THE EFFECTS OF DEMOGRAPHIC MISMATCH - IA de Investigación especializada en el MIT

LOS EFECTOS DEL DESACORDAMIENTO DEMOGRÁFICO

IN AN ELITE PROFESSIONAL SCHOOL

SETTING

Chris Birdsall

School of Public Service

Boise State University

Boise, ID 83725

chrisbirdsall@boisestate.edu

Seth Gershenson

(Autor correspondiente)

American University and IZA

Washington, corriente continua 20016

gershens@american.edu

Raymond Zuniga

Center for Public

Administration and Policy

Virginia Tech University

Blacksburg, Virginia 24061

raymondz@vt.edu

Abstracto
Ten years of administrative data from a diverse, privado, top-100
law school are used to examine the ways in which female and non-
white students beneﬁt from exposure to demographically sim-
ilar faculty in ﬁrst-year, required law courses. Arguably, causal
impacts of exposure to same-sex and same-race instructors on
course-speciﬁc outcomes such as course grades are identiﬁed by
leveraging quasi-random classroom assignments and a two-way
(student and classroom) ﬁxed eﬀects strategy. Having an other-
sex instructor reduces the likelihood of receiving a good grade
(A or A–) por 1 percentage point (3 por ciento) and having an other-
race instructor reduces the likelihood of receiving a good grade by
3 puntos de porcentaje (10 por ciento). The eﬀects of student–instructor
demographic mismatch are particularly salient for nonwhite and
female students. These results provide novel evidence of the per-
vasiveness of demographic-match eﬀects and of the graduate
school education production function.

https://doi.org/10.1162/edfp_a_00280

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457

Effects of Demographic Mismatch

INTRODUCCIÓN

1 .
A robust literature in the economics of education documents wide-ranging impacts
of student–teacher demographic match on both students and teachers. In K–12 class-
rooms, assignment to an other-race or other-sex teacher has been shown to harm
Logro estudiantil (Dee 2004, 2007) and increase student absences (Holt and Ger-
shenson 2019).1 Similarmente, racial mismatch lowers teachers’ perceptions of student
comportamiento (Dee 2005) and their expectations for students’ educational attainment (Ger-
shenson, Holt, and Papageorge 2016). The impact of faculty representation has also
been studied in the postsecondary context, particularly among ﬁrst-year undergradu-
ates (Bettinger and Long 2005; Hoﬀmann and Oreopoulos 2009; Carrell, Página, y
Oeste 2010; Fairlie, Hoﬀmann, and Oreopoulos 2014). These studies typically ﬁnd mod-
est eﬀects of having a same-sex or same-race instructor on course grades, the likelihood
of dropping a class, and choice of major. Lusher, Campbell, and Carrell (2015) show sim-
ilar eﬀects of having a same-race teaching assistant (recitation section leader) on course
grades and oﬃce-hour and course attendance. Even in online environments, instruc-
tores, particularly white instructors, are more likely to respond to white male students’
comments (Baker et al. 2018).

Sin embargo, the extant literature has yet to investigate the extent of student–instructor
demographic mismatch eﬀects in the postgraduate or professional school setting.2 The
current study contributes to this gap in the literature by showing that the consequences
of student–instructor demographic mismatch are just as pronounced in an elite, pro-
fessional school setting as they are in K–12, community college, and ﬁrst-year under-
graduate classrooms. Doing so is important for at least three reasons.

Primero, this study enhances our understanding of the production of graduate degrees.
Remarkably little is known about the nature of the law school education production
función, or that for graduate school more generally.3 This is troubling, as graduate
students comprise a nontrivial segment of the U.S. postsecondary student population:
acerca de 15 percent of postsecondary students are graduate students and about 40 por ciento
of outstanding student loan debt was accumulated to ﬁnance graduate degrees (Delisle
2014). Graduate degrees themselves facilitate entrance into many high-status and high-
paying professions central to the modern economy. The legal profession is one promi-
nent example: Nearly all states require that lawyers hold a Juris Doctor (JD) from an
American Bar Association (ABA)-accredited law school, lawyers constitute about 1 por-
cent of the U.S. labor force, and law ﬁrm revenues constitute about 1 percent of U.S.
gross domestic product (Azmat and Ferrer 2017). The current study provides evidence
on some of the educational inputs and environments that aﬀect law school students’
logro, skill development, choice of specialization, and persistence.

1. Mismatch is not universally harmful, sin embargo, as Antecol, Eren, and Ozbeklik (2015) ﬁnd that less-prepared

female math teachers reduce female students’ achievement but have no such eﬀect on male students.

2. There is a litany of qualitative and anecdotal evidence of such demographic biases in legal education (Banks
1988; Guinier et al. 1994; Darling-Hammong and Holmquist 2015), but to our knowledge there is no credi-
bly identiﬁed, quantitative evidence on the impact of law student–instructor demographic match on student
resultados.

3. Exceptions include recent natural experiments involving ﬁrst-year law students at Stanford, who were randomly
assigned to small classes (Ho and Kelman 2014) and at Minnesota, where students were randomly assigned to
receive individualized feedback (Schwarcz and Farganis 2017). Neumark and Gardecki (1998) ﬁnd that increas-
ing female faculty members in economics departments improved time to completion and completion rates for
female graduate students.

458

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Chris Birdsall, Seth Gershenson, and Raymond Zuniga

Segundo, the current study sheds light on the role that institutions play in per-
petuating demographic wage, skill, and partnership gaps in the legal profession. Para
ejemplo, female lawyers earn lower salaries and are less likely to be promoted to part-
ner than their male counterparts, even after conditioning on basic employee and ﬁrm
características (Wood, Corcoran, and Courant 1993; Dinovitzer, reichman, and Sterling
2009; Azmat and Ferrer 2017).4Azmat and Ferrer (2017) show that performance gaps
explain much of the previously unexplained sex gap in lawyers’ earnings, though the
exact sources of gaps in performance and specialization among practicing lawyers re-
main unclear. Law school environments and mentoring practices might contribute to
this divergence in post–law school productivity, even when male and female students
enter law school with similar skills (Bertrand 2011; Ho and Kelman 2014). We test this
hypothesis by examining whether the demographic match between law students and
instructors aﬀects student outcomes. Doing so will inform law school policy and prac-
tice by identifying the malleable factors that inﬂuence the success of underrepresented
graduate school students and our understanding of the importance that faculty play in
the production of graduate education more generally. En efecto, law schools are repre-
sentative of a broad class of professional graduate schools and programs from which
professional service providers are recruited directly into the labor market (p.ej., busi-
ness, engineering; Oyer and Schaefer 2015).

Finalmente, there are social consequences of demographic gaps in the receipt of law
degrees and in the career paths of law school graduates (Holder 2001). Por ejemplo,
the underrepresentation of racial and ethnic minorities in the U.S. judiciary likely con-
tributes to documented demographic disparities in sentencing (Mustard 2001). En efecto,
implicit association tests show that white judges often hold implicit (unconscious)
biases against nonwhite defendants (Rachlinski and Johnson 2009). In the ﬁeld,
emotional shocks associated with the outcomes of football games have been shown to
increase the sentences assigned by judges, particularly for black defendants (Eren and
Mocan 2016). And regarding the demographic pay gaps discussed above, a lack of rep-
resentation among law school faculty and/or how law school faculty interact with and
mentor women and students of color can cause sorting into specializations and other
behavioral responses that aﬀect prestige, pay, and upward mobility. Por último, prejuicios
against women and people of color can produce self-fulﬁlling prophecies in which
members of stereotyped groups ultimately conform to what were initially incorrect be-
liefs (Steele 1997; Loury 2009; Papageorge, Gershenson, and Kang 2016). Institutional
factores, such as faculty composition, can therefore perpetuate the underrepresentation
of certain demographic groups in the legal profession (Wilkins and Gulati 1996).

Específicamente, we use rich administrative data from a top-100 law school in which ﬁrst-
year students are at least quasi-randomly assigned to course sections in conjunction
with an array of arguably causal ﬁxed-eﬀects identiﬁcation strategies to show that hav-
ing a demographically mismatched ﬁrst-year law instructor signiﬁcantly reduces the
probability of receiving a “good grade” (A/A–) in the course. En tono rimbombante, we ﬁnd no
such eﬀects on the likelihood of dropping a course, which suggests the course-grade

4. This is consistent with “glass ceilings” and pay gaps in top management positions (Bertrand and Hallock 2001),

as well as in the labor force more generally (Altonji and Blank 1999).

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459

Effects of Demographic Mismatch

analyses are not biased by missing grades for courses that students dropped, and is
likely due to the relatively rigid ﬁrst-year requirements for progressing in the program.
Other-race eﬀects tend to be larger in magnitude than other-sex eﬀects, particularly
among nonwhite and nonwhite female students, though both are statistically and
economically signiﬁcant. There are cumulative eﬀects of exposure to demographically
mismatched ﬁrst-semester instructors on second-semester course grades in two-
course sequences, suggesting that such eﬀects persist, though we ﬁnd no evidence of
contemporaneous spillover eﬀects of exposure to demographically matched faculty on
performance in unrelated courses.5 Classroom environments such as class size and
class composition moderate the impact of student–instructor demographic mismatch
in ways that hint at the mechanisms through which such eﬀects operate. That we ﬁnd
such eﬀects in an elite professional school setting suggests that the phenomena of im-
plicit bias, stereotype threat, and role-model eﬀects are broad, societal phenomena that
permeate beyond relatively vulnerable populations of schoolchildren and community
college students, and have implications for all social interactions, even those involving
high-achieving individuals. En efecto, a recent ﬁeld experiment ﬁnds that black men
are more likely to select preventive services and talk to the doctor about their health
problems when the doctor is of the same race (Alsan, Garrick, and Graziani 2018).

The paper proceeds as follows: Sección 2 describes the administrative data and in-
stitutional details. Sección 3 introduces the identiﬁcation strategy. Sección 4 presents
the results. Sección 5 concluye.

2 . DATA A N D I N S T I T U T I O N A L D E TA I L S
This section describes the administrative data analyzed in the current study. We ﬁrst
describe the institutional context and the formation of the analytic sample, then we
summarize the analytic sample.

Administrative Data
All analyses use longitudinal administrative data from a private, top-100 law school
(LS) located in a major urban center. The LS enrolls approximately 1,000 students per
año, on average, and employs approximately 200 full-time and part-time faculty. Es
one of the most demographically and geographically diverse top-ranked law schools.
The most recent U.S. Noticias & World Report (A NOSOTROS. Noticias) rankings rank the LS in the
arriba 100.6 Demographically, LS ranks in the top 50 ABA-approved law schools for both
racial/ethnic minority and female JD-student enrollment.7 Thus, although LS is one of
the more demographically diverse law schools in the United States, it is not an outlier
and is comparable to other highly ranked, national law schools in this regard.

