NBER WORKING PAPER SERIESSTILL WORTH THE TRIP?
SCHOOL BUSING EFFECTS IN BOSTON AND NEW YORK
Joshua Angrist
Guthrie Gray-Lobe
Clemence M. Idoux
Parag A. Pathak
Working Paper 30308
http://www.nber.org/papers/w30308

NATIONAL BUREAU OF ECONOMIC RESEARCH
1050 Massachusetts Avenue
Cambridge, MA 02138
July 2022

Thanks to Adrian Blattner, Kate Bradley, Nicolas Jimenez, Vendela Norman, Chetan Patel andLuke Stewart for exceptional research assistance and to Eryn Heying, Jennifer Jackson, Jim Shenand Anna Vallee for dependable administrative support. We gratefully acknowledge funding
from the Spencer Foundation. This paper reports on research conducted under data use
agreements between MIT, the project principal investigators (Angrist and Pathak), the Boston
Public Schools, and the New York City Department of Education. This paper reflects the views of
the authors alone. We are grateful to Zachary Bleemer, Jesse Bruhn, and Derek Neal forcomments and participants at the NBER Fall 2021 Education conference, Uppsala University,
CESifo, University of Chicago, and the 2022 IAAE meetings for feedback. The work discussed
here was funded in part by the Laura and John Arnold Foundation, the National Science
Foundation, and the W.T. Grant Foundation. Joshua Angrist's daughter teaches in a Boston
charter school. The views expressed herein are those of the authors and do not necessarily reflect
the views of the National Bureau of Economic Research.
NBER working papers are circulated for discussion and comment purposes. They have not been
peer-reviewed or been subject to the review by the NBER Board of Directors that accompanies
official NBER publications.
© 2022 by Joshua Angrist, Guthrie Gray-Lobe, Clemence M. Idoux, and Parag A. Pathak. All
rights reserved. Short sections of text, not to exceed two paragraphs, may be quoted without
explicit permission provided that full credit, including © notice, is given to the source.

Still Worth the Trip? School Busing Effects in Boston and New York
Joshua Angrist, Guthrie Gray-Lobe, Clemence M. Idoux, and Parag A. Pathak
NBER Working Paper No. 30308
July 2022
JEL No. D47,I20
ABSTRACT
School assignment in Boston and New York City came to national attention in the 1970s as
courts across the country tried to integrate schools. Today, district-wide choice allows Boston and
New York students to enroll far from home, perhaps enhancing integration. Urban schooltransportation is increasingly costly, however, and has unclear integration and educationconsequences. We estimate the causal effects of non-neighborhood school enrollment and school
travel on integration, achievement, and college enrollment using an identification strategy that
exploits partly-random assignment in the Boston and New York school matches. Instrumental
variables estimates suggest distance and travel boost integration for those who choose to travel,
but have little or no effect on test scores and college attendance. We argue that small effects on
educational outcomes reflect modest effects of distance and travel on school quality as measured
by value-added.
Joshua Angrist
Department of Economics, E52-436
MIT
77 Massachusetts Avenue
Cambridge, MA 02139
and NBER
angrist@mit.edu
Guthrie Gray-Lobe
University of Chicago
graylobe@uchicago.edu

Clemence M. Idoux
MIT
cidoux@mit.edu
Parag A. Pathak
Department of Economics, E52-426
MIT
77 Massachusetts Avenue
Cambridge, MA 02139
and NBER
ppathak@mit.edu

