L.J Zigerell

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On October 27, 2019, U.S. Representative Katie Hill announced her resignation from Congress after her involvement in a sex scandal, claiming that she was leaving "because of a double standard".

There is a recently published article that reports on an experiment that can be used to assess such a double standard among the public, at least with an MTurk sample of over 1,000, with women about 45% of the sample: Barnes et al. 2018 "Sex and corruption: How sexism shapes voters' responses to scandal" in Politics, Groups, and Identities (ungated). Participants in the Barnes et al. 2018 experiment indicated on a four-point scale how likely they would be to vote for a representative in the next election; the experiment manipulated the hypothetical U.S. Representative's sex (man or woman) and the type of scandal that the representative had been involved in (corruption or sex).

Results in Barnes et al. 2018 Figure 1 indicated that, compared to the reported vote likelihoods for the male representative among participants assigned to the male representative involved in the sex scandal, participants assigned to the female representative involved in the sex scandal were not less likely to vote for the female representative.

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The Monkey Cage published a post by Michael Tesler, entitled "Was Rep. Katie Hill held to a higher standard than men in Congress? This research suggests she was". The post did not mention the Barnes et al. 2018 experiment.

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Mischiefs of Faction published a post by Gregory Koger and Jeffrey Lazarus that did mention the Barnes et al. 2018 experiment, but the Koger/Lazarus post did not mention the null finding across the full sample. The post instead mentioned the finding of a correlate of relative disfavoring of the female candidate (links omitted in the quoted passage below):

One answer is that there is sexist double standard for female politicians. One recently published article (ungated) by Tiffany Barnes, Emily Beaulieu, and Gregory Saxton finds that citizens are more likely to disapprove of a sex scandal by a female politician if they a) generally disapprove of women "usurping men's power," or b) see themselves as protectors of women, with protection contingent upon conformity to traditional gender roles. Both dynamics help explain why alleged House-rule-breaker Hill is resigning, while alleged federal-lawbreaker Hunter was reelected in 2018 and shows no interest in resigning.

The Koger/Lazarus post doesn't explain why these correlates are more important than the result among all participants or, for that matter, more important than the dynamic in Barnes et al. 2018 Figure 2 among participants with low hostile sexism scores.

The Koger/Lazarus post suggests that the Barnes et al. 2018 experiment detected a correlation between relative disfavoring of the female politician involved in a sex scandal and participant responses to a benevolent sexism scale (the "b" part of the passage quoted above). I don't think that is a correct description of the results: see Barnes et al. 2018 Table 1, Barnes et al. 2018 Figure 2, and/or the Barnes et al. 2018 statement that "Participants are thus unlikely to differentiate between the sex of the representative when responding to allegations about the representative's involvement in a sex scandal, regardless of the participant's level of benevolent sexism" (p. 13).

For what it's worth, the Barnes et al. 2018 abstract can be read as suggesting that the experiment did detect a bias among persons with high scores on a benevolent sexism scale.

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Barnes et al. 2018 is a recently published large-sample experiment that found that, in terms of vote likelihood, participants assigned to a hypothetical female U.S. Representative involved in a sex scandal treated that female representative remarkably similar to the way in which participants assigned to the hypothetical male representative involved in a sex scandal treated that male representative. This result is not mentioned in two political science blog posts discussing the claim of a gender double standard made by a female U.S. Representative involved in a sex scandal.

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The Peterson et al. 2019 PLOS ONE article "Mitigating gender bias in student evaluations of teaching" reported on an experiment conducted with students across four Spring 2018 courses: an introduction to biology course taught by a female instructor, an introduction to biology course taught by a male instructor, an introduction to American politics course taught by a female instructor, and an introduction to American politics course taught by a male instructor. Students completing evaluations of these teachers were randomly assigned to receive or to not receive a statement about how student evaluations of teachers are often biased against women and instructors of color.

The results clearly indicated that "this intervention improved the SET scores for the female faculty" (p. 8). But that doesn't address the mitigation of bias in the title of the article because, as the article indicates, "It is also possible that the students with female instructors who received the anti-bias language overcompensated their evaluations for the cues they are given" (p. 8).