The main analytic sample is restricted to students’ ﬁrst-year required courses for
tres razones. Primero, entering students take the same set of courses during their ﬁrst
two semesters of law school. Most courses are semester-speciﬁc, meaning that course
A is usually taken in the fall semester and course B is taken in the spring semester.

5. See Appendix table A.1.
6. See http://grad-schools.usnews.rankingsandreviews.com/best-graduate-schools/top-law-schools/law-rankin

gs/page+4.

7. Rankings calculated as average percent enrollment from 2009 a 2013 using data obtained from the American

Bar Association (www.americanbar.org/groups/legal_education/resources/statistics.html).

460

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Chris Birdsall, Seth Gershenson, and Raymond Zuniga

Segundo, the majority of ﬁrst-year courses are assessed using a blind grading system.8
This speaks to the mechanisms through which observed mismatch eﬀects operate, como
it precludes explicit grading biases of the type documented by Lavy (2008) de ser
the primary mechanism. Finalmente, at least in some years, student assignments to speciﬁc
class sections, made by LS advisors and administrators, were quasi-random.9 Similarly,
the courses taken in each semester of the ﬁrst year are randomly assigned by school
administradores. About three to four sections of each course are oﬀered in a semester in
which the course is oﬀered, with the exception of one writing course that has smaller
class sizes and thus has about twenty-ﬁve sections per semester. We verify, and exploit,
this random assignment in the empirical analysis.

The administrative data include detailed information on course-speciﬁc outcomes,
such as grades, dropout behavior, and taking an elective course in the same concentra-
tion in the second year or beyond, as well as student-level outcomes such as persistence,
graduation, and engagement with the LS’s Law Journals, for every student who entered
the JD program between fall 2000 and fall 2011. Además, we observe student de-
mographic characteristics, such as sex, edad, and race/ethnicity, as well as Law School
Admission Test (LSAT) puntuaciones, undergraduate grade point average (GPA), and home
ZIP Code.10 We use home ZIP Codes to construct measures of distance from LS and to
collect the median income and fraction of adults who have a college degree in each ZIP
Code from the 2000 y 2010 A NOSOTROS. censuses, which proxy for students’ socioeconomic
estado. Administrative data on instructors include rank (p.ej., tenure line, tenured, anuncio-
junct) and years at LS. Demographic information (es decir., race/ethnicity and sex) and rank
of faculty members’ JD-granting institutions were determined by reviewing public re-
sumes, curriculum vitae, and Web sites.11

Sample and Summary Statistics
Our aim is to estimate the impact of student–instructor demographic match in ﬁrst-year
required courses. The primary unit of analysis is therefore the student-course level.
There are ten required courses in the ﬁrst year, which cover subjects such as proce-
dure, constitutional law, and property law. The main analytic sample includes 36,560
student-course observations from more than 1,000 unique course sections.12 Panel A
de mesa 1 summarizes the student-course data, separately by students’ race and sex. On
promedio, white students have higher ﬁrst-year course grades than nonwhite students.
There is no appreciable sex gap in ﬁrst-year course grades. Dropping ﬁrst-year required
courses is exceedingly rare, likely because they are required and students are gener-
ally forbidden from switching sections. White students and nonwhite students have

8. Desafortunadamente, the data do not identify which, if any, courses were subject to non-blind grading. Another com-
plication is that students may challenge their grades in some circumstances, at which point the grading is no
longer blind, and more advantaged students may feel more conﬁdent in challenging grades. Desafortunadamente, nosotros
do not observe which grades were challenged.

9. The assignment protocol changed about midway through the period of study, though both processes were ar-
guably conditionally random. dicho eso, we do not assume or rely on random assignment in the main analysis
and instead rely on a quasi-experimental two-way ﬁxed-eﬀects identiﬁcation strategy. Sin embargo, a series of bal-
ance and Hausman-style tests suggests that assignments were, En realidad, as good as random.

10. Desafortunadamente, LSAT and undergraduate GPA data are missing for a large, nonrandom subset. Respectivamente, nosotros

rely on these data sparingly and do not report demographic group means for these variables.

11. The rank of instructors’ JD programs comes from the usual U.S. News Rankings.
12. We report all sample sizes rounded to the nearest ten.

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461

Effects of Demographic Mismatch

Mesa 1. Sample Statistics for First-Year Required Courses

Blanco

Nonwhite

Male

Female

Significar

Dakota del Sur

Significar

Dakota del Sur

Significar

Dakota del Sur

Significar

Dakota del Sur

Grupo A: Student-Course Level

0.49

3.36

0.80

0.003

0.40

0.56

0.04

0.51

0.18

0.93

0.46

3.14

0.81

0.003

0.23

0.67

0.10

0.53

0.95

0.92

0.51

3.27

0.80

0.003

0.33

0.61

0.07

0.42

0.41

0.93

0.50

3.29

0.81

0.003

0.34

0.60

0.06

0.58

0.50

0.92

23,200

13,360

15,250

21,320

Grupo B: Student Level

Course grade (0-4)

Take another course

Dropped course

Calificación: A

Calificación: B

Calificación: C, D, F

Other-sex instructor

Other-race instructor

Same instructor

Observaciones

Age (first semester)

25.5

2.6

25.4

2.4

25.7

2.7

25.3

2.5

Female student

Black student

Latinx student

Asian student

White student

Other race student

Persist to second year

Joined top law review at LS

Graduated in 5 años

Observaciones

Nonwhite instructor

Black instructor

Latinx instructor

Asian instructor

White instructor

Female instructor

Years of experience at LS

Has JD

0.54

0.00

1.00

0.00

0.89

0.14

0.82

0.66

0.21

0.37

0.34

0.00

0.08

0.91

0.06

0.82

0.00

0.05

0.12

0.10

0.70

0.03

0.88

0.12

0.81

1.00

0.10

0.14

0.59

0.03

0.90

0.11

0.82

2,890

1,680

1,910

2,660

Grupo C: Instructor Level

1.00

0.47

0.23

0.30

0.00

0.57

3.00

0.97

0.15

0.08

0.02

0.05

0.85

0.00

7.37

0.94

5.89

9.64

0.00

1.00

0.47

5.76

0.95

0.20

0.08

0.06

0.80

1.00

3.15

0.96

10.90

6.24

Rank of JD school

37.6

36.1

42.4

44.1

36.1

39.9

40.6

34.5

Has PhD

Has master of laws degree

Has bachelor of laws degree

0.10

0.09

0.04

0.03

0.21

0.00

0.08

0.13

0.05

0.10

0.09

0.01

Observaciones

140

Notas: The Dropped course descriptive statistics are based on slightly larger samples (23,300 for white students, 13,430
for nonwhite students, 15,320 for male students, y 21,400 for female students) because including dropped courses
increases the number of student-course level observations for students who drop classes. There are no Other race instructors
in the analytic sample. Same instructor in panel A is a binary variable indicating the student had the same instructor in
the previous course. JD = Juris Doctor; SD = standard deviation; LSAT = Law School Admission Test; LS = Law School.

462

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Chris Birdsall, Seth Gershenson, and Raymond Zuniga

Mesa 2. Sample Statistics for First-Year Required Courses

Course Level Characteristics

Significar

Dakota del Sur

Course Name

Percent

Class size

Female student

Age (first semester)

Black student

Latinx student

Asian student

White student

Other student

Female instructor

Black instructor

Asian instructor

Latinx instructor

White instructor

More than one instructor race choice in term

More than one instructor race choice in academic year

More than one instructor sex choice in term

More than one instructor sex choice in academic year

5.76

2.30

6.14

5.47

28.60

31.29

5.85

1.92

6.53

1,040

41.60

34.00

Civil Procedure

Civil Procedure II

Constitutional Law

Contracts

Torts

Legal Writing I

Legal Writing II

Property

Property II

Criminal Law

Observaciones

0.59

25.90

0.08

0.13

0.63

0.03

0.45

0.08

0.02

0.04

0.87

0.74

0.75

0.94

0.95

0.14

2.33

0.07

0.10

0.13

0.05

0.50

0.26

0.15

0.19

0.34

0.44

0.43

0.24

0.21

Observaciones

1,040

Notas: Classroom level demographics are presented as proportions. SD = standard deviation.

near-equal likelihoods of having an other-sex instructor, whereas female students are
more likely than male students to have an other-sex instructor. Nonwhite students are
much more likely to have an other-race instructor than are white students, as the ma-
jority of instructors are white.

Panel B of table 1 reports descriptive statistics at the student level. The average age
of ﬁrst-year JD students is about 25 years for all demographic groups. Whereas female
students form a majority of both white and nonwhite students, the representation of fe-
male students is greater among nonwhite students than among white students. Among
nonwhite students, 21 el porcentaje son negros, 37 percent are Latinx, y 34 percent are Asian.
Graduation rates are similar across demographic groups, which for students are coded
as White, Negro, Latinx, asiático, or Other.

Finalmente, panel C of table 1 reports descriptive statistics at the instructor level, for in-
structors who taught at least one ﬁrst-year required course between 2000 y 2012. On
promedio, white instructors have more experience at LS than nonwhite instructors, y
male instructors have more experience than female instructors. Acerca de 47 por ciento de
white instructors are female, mientras 57 percent of nonwhite instructors are female. Alabama-
most half of nonwhite faculty are black, 23 percent are Latinx, y 30 percent are Asian;
unlike for students, there is no “Other race” category for instructors. In the empirical
modelos, same-race is coded as an exact racial group match, as opposed to an indica-
tor for both student and teacher being nonwhite. The average instructor attended a
JD program ranked in the top 50 by U.S. Noticias. White and male instructors attended
slightly higher-ranked programs, on average, than did nonwhite and female instructors,
respectivamente.

Mesa 2 reports descriptive statistics at the classroom (es decir., course-section) nivel.
Hay 1,040 unique ﬁrst-year required course oﬀerings in the analytic sample. El

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463

Effects of Demographic Mismatch

average class contained about 42 estudiantes, 59 percent of whom were female. The ma-
jority (87 por ciento) of courses were taught by white faculty, 8 percent were taught by
black instructors, 4 percent by Latinx instructors, y 2 percent by Asian instructors.
Mesa 2 also reports the frequency of the ten courses that constitute the analytic sam-
por ejemplo. Some courses appear less often either because they had smaller average class sizes,
were merged into a single course, or ceased to be required between 2000 y 2012. Still,
outliers here are the legal writing classes, which are overrepresented because of their
smaller class size. Subject-speciﬁc summary statistics are provided in table A.2, cual
shows that the average writing class has ﬁfteen students whereas the other classes av-
erage ﬁfty to eighty students. Because of the notably smaller class size and the diﬀerent
structure of writing classes, as a sensitivity analysis, we reestimate the baseline model
on a sample that excludes the writing classes in table A.3 and conﬁrm the main results
are not driven by student outcomes in these unique classes.