A data appendix is available at http://www.nber.org/data-appendix/w30308

1

Introduction
Bus transportation has been an integral part of the public education system for years,
and was perhaps the single most important factor in the transition from the one-roomschoolhouse to the consolidated school ... we find no basis for holding that the local
school authorities may not be required to employ bus transportation as one tool ofschool desegregation. Desegregation cannot be limited to the walk-in school.
Swann v. Charlotte-Mecklenburg Board of Education, 402 U.S. 1, 1971
One of the most polarizing policy debates in American cities concerns the impact of school

assignment on racial integration in public schools. Neighborhood-based assignment, once common
in cities and still the norm in suburban school districts, necessarily reflects patterns of residential
segregation. Non-neighborhood school assignment may mitigate the segregating effects of zoned
neighborhood assignment. At the same time, travel to non-neighborhood schools can be costly.
This is documented in Figure 1, which plots average annual per-pupil transportation expenditurein the 100 largest US school districts (by enrollment) for 1997-2017. The Boston and New York City
school districts are at or near the top of per-pupil transportation costs, spending $1,200-$2,100 per
student (in 2017 dollars) annually. Boston and New York transportation spending is also growing:
the cost of getting kids to school in these bellwether cities roughly doubled in the two decades
covered by the figure.
School transportation expenditures today are driven in part by the fact that many large urban
school districts allow families to choose schools district-wide, lengthening school commutes for some.
District-wide choice is a feature of school assignment in Boston, Chicago, Denver, Indianapolis,
Newark, New Orleans, Tulsa, and Washington, DC, to name a few. In choice districts, seats atover-subscribed schools are typically allocated by algorithms that reflect family preferences in theform of a rank-order list and a limited set of school priorities. In the 1970s and 1980s, by contrast,
non-neighborhood schooling in urban districts arose largely through court action (or the threat ofcourt action) meant to integrate segregated schools. Today’s voluntary choice schemes evolved as
courts withdrew. Choice in large urban districts is appealing because choice systems potentiallydecouple school assignment from underlying residential segregation. Moreover, where school quality
is unevenly distributed over neighborhoods, district-wide choice affords all students a shot at schools
viewed as high-quality.1
This paper asks whether school travel in the modern choice paradigm is working as hoped,
boosting integration and learning, especially for minority students. Our investigation focuses on
Boston and New York, two cities of special interest because of their high transportation costs andbecause they’ve long been battlegrounds in the fight over school integration. We estimate the effects
of non-neighborhood school enrollment for students for whom school travel is facilitated by school
choice. In both cities, students who opt for non-neighborhood schooling have higher test scores and1

An extensive literature examines the design and impact of modern school choice systems. Empirical analyses
include Chubb and Moe (1990), Hoxby (2003), and Kahlenberg (2003); theoretical models of school choice aredeveloped in Avery and Pathak (2021), Barseghyan, Clark and Coate (2019), and Grigoryan (2021).

1

are more likely to go to college than those who travel less. But these estimates may reflect selection
bias arising from the fact that more motivated or better-off families are more likely to travel.
We solve the problem of selection bias using the conditional random assignment to schools
embedded in Boston and New York’s school matching algorithms. A given student may be offereda seat at a school in his or neighborhood, or a seat farther away. Conditional on an applicant’s
preferences and school priorities, modern choice algorithms randomize seat assignment, thereby
manipulating distance and travel independently of potential outcomes. The estimation strategy that
exploits this variation builds on the propensity score and instrumental variables methods developedin Abdulkadiroğlu et al. (2017) and Abdulkadiroğlu et al. (2022). These methods are extended here
to causal models where the control function needed to eliminate omitted variables bias depends ona multinomial propensity score as well as a vector of observed covariates.2 This extension addresses
the fact that non-neighborhood assignment depends on an applicant’s residential location as wellas on their assigned school.
Instrumental variables (IV) estimates using conditionally randomized school offers as instruments for school travel show that the modern choice paradigm helps integrate schools. Minority
applicants who travel enroll in schools with fewer minority peers as a result. About forty percent of
our sample of students attend schools that have more than 90% Black or Hispanic peers, a measureof minority isolation.3 Non-neighborhood school enrollment decreases minority isolation markedly.
For Black Boston students, in particular, non-neighborhood attendance reduces the probability ofattending an isolated school by 17 percentage points. The integrating effects of non-neighborhood
assignment, however, do not appear to increase student achievement or college-going. IV estimatesof non-neighborhood school effects on achievement are close to zero and mostly precise enough torule out modest positive effects. Non-neighborhood school attendance likewise appears to leavecollege attendance unchanged. Models that parameterize non-neighborhood enrollment by travel
time generate similar results.
Non-neighborhood schools may change the school environment by altering class size or characteristics of instructional staff, as well as through integration. We summarize school-based effectsof travel with school value-added, a measure of a school’s causal effect on achievement. We thenask whether modest effects of travel on achievement and college attendance can be explained bymodest effects on value-added. Travel indeed results in only small increases in value-added. Moreover, models that use both offered travel and offered value-added as instruments for value-added of
the school attended pass an over-identification test. This result supports an exclusion restriction
2
Heckman and Robb (1985) introduce the term control function to refer to functions that, when added to aregression model for causal effects, eliminate selection bias.
3
Such measures have a long history in public discussion of segregated schools. The Morgan v. Hennigan 379 F.
Supp. 410 (D. Mass. 1974) decision, for example, discusses “racially identifiable schools,” noting that 84% of white
students attended schools that were more than 80% white, while 62% of Black students attended schools that weremore than 70% Black. Cohen (2021) likewise define intensely segregated schools to be those with 90% students ofcolor, defined as all nonwhites. Similarly, Potter (2022) defines segregated schools as those where 90% of students areof the same race. Descriptive evidence that racial isolation is harmful to minorities has motivated integration policy
since at least United States Commission on Civil Rights (1967), a companion to the influential Coleman Report(Coleman, 1966).