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For the sake of illustration, let's assume that the two American politics teachers were equal to each other and that the two biology teachers were equal to each other; if so, data from the Peterson et al. 2019 experiment for the v19 overall evaluation of teaching item illustrate how the treatment can both mitigate and exacerbate gender bias in student evaluations.

Here are the mean student ratings on v19 for the American politics instructors:

4.65     Male American politics teacher CONTROL

4.17     Female American politics teacher CONTROL

4.58     Male American politics teacher TREATMENT

4.53     Female American politics teacher TREATMENT

So, for the American politics teachers, the control had a 0.49 disadvantage for the female teacher (p=0.02), but the treatment had only a 0.05 disadvantage for the female teacher (p=0.79). But here are the means for the biology teachers:

3.72     Male biology teacher CONTROL

4.02     Female biology teacher CONTROL

3.73     Male biology teacher TREATMENT

4.44     Female biology teacher TREATMENT

So, for the biology teachers, the control had a 0.29 disadvantage for the male teacher (p=0.25), and the treatment had a 0.71 disadvantage for the male teacher (p<0.01).

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I did not see any data reported on in the PLOS ONE article that can resolve whether the treatment mitigated or exacerbated or did not affect gender bias in the student evaluations of the biology teachers or the American politics teachers. The article's claim about addressing the mitigation of bias is, by my read of the article, rooted in the "decidedly mixed" (p. 2) literature and, in particular, on their reference 5, to MacNell et al. 2015. For example, from Peterson et al. 2019:

These effects [from the PLOS ONE experiment] were substantial in magnitude; as much as half a point on a five-point scale. This effect is comparable with the effect size due to gender bias found in the literature [5].

The MacNell et al. 2015 sample was students evaluating assistant instructors for an online course, with sample sizes for the four cells (actual instructor gender X perceived instructor gender) of 8, 12, 12, and 11. That's the basis for "the effect size due to gender bias found in the literature": a non-trivially underpowered experiment with 43 students across four cells evaluating *assistant* instructors in an *online* course.

It seems reasonable that, before college or university departments use the Peterson et al. 2019 treatment, there should be more research to assess whether the treatment mitigates, exacerbates, or does not change gender bias in student evaluations in situations in which the treatment is used. For what it's worth, the gender difference has been reported to be about 0.13 on a five-point scale based on a million or so Rate My Professors evaluations, using the illustration of 168 additional steps for a 5,117-step day. If the true gender bias in student evaluations were 0.13 units against women, the roughly 0.4-unit or 0.5-unit Peterson et al. 2019 treatment effect would have exacerbated gender bias in student evaluations of teaching.

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NOTES:

1. Thanks to Dave Peterson for comments.

2. From what I can tell, if the treatment truly mitigated gender bias among students evaluating the biology teachers, that would mean that the male biology teacher truly did a worse job teaching than the female biology teacher did.

3. I created a index combining the v19, v20, and v23 items, which respectively are the overall evaluation of teaching, a rating of teaching effectiveness, and the overall evaluation of the course. Here are the mean student ratings on the index for the American politics instructors:

4.56     Male American politics teacher CONTROL

4.21     Female American politics teacher CONTROL

4.36     Male American politics teacher TREATMENT

4.46     Female American politics teacher TREATMENT

So, for the American politics teachers, the control had a 0.35 disadvantage for the female teacher (p=0.07), but the treatment had a 0.10 advantage for the female teacher (p=0.59). But here are the means for the biology teachers:

3.67     Male biology teacher CONTROL

3.90     Female biology teacher CONTROL

3.64     Male biology teacher TREATMENT

4.39     Female biology teacher TREATMENT

So, for the biology teachers, the control had a 0.23 disadvantage for the male teacher (p=0.35), and the treatment had a 0.75 disadvantage for the male teacher (p<0.01).

4. Regarding MacNell et al. 2015 being underpowered, if we use the bottom right cell of MacNell et al. 2015 Table 2 to produce a gender bias estimate of 0.50 standard deviations, the statistical power was 36% for an experiment with 20 student evaluations of instructors who were a woman or a man pretending to be a woman and 23 student evaluations of instructors who were a man or a woman pretending to be a man. If the true effect of gender bias in student evaluations is, say, 0.25 standard deviations, then the MacNell et al. study had a 13% chance of detecting that effect.

