 at the journal-year level. \begin{align} a_{jt}=\alpha+\beta e_{jt}+\gamma g_{jt}+\theta r_{jt}+\phi_{t}+ \eta_{j}+\epsilon_{jt} . \end{align}(1) The primary dependent variable $$a_{jt}$$ is the percent of articles with at least one conservative author. One advantage of this measure is that it lends itself to easy substantive interpretation. It is also possible that the students selecting articles are aware of whether an author is conservative or liberal but unaware of the degree to which an author is conservative or liberal. One disadvantage of this measure is that it discards information that is contained within the continuous measure of ideology. Therefore, we also use the mean CFscore of the authors of each accepted article as a second dependent variable. The independent variable of interest $$e_{jt}$$ is either the percent of donating editors who are conservative or the mean CFscore of the donating editors. In the preferred specification, we include year fixed effects $$\phi_{t}$$ ⁠, journal fixed effects $$\eta_{j}$$ ⁠, and controls for editor gender and race (⁠ $$g_{jt}$$ and $$r_{jt}$$ ⁠). For the gender and race controls, we use the percent of female editors and the percent of non-white editors. The coefficient of interest is $$\beta$$ ⁠. It asks, for a given mix of editors in terms of gender and race, is within-journal variation in the ideology of the editors associated with a different likelihood of publishing articles written by conservative authors? The articles selected by one law review in a given year are not independent of the articles selected at other journals in the year, which can create mutual dependence in the error terms within a year. In the main results, we thus cluster standard errors at the year level. Below, we find that the size of the standard errors are similar using different levels of clustering. 4.2. Results Panel A of Table 2 reports the results of regressing the percent of conservative authors on the percent of conservative editors. Column 1 includes year fixed effects, Column 2 adds law review fixed effects, Column 3 adds controls for gender and race, and Column 4 adds journal time trends. Column 3 reports the results from estimating Equation 1 and is our preferred specification. The estimate indicates that a board with 1 percentage point more conservative editors accept 0.6% more articles written by conservative authors (0.0093 percentage points from a baseline of 0.148).19 To interpret the magnitude of the effect, first consider that the within-journal standard deviation of editor ideology is 24% of conservative editors on average across the journals. Therefore, the estimate suggests that a 1 standard deviation conservative shift in a board’s ideology is associated with a 14% increase in the number of articles published by conservative authors. As another way to interpret the magnitude of the effect, consider that across the law reviews, on average a law review’s least conservative board has 72% fewer conservatives than the law reviews most conservative board. Therefore, the estimate suggests that a law review would accept 43% more articles written by conservative authors in a year with their most conservative editors compared to a year with their most liberal editors.20 Table 2. Relationship Between Editor Ideology on Author Ideology . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 Note: The regressions are at the journal-year level. Standard errors clustered by year in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. Open in new tab Table 2. Relationship Between Editor Ideology on Author Ideology . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 . (1) . (2) . (3) . (4) . A. Outcome: percent conservative author Percent conservative editors 0.098*** 0.096** 0.093** 0.120*** (0.030) (0.035) (0.037) (0.037) Dep Var mean 0.148 0.148 0.148 0.148 B. Outcome: mean author CFscore Mean editor CFscore 0.094* 0.090* 0.083 0.092 (0.049) (0.050) (0.053) (0.057) Dep Var mean −0.890 −0.890 −0.890 −0.890 Covariates Year FE Yes Yes Yes Yes Journal FE No Yes Yes Yes Gender and race controls No No Yes Yes Journal time trends No No No Yes N 234 234 234 234 Note: The regressions are at the journal-year level. Standard errors clustered by year in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. Open in new tab Panel B reports the results of regressing the mean CFscore of authors on the mean CFscore of editors. Although the results are not statistically significant at conventional levels in all specifications, they are consistent with the estimates in Panel A. The results in Column 3 indicate that a 1 CFscore point more conservative board accepts articles written by authors that are 0.083 CFscore points more conservative. Figure 3 assesses the sensitivity of the results to alternative modeling choices while using the same specifications as in Table 2. First, we assess the sensitivity of the results to different levels of analysis. The main specification was at the journal-year level, but we also estimate these same specifications at the article level, as indicated on the left-hand side of the figure. This means that the ideology of authors varies within a journal-year, but the ideology of editors is constant within the journal-year. The dependent variable is either an