2

claiming that travel has little or no effect on education outcomes except through value-added. A
parsimonious explanation for our findings, therefore, is that travel facilitates integration but does
not translate into large enough changes in value-added to change education outcomes much.
Our analysis builds on a wide range of previous work. A recent study closely related to ours
by Cordes, Rick and Schwartz (2022) concludes that long bus rides reduce attendance and increasechronic absenteeism among New York elementary school students, with little effect on test scores(this study uses idiosyncratic variation in bus routing to identify causal effects). Chingos andMonarrez (2020) surveys mostly-descriptive research on the link between school choice and segregation, while Monarrez (2020) considers the extent to which race determines school attendanceboundaries. The analysis reported here likewise connects with extensive academic research considering the effects of school choice on students, including Hastings and Weinstein (2008), Deming(2011), Deming et al. (2014), and Campos and Kearns (2022). Other related research examines
the consequences of attendance at various types of schools or sectors, such as charter and pilot
schools, exam schools, magnet schools, and schools with high value-added.4 This work largely
ignores questions related to distance and travel.
We also build on research that considers integration effects directly, including Welch and Light(1987), Hoxby (2000b), Rossell and Armor (1996), Rivkin and Welch (2006), and Hanushek, Kainand Rivkin (2009). The end of de jure segregation has been shown to have yielded importanteconomic gains for Blacks (e.g., Smith and Welch (1989) and Card and Krueger (1992)). Guryan(2004), Johnson (2019), and Anstreicher, Fletcher and Thompson (2022) likewise report estimatesshowing integration-induced education gains for Black students outside the South. But the changes
studied in this earlier work typically coincided with major changes in per-pupil expenditure. Evidence from recent periods is more mixed (see, e.g., Hoxby (2000b) and Card and Rothstein (2007)).
This may reflect the fact that average spending per-pupil today often increases with higher minority
enrollment, reflecting the higher costs of educating special needs and limited English proficiency
students. It’s noteworthy, therefore, that our econometric framework uses school assignment lotteries to isolate distance and travel effects while implicitly holding district-level variables related
to spending fixed.
The next section sketches the history of desegregation efforts and assignment regimes in the
Boston and New York school districts. Section 3 discusses the data used in this study and presents
descriptive statistics. Section 4 reports OLS estimates and details the econometric framework used
to estimate causal effects of school distance and travel. Section 5 reports the estimates coming
out of this framework. Following a discussion of effects on achievement and college attendance,
this section considers causal effects on school value-added. The paper concludes with a simulation
characterizing the integration consequences of a neighborhood-focused cost-reducing centralized
4

