Researchers often have the flexibility to report only the results they want to report, so an important role for peer reviewers is to request that researchers report results that a reasonable skeptical reader might suspect have been strategically unreported. I'll discuss two publications where obvious peer review requests do not appear to have been made and, presuming these requests were not made, how requests might have helped readers better assess evidence in the publication.
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Example 1. Ahlquist et al. 2014 "Alien Abduction and Voter Impersonation in the 2012 U.S. General Election: Evidence from a Survey List Experiment"
Ahlquist et al. 2014 reports on two list experiments: one list experiment is from December 2012 and has 1,000 cases, and another list experiment is from September 2013 and has 3,000 cases.
Figure 1 of Ahlquist et al. 2014 reports results for the 1,000-person list experiment estimating the prevalence of voter impersonation in the 2012 U.S. general election; the 95% confidence intervals for the full sample and for each reported subgroup cross zero. Figure 2 reports results for the full sample of the 3,000-person list experiment estimating the prevalence of voter impersonation in the 2012 U.S. general election, but Figure 2 did not include subgroup results. Readers are thus left to wonder why subgroup results were not reported for the larger sample that had more power to detect an effect among subgroups.
Moreover, the main voting irregularity list experiment reported in Ahlquist et al. 2014 concerned voter impersonation, but, in footnote 15, Ahlquist et al. discuss another voting irregularity list experiment that was part of the study, about whether political candidates or activists offered the participant money or a gift for their vote:
The other list experiment focused on vote buying and closely mimicked that described in Gonzalez-Ocantos et al. (2012). Although we did not anticipate discovering much vote buying in the USA we included this question as a check, since a similar question successfully discovered voting irregularities in Nicaragua. As expected we found no evidence of vote buying in the USA. We omit details here for space considerations, though results are available from the authors and in the online replication materials...
The phrasing of the footnote is not clear whether the inference of "no evidence of vote buying in the USA" is restricted to an analysis of the full sample or also covers analyses of subgroups.
So the article leaves at least two questions unanswered for a skeptical reader:
- Why report subgroup analyses for only the smaller sample?
- Why not report the overall estimate and subgroup analyses for the vote buying list experiment?
Sure, for question 2, Ahlquist et al. indicate that the details of the vote buying list experiment were omitted for "space considerations"; however, the 16-page Ahlquist et al. 2014 article is shorter than the other two articles in the journal issue, which are 17 pages and 24 pages.
Peer reviewer requests that could have helped readers were to request a detailed report on the vote buying list experiment and to request a report of subgroup analyses for the 3,000-person sample.
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Example 2. Sen 2014 "How Judicial Qualification Ratings May Disadvantage Minority and Female Candidates"
Sen 2014 reports logit regression results in Table 3 for four models predicting the ABA rating given to U.S. District Court nominees from 1962 to 2002, with ratings dichotomized into (1) well qualified or exceptionally well qualified and (2) not qualified or qualified.
Model 1 includes a set of variables such as the nominee's sex, race, partisanship, and professional experience (e.g., law clerk, state judge). Compared to model 1, model 2 omits the partisanship variable and adds year dummies. Compared to model 2, model 3 adds district dummies and interaction terms for female*African American and female*Hispanic. And compared to model 3, model 4 removes the year dummies and adds a variable for years of practice and a variable for the nominee's estimated ideology.
The first question raised by the table is the omission of the partisanship variable for models 2, 3, and 4, with no indication of the reason for that omission. The partisanship variable is not statistically significant in model 1, and Sen 2014 notes that the partisanship variable "is never statistically significant under any model specification" (p. 44), but it is not clear why the partisanship variable is dropped in the other models because other variables appear in all four models and never reach statistical significance.
The second question raised by the table is why years of practice appears in only the fourth model, in which roughly one-third of cases are lost due to the inclusion of estimated nominee ideology. Sen 2014 Table 2 indicates that male and white nominees had substantially more years of practice than female and black nominees: men (16.87 years), women (11.02 years), whites (16.76 years), and blacks (10.08 years); therefore, any model assessing whether ABA ratings are biased should account for sex and race differences in years of practice, under the reasonable expectation that nominees should receive higher ratings for more experience.