R code:

library(pwr)

pwr.t2n.test(n1=20, n2=23, d=0.50, sig.level=0.05)

pwr.t2n.test(n1=20, n2=23, d=0.25, sig.level=0.05)

5. Stata code:

* Overall evaluation of teaching

ttest v19 if bio==0 & treatment==0, by(female)

ttest v19 if bio==0 & treatment==1, by(female)

ttest v19 if bio==1 & treatment==0, by(female)

ttest v19 if bio==1 & treatment==1, by(female)

* Teaching effectiveness:

ttest v20 if bio==0 & treatment==0, by(female)

ttest v20 if bio==0 & treatment==1, by(female)

ttest v20 if bio==1 & treatment==0, by(female)

ttest v20 if bio==1 & treatment==1, by(female)

* Overall evaluation of the course

ttest v23 if bio==0 & treatment==0, by(female)

ttest v23 if bio==0 & treatment==1, by(female)

ttest v23 if bio==1 & treatment==0, by(female)

ttest v23 if bio==1 & treatment==1, by(female)

 

sum v19 v20 v23

pwcorr v19 v20 v23

factor v19 v20 v23, pcf

gen index = (v19 + v20 + v23)/3

sum index v19 v20 v23

 

ttest index if bio==0 & treatment==0, by(female)

ttest index if bio==0 & treatment==1, by(female)

ttest index if bio==1 & treatment==0, by(female)

ttest index if bio==1 & treatment==1, by(female)

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In the 2019 PS: Political Science & Politics article "How Many Citations to Women Is 'Enough'? Estimates of Gender Representation in Political Science", Michelle L. Dion and Sara McLaughlin Mitchell address a question about "the normative standard for the amount women should be cited" (p. 1).

The first proposed Dion and Mitchell 2019 measure is the proportion of female members of the American Political Science Association (APSA) by section and primary field, using data from 2018. According to Dion and Mitchell 2019: "When political scientists compose course syllabi, graduate reading lists, and research bibliographies, these membership data provide guidance about the minimum representation of scholarship by women that should be included to be representative by gender" (p. 3).

But is APSA section membership in 2018 a reasonable benchmark for gender representation in course syllabi that include readings from throughout history?

Hardt et al. 2019 reported on data for readings assigned in the training of political science graduate students. Below are percentages of graduate student readings in these data that had a female first author:

Time PeriodFemale First Author %
Before 19703.5%
1970 to 19796.7%
1980 to 198911.3%
1990 to 199915.7%
2000 to 2009 21.0%
2010 to 201824.6%

So the pattern is increasing representation of women over time. If this pattern reflects increasing representation of women over time in APSA section membership or increasing representation of women among the set of researchers whose research interests include the topic of a particular section, then APSA section membership data from 2018 will overstate the percentage of women needed to ensure fair gender representation on syllabi or research bibliographies. For illustrative purposes, if a section had 20% women across the 1990s, 30% women across the 2000s, and 40% women across the 2010s, a fair "section membership" benchmark for gender representation on syllabi would not be 40%; rather, a fair "section membership" benchmark for gender representation on syllabi would be something like 20% women for syllabi readings across the 1990s, 30% women for syllabi readings across the 2000s, and 40% women for syllabi readings across the 2010s.

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Dion and Mitchell 2019 propose another measure that is biased in the same direction and for the same reason: gender distribution of authors by journal from 2007 to 2016 inclusive for available years.

About 68% of readings in the Hardt et al. 2019 graduate training readings data were published prior to 2007: 15% of these pre-2007 readings had a first female author, but 24% of the 2007-2016 readings in the data had a first female author.

Older readings are included on Hardt et al. 2019 readings with decent frequency: 42% of readings that had the gender of the first author coded were published before 2000. However, the Dion and Mitchell 2019 measure of journal representation from 2007 to 2016 ignores these older readings, which produces a biased measure favoring women if fair representation means representation that matches the representation in the relevant pool of syllabi-worthy journal articles.

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In a sense, this bias in the Dion and Mitchell 2019 measures might not matter much if the measures are used in the biased manner that Dion and Mitchell 2019 proposed (p. 6):

We remedy this gap by explicitly providing conservative estimates of gender diversity based on organization membership and journal article authorship for evaluating gender representation. Instructors, researchers, and editors who want to ensure that references are representative can reference these as floors (rather than ceilings) for minimally representative citations.