A non-exhaustive list of relevant studies includes Cullen, Jacob and Levitt (2006); Abdulkadiroğlu et al. (2011);
Abdulkadiroğlu et al. (2017); Angrist et al. (2016a); Lucas and Mbiti (2014); Ajayi (2014); Hoxby, Murarka and Kang
(2009); Dobbie and Fryer (2011, 2014); Abdulkadiroğlu et al. (2016). Chubb and Moe (1990) suggest that choiceengenders competition that may promote quality; research exploring these considerations includes Hoxby (2000a),
Hastings, Kane and Staiger (2009), and Campos and Kearns (2022).

3

assignment scheme. The simulation highlights the trade-offs between lower transportation spending
and reduced integration. At the same time, while integration may be of intrinsic value, our estimatessuggest that in urban districts today, reduced integration is unlikely to reduce human capital.

2

Background

2.1

A Tale of Two Cities: Court-Ordered and Voluntary Integration

A seemingly quotidian matter, school transportation in many districts is the legacy of decades ofracial strife. The debate over busing in the Boston Public Schools (BPS) came to national attentionin April 1976, when the front page of the Boston Herald American featured a photo captioned “TheSoiling of Old Glory” (Masur, 2008). Snapped on Boston’s City Hall Plaza, this picture showed
an angry white teen using the American flag to attack African American attorney Ted Landsmark.
The attacker was a participant in an unruly and sometimes-violent anti-school-busing protest, whilethe victim was a bystander soon to play a prominent role in Boston school policy debates.
Massachusetts’ Racial Imbalance Act of 1965 laid the legal groundwork for school busing in
Boston. The Act defined racial imbalance in statistical terms and required that schools deemed
racially imbalanced desegregate or lose state funding. This legislation notwithstanding, until 1974,
Boston students attended schools in catchment areas designed to segregate by race. The elected
Boston School Committee of the 1960s failed to cooperate with state efforts to desegregate schools.
School committee defiance ultimately led to a 1974 Federal District Court ruling imposing thestate’s busing plan on the city. United States District Judge Arthur Garrity, the presiding judge
in the case, effectively managed Boston school assignment until 1983, with the state taking overthrough 1988. Garrity oversaw a mandatory busing plan that divided Boston into 867 residential
geocodes (shown in Figure A2). Each geocode was paired with a particular school in an effort toengineer racially-balanced enrollment. Only in 1989 did responsibility for school assignment revert
to the district.
Boston’s “controlled choice” assignment plan of the early 1990s, described in Willie and Alves(1996) and Willie, Edwards and Alves (2002), initially targeted racial balance. In 1997, however,the Boston desegregation case was officially closed. Two years later, the Boston School Committee
voted to eliminate the use of race and ethnicity for purposes of school assignment. Since the 20002001 school year, Boston school assignment has ignored race. From 1999 to 2004, the nascent
Boston school match used the immediate acceptance algorithm, a widely-criticized assignment
mechanism (Abdulkadiroğlu and Sönmez, 2003; Pathak and Sönmez, 2008). The Boston school
match has since employed the student-proposing deferred acceptance algorithm (DA) to assign
seats at public schools other than charter and exam schools. DA in Boston uses a random lottery
number to distinguish otherwise identical applicants. The Boston match relies on choice rather
than court-ordered busing to facilitate school access across neighborhood.5
5The match includes traditional and pilot schools. Boston pilot schools, run by the district, are meant to bea model halfway between the broad autonomy of state-authorized charter schools and traditional public schools.