I D E N T I F I C AT I O N S T R AT E G Y

3 .
This section describes the main identiﬁcation strategy used to estimate the causal ef-
fects of student–instructor demographic match on course-speciﬁc outcomes. We ﬁrst
introduce the preferred two-way ﬁxed eﬀects (FE) especificación. We then discuss the key
identifying assumptions and present a test of the “endogenous sorting” threat to iden-
tiﬁcation. Finalmente, we describe a three-way FE speciﬁcation used to identify the eﬀect
of mismatch in the ﬁrst course of two-course sequences on performance in the second
curso.

Baseline Model
Our primary interest is in how student–instructor demographic match aﬀects outcomes
(y) at the student-course level. Específicamente, we are interested in δ in the linear regression
modelo:

yi jcst = β0 + β1Xi + β2Wj + β3Zcst + δOtheri j + (cid:4)i jcst,

(1)

where X, W., and Z are vectors of observed student (i), instructor (j), and course-section
(cs) características, respectivamente; t indexes semesters; Other is a vector of variables that
measure the degree of demographic similarity between student and instructor; y
(cid:4) represents the unobserved determinants of y.13 We operationalize Other in various
maneras, such as a set of four mutually exclusive race-by-sex indicators (es decir., misma raza
and other sex, same sex and other race, same race and same sex, other race and other
sexo) and simpler deﬁnitions that include binary indicators for other sex and/or other
carrera. Sin embargo, in all speciﬁcations, race matches are coded as speciﬁc matches such as
black-black, Latinx-Latinx, Etcétera, as opposed to “minority-minority.”

Given that course-section assignments are allegedly conditionally (on X) aleatorio,
ordinary least squares (OLS) estimates of equation 1 might well be unbiased and

13. We consider models that allow the eﬀect of Other to vary by subject, but ﬁnd no systematic evidence of diﬀer-
ential eﬀects by subject, perhaps because we are under-powered to do so. Respectivamente, we report estimates of
the average eﬀect of student-instructor demographic match that are averages across subjects.

464

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3

Chris Birdsall, Seth Gershenson, and Raymond Zuniga

have a causal interpretation. Sin embargo, if the quasi-random assignment rule is im-
perfectly followed, these estimates might be biased. Por ejemplo, unobserved student
characteristics might jointly predict outcomes and assignment to an other-race teacher.
Similarmente, equation 1 fails to control for unobserved instructor attributes, such as grad-
ing policies or teaching style. Respectivamente, we follow Fairlie, Hoﬀmann, and Oreopoulos
(2014) and augment equation 1 to condition on both student and classroom FE, cual
yields our preferred speciﬁcation:

yik = θi + ωk + δOtherik + (cid:4)I.

(2)

Several aspects of equation 2 merit attention. Primero, the vectors X, W., and Z fall out of
the model because they are colinear with the FE. Segundo, we collapse the subscripts jcst
into a single k subscript because identiﬁcation now comes from within-classroom varia-
tion in Other and classrooms are instructor-, course-, section-, and semester-speciﬁc: el
classroom FE (Vaya) subsumes instructor, curso, semester, and year FE. Específicamente, el
classroom FE uniquely identify each course section taught in a given semester and thus
control for the course’s location (aula) quality, meeting day(s) y tiempo, class size,
and class composition. Thus the classroom FE also ensure that identiﬁcation comes
from students who experienced the same lectures, assignments, and grading prac-
tices. Tercero, equation 2 is only identiﬁed for outcomes that vary within students across
courses, such as course grades, due to the student FE (i ). Finalmente, there is a possible
sample selection issue for the analyses of course grades, since grades are only observed
for students who complete the course, and it is possible that student–instructor demo-
graphic mismatch aﬀects the likelihood that students complete the course. This turns
out to be a practically unimportant concern, as dropping courses is quite rare (ocurre
in only 0.6 percent of cases) and we ﬁnd no evidence that demographic mismatch af-
fects course dropouts.14 We estimate equation 2 using the estimation routine proposed
by Correia (2016) and compute two-way cluster-robust standard errors, which allows
for correlation both within instructors across semesters, and within students across
courses (Cameron, gelbach, y molinero 2012).15

Sorting Test
Although the two-way FE in equation 2 address many threats to validity, one poten-
tial threat remains: diﬀerential sorting by student race or sex (Fairlie, Hoﬀmann and
Oreopoulos 2014). Por ejemplo, the student FE control for scenarios in which high-
ability students sort into female-taught courses, but does not adequately control for
sex-speciﬁc sorting processes in which high-ability female students sort into female-
taught courses and high-ability male students sort into male-taught courses. To discern
the extent to which diﬀerential sorting on unobservables occurs, we follow Fairlie, Hoﬀ-
mann, and Oreopoulos (2014) in implementing a formal test for diﬀerential sorting
on observables. The test relies on the intuition of diﬀerence-in-diﬀerences estimators

14. This is perhaps unsurprising, as we are investigating required ﬁrst-year courses.
15. Clustering along only one dimension and/or at lower levels yields nearly identical inferences and slightly
smaller standard errors for the main course-grade results. Respectivamente, we report the more conservative two-way
clustered standard errors in the main text. This is motivated by the guidance in Angrist and Pischke (2009),
which suggests clustering at the highest level.

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465

Effects of Demographic Mismatch

and the bounding procedure of Altonji, Elder, and Taber (2005). It is best illustrated
via an example. Suppose we want to test for diﬀerential sorting by sex. We would ﬁrst
compute the mean of observed student characteristic L (p.ej., LSAT score) in classroom
k for each sex g: ¯Lg

k . Then estimate the linear regression
Female = g

(cid:2)

(cid:3)

+ γ3Femalek × 1

= γ0 + γ1Femalek + γ21

(cid:2)

Female = g

(cid:3)

(3)

¯Lg
k

where Female is a binary indicator equal to 1 if the section-k teacher is female, and zero
de lo contrario; 1{·} is the indicator function; and γ 3 is the parameter of interest. Speciﬁ-
cally, γ 3 represents “the diﬀerence-in-diﬀerences estimate” of the average diﬀerence in
observed characteristics between female and male students in female- and male-taught
courses. If γ 3 is signiﬁcantly diﬀerent from zero, there are diﬀerences by student sex in
sorting into courses on observables that systematically vary with the sex of the instruc-
colina. Alternativamente, if the OLS estimate of γ 3 in equation 3 is statistically indistinguishable
from zero, there is no evidence of diﬀerential sorting on observables, and thus diﬀer-
ential sorting on unobservables in a way that would bias the two-way FE estimates of
equation 2 is unlikely.

Cross-Semester Effects in Two-Course Sequences
Finalmente, we consider whether exposure to an other-race or other-sex instructor in the ﬁrst
course of a two-course sequence aﬀects performance in the second course. Naturalmente,
this analysis can only be conducted for the subset of ﬁrst-year courses that are part
of a required two-course sequence.16 While this question can be addressed using the
baseline two-way FE model given in equation 2, it is also possible to further increase the
estimates’ validity by augmenting equation 2 to condition on a second-semester course
FE (ϕ).17 Específicamente, we estimate three-way FE models of the form

yis2 = θi + Vaya(i)
s1

+ ϕ(i)
s2

+ δOtheris1 + (cid:4)es,

(4)

dónde 1 y 2 index semesters and s indexes subjects. Estimates of δ in equation 4
are robust to excluding the second-semester course FE, which is reassuring because it
suggests the demographic background of the ﬁrst-semester instructor does not aﬀect
second-semester classroom assignments. Estimates of equation 4 report standard er-
rors clustered along three dimensions: alumno, semester 1 instructor, and semester 2
instructor.

4 . RESULTADOS
This section presents the empirical results. We ﬁrst present estimates of the sort-
ing test characterized by equation 3. We then present the baseline two-way FE esti-
compañeros, followed by tests for heterogeneous impacts of student–instructor demographic
mismatch.

16. There are three such sequences: Civil Procedure I & II, Legal Writing I & II, and Property Law I & II.
17. This is similar to the identiﬁcation strategy used by Figlio, Schapiro, and Soter (2015) to identify the impact of
adjunct instructors, though in that case the ﬁrst-semester course FE were not included because adjunct status
varies only at the classroom level.

466

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Chris Birdsall, Seth Gershenson, and Raymond Zuniga

Mesa 3. Sorting Test Estimates

Outcome

LSAT

UGPA

Median Income (ZIP)

% Adult w/BA (ZIP)

In/Nearby State

Student Age

Nonwhite instructor

Nonwhite student

−0,025
(0.058)

0.078
(0.248)
−4.848*** −0.149***
(0.107)

Nonwhite instructor

* Nonwhite student

Constant

0.376
(0.263)
160.790***
(0.091)

(0.033)
−0.067
(0.104)
3.460***
(0.023)

Grupo A: Sorting by Race

−3,874.264***
(1,268.960)
−32,14.724***
(577.044)

49.169
(1,210.234)
78,674.542***
(529.096)

Observaciones

1,820

490

2,010

Grupo B: Sorting by Sex

Female instructor

Female student

Female instructor

* Female student

Constant

0.255
(0.167)
−1.048***
(0.115)
−0.036
(0.181)
159.560***
(0.115)

−0.059
(0.060)
0.132***
(0.046)

0.013
(0.073)
3.337***
(0.038)

−623.512
(1,124.828)
−1,477.353**
(727.315)
−1,359.981
(1,149.638)
78,731.551***
(760.778)

Observaciones

1,860

480

2,090

4.051***
(1.361)
−2.406***
(0.288)
−1.867**
(0.813)
37.980***
(0.455)

2,010

1.168
(0.814)

0.495
(0.317)
−0.809
(0.513)
36.831***
(0.550)

2,090

−0.019
(0.015)
−0.027***
(0.010)

0.025
(0.025)
0.530***
(0.006)

2,020

0.008
(0.013)
0.040***
(0.012)
−0,010
(0.017)
0.492***
(0.009)

2,090

0.004
(0.068)
−0.181***
(0.049)

0.104
(0.104)
25.560***
(0.033)

2,020

−0.093
(0.066)
−0.369***
(0.057)

0.001
(0.081)
25.738***
(0.046)