indicator variable for whether there is at least one conservative author for a given article or the author CFscore (if there are multiple authors, the mean CFscore). Second, we assess the possibility that the specification did not properly account for trends by estimating a first-difference specification, as indicated on the left hand side of the figure. The dependent variable is the change in the percent conservative authors (mean author CFscore) from one year to the next, and the independent variable is the change in the percent conservative editors (mean editor CFscore) from one year to the next. Finally, we assess the sensitivity of the results to different levels of clustering. For each combination of control variables and level of analysis, we estimate the specification without a clustering adjustment (as indicated by “No”), clustering by journal (as indicated by “Journal”), and clustering by year (as indicated by “Year”). Figure 3. Open in new tabDownload slide Sensitivity Tests to Controls and Clustering. Note: The Figure reports the point estimate and 90 percent confidence interval for a series of regressions. The left panel reports the results of regressing the percent of conservative authors on the percent of conservative editors. The right panel reports the results of regressing the mean CFscore of authors on the mean CFscore of editors. As indicated on the left hand side of the figure, the top section estimates the specifications at the article level, the middle section estimates the specifications at the journal-year level, and the bottom section estimates a first-difference specification at the journal-year level. Within a section, the controls correspond to the specifications in Table 2. For each combination of controls and level of analysis, the figure reports regressions without a clustering adjustment (as indicated by “No”), clustering by journal (as indicated by “Journal”), and clustering by year (as indicated by “Year”). Figure 3. Open in new tabDownload slide Sensitivity Tests to Controls and Clustering. Note: The Figure reports the point estimate and 90 percent confidence interval for a series of regressions. The left panel reports the results of regressing the percent of conservative authors on the percent of conservative editors. The right panel reports the results of regressing the mean CFscore of authors on the mean CFscore of editors. As indicated on the left hand side of the figure, the top section estimates the specifications at the article level, the middle section estimates the specifications at the journal-year level, and the bottom section estimates a first-difference specification at the journal-year level. Within a section, the controls correspond to the specifications in Table 2. For each combination of controls and level of analysis, the figure reports regressions without a clustering adjustment (as indicated by “No”), clustering by journal (as indicated by “Journal”), and clustering by year (as indicated by “Year”). Figure 3 reports the point estimates and 90% confidence intervals for these regressions. These results show that the size of the point estimates and the standard errors are not highly sensitive to the level of analysis, the way trends are accounted for, and the level of clustering. Overall, although the estimates in some specifications do not quite reach statistical significance, the results are consistent across the specifications. 5. Mechanisms There are two main potential explanations for the positive relationship between editor and author political ideology. First, editors could have a preference for accepting or rejecting articles on the basis of ideology (Becker, 1957). Second, editors could attempt to choose the articles that will be most cited, observe noisy signals of quality, and are better at screening articles written by authors with shared ideology (Phelps, 1972 Arrow, 1973; Aigner and Cain, 1977). Although both of these explanations predict that editors will accept more articles written by authors with shared ideology (which we refer to as “likeminded articles”), the explanations have conflicting predictions about the citations of likeminded articles and non-likeminded articles. If likeminded articles are selected more often because of a preference, the likeminded articles will have fewer citations. This is a standard prediction from Becker (1957).21 Therefore, if likeminded articles have more citations, it cannot be the case that a taste for selecting likeminded articles is driving the relationship between editor and author political ideology.22 To test between these explanations, we generate a dataset at the journal-year-author ideology level. That is, for each journal-year, there are two observations: the average number of citations for liberal authors and the average number of citations for conservative authors. Let $$c_{jt}$$ be an indicator variable for conservative author. We estimate Equation 2. \begin{align} \ln(\text{citations}_{jtc})=\alpha+\beta p_{jt}\times c_{jt}+ \sigma c_{jt}+\phi_{jt}+\epsilon_{jt} , \end{align}(2) where $$\ln(\text{citations}_{jtc})$$ is the natural log of the average article citations published in journal $$j$$ in year $$t$$ of author of ideology $$c_{jt}$$ ⁠, $$p_{jt}$$ is the percent of donating editors that are