The Dion and Mitchell 2019 suggestion above is that instructors, researchers, and editors who want to ensure that references are representative use a conservative estimate as a floor. Both the conservative nature of the estimate and its use as a floor would produce a bias favoring women, so I'm not sure how that is helpful for instructors, researchers, and editors who want to ensure that references are representative.

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NOTE:

1. Stata code for the analysis of the Hardt et al. 2019 data:

tab female1 if year<1970

tab female1 if year>=1970 & year<1980

tab female1 if year>=1980 & year<1990

tab female1 if year>=1990 & year<2000

tab female1 if year>=2000 & year<2010

tab female1 if year>=2010 & year<2019

 

tab female1

tab female1 if year<2000

di 36791/87398

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"The Gender Readings Gap in Political Science Graduate Training" by Heidi Hardt, Amy Erica Smith, Hannah June Kim, and Philippe Meister was recently published in the Journal of Politics and featured in a Monkey Cage blog post. The Kim Yi Dionne header for the Monkey Cage post indicated that:

Throughout academia, including in political science, women haven't achieved parity with men. As this series explores, implicit bias holds women back at every stage, from the readings professors assign to the student evaluations that influence promotions and pay, from journal publications to book awards.

The abstract to the JOP article indicates that "Introducing a unique data set of 88,673 citations from 905 PhD syllabi and reading lists, we find that only 19% of assigned readings have female first authors". This 19% for assigned readings is lower than the 21.5% of publications in the top three political science journals between 2000 and 2015 (bottom of page 2 of the JOP article). However, the 19% is based on assigned readings published at any time in history, including authors such as Plato and Sun Tzu. My analysis of the data for the article indicated that 22% of assigned readings have female first authors when the assigned readings are limited to assigned readings published between 2000 and 2015 inclusive. The top three publications benchmark therefore produces an estimate of the gender readings gap in political science graduate training for 2000 to 2015 publications that is less than one percent and trivially advantages women.

Figure 1 in the Hardt et al. JOP article reports percentages by subfield, with benchmarks for published top works, which I think are articles in top 10 journals; the first and third numeric columns in the table below are data reported in Figure 1. Using the benchmark for published top works, my analysis limiting the assigned readings to assigned readings published between 2000 to 2015 inclusive (the middle numeric column) produced a difference greater than 1% that disadvantaged female first authors for only one of the five subfields with benchmark data (comparative politics):

Topic% Female
1st Author
Readings
(All Time)		% Female
1st Author
Readings
(2000-2015)		% Female
1st Author
Top Pubs
(2000-2015)
Methodology 11.5713.6411.36
Political Economy 16.7518.03 NA
American 15.6618.46 19.07
Comparative 20.5523.26 28.76
IR 19.9623.41 22.42
Theory 25.0531.58 29.39

For an example topic most relevant to my work, the Hardt et al. Figure 1 gender gap for American politics is 3.41 percentage points (15.66 compared to 19.07), but falls to 0.61 percentage points (18.46 compared to 19.07) when the time frame of the assigned readings is set to the 2000-2015 time frame of the top publications benchmark. Invocation of an implicit bias that holds back women might be premature if the data indicate a gap of less than 1 percentage point in an analysis that does not include relevant control variables such as any gender gap in how "syllabus-worthy" publications are within the set of top publications. The 5.50 percentage point gender gap for comparative politics might be large enough to consider implicit bias in that subfield, but that's a localized concern.

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NOTES

1. [*] The post title alludes to this tweet.

2. The only first authors coded female before 1776 are Titus Livy and Sun Tzu (tab surname1 if female1==1 & year<1776).

3. Code below:

* Insert this command into the Hardt et al. do file after Line 11 ("use 'Hardt et al. JOP_Replication data.dta', clear"):
keep if year>=2000 & year<=2015

* Insert these commands into the Hardt et al. do file after new Line 124 ("tab1 gender1 if gender1 < 3 [aweight=wt] // THE TOPLINE RESULTS WE REPORT EXCLUDE THOSE 304 OBSERVATIONS"):
tab1 gender1 if gender1 < 3 [aweight=wt] // This should report 21.86%
tab1 gender1 if gender1 < 3 // This should report 22.20%

* Insert this command into the Hardt et al. do file before new Line 184 ("restore"):
tab topic mn

* Run the Hardt+et+al.+JOP_Replication+code-1.do file until and including new Line 126 ("tab1 gender1 if gender1 < 3 // This should report 22.20%"). These data indicate that, of first authors coded male or female, about 22% were female.