2,090

Notas: Each column represents tests for sorting on a different student background characteristic. In/Nearby State is a binary variable indicating
the student’s home address is within the same state as the institution or a bordering state. Standard errors in parentheses are clustered by
curso. LSAT = Law School Admission Test; UGPA = undergraduate grade point average; BA = Bachelor of Arts degree.
**pag < 0.05; ***p < 0.01. Sorting Test Estimates Table 3 presents estimates of the sorting test characterized by equation 3.18 Panel A reports estimates for diﬀerential sorting by race, comparing the average characteristics of white and nonwhite students. Panel B does the same for diﬀerential sorting by sex, comparing the average characteristics of male and female students. We perform the sorting test for six outcomes: LSAT score, undergraduate GPA, median income in student’s home ZIP Code, percent of population with college de- gree in student’s home ZIP Code, a binary indicator equal to one if the student came from the surrounding tristate area, and student age.19 The LSAT and undergraduate GPA variables likely measure a combination of students’ cognitive and noncognitive skills (Heckman and Kautz 2012). The ZIP Code information proxies for the student’s socioeconomic background, which is an important predictor of undergraduate college success (Bailey and Dynarski 2011). The “In/Nearby State” indicator provides a crude measure of students’ distances from home, which is known to predict undergraduate enrollments (Alm and Winters 2009; Cooke and Boyle 2011). Only one of the twelve estimates of γ 3 in table 3 is statistically signiﬁcant, which suggests little diﬀerential sorting on observables by sex or race. Given the multiple hy- potheses tested, it is possible that the signiﬁcant result in panel A is spurious: Indeed, 18. The sorting test estimates remain essentially unchanged when course name and year FE are added to the re- gression. 19. Data on LSAT and undergraduate GPA are missing for many students, so these results should be interpreted with caution. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d . / f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 467 Effects of Demographic Mismatch Table 4. Impact of Demographic Mismatch on First-Year Required Course Outcomes Other-sex Other-race Differences in coefficients (P) Observations Course fixed effects Student fixed effects Continuous Grade A Grade A/A- Grade C, D, F Grade Take Another Dropped Course (1) −0.016** (0.007) −0.037** (0.016) 0.214 36,560 Yes Yes (2) (3) −0.008** (0.004) −0.015** (0.007) 0.455 36,560 Yes Yes −0.013** (0.007) −0.028*** (0.011) 0.186 36,560 Yes Yes (4) 0.001 (0.003) 0.009 (0.007) 0.256 36,560 Yes Yes (5) 0.016 (0.010) −0.000 (0.008) 0.197 18,620 Yes Yes (6) −0.000 (0.000) 0.001 (0.001) 0.867 36,730 Yes Yes Notes: Each column represents a different model specification. The outcomes are measured as follows: Continuous Grade measures a student’s received grade on a 0—4 scale (F—A); A Grade is a binary indicator for whether a student received an A grade; A or A— Grade is a binary indicator for whether a student received an A or A— grade; C, D, or F Grade is a binary indicator for whether a student received a C, D, or F grade; Take Another is a binary indicator for whether a student takes a subsequent elective course in the same field after his first year; and Dropped Course is a binary indicator for whether a student drops the course before the end of the semester. Column 5 has fewer observations because not all required courses correspond to elective course subjects. Difference in coefficients compares the other-sex effect to the other-race effect. Standard errors in parentheses are clustered by student and instructor. **p < 0.05; ***p < 0.01. it loses its statistical signiﬁcance after adjusting for multiple comparisons (Schochet 2009). Moreover, this result suggests sorting in the “wrong” direction, in the sense that nonwhite students assigned to nonwhite faculty are from lower socioeconomic back- grounds, which would bias against ﬁnding a positive impact of demographic match on student outcomes. In sum, the general lack of sorting on observables observed in table 3 suggests diﬀerential sorting on unobservables is unlikely to bias two-way FE estimates of equation 2. The lack of endogenous sorting is unsurprising given LS’s claims that students were at least quasi-randomly assigned to classrooms. We further test this claim below by examining the sensitivity of the baseline estimates to controlling for student FEs. Main Results Table 4 reports two-way FE estimates of equation 2 using a simple deﬁnition of Other: binary indicators for whether or not the student had an other-sex and other-race in- structor. The ﬁrst four columns of table 4 use diﬀerent deﬁnitions of the course grade as the outcome. Column 1 uses a continuous measure of the course grade, which is measured on a 0 to 4 scale. Having an other-sex and other-race teacher signiﬁcantly reduced the student’s course grade by 0.02 and 0.04, respectively, though these esti- mates are not signiﬁcantly diﬀerent from one another. These eﬀects represent small ((cid:2)1 percent) changes from the average course grade of 3.36. Although small in mag- nitude, recall that these are course-speciﬁc eﬀects that might add up to nontrivial dif- ferences in cumulative GPA that preclude underrepresented students from prestigious internships after the ﬁrst year or alter class rankings in ways that aﬀect initial job place- ments and starting salaries. Additionally, these small eﬀects could be due to the eﬀect of student–instructor de- mographic mismatch operating on particular margins of the course-grade distribution. Accordingly, in columns 2 and 3 we estimate linear probability models in which the out- comes are binary indicators for “good” grades, deﬁning a good grade as an A or an A 468 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / f / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d . / f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Chris Birdsall, Seth Gershenson, and Raymond Zuniga or A−, respectively. Consistent with the results in column 1, columns 2 and 3 show signiﬁcant, negative eﬀects of demographic mismatch on the probability that students receive a good grade regardless of how good grade is coded. That the eﬀect on having an A is smaller than that on the more inclusive deﬁnition of good grade suggests that demographic match eﬀects operate on both the A/A− and A−/B+ margins. Column 4 shows that there is no eﬀect of student–instructor demographic mismatch on the like- lihood of receiving a “bad grade” (less than B−). These results show that demographic mismatch aﬀects grades, primarily by aﬀecting the likelihood of receiving top grades (A or A−). Racial mismatch eﬀects tend to be larger than sex mismatch eﬀects, but these diﬀerences are not statistically signiﬁcant. These eﬀects are arguably economically sig- niﬁcant, as the other-race eﬀect of 0.03 constitutes 9 percent of the sample average “good-grade” rate and might add up to have a nontrivial eﬀect on cumulative GPA. The remaining columns of table 4 show that there are neither eﬀects of mismatch on the likelihood that the student takes an elective course in the subject in the second year or beyond nor on the likelihood the student drops the course.20 The latter null result is im- portant, as it suggests that the sample selection inherent in the course-grade analyses is negligible. Because an important contribution of the current paper is the identiﬁcation of causal eﬀects of same-race and same-sex instructors on course outcomes, we now leverage the alleged quasi-random assignment of students to course sections to cross- validate the baseline two-way FE estimates. The intuition of the Hausman test (Haus- man 1978) suggests that if student assignments to course sections were conditionally random, then the estimates should be robust to the inclusion of student FE, as the claim is that students are randomly assigned to course sections (classrooms). Similar intu- ition motivates the common practice of verifying that experimental estimates of causal eﬀects are robust to conditioning on predetermined characteristics in treatment-eﬀect regressions (Angrist and Pischke 2009). In table 5, we show that the baseline estimates are quite robust to the inclusion of student and/or classroom FE. This lends additional support to a causal interpretation of the baseline estimates and to the claim that students were randomly assigned to ﬁrst- year courses.21 Speciﬁcally, column 2 shows that the “naive OLS” mismatch eﬀects in column 1 are robust to controlling for observed student characteristics such as LSAT score, undergraduate GPA, socioeconomic status, and distance to the law school. This suggests students were, in fact, randomly assigned to course sections.22 Columns 3 and 4 compare student random eﬀects and student FE estimators, in the spirit of the original Hausman test, and again ﬁnd the point estimates are robust to controlling for unobserved student heterogeneity. Finally, columns 5 and 6 show the results are robust to conditioning on classroom FE, which means that the mismatch eﬀects are not driven by diﬀerential teacher or classroom characteristics, such as teaching or grading 20. The sample size for subsequent course taking is smaller because there are not subsequent courses in all required ﬁrst-year courses. 21. Because table 5 shows the pooled OLS estimates can be given a causal interpretation, we can also estimate pooled logit models to verify that the baseline linear model provides reasonable approximations of the partial eﬀects of interest. Accordingly, table A.4 reports logit average partial eﬀects (APE) that are comparable to the linear estimates reported in table 4. The logit APE are quite similar to the linear coeﬃcient estimates, suggesting that the main results are robust to the functional form choice. 22. We include missing-data dummies to allow use of the full sample. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d f . / f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 469 Effects of Demographic Mismatch Table 5. Impact of Demographic Mismatch on First-Year Required Course Outcomes Other-sex Other-race Female instructor Nonwhite instructor Nonwhite student Female student A/A— Grade (1) (2) (3) (4) (5) (6) −0.012** (0.005) −0.024** (0.009) 0.041*** (0.005) 0.009 (0.008) −0.152*** (0.011) 0.038*** (0.008) −0.011** (0.005) −0.027*** (0.009) 0.029*** (0.005) 0.021*** (0.008) −0.088*** (0.011) 0.044*** (0.008) −0.012*** (0.005) −0.031*** (0.009) 0.031*** (0.005) 0.017** (0.008) −0.085*** (0.011) 0.042*** (0.008) −0.013* (0.007) −0.033*** (0.012) 0.031* (0.018) 0.015 (0.016) −0.012* (0.007) −0.023* (0.013) −0.013** (0.007) −0.028*** (0.011) −0.088*** (0.013) 0.042*** (0.009) Observations Cohort class dummies Course subject type dummies Student characteristics Course FE Student RE Student FE 36,560 36,560 36,560 36,560 36,560 36,560 Yes No No No No No Yes Yes Yes No No No Yes Yes Yes No Yes No No Yes No No No Yes No No Yes Yes No No No No No Yes No Yes Notes: Each column represents a different model specification. The outcome A/A— Grade is a binary indicator for whether a student received an A or A— grade. Course Subject Types are Civil Procedure, Constitutional, Contracts, Criminal, Legal Writing, Property, and Torts. Student Characteristics are age, Law School Admission Test, undergraduate grade point average, median income, and percent of adults with Bachelor of Arts degree in home ZIP Code, in/nearby state, and missing data indicators for each. Standard errors in parentheses are clustered by student in columns 1—4 and by student and instructor in columns 5 and 6. FE = fixed effects; RE = random effects. *p < 0.1, **p < 0.05, ***p < 0.01. practices, or the physical location or condition of the classroom. Column 6 replicates the baseline two-way FE estimates of equation 2. Heterogeneity Having established arguably causal impacts of student–instructor demographic mis- match on course grades, we now test for possible heterogeneity in such eﬀects. First, we investigate possible heterogeneity by student background and by the precise type of de- mographic mismatch, because understanding the determinants of success for students from historically underrepresented groups is of paramount policy interest.23 Second, we investigate whether these demographic mismatch eﬀects are moderated by the de- mographic composition or the size of speciﬁc classrooms, as classroom environments might moderate the impact of mismatch (Inzlicht and Ben-Zeev 2000; Ho and Kelman 2014).24 23. We ﬁnd no evidence of heterogeneity along other observable student dimensions, such as students’ ability (LSAT score), age, home region, and ZIP Code socioeconomic status. Nor do we ﬁnd evidence of heterogeneity by observable instructor characteristics, such as experience, rank of JD program, or faculty rank (i.e., adjunct, teaching-track, tenure-line, tenured). These null results are not reported in tabular form in the interest of brevity. 