conservative, and $$\phi_{jt}$$ are journal-year fixed effects.23 The coefficient $$\beta$$ on the interaction term captures the differential effect of the conservativeness of the editorial board on citations of articles written by conservative authors. Equation 2 produces an unbiased estimate for $$\beta$$ under two assumptions. The first assumption is that student editor feedback in the editing process changes citations to a likeminded article the same as a non-likeminded article. Although we have no support for the assumption, we are skeptical that differential effort that students put into editing articles because of ideology can be material in changing citations to the article. The second assumption is that the additional likeminded articles that are accepted are not more likely to be drawn from highly cited fields. This assumption would be violated if, for example, a board decides to publish one more likeminded article from a high citation field (e.g., constitutional law) instead of a non-likeminded article from a low citation field (e.g., tax law).24 In Table 3, Column 1 includes the main effect on percent conservative editors, the main effect on conservative author, year fixed effects, and journal fixed effects. Column 2 adds the interaction term, Column 3 adds the controls for gender and race, and Column 4 adds journal time trends. Column 5 estimates Equation 2 by replacing the journal time trends with journal-year fixed effects, which allows for a comparison of the citations of articles written by liberal and conservative authors within a journal-year. Because there is no variation in editor ideology within a journal-year, the main effect on percent conservative editors and the controls for race and gender drop out of the regression with journal-year fixed effects. In Columns 2–4, the main effect on percent conservative editors is negative, suggesting that more conservative editors accept liberal articles that are cited less. The estimate on the interaction term is positive, statistically significant, and stable across the specifications. The point estimates for Columns 2–5 indicate that moving from 0% conservative editors to 100% conservative editors is associated with a 55% increase in citations for articles written by conservative authors. To interpret the estimate, note again that the within-journal standard deviation of editor ideology is 24% of conservative editors on average across the journals. This means that a 1 standard deviation shift in a board’s ideology is associated with a 13% change in citations for articles written by conservative authors. Table 3 thus provides no evidence that the relationship between editor and author ideology is driven by a preference for selecting articles on the basis of ideology. Table 3. Relationship Between Editor–Author Ideology and Citations . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 Note: The regressions are at the journal-year-ideology level. Standard errors clustered by year are in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. The sample is restricted to journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author, so the sample size is lower than in Table 2. See text for details. Regressions are weighted by the number of articles. The main effect on “Conservative author” is included in the specifications but is not reported. Open in new tab Table 3. Relationship Between Editor–Author Ideology and Citations . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 . ln(Citations) . . (1) . (2) . (3) . (4) . (5) . Percent conservative editors 0.13 −0.15 −0.19 −0.16 (0.18) (0.15) (0.16) (0.19) Percent conservative editors 0.55** 0.55** 0.55** 0.55* $$\quad$$ $$\times$$ At least one conservative author (0.23) (0.23) (0.23) (0.30) Covariates Year FE Yes Yes Yes Yes No Journal FE Yes Yes Yes Yes No Gender and race controls No No Yes Yes No Journal time trends No No No Yes No Journal-year FE No No No No Yes N 296 296 296 296 296 Note: The regressions are at the journal-year-ideology level. Standard errors clustered by year are in parentheses. $${}^{*}$$P  $$<$$ 0.1, $${}^{**}$$P  $$<$$ 0.05, $${}^{***}$$P  $$<$$ 0.01. The sample is restricted to journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author, so the sample size is lower than in Table 2. See text for details. Regressions are weighted by the number of articles. The main effect on “Conservative author” is included in the specifications but is not reported. Open in new tab To further investigate the relationship, Figure 4 reports a binned scatterplot and a line of best fit of the relationship of interest. The y-axis is the difference between the natural log of the mean citations of articles written by conservative authors in a journal-year and the natural log of the mean citations of articles written by liberal authors in the same journal-year. A positive number indicates that the articles written by conservative authors were cited more on average than the articles written by liberal authors. The x-axis is the percent of donating editors that are conservative. The positive and statistically significant relationship indicates that more conservative boards accept articles written by conservative authors that are cited more than the articles written by liberal authors that they