* Run new Line 127 to new Line 184 ("tab topic mn"). Line 184 should output data for the middle column in the table in this post. See the "benchmark_teelethelen" lines for data for the right column in the table.

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The Enders 2019 Political Behavior article "A Matter of Principle? On the Relationship Between Racial Resentment and Ideology" interprets its results as "providing disconfirmatory evidence for the principled conservatism thesis" (p. 3 of the pdf). This principled conservatism thesis "asserts that adherence to conservative ideological principles causes what are interpret[ed] as more resentful responses to the individual racial resentment items, especially those that deal with subjects like hard work and struggle" (p. 5 of the pdf).

So how could we test whether adherence to conservative principles causes what are interpreted as resentful responses to racial resentment items? I think that a conservative principle informing a "strongly agree" response to the racial resentment item that "Irish, Italians, Jewish, and many other minorities overcame prejudice and worked their way up. Blacks should do the same without any special favors" might be an individualism that opposes special favors to reduce inequalities of outcome, so that, if a White participant strongly agreed that Blacks should work their way up without special favors, then—to be principled—that White participant should also strongly agree that poor Whites should work their way up without special favors.

Thus, testing the principled conservatism thesis could involve asking participants the same racial resentment items with a variation in targets or a variation to a domain in which Blacks tend to outperform Whites. If there is a concern about social desirability affecting responses when participants are asked the same item with a variation in target or domain, the items could be experimentally manipulated and responses compared at an aggregate level. This type of analysis involved manipulating the target of racial resentment items to be Blacks or another group has recently been conducted and reported on in a paper by Carney and Enos, but this paper is not cited in Enders 2019, and I would have hoped that the peer reviewers would have requested or required a discussion of information in that paper that relates to the principled nature of conservatives' responses to racial resentment items.

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Instead of manipulating the target of racial resentment items, Enders 2019 tested the principled conservatism thesis with an analysis that assessed how responses to racial resentment items associated with attitudes about limited government and with preferences about federal spending on, among other things, public schools, child care, and the environment. From what I can tell, Enders 2019 assessed the extent to which participants are principled in a test in which principled conservative responses are only those responses in which responses expected from a conservative to racial resentment items match responses expected from a conservative to items measuring preferences about federal spending or match responses expected from a conservative to items measuring attitudes about limited government. As I think Enders 2019 suggests, this is a consistency across domains at the level of "conservatism" and is not a consistency across targets within the domain of the racial resentment items: "If I find that principled conservatism does not account for a majority of the variance in the racial resentment scale under these conditions, then I will have reasonably robust evidence against the principled conservatism thesis" (p. 7 of the pdf).

But I don't think that the level of "conservatism" is the correct level for assessing whether perceived racially prejudiced responses to racial resentment items reflect "adherence to (conservative) ideological principles" (p. 2 of the pdf). Enders 2019 indicates that "Critics argue that racially prejudiced responses to the items that compose the racial resentment scale are observationally equivalent to the responses that conservatives would provide" (abstract). However, at least for me, my criticism of the racial resentment items as producing unjustified inferences of racial bias is not limited to inferences about responses from self-identified conservatives: "This statement [about whether, if blacks would only try harder, they could be just as well off as whites] cannot be used to identify racial bias because a person who agreed with the statement might also agree that poor whites who try harder could be just as well off as middle-class whites" (p. 522 of this article). I don't perceive any reason why a person who supports increased federal spending on the public schools, child care, and the environment cannot also have a principled objection to special favors to reduce inequalities of outcome.

And even if "conservatism" were the correct level of analysis, I don't think that the Enders 2019 operationalizations of principled conservatism—as a preference for limited government and as a preference for decreased federal spending—are valid because, as far as I can tell, these operationalizations of principled conservatism are identical to principled libertarianism.