24. A relevant question here is whether class characteristics vary by subject. Table A.2 reports mean course char- acteristics by subject. The primary outlier is leal writing, which has signiﬁcantly smaller classes than the other 470 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / f / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d . / f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Chris Birdsall, Seth Gershenson, and Raymond Zuniga Table 6. Impact of Demographic Mismatch on First-Year Required Course Outcomes All Students Female Students Nonwhite Students Nonwhite Female Students (1) (2) (3) (4) Other-sex Other-race Female faculty Nonwhite faculty Same race, Mismatch sex (1) Mismatch race, Same sex (2) Mismatch race, Mismatch sex (3) Female faculty Nonwhite faculty Difference in Coefficients (P) 1 = 2 1 = 3 2 = 3 Observations Course fixed effects Student fixed effects −0.013* (0.007) −0.033*** (0.012) 0.031* (0.018) 0.015 (0.016) −0.013 (0.008) −0.033** (0.013) −0.046*** (0.015) 0.031* (0.018) 0.015 (0.016) 0.111 0.018** 0.155 36,560 No Yes Panel A −0.035* (0.019) −0.031** (0.013) 0.028 (0.018) Panel B −0.038 (0.023) −0.034** (0.017) −0.066*** (0.024) 0.028 (0.018) 0.876 0.048** 0.083* 21,320 No Yes −0.017* (0.009) −0.046* (0.024) 0.033* (0.017) 0.011 (0.016) −0.093*** (0.032) −0.083** (0.032) −0.096*** (0.033) 0.033* (0.017) 0.012 (0.016) 0.666 0.931 0.176 13,360 No Yes −0.041** (0.019) −0.052* (0.028) 0.020 (0.019) −0.094* (0.049) −0.078* (0.043) −0.116** (0.045) 0.021 (0.019) 0.599 0.473 0.052* 8,790 No Yes Notes: Each column in each panel represents a different model specification. The outcome A or A— Grade is a binary indicator for whether a student received an A or A— grade. The omitted category in panel B is Same Race, Same Sex. Estimates are not shown for course subject dummies. In some samples, estimates are not shown for certain instructor effects because they are perfectly colinear with other-sex or other-race parameters. Standard errors in parentheses are clustered by student and instructor. *p < 0.1; **p < 0.05; ***p < 0.01. Panel A of table 6 estimates the baseline student-FE speciﬁcation, sans classroom FE, to enable identiﬁcation of mismatch eﬀects for speciﬁc demographic subgroups of the sample. We feel comfortable making this trade-oﬀ because table 5 shows that the full-sample estimates are robust to omitting the classroom FE. Column 1 of table 6 re- peats the estimates shown in column 4 of table 5 to facilitate comparisons. Columns 2 and 3 estimate this speciﬁcation separately for female and nonwhite students, respec- tively. We might expect these groups to be particularly aﬀected by faculty representa- tion, given the general overrepresentation of white men in the legal profession. These models yield two key ﬁndings. First, as expected, the other-sex eﬀect is driven by fe- male students’ grades and the other-race eﬀect is driven by nonwhite students’ grades. Speciﬁcally, for female students, the likelihood of receiving an A/A– increases by 3.5 percentage points (10 percent) when taught by a female instructor, compared with an subjects. However, we ﬁnd no evidence of systematic diﬀerences between legal writing and other subjects in tests for subject heterogeneity. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . f / / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d / f . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 471 Effects of Demographic Mismatch overall sex-match eﬀect of 1.3 percentage points (3 percent) in the full sample. Similarly, the race-match advantage for nonwhite students is 4.6 percentage points (20 percent), compared with 3.3 percentage points (9 percent) in the full sample.25 Second, the other- sex eﬀect is similar for both white and nonwhite students, and the other-race eﬀect is similar for both male and female students. This lack of heterogeneity is also interesting. Finally, column 4 shows that the harmful eﬀects of demographic mismatch are most pronounced for nonwhite female students, although these diﬀerences are not signif- icantly diﬀerent from the overall eﬀects of sex representation for women or of racial representation for nonwhite students. Panel B of table 6 generalizes the models estimated in panel A by allowing for multiplicative eﬀects of having both an other-race and other-sex instructor. Here, Other is speciﬁed as a set of four mutually exclusive categorical indicators, with same-sex and same-race serving as the omitted reference category. Column 1 shows that overall, relative to students whose instructors are of the same race and sex, any type of demographic mismatch leads to a lower likelihood of receiving a good grade. However, having a diﬀerent-race and diﬀerent-sex instructor is signiﬁcantly worse than instances in which demographic mismatch occurs along only one dimension. Column 2 shows that this is true for the female subsample as well, which is consistent with the results presented in panel A, and shows the eﬀect of having a diﬀerent-race and diﬀerent-sex instructor is more pronounced for female students than for male students. However, column 3 shows that nonwhite students are similarly harmed by any type of student–instructor demographic mismatch. Finally, and again consistent with the results presented in panel A, column 4 of panel B shows that nonwhite female students beneﬁt the most from intersectional demographic representation (i.e., having both a same-race and same-sex instructor). Next, we test for heterogeneity in the impact of student–instructor demographic mismatch by classroom characteristics, such as class size and class composition. Whether larger classrooms magnify or dampen the mismatch eﬀects documented pre- viously is theoretically ambiguous, as smaller classrooms could either shine a spotlight on implicit biases or facilitate relationships that supersede stereotypes. We also allow the eﬀect of mismatch to vary with the demographic composition of classrooms, as the impact of an other-race or other-sex instructor might be more pronounced in less di- verse settings in which female or nonwhite students feel isolated. Given the exploratory nature of this analysis, we model the heterogeneity using quadratics in class size and percent female (nonwhite). The quadratics are at least marginally jointly signiﬁcant in both cases.26 Appendix table A.5 reports the coeﬃcient estimates for these models, though for ease of interpretation we plot the marginal eﬀects as functions of class size and percent female (nonwhite). Figure 1 plots the marginal eﬀects (and corresponding 95 percent conﬁdence intervals) on the probability of receiving an A/A– of having an other-race or other-sex instructor as a function of class size for the range of class sizes observed in the analytic sample. Interestingly, there is essentially no eﬀect of mismatch in the 25. The nonwhite eﬀect itself is almost entirely driven by black students’ responses to black instructors, which is consistent with Fairlie, Hoﬀmann, and Oreopoulos (2014), although we focus on the aggregate nonwhite eﬀect because the race-speciﬁc analysis is underpowered due to the small share of Asian and Latinx instructors. 26. Cubic and nonparametric speciﬁcations yield qualitatively similar results. 472 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d / . f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Chris Birdsall, Seth Gershenson, and Raymond Zuniga Notes: Good Grade is defined as an A or A–. Each graph represents a different model specification. Figure 1. Average Partial Effects (APE) of Student—Instructor Mismatch on the Probability of Receiving a Good Grade as a Function of Class Size smallest classes. The other-sex eﬀect monotonically increases in magnitude with class size, though at a relatively slow pace, and only becomes statistically signiﬁcant in rela- tively large classes. The other-race eﬀect, meanwhile, exhibits a U-shaped pattern. The deleterious eﬀect of having an other-race instructor is largest in classrooms of about sixty students. One possible interpretation of this pattern is that the personal connec- tions and relative anonymity in very small and very large classes, respectively, mitigate the harm associated with having an other-race instructor. Similarly, ﬁgure 2 plots the marginal eﬀects on the probability of receiving an A/A– of having an other-race (other-sex) instructor as a function of the fraction of the class- room that is nonwhite (female). The other-race eﬀect is fairly constant at about −0.03 or −0.04, regardless of the proportion of nonwhite students in the class. However, the other-sex eﬀect is less linear. Intuitively, it is most pronounced when female students make up less than half the class. The other-sex eﬀect approaches zero when 60 to 70 percent of the class is female. This is suggestive of stereotype threat,27 whereby females disengage with law school when they perceive themselves as outsiders, and consistent with experimental evidence that shows the sex ratio of a classroom aﬀects a female student’s test performance but not a male student’s (Inzlicht and Ben-Zeev 2000). 27. Stereotype threat occurs when the presence of a white or male instructor triggers historically underrepresented students’ recognition of their outgroup status, which in turn causes emotional responses that hinder their academic performance and ultimately lessens their engagement with school (Steele 1997). l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d . / f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 473 Effects of Demographic Mismatch l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d . / f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Notes: Good Grade is defined as an A or A–. Each graph represents a different model specification. Figure 2. Average Partial Effects (APE) of Student—Instructor Mismatch on the Probability of Receiving a Good Grade as a Function of Class Composition Cross Semester Effects Finally, table 7 reports estimates of equation 4, which show the impact on performance in the second course of having an other-sex or other-race instructor in the ﬁrst course of a required two-course sequence. These are all required ﬁrst-year courses that take place in the fall and spring semesters of the ﬁrst year. The model is estimated for three outcomes: course grade, a binary indicator for “good grade” (i.e., A or A−), and a binary indicator for “bad grade” (i.e., < B−). These models can only be estimated for the subset of courses that are part of a two-course sequence. Panel A of table 7 shows results that are broadly similar to the baseline two-way FE estimates reported in table 4: There are negative eﬀects of student–instructor mis- match in the ﬁrst course on grades, and on the probability of receiving a good grade in the second course. Once again, the other-race eﬀect is about twice as large as the other- sex eﬀect, though here only the other-sex eﬀect is statistically signiﬁcant at traditional conﬁdence levels; this is due to the larger standard errors associated with the smaller sample of courses that constitute two-course sequences and the fact that there are more female faculty than nonwhite faculty in two-course sequences. That these estimates are qualitatively similar to the baseline estimates reported in table 4 lends further credence to a causal interpretation of the relationship between student–instructor demographic mismatch and course grades. Moreover, this similarity sheds some light on the mech- anisms at work, as the cross-semester eﬀects documented in table 7 suggest increased subject-speciﬁc learning that persists into the subsequent semester. 