accept. Figure 4. Open in new tabDownload slide Relationship between Editor Political Ideology and Difference in Citations to Articles from Liberal and Conservative Authors. Note: The figure reports a binned scatterplot and a line of best fit of the relationship of interest. The $$y$$ -axis is the difference between the natural log of the mean citations of articles written by conservative authors in a journal-year and the natural log of the mean citations of articles written by liberal authors in the same journal-year, where a positive number indicates that the articles written by conservative authors were cited more on average than the articles written by liberal authors. The $$x$$-axis is the percent of donating editors who are conservative. Figure 4. Open in new tabDownload slide Relationship between Editor Political Ideology and Difference in Citations to Articles from Liberal and Conservative Authors. Note: The figure reports a binned scatterplot and a line of best fit of the relationship of interest. The $$y$$ -axis is the difference between the natural log of the mean citations of articles written by conservative authors in a journal-year and the natural log of the mean citations of articles written by liberal authors in the same journal-year, where a positive number indicates that the articles written by conservative authors were cited more on average than the articles written by liberal authors. The $$x$$-axis is the percent of donating editors who are conservative. 6. Using Political Donations to Measure Ideology Measures of ideology based on political donations are increasingly used in social science research (e.g., Bonica et al., 2017a), but there are potentially important limitations with the approach.25 We assess whether two limitations of using CFscores to measure ideology—that they are based on lifetime donations and that they are not available for all authors and editors—are likely to bias the results. 6.1. Lifetime Measure of Ideology One concern with using CFscores as a measure of ideology is that they are based on lifetime donations. There are three reasons to believe that this approach does not raise identification concerns for the analysis. First, ideology of adults has been shown to be stable (e.g., Bonica, 2014), and research suggests that typically only major life changes are likely to alter ideology (Green et al., 2004). To put the stability of ideology in context, some evidence suggests that Americans are more likely to change their religion than their political party.26 Although many of the editors may have gone through these kind of major life changes, we think it is unlikely that this would occur in a systematic way that would drive correlations between average board ideologies and the articles that are accepted. Second, if editors’ ideology changes after law school and before subsequent political donations are made, this approach would likely introduce measurement error rather than create any bias in the estimates. Finally, the main concern for identification would be if the process of reviewing articles caused editors’ ideologies to change (i.e., reverse causation). For the results to be driven by reverse causation, editing one and a half more conservative articles would have to lead to a one standard deviation change in ideology of the entire editorial board. That is, for the combined group of editors, editing the article would need to have an effect on each editor’s ideology dramatically bigger than the demonstrated effect from profound life events, such as large changes in wealth (Bonica and Rosenthal, 2016). Although the students who spent the most time editing the additional conservative article may have had a deep enough level of intellectual engagement to change their ideology, such a change is unlikely to occur for the board overall in a given year. 6.2. Missing Ideology Data Our measure of ideology is based on political donations, and editors and authors that have not made a donation thus have missing ideology. For authors, missing ideology does not create any identification concerns. Because our sample of articles is restricted to those with at least one donating author, missing author ideologies changes the sample of articles. It therefore only changes the interpretation of the results. For editors, however, missing ideology creates potential identification concerns. Because we define a board’s conservativeness based on the ideology of the donating editors, missing editor ideology may bias the results.27 We investigate whether missing data may be driving the results under three different assumptions.28 First, it is possible that editors’ propensity to donate is uncorrelated with their ideology. If so, missing editor ideologies would be drawn from the same ideological distribution as the editors in our sample who have donated, implying that editors are effectively missing at random. If so, missing ideology would introduce only classical measurement error, which would attenuate the estimated coefficients towards zero but would not bias the estimated coefficients. If missing editor ideologies are random and introduce measurement error, restricting the sample to one in which we observe relatively more editor ideologies would decrease measurement error, leading to larger