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Enders 2019 asks "Why else would attitudes about racial issues be distinct from attitudes about other policy areas, if not for the looming presence and substantive impact of racial prejudice?" (p. 21 of the pdf). I think the correct response is that the principles that inform attitudes about these other policy areas are distinct from the principles that inform attitudes about issues in the racial resentment items, to the extent that these attitudes even involve principles.

I don't think that the principle that "the less government, the better" produces conservative policy preferences about federal spending on national defense or domestic law enforcement, and I don't see a reason to assign to racial prejudice an inconsistency between support for increased federal spending in these domains and agreement that "the less government, the better". And I don't perceive a reason for racial prejudice to be assigned responsibility for a supposed inconsistency between responses to the claim that "the less government, the better" and responses to the racial resentment statements that "Generations of slavery and discrimination have created conditions that make it difficult for blacks to work their way out of the lower class" or that "...if blacks would only try harder they could be just as well off as whites", because, as far as I can tell, there is no inconsistency in which a preference for limited government compels particular responses to these racial resentment items.

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NOTES

1. Enders 2019 noted that: "More recently, DeSante (2013), utilizing an experimental research design, found that the most racially resentful whites, as opposed to less racially resentful whites, were more likely to allocate funds to offset the state budget deficit than allocated such funds to a black welfare applicant. This demonstrates a racial component of racial resentment, even accounting for principled conservatism" (p. 6). But I don't think that this indicates a demonstration of a racial component of racial resentment, because there is no indication whether the preference for allocating funds to offset the state budget deficit instead of allocating funds to welfare recipients occurred regardless of the race of the welfare recipients. My re-analysis of data for DeSante 2013 indicated that "...when comparing conditions with two White applicants and conditions with two Black applicants, there is insufficient evidence to support the inference of a difference in the effect of racial resentment on allocations to offset the state budget deficit" (pp. 5-6).

2. I sent the above comments to Adam Enders in case he wanted to comment.

3. After I sent the above comments, I saw this Robert VerBruggen article on the racial resentment measure. I don't remember seeing that article before, but it has a lot of good points and ideas.

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Ethnic and Racial Studies recently published "Revisiting the Asian Second-Generation Advantage", by Van C. Tran, Jennifer Lee, and Tiffany J. Huang, which I will refer to below as Tran et al. 2019. Ethnic and Racial Studies has also published my comment, and a Tran et al. response. I'll reply to their response below...

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Here are three findings from Tran et al. 2019 important for the discussion below:

1. Table 2 indicates that U.S. second-generation Chinese, Indians, Filipinos, Vietnamese, and Koreans are more likely than native Whites to hold a college degree.

2. Table 2 indicates that U.S. second-generation Chinese, Indians, Filipinos, Vietnamese, and Koreans are more likely than native Whites to report being in a managerial or professional position.

3. Table 4 Model 1 does not provide evidence at p<.05 that U.S. second-generation Chinese, Indians, Filipinos, Vietnamese, or Koreans are less likely than native Whites to report being in a managerial or professional position, controlling for age, age squared, gender, region, survey year, and educational attainment.

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Below, I'll respond to what I think are the two key errors in the Tran et al. reply.

1.

From the first paragraph of the Tran et al. reply:

Given this Asian educational advantage, we hypothesized that second-generation Asians would also report an occupational advantage over whites, measured by their likelihood to be in a professional or managerial occupation.

It makes sense to expect the second-generation Asian educational advantage to translate to a second-generation Asian occupational advantage. And that is what Tran et al. 2019 Table 2 reported: 45% of native Whites reported being in a professional or managerial position, compared to 73% of second-generation Chinese, 79% of second-generation Indians, 52% of second-generation Filipinos, 53% of second-generation Vietnamese, and 60% of second-generation Koreans. Tran et al. 2019 even commented on this occupational advantage: "Yet despite variation among the second-generation Asian groups, each exhibits higher rates of professional attainment than native-born whites and blacks" (p. 2260). But here is the Tran et al. reply following immediately from the prior block quote:

Contrary to our expectation, however, we found that, with the exception of second-generation Chinese, the other four Asian ethnic groups in our study – Indians, Filipinos, Vietnamese and Koreans – report no such advantage in professional or managerial attainment over whites (Tran, Lee, and Huang 2019: Table 4, Model 1). More precisely, the four Asian ethnic groups are only as likely as whites to be in a managerial or professional occupation, controlling for age, the quadratic term of age, gender, education, and region of the country.