474 Chris Birdsall, Seth Gershenson, and Raymond Zuniga Table 7. Cross-Semester Effects of Demographic Mismatch in Two-Course Sequences Continuous Grade A/A— Grade C, D, F Grade (1) (2) (3) Panel A: Cross-Semester Effects Panel B: Cross-Semester Effects — Same Instructor Other-sex (OS) Other-race (OR) Course 1 FE Course 2 FE Student FE Other-sex Other-race OS * Same instructor OR * Same instructor Course 1 Fixed Effects Course 2 Fixed Effects Student Fixed Effects −0.032** (0.012) −0.077 (0.050) Yes Yes Yes −0.034** (0.016) −0.072 (0.048) Yes Yes Yes −0.074 (0.063) −0.206*** (0.063) 0.047 (0.065) 0.145*** (0.054) Yes Yes Yes −0.120** (0.060) −0.046 (0.070) 0.095* (0.057) −0.029 (0.060) Yes Yes Yes 0.004 (0.008) 0.016 (0.021) Yes Yes Yes 0.005 (0.031) 0.073* (0.043) −0.001 (0.030) −0.064 (0.039) Yes Yes Yes Notes: N = 4,340. Each column represents a different model specification. The outcomes are measured as follows: Continuous Grade measures a student’s re- ceived grade on a 0—4 scale (F—A). A/A— Grade is a binary indicator for whether a student received an A or A— grade. C, D, F Grade is a binary indicator for whether a student received a C, D, or F grade. Same Instructor indicates the student had the same instructor for both Courses 1 and 2 in two-course sequences. Estimates are not shown for Same Instructor in even numbered columns because it is perfectly correlated with the Courses 1 and 2 fixed effects. Standard errors in parentheses are clustered three ways: by student, first instructor, and second instructor. *p < 0.1, **p < 0.05, ***p < 0.01. Panel B of table 7 augments equation 4 to allow the cross-semester demographic match eﬀects to vary by student–instructor familiarity. Speciﬁcally, we interact the de- mographic mismatch indicators with indicators for whether the student had the same instructor in both semesters.28 This idea is motivated by recent research by Hill and Jones (2018) in the primary school setting, who show that students, particularly non- white students, beneﬁt from having the same classroom teacher in consecutive years. Intuitively, having the same instructor in consecutive semesters would foster a stronger relationship and better understanding of expectations and learning styles, which in turn might mitigate the harmful eﬀects of demographic mismatch. Indeed, this is precisely what the interaction terms in panel B of table 7 show: The other-sex mismatch eﬀects on good grades are signiﬁcantly smaller, and indistinguishable from zero, for students who had the same instructor in both courses of the two-course sequence. 28. The familiarity indicator itself is subsumed by the “Course-2 FE.” l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / f / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d f . / f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 475 Effects of Demographic Mismatch 5 . C O N C L U S I O N We use rich student–instructor matched administrative data from a large, private, top-100 law school to provide novel evidence on the causal relationship between student–instructor demographic match and student outcomes in the law school context. Two-way student and course ﬁxed-eﬀects models provide arguably causal estimates of the impact of such mismatch on short-run (course-speciﬁc) outcomes, such as course grades. Sorting and balance tests provide no evidence of endogenous sorting on observables into classrooms, which is consistent with at least quasi-random assignment of students to course sections in the law school, buttressing a causal interpretation of these results. The baseline estimates suggest that having an other-race or other-sex instructor in a ﬁrst-year required course signiﬁcantly reduces the likelihood of earning a good grade (i.e., A or A−) in the course. Speciﬁcally, having an other-sex instructor reduces the likelihood of receiving a good grade by 1 percentage point (3 percent) and having an other-race instructor reduces the likelihood of receiving a good grade by 3 percentage points (10 percent). The most comparable estimate in the extant literature comes from Fairlie, Hoﬀmann, and Oreopoulos (2014), who ﬁnd that having a same-race commu- nity college instructor increases the probability of having a good grade ((cid:3) B) in ﬁrst-year undergraduate courses by about 3 percentage points (5 percent).29 That we document similarly sized eﬀects in ﬁrst-year courses at a top-100 law school suggests that even high-achieving college graduates’ graduate and professional school outcomes are inﬂu- enced by the demographic representation of their instructors. This result has the potential to contribute to pay gaps, as Oyer and Schaefer (2019) provide descriptive evidence of a wage-class rank gradient in law schools outside the top ten.30 However, we ﬁnd no eﬀects of student–instructor demographic mismatch on dropping courses or taking subsequent courses in the same ﬁeld, nor do we ﬁnd eﬀects at other points of the grade distribution. Consistent with previous research in the K–12 context, these eﬀects are stronger for underrepresented groups such as female and nonwhite students. The eﬀects are most pronounced for nonwhite female students. What behaviors drive these results? Unfortunately, the mechanisms at work cannot be precisely identiﬁed with these administrative data.31 However, we can make some informed speculation and perhaps rule out some possible channels. For example, the importance of blindly graded written exams in determining course grades suggests that instructors’ grading biases, conscious or not, are not driving these results (Lavy 2008; Hanna and Linden 2012). Of course, this does not rule out the possibility that implicit biases aﬀect how instructors interact with students, which could in turn aﬀect student engagement, and ultimately academic performance. That racial mismatch eﬀects are observed in medium-sized but not in small or large classes suggests that stereotype threat is not the sole explanation, as such eﬀects should not vanish in classrooms of a 29. Grade inﬂation in graduate school accounts for the diﬀerent deﬁnitions of “good grade,” as a C is often consid- ered failing in graduate and professional schools. 30. Our own analyses of the publicly available After the JD survey data conﬁrm the positive association between law school GPA and earnings both overall, and for speciﬁc demographic groups, for lawyers who attended non-top ten law schools. See Appendix B for details. 31. Dee (2004), Ferguson (2003), Gershenson, Holt, and Papageorge (2016), Papageorge, Gershenson, and Kang (2016), and Dee and Gershenson (2017) provide rich discussions of the channels through which demographic representation might aﬀect student outcomes. 476 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d . / f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Chris Birdsall, Seth Gershenson, and Raymond Zuniga certain size. Similarly, because sex mismatch eﬀects primarily exist in classrooms with fewer female students suggests, whatever the channel, they are more salient in less representative classroom environments. Moving forward, it is important that future re- search, in all academic environments, seeks to better understand the speciﬁc channels through which student–instructor demographic match eﬀects operate and to use this information to better design instructor-facing interventions and instructor training. Finally, these results suggest that diversity in the legal profession, and the status of women and people of color in the legal profession, would be improved by increas- ing the diversity of law school faculty. However, whether and how these results would generalize to other law schools, particularly those with less diverse student and fac- ulty populations, remains an open question worthy of future exploration. There are also questions regarding the general equilibrium responses to the hiring of a more diverse faculty, particularly in the law context, which might exacerbate demographic gaps in law oﬃces and the judiciary. There are also potential supply-side limitations of such faculty in the short run. For these reasons, another potential policy response is to provide law school (and university) faculty with theoretically informed implicit bias training, which has proven to be eﬀective in some early pilots (Carnes et al. 2015). Similarly, Darling-Hammong and Holmquist (2015) provide suggestions to law school faculty on how to better serve historically underrepresented students, many of which echo the theoretically-informed, “WISE” interventions and strategies advocated by so- cial psychologists (Walton 2014; Okonofua, Paunesku, and Walton 2016). ACKNOWLEDGMENTS Scott Carrell, Stephen B. Holt, Michal Kurlaender, Nicholas Papageorge, and participants at the 2016 APPAM Fall Conference, 2016 Access Group Legal Education Research Symposium, 2017 Royal Economic Society Symposium for Junior Researchers, and 2017 Society of Labor Economists Annual Meeting provided many helpful comments. The authors are thankful for ﬁnancial support from the Research Grant Program of the AccessLex Institute/Association for Institutional Research (AIR). Opinions reﬂect those of the authors and not necessarily those of the granting agency. We also thank Stephanie Cellini and three anonymous referees for their helpful comments and suggestions. Kimberly Trocha provided excellent research assistance. An earlier draft of this paper was circulated as IZA Discussion Paper No. 10459, “Stereotype Threat, Role Models, and Demographic Mismatch in an Elite Professional School Setting.” REFERENCES Alm, James, and John V. Winters. 2009. Distance and intrastate college student migration. Eco- nomics of Education Review 28(6): 728–738. Alsan, Marcella, Owen Garrick, and Grant C. Graziani. 2018. Does diversity matter for health? Experimental evidence from Oakland. NBER Working Paper No. 24787. Altonji, Joseph G., and Rebecca M. Blank. 1999. Race and gender in the labor market. 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Schapiro, and Kevin B. Soter. 2015. Are tenure track professors better teachers? Review of Economics and Statistics 97(4): 715–724. Gershenson, Seth, Stephen B. Holt, and Nicholas W. Papageorge. 2016. Who believes in me? The eﬀect of student–teacher demographic match on teacher expectations. Economics of Education Review 52:209–224. Guinier, Lani, Michelle Fine, Jane Balin, Ann Bartow, and Deborah Lee Stachel. 1994. Becoming gentlemen: Women’s experiences at one ivy league law school. University of Pennsylvania Law Review 143(1): 1–110. Hanna, Rema N., and Leigh L. Linden. 2012. Discrimination in grading. American Economic Jour- nal: Economic Policy 4(4): 146–168. Hausman, Jerry A. 1978. Speciﬁcation tests in econometrics. Econometrica 46(6): 1251–1271. Heckman, James J., and Tim Kautz. 2012. Hard evidence on soft skills. Labour Economics 19(4): 451–464. Hill, Andrew J., and Daniel B. Jones. 2018. A teacher who knows me: The academic beneﬁts of repeat student-teacher matches. Economics of Education Review 64: 1–12. Ho, Daniel E., and Mark G. Kelman. 2014. Does class size aﬀect the gender gap? A natural ex- periment in law. Journal of Legal Studies 43(2): 291–321. Hoﬀmann, Florian, and Philip Oreopoulos. 2009. A professor like me: The inﬂuence of instruc- tor gender on college achievement. Journal of Human Resources 44(2): 479–494. Holder, Eric H. 2001. The importance of diversity in the legal profession. Cardozo Law Review 23(6): 2241–2251. Holt, Stephen B., and Seth Gershenson. 