Peer reviewer requests that could have helped readers were to request a discussion of the absence of the partisanship variable from models 2, 3, and 4, and to request that years of experience be included in more of the models.
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Does it matter?
Data for Ahlquist et al. 2014 are posted here. I reported on my analysis of the data in a manuscript rejected after peer review by the journal that published Ahlquist et al. 2014.
My analysis indicated that the weighted list experiment estimate of vote buying for the 3,000-person sample was 5 percent (p=0.387), with a 95% confidence interval of [-7%, 18%]. I'll echo my earlier criticism and note that a 25-percentage-point-wide confidence interval is not informative about the prevalence of voting irregularities in the United States because all plausible estimates of U.S. voting irregularities fall within 12.5 percentage points of zero.
Ahlquist et al. 2014 footnote 14 suggests that imputed data on participant voter registration were available, so a peer reviewer could have requested reporting of the vote buying list experiments restricted to registered voters, given that only registered voters have a vote to trade. I did not see a variable for registration in the dataset for the 1,000-person sample, but the list experiment for the 3,000-person sample produced the weighted point estimate that 12 percent of persons listed as registered to vote were contacted by political candidates or activists around the 2012 U.S. general election with an offer to exchange money or gifts for a vote (p=0.018).
I don't believe that this estimate is close to correct, and, given sufficient subgroup analyses, some subgroup analyses would be expected to produce implausible or impossible results, but peer reviewers requesting these data might have produced a more tentative interpretation of the list experiments.
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For Sen 2014, my analysis indicated that the estimates and standard errors for the partisanship variable (coded 1 for nomination by a Republican president) inflate unusually high when that variable is included in models 2, 3, and 4: the coefficient and standard error for the partisanship variable are 0.02 and 0.11 in model 1, but inflate to 15.87 and 535.41 in model 2, 17.90 and 1,455.40 in model 3, and 18.21 and 2,399.54 in model 4.
The Sen 2014 dataset had variables named Bench.Years, Trial.Years, and Private.Practice.Years. The years of experience for these variables overlap (e.g., nominee James Gilstrap was born in 1957 and respectively has 13, 30, and 30 years for these variables); therefore, the variables cannot be summed to construct a variable for total years of legal experience that does not include double- or triple-counting for some cases. Bench.Years correlates with Trial.Years at -0.47 and with Private.Practice.Years at -0.39, but Trial.Years and Private.Practice.Years correlate at 0.93, so I'll include only Bench.Years and Trial.Years, given that Trial.Years appears more relevant for judicial ratings than Private.Practice.Years.
My analysis indicated that women and blacks had a higher Bench.Years average than men and whites: men (4.05 years), women (5.02 years), whites (4.02 years), and blacks (5.88 years). Restricting the analysis to nominees with nonmissing nonzero Bench.Years, men had slightly more experience than women (9.19 years to 8.36 years) and blacks had slightly more experience than whites (9.33 years to 9.13 years).
Adding Bench.Years and Trial.Years to the four Table 3 models did not produce any meaningful difference in results for the African American, Hispanic, and Female variables, but the p-value for the Hispanic main effect fell to 0.065 in model 4 with Bench.Years added.
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I estimated a simplified model with the following variables predicting the dichotomous ABA rating variable for each nominee with available data: African American nominee, Hispanic nominee, female nominee, Republican nominee, nominee age, law clerk experience, law school tier (from 1 to 6), Bench0 and Trial0 (no bench or trial experience respectively), Bench.Years, and Trial.Years. These variables reflect demographics, nominee quality, and nominee experience, with a presumed penalty for nominees who lack bench and/or trial experience. Results are below:
The female coefficient was not statistically significant in the above model (p=0.789), but the coefficient was much closer to statistical significance when adding a control for the year of the nomination:
District.Court.Nomination.Year was positively related to the dichotomous ABA rating variable (r=0.16) and to the female variable (r=0.29), and the ABA rating increased faster over time for women than for men (but not at a statistically-significant level: p=0.167), so I estimated a model that interacted District.Court.Nomination.Year with Female and with the race/ethnicity variables:
The model above provides some evidence for an over-time reduction of the sex gap (p=0.095) and the black/white gap (0.099).