point estimates and more precision. We tested this possibility by restricting our sample to boards with at least three editors with donations and to years when there were relatively more editors donating (1990 to 2000).29 We find that that the size of the point estimates increase, suggesting that measurement error for missing editor ideology was driving down the size of the estimates in Table 2. Second, it is possible that missing editors have similar ideologies to their fellow law school classmates. To test how this possibility would change the results, we use data on the percentage of conservative graduates from each law school-year from Bonica et al. (2016). We then assume that editors with missing ideology are ideologically represented by the alumni of their law school in the 5 years around when they graduated and calculate the percent conservative editors for all the board—editors that made and have not made donations—after filling in the missing editor ideologies with this average conservativeness. Unlike the last tests that reduced measurement error by restricting the sample, this approach introduces measurement error into our measure of editor ideology. As expected, we find that the standard errors increase (more than doubling in some specifications) when using this approach. Although the estimates are not statistically significant in most specifications, the point estimates remain positive in each of them. This provides some evidence that observing the missing editor ideologies would not change the direction of the point estimates. Third, it is possible that donating editors have systematically different ideologies from non-donating editors.30 If donors have different ideological preferences than non-donors, it could systematically bias the estimates. We investigate how the results would change if missing editors have less intense ideological preferences than donating editors. To do so, we follow Bonica et al. (2019) and use a back-of-the-envelope adjustment to correct for missing data. Assume that in a journal-year the mean ideology of missing editors is equal to $$\rho$$ times the mean ideology of the non-missing editors: \begin{align*} e_{jt}^{M}=\rho\,e_{jt},\end{align*} where $$e_{jt}^{M}$$ is the ideology of missing editors and $$\rho < 1$$ corresponds to the case in which editors with more intense ideological preferences are more likely to donate. In this case, the true ideology of editors, $$e_{jt}^{*}$$ ⁠, is: \begin{align*} e_{jt}^{*}=(1-\mu)e_{jt}+\mu e_{jt}^{M}, \end{align*} where $$\mu$$ is the proportion of missing editors. In this setting, Bonica et al. (2019) show that obtaining the true effect of ideology requires scaling the coefficient estimated from the sample of donors by a factor of $$\frac{1}{1-\mu(1-\rho)}$$ ⁠.31 Given that we observe 34 percent of editors donations (⁠ $$\mu=0.66)$$ ⁠, the point estimate in Table 2, Panel B, Column 3 of $$\hat{\beta}=0.093$$ implies that the true coefficient is $$\beta=\frac{0.093}{0.34+.66*\rho}$$ ⁠. Because $$\rho$$ is between 0 and 1, the true value of $$\beta$$ under these assumptions is between $$0.093$$ and $$0.273$$ ⁠. As the extent to which donors have stronger ideological views relative to non-donors increases, the true coefficient increases. Because it is unlikely to be the case that editors with missing ideology actually have more intense preferences than those whose ideology we observe, the estimates likely provide a lower bound for the true effect. Taken together, these results suggest that missing editor ideology may be moderately biasing the size of the estimated coefficients toward zero, but they do not suggest that missing editor ideology is driving our finding of a non-zero effect. 7. Conclusion This article studied the role that political ideology plays in the selection process for law review articles. We matched the identities of student editors and authors of accepted articles to a measure of political ideology based on political donations. We find that the number of accepted articles written by conservative authors is increasing in the conservativeness of a law review’s editorial board. This finding contributes to the literature on disparate outcomes in the article selection process (e.g., Blank, 1991; Abrevaya and Hamermesh, 2012; Hengel, 2016; Colussi, 2018) by examining both a new setting (the legal academy) and a new dimension along which disparate outcomes can occur (political ideology). We then investigated whether this relationship was driven by student editors having a preference for publishing articles that promote their political ideology or by student editors being objectively better at assessing the contribution of articles written by authors with shared ideology. To do so, we assessed whether articles whose authors and editors share an ideology are cited more than articles whose authors and editors have different ideologies. We found evidence inconsistent with the preference explanation and consistent with the screening explanation. This second finding contributes to the literature exploring the underlying causes of disparate outcomes (e.g., Levitt, 2004; Antonovics and Knight, 2009; Ewens et al., 2014). The results shed light on important debates in the legal academy. Academic careers are based on publishing (Frey and Rost, 2010), and the journal in which a scholar publishes exerts a strong influence on that individual’s job opportunities (Diamond, 1986). Moreover, academic articles published in journals remain the primary mechanism for disseminating research, so the journal in which an article is published affects the article’s reach and influence. The fact that ideology plays a role the selection process for law review articles thus has ramifications for both career trajectories and the dissemination of knowledge. Acknowledgement We thank Thomas Drueke for help constructing the data and Kimberly Rubin for excellent research assistance. For helpful comments, we are grateful to Adam Bonica, Michael Frakes, Erik Hovenkamp, William Hubbard, J.J. Prescott, Maya Sen, and participants at the 2018 American Law and Economics Association Annual Meeting. Footnotes 1. " A few law reviews (e.g., Harvard Law Review, University of Chicago Law Review, and the Yale Law Journal) have recently begun to send some articles out to expert faculty referees. During our sample period (1990 – 2005), expert reviews in law review article selection were very uncommon. If we exclude the few journals that might have sent articles out for review during our sample period, the results are largely unchanged in both an economic and statistical sense. 2. " See, e.g., Ellman (1983), Leibman and White (1989), Merritt (1998), Christensen and Oseid (2007), Nance and Steinberg (2009), and Higdon (2016). Recent lawsuits have been filed challenging the use of race and gender in law review article selection decisions (Van Voris, 2018). 3. " See Posner (1995) at 1133 (“The change in the character of legal scholarship has been accompanied by a collapse of political consensus among legal scholars and by a vast expansion in constitutional law, which is the most political field of law as a consequence of the nature of the issues it addresses, the remoteness of the governing text, and the field’s domination by a court (the Supreme Court) from which there is no possibility of appeal to a still higher court to keep the judges in line. Legal scholarship became more political at the same time that it was becoming more centrifugal. These developments beached not only a number of doctrinal scholars but also most student editors. They were now dealing with a scholarly enterprise vast reaches of which they could barely comprehend, and they were being tempted by the increasing politicization of the enterprise to employ political criteria in their editorial decisions.”). 4. " It is worth emphasizing that because law students make publication decisions, the article selection process for law reviews is probably unlike other article selection processes. Any findings of a relationship between political ideology and article selection for laws reviews thus might not be generalizable to the article selection process in other disciplines, and any findings of a relationship between political ideology and article selection in other disciplines might not be generalizable to the article selection process in law reviews. 5. " We do not include the Harvard Law Review in our sample because the masthead does not distinguish between editorial positions and allow all editors to vote on which articles to accept. The large number of editors thus implies that there would be almost no year-to-year variation in the ideology of the board. We do not include New York University Law Review because there is not a one-to-one correspondence between boards and volumes. As a result, we cannot identify precisely which boards chose which articles. Nonetheless, we reran the analysis with New York University in the sample while coding students as accepting articles with a publication date in the year they have a board position on the masthead, and the results are consistent. 6. " An earlier version of this article used more years of data. At the advice of a referee, we use 2005 as the end year because the percent of editors making political donations noticeably decreased in the later years of the sample. 7. " Mastheads are usually structured with the highest ranking position on the top (editor-in-chief) and positions listed in decreasing rank down the page of the masthead. We hand-coded all positions that are at or near the same level as the lowest ranking title that has voting rights. We exclude editors in charge of comments and book reviews as non-voting even if they are at or above the lowest voting member on the masthead. 8. " Supplementary Appendix B reports the distribution of the overall number of members per journal-year and the number of donating members per journal-year. Of the members who have made donations, the mean and median number per journal-year in our sample is 3, with 75% having at least 2 members. 9. " https://genderize.io/ 10. " https://github.com/appeler/ethnicolr 11. " An earlier version of this article included home school authors in the main sample. We excluded home school authors from the main sample at the advice of a referee. 12. " Nance and Steinberg (2008) find that editors make decisions in part because of the prestige of the author or their institution. As a robustness check, we estimated the relationship between editor on author ideology after excluding authors from the top 15 law schools, and the results are consistent. 