2019. The impact of demographic representation on absences and suspensions. Policy Studies Journal 47(4): 1069–1099. Inzlicht, Michael, and Talia Ben-Zeev. 2000. A threatening intellectual environment: Why fe- males are susceptible to experiencing problem-solving deﬁcits in the presence of males. Psycho- logical Science 11(5): 365–371. l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / f / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d / f . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 479 Effects of Demographic Mismatch Lavy, Victor. 2008. Do gender stereotypes reduce girls’ or boys’ human capital outcomes? Evi- dence from a natural experiment. Journal of Public Economics 92(10): 2083–2105. Loury, Glenn C. 2009. The anatomy of racial inequality. Cambridge, MA: Harvard University Press. Lusher, Lester, Doug Campbell, and Scott Carrell. 2015. TAs like me: Racial interactions between graduate teaching assistants and undergraduates. NBER Working Paper No. 21568. Mustard, David B. 2001. Racial, ethnic, and gender disparities in sentencing: Evidence from the U.S. federal courts. Journal of Law and Economics 44(1): 285–314. Neumark, David, and Rosella Gardecki. 1998. Women helping women? Role model and mentor- ing eﬀects on female Ph.D. students in economics. Journal of Human Resources 33(1): 220–246. Okonofua, Jason A., David Paunesku, and Gregory M. Walton. 2016. Brief intervention to en- courage empathic discipline cuts suspension rates in half among adolescents. Proceedings of the National Academy of Sciences U.S.A. 113(19): 5221–5226. Oyer, Paul, and Scott Schaefer. 2015. Firm/employee matching: An industry study of U.S. lawyers. ILR Review 69(2): 378–404. Oyer, Paul, and Scott Schaefer. 2019. The returns to elite degrees: The case of American lawyers. ILR Review 72(2): 446–479. Papageorge, Nicholas W., Seth Gershenson, and Kyungmin Kang. 2016. Teacher expectations matter. IZA Discussion Paper No. 10165. Rachlinski, Jeﬀrey J., Sheri Lynn Johnson. 2009. Does unconscious racial bias aﬀect trial judges? Notre Dame Law Review 84(3): 1195–1246. Schochet, Peter Z. 2009. An approach for addressing the multiple testing problem in social policy impact evaluations. Evaluation Review 33(6): 539–567. Schwarcz, Daniel, and Dion Farganis. 2017. The impact of individualized feedback on law student performance. Journal of Legal Education 67(1): 139–175. Steele, Claude M. 1997. A threat in the air: How stereotypes shape intellectual identity and per- formance. American Psychologist 52(6): 613–629. Walton, Gregory M. 2014. The new science of wise psychological interventions. Current Directions in Psychological Science 23(1): 73–82. Wilkins, David B., and G. Mitu Gulati. 1996. Why are there so few black lawyers in corporate law ﬁrms? An institutional analysis. California Law Review 84(3): 493–625. Wood, Robert G., Mary E. Corcoran, and Paul N. Courant. 1993. Pay diﬀerences among the highly paid: The male–female earnings gap in lawyers’ salaries. Journal of Labor Economics 11(3): 417–441. 480 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . f / / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d f / . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Chris Birdsall, Seth Gershenson, and Raymond Zuniga A P P E N D I X A Table A.1. Baseline Model Allowing for Contemporaneous Spillovers Continuous Grade A/A— Grade (1) (2) (3) (4) −0.017** (0.007) −0.003 (0.013) −0.037** (0.016) −0.003 (0.011) Other-sex (OS) Another OS Other-race (OR) Another OR OS * Another OS OR * Another OR Observations 36,560 Course fixed effects Student fixed effects Yes Yes 0.017 (0.029) 0.033 (0.025) −0.053*** (0.019) −0.010 (0.014) −0.048* (0.028) 0.023 (0.022) 36,560 Yes Yes −0.012* (0.007) 0.009 (0.011) −0.028*** (0.011) −0.001 (0.010) 36,560 Yes Yes −0.004 (0.028) 0.021 (0.019) −0.028 (0.019) −0.001 (0.011) −0.016 (0.028) −0.000 (0.022) 36,560 Yes Yes Notes: Each column represents a different model specification. The outcomes are measured as follows: Continuous Grade measures a student’s received grade on a 0—4 scale (F—A). A/A— Grade is a binary indicator for whether a student received an A or A— grade. Standard errors in parentheses are clustered by student and instructor. *p < 0.1; **p < 0.05; ***p < 0.01. Table A.2. Mean Course Characteristics by Subject Subject Civil Procedure Constitutional Contracts Criminal Law Legal Writing Property Torts N 80 60 60 70 620 80 60 Course Size Female Students White Students Female Faculty White Faculty 83.1 83.1 75.0 76.8 15.5 85.0 79.2 0.60 0.58 0.59 0.59 0.59 0.59 0.58 0.65 0.63 0.62 0.65 0.63 0.64 0.63 0.21 0.14 0.31 0.57 0.50 0.60 0.42 0.82 0.69 0.84 0.62 0.92 0.79 1.00 Notes: The unit of analysis is course sections. Each statistic reported is the average across course sections: average size, percent female students in class, percent white students in class, percent of course sections taught by female faculty, and percent of course sections taught by white faculty. Table A.3. Impact of Demographic Mismatch on Non-Writing First-Year Required Course Outcomes Other-sex Other-race Differences in coefficients (P) Observations Continuous Grade A Grade A/A— Grade C, D, F Grade Take Another Dropped Course (1) −0.011 (0.008) −0.042** (0.017) 0.071* 28,290 (2) (3) −0.005 (0.004) −0.017** (0.007) 0.151 28,290 −0.012 (0.008) −0.034*** (0.011) 0.061* 28,290 (4) −0.001 (0.003) 0.011 (0.008) 0.119 28,290 (5) 0.016 (0.010) 0.000 (0.008) 0.198 18,620 (5) 0.000 (0.000) 0.001 (0.001) 0.271 28,400 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d f / . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 481 Effects of Demographic Mismatch Table A.3. Continued. Continuous Grade A Grade A/A— Grade C, D, F Grade Take Another Dropped Course Course fixed effects Student fixed effects (1) Yes Yes (2) Yes Yes (3) Yes Yes (4) Yes Yes (5) Yes Yes (5) Yes Yes Notes: Each column represents a different model specification. The outcomes are measured as follows: Continuous Grade measures a student’s received grade on a 0—4 scale (F—A); A Grade is a binary indicator for whether a student received an A grade; A or A— Grade is a binary indicator for whether a student received an A or A— grade; C, D, F Grade is a binary indicator for whether a student received a C, D, or F grade; Take Another is a binary indicator for whether a student takes a subsequent elective course in the same field after his first year; and Dropped Course is a binary indicator for whether a student drops the course before the end of the semester. Column 5 has fewer observations because not all required courses correspond to elective course subjects. Difference in coefficients compares Other-sex effect against Other-race effect. Standard errors in parentheses are clustered by student and instructor. *p < 0.1; **p < 0.05; ***p < 0.01. Table A.4. Average Partial Effects) Impact of Demographic Mismatch on First-Year Required Course Outcomes (Logit A/A— Grade C, D, F Grade Take Another Dropped Course Other-sex Other-race Female instructor Nonwhite instructor Nonwhite student Female student (1) −0.011** (0.005) −0.029*** (0.010) 0.029*** (0.005) 0.025*** (0.009) −0.088*** (0.012) 0.044*** (0.008) (2) 0.002 (0.002) 0.007 (0.004) −0.001 (0.003) −0.002 (0.003) 0.030*** (0.005) −0.019*** (0.004) Observations 36,560 36,560 (3) 0.012** (0.006) −0.008 (0.010) 0.002 (0.007) −0.009 (0.009) 0.038*** (0.013) 0.000 (0.009) 18,540 (4) 0.001 (0.000) 0.001 (0.001) −0.000 (0.001) 0.001 (0.001) −0.001 (0.001) −0.000 (0.001) 36,730 Notes: Each column represents a different model specification. The outcomes are measured as follows: A/A— Grade is a binary indicator for whether a student received an A or A— grade. C, D, F Grade is a binary indicator for whether a student received a C, D, or F grade. Take Another is a binary indicator for whether a student takes a subsequent course in the same field. Dropped Course is a binary indicator for whether a student drops the course before the end of the semester. Column 3 has fewer observations because not all required courses correspond to elective course subjects. Standard errors in parentheses are clustered by student and instructor. **p < 0.05; ***p < 0.01. Table A.5. Heterogeneity by Course Size and Percent Female (Nonwhite) in Course Course Size Percent Female (Nonwhite) in Course (1) (2) (3) (4) Other-sex (OS) OS * Course size OS * Course size (Sq) 0.003828 (0.024974) 0.000052 (0.001052) −0.000003 (0.000009) −0.245622 (0.176855) 482 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d / f . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 Chris Birdsall, Seth Gershenson, and Raymond Zuniga Table A.5. Continued. OS * Percent female OS * Percent female (Sq) Other-race (OR) OR * Course size OR * Course size (Sq) OR * Percent nonwhite Course Size Percent Female (Nonwhite) in Course (1) (2) (3) (4) 0.007005 (0.005837) −0.000051 (0.000048) 0.020580 (0.024309) −0.002240** (0.000928) 0.000018** (0.000008) 0.028642 (0.094617) −0.003086 (0.004580) 0.00004 (0.000056) 0.052* 36,560 Yes Yes l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . OR * Percent nonwhite (Sq) p value for joint significance tests Observations Course fixed effects Student fixed effects 0.076* 36,560 Yes Yes 0.005*** 36,560 Yes Yes 0.088* 36,560 Yes Yes Notes: The covariates are defined as follows: Other-sex is a binary indicator for whether the student’s sex is different from the instructor. Other-race is a binary indicator for whether the student’s race is different from the instructor. Course size measures the total number of students in the classroom. Percent Female measures the percentage of female students in the classroom. Percent Nonwhite measures the percentage of nonwhite students in the classroom. Sq indicates quadratic term. Standard errors in parentheses. *p < 0.1; **p < 0.05; ***p < 0.01. A P P E N D I X B This appendix uses publicly available data from After the JD (AJD) to document the descriptive relationship between law school grades and early-career salaries for individ- uals who earned JDs from non–top 10 law schools.32 The motivation for this appendix is to show the impacts of student–instructor mismatch on course grades documented in the current study likely translate into demographic pay gaps among early-career law professionals. The public-use AJD data report annual earnings in eight bins: <$40,000, $40,000- $49,999, $50,000-$59,999, $60,000-$74,999, $75,000-$99,999, $100,000- $124,999, $125,000-$149,999, and >$150,000. Respectivamente, we estimate descriptive
ordered-logit models in which this categorical annual-earnings variable is the de-
variable pendiente. Appendix table B.1 reports the ordered-logit coeﬃcients for the full
sample. The parsimonious speciﬁcations in columns 1 y 2 document the uncon-
ditional female pay gap and wage-GPA gradient, respectivamente. The omitted reference
category for the GPA variable is <3.0. Column 4 shows that these patterns are robust to controlling for law school quality. Because the ordered-logit coeﬃcients are not directly interpretable, table B.2 re- ports the average partial eﬀects (APE) of these covariates on the probability of being in each earnings band for the fully-speciﬁed, full-sample estimates reported in column 4 32. The AJD is a representative survey of new law-school graduates, conducted by the American Bar Foundation, in 2002, 2007, and 2010. See www.americanbarfoundation.org/research/project/118 for further information. / / f e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d / f . f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 483 Effects of Demographic Mismatch Table B.1. Descriptive Ordered-Logit Earnings Regressions: Coefficient Estimates (1) (2) (3) (4) −0.45*** (0.07) −0.02 (0.11) −0.10 (0.11) 0.62*** (0.13) 0.06 (0.19) −0.49*** (0.07) 0.11 (0.12) 0.04 (0.12) 0.63*** (0.14) 0.10 (0.19) 1.90*** (0.16) 1.65*** (0.13) 1.09*** (0.13) 0.59*** (0.12) 1.35*** (0.10) 1.82*** (0.16) 1.59*** (0.13) 1.04*** (0.13) 0.56*** (0.12) 1.34*** (0.10) Female Black Latinx Asian Other race > 3.75 grade point average (GPA)