The next model is the second model reported above, but with estimated nominee ideology added, coded with higher values indicating higher levels of conservatism:
So there is at least one reasonable model specification that produces evidence of bias against conservative nominees, at least to the extent that the models provide evidence of bias. After all, ABA ratings are based on three criteria—integrity, professional competence, and judicial temperament—but the models include information for only professional competence, so a sex, race, and ideological gap in the models could indicate bias and/or could indicate a sex, race, and ideological gap in nonbiased ABA evaluations of integrity and/or judicial temperament and/or elements of professional competence that are not reflected in the model measures. Sen addressed the possibility of gaps in these other criteria, starting on page 47 of the article.
For what it's worth, evidence of the bias against conservatives is stronger when excluding the partisanship control:
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The above models for the Sen reanalysis should be interpreted to reflect the fact that there are many reasonable models that could be reported. My assessment from the models that I estimated is that the black/white gap is extremely if not completely robust, the Hispanic/white gap is less robust but still very robust, the female/male gap is less robust but still somewhat robust, and the ideology gap is the least robust of the group.
I'd have liked for the peer reviewers on Sen 2014 to have requested results for the peer reviewers' preferred model, with requested models based only on available data and results reported in at least an online supplement. This would provide reasonable robustness checks for an analysis for which there are many reasonable model specifications. Maybe that happened: the appendix table in the working paper version of Sen 2014 is somewhat different than the published logit regression table. In any event, indicating which models were suggested by peer reviewers might help reduce skepticism about the robustness of reported models, to the extent that models suggested by a peer reviewer have not been volunteered by the researchers.
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NOTES FOR AHLQUIST ET AL. 2014:
1. Subgroup analyses might have been reported for only the smaller 1,000-person sample because the smaller sample was collected first. However, that does not mean that the earlier sample should be the only sample for which subgroup analyses are reported.
2. Non-disaggregated results for the 3,000-person vote buying list experiment and disaggregated results for the 1,000-person vote buying list experiment were reported in a prior version of Ahlquist et al. 2014, which Dr. Ahlquist sent me. However, a reader of Ahlquist et al. 2014 might not be aware of these results, so Ahlquist et al. 2014 might have been improved by including these results.
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NOTES FOR SEN 2014:
1. Ideally, models would include a control for twelve years of experience, given that the ABA Standing Committee on the Federal Judiciary "...believes that a prospective nominee to the federal bench ordinarily should have at least twelve years' experience in the practice of law" (p. 3, here). Sen 2014 reports results for a matching analysis that reflects the 12 years threshold, at least for the Trial.Years variable, but I'm less confident in matching results, given the loss of cases (e.g., from 304 women in Table 1 to 65 women in Table 4) and the loss of information (e.g., cases appear to be matched so that nominees with anywhere from 0 to 12 years on Trial.Years are matched on Trial.Years).
2. I contacted the ABA and sent at least one email to the ABA liaison for the ABA committee that handles ratings for federal judicial nominations, asking whether data could be made available for nominee integrity and judicial temperament, such as a dichotomous indication whether an interviewee had raised concerns about the nominee's integrity or judicial temperament. The ABA Standing Committee on the Federal Judiciary prepares a written statement (e.g., here) that describes such concerns for nominees rated as not qualified, if the ABA committee is asked to testify at a Senate Judiciary Committee hearing for the nominee (see p. 8 here). I have not yet received a reply to my inquiries.
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GENERAL NOTES
1. Data for Ahlquist et al. 2014 are here. Code for my additional analyses is here.
2. Dr. Sen sent me data and R code, but the Sen 2014 data and code do not appear to be online now. Maya Sen's Dataverse is available here. R code for the supplemental Sen models described above is here.
My code contains descriptions of corrections and coding decisions that I made. Data from the Global Terrorism Database is not permitted to be posted online without permission, so the code is the only information about the dataset that I am posting for now. However, the code describes how you can build your own dataset with Stata.