The finding contrary to the Tran et al. expectation (from Tran et al. 2019 Table 4 Model 1) was not from what the other four Asian ethnic groups reported but was from a model predicting what was reported controlling for educational attainment and other factors. Tran et al. therefore expected an educational advantage to cause an occupational advantage that remained after controlling for the educational advantage. The Tran et al. reply states this expressly (p. 2274, emphasis in the original):

Because second-generation Asians hold such a significant educational advantage over whites, we had expected that second-generation Asians would also report an occupational advantage over whites, even after controlling for respondents' education.

Properly controlling for a factor means to eliminate the factor as an explanation. For instance, men having a higher average annual salary than women have might be due to men working more hours on average per year than women work. Comparing the average hourly salary for men to the average hourly salary for women controls for hours worked and eliminates the explanation that the any residual gender difference in average annual salary is due to a gender difference in hours worked per year. The logic of the Tran et al. expectation applied to the gender salary gap would produce expectations such as: Because men work more hours on average than women work, we expected that men would have a higher average annual salary than women have, even after controlling for the fact that men work more hours on average than women work.

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2.

From the Tran et al. reply (p. 2274, emphasis added):

Given that second-generation Asians are more likely to have graduated from college than whites, we hypothesized that they would evince a greater likelihood of attaining a professional or managerial position than whites, as is the case for the Chinese. Instead, we found that second-generation Chinese are the exception, rather than the norm, among second-generation Asians. Hence, we concluded that second-generation Asians are over-credentialed in education in order to achieve parity with whites in the labor market.

I think that there are two ways that labor market parity can be properly conceptualized in the context of this analysis. The first is for labor market outcomes for second-generation Asians to equal labor market outcomes for native Whites, without controlling for any factors; the second is for labor market outcomes for second-generation Asians to equal to labor market outcomes for native Whites, controlling for particular factors. Tran et al. appear to be using the "controlling for" conceptualization of parity. Now to the bolded statement...

Ignoring the advantage for second-generation Chinese, and interpreting as parity insufficient evidence of a difference in the presence of statistical control, Tran et al. 2019 provided evidence that second-generation Asians are over-credentialed in education relative to native Whites *and* that second-generation Asians have achieved labor market parity with native Whites. But I do not see anything in the Tran et al. 2019 analysis or reply that indicates that second-generation Asians need to be over-credentialed in education "in order to achieve" this labor market parity with native Whites.

Returning to the gender salary gap example, imagine that men have a higher average annual salary than women have, but that this salary advantage disappears when controlling for hours worked, so that men have salary parity with women; nothing in that analysis indicates that men need to overwork in order to achieve salary parity with women.

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So I think that the two key errors in the Tran et al. reply are:

1. The expectation that the effect of education will remain after controlling for education.

2. The inference from their reported results that second-generation Asians need to be over-credentialed in order to achieve labor market parity with natives Whites.

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Racial resentment and symbolic racism are terms used to describe a set of measures used in racial attitudes research, including statements such as "Irish, Italians, Jewish and many other minorities overcame prejudice and worked their way up. Blacks should do the same without any special favors". This item and at least some of the other racial resentment items confound racism and nonracial ideology; in this "special favors" item, an individualist who believes that everyone should work their way up without special favors would select a response on the same side of the scale as an antiBlack racist who believes that only Blacks should work their way up without special favors.

Feldman and Huddy (2005) concluded that "racial resentment is an inadequate measure of prejudice because it confounds prejudice and political ideology" (p. 181), which is consistent with factor analysis of racial resentment items (Sears and Henry 2003: 271). Some research has addressed this confounding with what Feldman and Huddy (2005: 171) call the multivariate approach, in which the analysis includes statistical control for related ideological values. The logic of this multivariate approach is that racial resentment confounds ideology and antiBlack animus so that controlling for ideology should permit the residual association of racial resentment to be interpreted as the association due to antiBlack animus.