3.5—3.74 GPA

3.25—3.49 GPA

3.0—3.24 GPA

Missing GPA

Top 10 law school

11—20 law school

21—100 law school

Observaciones

3,785

3,892

3,785

−0.49***
(0.07)

0.02
(0.11)
−0.01
(0.12)
0.42***
(0.13)

0.06
(0.20)
1.68***
(0.18)
1.42***
(0.14)
0.87***
(0.13)
0.48***
(0.12)
1.16***
(0.10)
2.21***
(0.15)
1.45***
(0.13)
0.38***
(0.07)

3,755

Notas: Each column represents a different model specification. Cut points not shown. Estándar
errors in parentheses.
***pag < 0.01. Table B.2. Descriptive Ordered-Logit Earnings Regressions: Average Partial Effects 0—39K 40—49K 50—59K 60—74K 75—99K 100—124K 125—149K (1) (2) (3) (4) (5) (6) (7) Female Black Latinx Asian Other race > 3.75 GPA

3.5—3.74 GPA

3.25—3.49 GPA

3.0—3.24 GPA

Missing GPA

0.04***
(0.01)
−0.00
(0.01)

0.00
(0.01)
−0.03***
(0.01)
−0.00
(0.02)
−0.13***
(0.02)
−0.11***
(0.01)
−0,07***
(0.01)
−0.04***
(0.01)
−0.09***
(0.01)

0.04***
(0.01)
−0.00
(0.01)

0.00
(0.01)
−0.04***
(0.01)
−0.00
(0.02)
−0.15***
(0.02)
−0.13***
(0.01)
−0.08***
(0.01)
−0.04***
(0.01)
−0.10***
(0.01)

0.02***
(0.00)
−0.00
(0.00)

0.00
(0.00)
−0.02***
(0.01)
−0.00
(0.01)
−0,07***
(0.01)
−0.06***
(0.01)
−0.03***
(0.01)
−0.02***
(0.01)
−0.05***
(0.00)

0.00**
(0.00)
−0.00
(0.00)

0.00
(0.00)
−0.00*
(0.00)
−0.00
(0.00)
−0.01**
(0.00)
−0.01**
(0.00)
−0.00**
(0.00)
−0.00*
(0.00)
−0.01**
(0.00)

−0.02***
(0.00)

0.00
(0.00)
−0.00
(0.00)
0.02***
(0.01)

0.00
(0.01)
0.06***
(0.01)
0.05***
(0.01)
0.03***
(0.01)
0.02***
(0.00)
0.04***
(0.00)

−0.02***
(0.00)

0.00
(0.00)
−0.00
(0.01)
0.02***
(0.01)

0.00
(0.01)
0.07***
(0.01)
0.06***
(0.01)
0.04***
(0.01)
0.02***
(0.01)
0.05***
(0.00)

−0.02***
(0.00)

0.00
(0.01)
−0.00
(0.01)
0.02***
(0.01)

0.00
(0.01)
0.08***
(0.01)
0.07***
(0.01)
0.04***
(0.01)
0.02***
(0.01)
0.06***
(0.01)

>150K)
(8)

−0.04***
(0.01)

0.00
(0.01)
−0.00
(0.01)
0.03***
(0.01)

0.00
(0.02)
0.13***
(0.01)
0.11***
(0.01)
0.07***
(0.01)
0.04***
(0.01)
0.09***
(0.01)

484

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oh
a
d
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d

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t
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5
3
4
5
7
1
8
9
3
7
4
5
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d
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0
2
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Chris Birdsall, Seth Gershenson, and Raymond Zuniga

Table B.2. Continuado.

0—39K

40—49K

50—59K

60—74K

75—99K

100—124K

125—149K

(1)

(2)

(3)

(4)

(5)

(6)

(7)

Top 10 law school

11-20 law school

21-100 law school

−0.17***
(0.01)
−0.11***
(0.01)
−0.03***
(0.01)

−0.20***
(0.02)
−0.13***
(0.01)
−0.03***
(0.01)

−0.09***
(0.01)
−0.06***
(0.01)
−0.02***
(0.00)

Observaciones

3,755

−0.01**
(0.00)
−0.01**
(0.00)
−0.00**
(0.00)

3,755

0.08***
(0.01)
0.06***
(0.01)
0.01***
(0.00)

3,755

0.09***
(0.01)
0.06***
(0.01)
0.02***
(0.00)

3,755

0.11***
(0.01)
0.07***
(0.01)
0.02***
(0.00)

3,755

>150K)
(8)

0.18***
(0.01)
0.12***
(0.01)
0.03***
(0.01)

3,755

Notas: Standard errors in parentheses.
*pag < 0.1; **p < 0.05; ***p < 0.01. Table B.3. Descriptive Ordered-Logit Earnings Regressions by Demographic Background: Coefficient Estimates Male (1) Female (2) White (3) Black (4) Latinx (5) −0.49*** (0.08) −0.97*** (0.23) −0.65** (0.27) Asian (6) −0.28 (0.25) 0.15 (0.16) 0.04 (0.17) 0.27 (0.20) 0.13 (0.28) 1.62*** (0.29) 1.54*** (0.19) 0.92*** (0.18) 0.43** (0.17) 1.15*** (0.14) 2.26*** (0.20) 1.47*** (0.17) 0.34*** (0.10) 1,995 −0.09 (0.16) −0.09 (0.18) 0.53*** (0.18) −0.03 (0.29) 1.70*** (0.22) 1.31*** (0.20) 0.83*** (0.19) 0.53*** (0.17) 1.18*** (0.15) 2.15*** (0.24) 1.43*** (0.20) 0.41*** (0.11) 1,760 1.69*** (0.19) 1.48*** (0.16) 0.87*** (0.15) 0.51*** (0.14) 1.27*** (0.12) 2.15*** (0.18) 1.51*** (0.16) 0.42*** (0.08) 2,703 17.99*** (1.07) 3.34*** (0.68) 2.41*** (0.64) 0.83** (0.39) 1.00*** (0.29) 2.49*** (0.41) 1.53*** (0.38) 0.36 (0.28) 330 0.61 (0.84) 2.86*** (0.81) 0.40 (0.53) 0.42 (0.43) 0.71** (0.33) 3.02*** (0.50) 0.85 (0.54) 0.33 (0.30) 312 1.44** (0.59) 0.62 (0.56) 0.48 (0.35) −0.10 (0.41) 2.08*** (0.45) 1.03*** (0.34) 0.13 (0.30) 341 Female Black Latinx Asian Other Race > 3.75 GPA

3.5—3.74 GPA

3.25—3.49 GPA

3.0—3.24 GPA

Missing GPA

Top 10 law school

11—20 law school

21—100 law school

Observaciones

Notas: Each column represents a different model specification. Cut points not shown. Standard errors in
parentheses.
**pag < 0.05; ***p < 0.01. of table B.1. Here we see that female lawyers are 2 to 4 percentage points more likely than male lawyers to be in the lowest-earning categories and 2 to 4 percentage points less likely than male lawyers to be in the highest-earning categories. The APE for the categorical GPA indicators show that each 0.25 increase in GPA is associated with a 2 to 4 percentage point increase in the probability of being in one of the high-earnings l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . / f / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d / . f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 485 Effects of Demographic Mismatch Table B.4. Descriptive Ordered-Logit Earnings Regressions by Law School Rank: Coefficient Estimates Top 10 (1) −0.55** (0.24) 0.07 (0.33) 0.42 (0.37) 0.57 (0.37) 1.13* (0.64) −0.12 (1.02) 0.80 (0.85) 0.97 (0.82) 0.42 (0.81) 0.52 (0.78) 370 11-20 (2) −0.44** (0.20) 0.11 (0.28) −0.60 (0.37) 0.23 (0.30) −0.36 (0.46) 2.72*** (0.43) 2.15*** (0.38) 1.50*** (0.42) 1.99*** (0.41) 2.40*** (0.33) 467 21-100 Outside 100 (3) (4) −0.44*** (0.10) −0.07 (0.17) −0.00 (0.17) 0.33* (0.20) −0.28 (0.26) 1.98*** (0.26) 1.62*** (0.21) 1.07*** (0.20) 0.42** (0.19) 1.33*** (0.16) 1,737 −0.60*** (0.12) 0.06 (0.23) 0.10 (0.27) 0.72*** (0.27) 0.67 (0.41) 1.54*** (0.31) 1.33*** (0.26) 0.50** (0.21) 0.41** (0.18) 0.90*** (0.16) 1,181 Female Black Latinx Asian Other race > 3.75 GPA

3.5—3.74 GPA

3.25—3.49 GPA

3.0—3.24 GPA

Missing GPA

Observaciones

Notas: Each column represents a different model specification. Cut points not
mostrado. Standard errors in parentheses.
*pag < 0.1; **p < 0.05; ***p < 0.01. brackets, and a symmetric decrease in the probability of being in a low-earning bracket. Importantly, this suggests that even a relatively small change in GPA attributable to student–instructor demographic mismatch in ﬁrst-year law courses might substan- tively aﬀect early-career earnings. Table B.3 estimates the fully speciﬁed ordered-logit model separately by sex and race. The key results here are: (1) the sex pay gap exists for white, black, and Latinx lawyers and (2) the wage-GPA gradient exists in the male, female, white, and black subsamples. Table B.4 similarly shows that the wage–GPA gradient exists for graduates of all law schools outside the U.S. News Top 10. This is consistent with results reported in Oyer and Schaefer (2019). The U.S. News rank of the law school studied in the current paper falls in the 21–100 range (column 3), for which grades are quite important. 486 l D o w n o a d e d f r o m h t t p : / / d i r e c t . m i t . f / / e d u e d p a r t i c e - p d l f / / / / 1 5 3 4 5 7 1 8 9 3 7 4 5 e d p _ a _ 0 0 2 8 0 p d / . f f b y g u e s t t o n 0 7 S e p e m b e r 2 0 2 3 THE EFFECTS OF DEMOGRAPHIC MISMATCH image

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