13. " For example, Bonica (2019) validates CFscores against a battery of policy items and finds that they are “powerful predictors of policy preferences for a wide range of issues and successfully discriminate between donors from the same party.” 14. " The results are consistent under four alternative ways of handling co-authored articles: (1) making the unit of observation the donating author rather than the article; (2) defining an article as conservative only if there is at least one conservative author and no liberal authors; (3) using the most liberal or conservative author’s CFscore rather than the mean of the author’s CFscores; and (4) dropping all coauthored articles. 15. " Figure 1 reports the mean donation rates across articles rather than at the individual level. The fact that the same author publishes multiple articles explains why the percent of authors with donations averaged over articles is roughly the same as the percent of authors who have had a donations in the matched sample. 16. " Table D1 in the Supplementary Appendix reports the mean and standard deviation of the percent conservative editors by journal, and shows that there is considerable variation of editor ideology within a journal over time. Across the journals, the average and standard deviation percent conservative editors is 20 and 24, respectively. 17. " Chilton and Posner (2015) find that the substance of articles partly reflects the ideology of their authors. 18. " For discussions of race and omitted variable bias, see Clarke and Rothenberg (2018), Liscow and Woolston (2018), and Miller (2019). 19. " In Panel A of Table 2, the dependent variable takes the value of 0 if there are no conservative authors and the value of 1 if 100% of the authors are conservative, and the independent variable takes the value of 0 if there are no conservative editors and the value of 1 if 100% of the editors are conservative. As such, the point estimate of 0.093 indicates that moving from a board with 0% conservatives to 100 percent conservatives increases the probability of selecting a conservative author by 9.3 percentage points. To interpret the coefficient as a 1 percentage point increase in the percent conservative editors, the point estimate is divided by 100. 20. " Imagine if student editors matched the ideology of the public. In our sample, 21% of editors are conservative, but 50% of the donating public are conservative. If student editors had matched the ideology of the public, the estimate suggests that the 15 law reviews would have accepted 17% more conservative articles. 21. " See Mungan (2018) for a review of this literature. 22. " Screening could lead to more likeminded articles being accepted, and the additional articles could be less likely to be cited on the whole. As a result, it is not necessarily the case that differential screening ability would lead to higher citations for the average likeminded article. Nonetheless, if we observe that likeminded articles are more highly cited than we would expect, this would suggest that the increase in citations of likeminded articles resulting from greater screening ability first order dominates any decrease in citations from the additional likeminded articles being published. 23. " With journal-year fixed effects, the regression is estimated using journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author. For the specifications without journal-year fixed effects, we restrict the sample to the same journal-years in which at least one published article was written by a conservative author and at least one published article was written by a liberal author in order to assess differences in impact between author ideology within an editorial board. This means that the sample size is not double the sample size in Table 2. 24. " We have been unable to obtain data on the subject matter of articles. If we had data on the subject matter of articles, we would include subject matter fixed effects. 25. " For a general discussion of uncertainty when measuring ideology, see Bailey and Spitzer (2018). 26. " As discussed in The Economist (2018), “datasets do not line up in a way that makes the conjecture possible to prove, but it is a fair bet that, at least among those most engaged in politics, Americans are more likely to change their religion than to change their party.” 27. " See Lee (2017) for an example of law and economics research confronting classical measurement error. 28. " This discussion and analysis follows Bonica et al. (2019). These results are omitted for brevity, but they are available in the working paper version of this article. 29. " The results tell the same story using different thresholds. 30. " We are unaware of any reason to think that the ideologies of non-donors are meaningfully different from the ideologies of donors. Prior research using surveys and using CFscores has produced consistent estimates of the ideologies of lawyers. For instance, Peppers and Zorn (2008) surveyed Supreme Court clerks and found that 75% were democrats and 25% were republicans; when analyzing the same population using the CFscore, Bonica et al. (2017b) found the exact same breakdown to the percent. 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