The analysis below approaches from the opposite direction: racial resentment confounds ideology and antiBlack animus so that controlling for antiBlack animus should permit the residual association of racial resentment to be interpreted as the association due to ideology. Moreover, if controls for ideology and for antiBlack animus are both included, then the association of racial resentment with an outcome variable should be zero. But this is not even close to being true, as illustrated below in a figure that reports the association of racial resentment with racial or possibly racialized outcome variables, using different sets of statistical control.

In each panel above, the top estimate indicates the association of racial resentment with the outcome variable controlling for only demographics. The second and third estimates respectively indicate the association of racial resentment with outcome variables after controls for demographics and racial attitudes and after controls for demographics and ideology. The fourth and fifth estimates respectively indicate the association of racial resentment with outcome variables after controls for demographics, ideology, and racial attitudes and after controls for demographics, ideology, and racial animus. The key comparison is between the third estimate and the fourth and fifth estimates: the measures of racial attitudes and racial animus had relatively little impact on the racial resentment estimate once the controls for ideology were included in the analysis. For example, in the top left panel, the coefficient for racial resentment was 0.51 controlling for demographics and ideology, was 0.48 controlling for demographics, ideology, and racial attitudes, and was 0.52 controlling for demographics, ideology, and racial animus. In a common racial resentment association analysis, the 0.51 coefficient controlling for demographics and ideology would be assigned to antiBlack animus, but the addition of seven racial attitudes controls accounted for only 0.03 of the 0.51 coefficient and the inclusion of six antiBlack animus controls did not even reduce the 0.51 coefficient. (see the Notes below for more description on the measurements).

A reasonable critique of the above analysis is that racial resentment taps a form of antiBlack racism that is not captured or is not well captured in the included measures of racial attitudes and racial animus. But, from what I can tell, that is an equally valid criticism of analyses that control for ideology: the nonracial ideology captured in racial resentment measures is not captured or not well captured in the included measures of ideology.

NOTES

1. The sample for the analysis was the 3,261 non-Hispanic Whites who completed face-to-face or online the pre- and post-election surveys, conducted between 8 September 2012 and 24 January 2013, and who were not listwise deleted from a model due to missing data for a variable. Each variable in the analysis was coded to range from 0 to 1. Linear regressions without weights were used to predict values of the outcome variables.

The racial resentment measure summed responses to the four ANES 2012 racial resentment items. Models included demographic controls for participant sex, marital status, age, education level, and household family income. Ideological controls were self-reported partisanship, self-reported ideology, an item about guaranteed jobs, an index of attitudes about the role of government, a moral traditionalism index, an authoritarianism index, and an egalitarianism index.

One set of models included seven controls for racial attitudes: a feeling thermometer difference of ratings of Whites and ratings of Blacks, a rating difference for Blacks and for Whites in general on a laziness stereotype scale, a rating difference for Whites and for Blacks in general on an intelligence stereotype scale, an item rating admiration of Blacks, an item rating sympathy for Blacks, an item measuring the perceived political influence of Blacks relative to Whites, and a difference in ratings of the level of discrimination in the United States today against Whites and against Blacks. Another set of models included six dichotomous controls that attempted to isolate antiBlack animus: a more than 20-point feeling thermometer rating difference in which Whites were rated higher than Blacks and with Whites rated at or above 50 and Blacks rated below 50, a rating of Blacks as lazier in general than Whites, a rating of Whites as more intelligent in general than Blacks, an indication of never feeling sympathy for Blacks, an indication that Blacks have too much influence in American politics but Whites don't, and an indication that there is no discrimination against Blacks in the United States today but that there is discrimination against Whites in the United States today.

2. Code for the analysis is here.

3. Results for the 2016 ANES are below:

4. Code for the 2016 ANES analysis is here.

5. Citations:

American National Election Studies (ANES). 2016. ANES 2012 Time Series Study. Ann Arbor, MI: Inter-university Consortium for Political and Social Research [distributor], 2016-05-17. https://doi.org/10.3886/ICPSR35157.v1.

American National Election Studies, University of Michigan, and Stanford University. 2017. ANES 2016 Time Series Study. Ann Arbor, MI: Inter-university Consortium for Political and Social Research [distributor], 2017-09-19. https://doi.org/10.3886/ICPSR36824.v2.

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