4Following the end of court-ordered busing in Boston, intense segregation of Black and Hispanic
students initially increased. Figure 2 describes the evolution of school-level racial exposure from1988 to 2018, plotting the proportion of a student’s schoolmates who are Black or Hispanic, as
well as the proportion attending racially isolated schools, defined here as schools that are at least
80% or at least 90% Black or Hispanic. Panel (a) of the figure shows that in 1988, less than 15
percent of Boston’s Black students were enrolled in intensely segregated schools, defined as thosewith at least 90 percent minority enrollment. By 2003, this figure peaked at 50 percent. While
Black students’ exposure to other Black students has fallen since 2003, Black exposure to Hispanics
has increased. The combination of falling Black exposure and rising Hispanic exposure generated
relatively stable combined minority exposure over time. A measure of minority isolation basedon an 80% threshold likewise stabilized around 2003. As can be seen on the right side of Panel(a), the evolution of Hispanic exposure to minority peers in Boston mostly mirrors that seen forBlacks. A higher level and more steeply-sloping increase in Boston Hispanic’s peer share Hispanic
is a noteworthy difference.6
Desegregation efforts in New York have been voluntary rather than a consequence of court
action. In the 1950s and 1960s, New York City school assignment was mostly neighborhoodbased. Unsurprisingly, segregated neighborhoods led to similarly segregated neighborhood schools,
though not necessarily by design. In the 1960s, critics of the city’s de facto segregation argued
that schools attended by Black children were overcrowded, run-down, and staffed by inexperienced
teachers. Attempts both to mandate (and to proscribe) cross-neighborhood busing neverthelessfoundered (Delmont, 2016). Dissatisfaction with educational opportunities for New York’s minority
children came to a head in February 1964, with a boycott in which nearly half a million mostly
nonwhite students stayed home, one of the largest protests in US history. The anti-segregation
boycott was followed that year by a white-led counter-boycott. Decentralized community control ofschools gave way in 2004 to city-wide administration through the NYC Department of Education(Abdulkadiroğlu et al., 2005; Ravitch, 2011). Since then, New Yorkers have debated the role ofneighborhoods and other geographical considerations in the city’s assignment system. A 2021
reform proposal, for instance, aimed to remove school priorities based on neighborhoods in thecentralized match (Veiga, 2021).
Contemporary discussions of New York school segregation often focus on the fact that white andupper income families have many options that effectively bypass mostly-minority traditional publicschools.7 Alternative options include private schools, screened public schools that select applicants
according to a variety of criteria, and highly coveted seats at the city’s exam or specialized highschools, including the renowned Stuyvesant, Brooklyn Tech, and Bronx Science. New York’s manyother selective enrollment “screened schools” came to prominence in the 1970s, when the city
Abdulkadiroğlu et al. (2011) estimates charter and pilot school effects on test scores.
6
Data for Figure 2 (further detailed in Online Appendix B) are from the Common Core survey, documented in
https://nces.ed.gov/ccd/pubschuniv.asp. Caetano and Maheshri (2022) note the growing importance of Hispanic
enrollment for segregation trends nationwide.
7
This viewpoint is reflected in the New York Times’ widely-heard 2020 podcast, Nice White Parents.

5expanded the use of selective admissions in the hope of encouraging mostly white and Asian middle
class families to remain in city schools.
Measures of segregation in New York public schools have declined since the late 1990s, fallingfrom levels much above those initially seen in Boston. New York segregation trends are documented
in Panel (b) of Figure 2. In 1988, over 70% of Black New York students attended intensely segregated schools (again, defined as those with over 90% minority enrollment). By 2018, this proportion
had fallen to around 50%. The trend in minority isolation based on an 80% cutoff, as well as overallminority exposure, slopes more gently downward over this period than does the trend in intense
segregation. Still, minority isolation and minority exposure in New York show a marked drop over
the three decades spanned by Figure 2. Like Boston, New York has seen steady growth in the
Hispanic enrollment share, a fact reflected in increasing exposure to Hispanic peers and decreasing
exposure to Black peers among both Black and Hispanic students. As in Boston, the level of peer
share Hispanic is markedly higher for Hispanic New Yorkers than for Blacks.8
Boston and New York segregation patterns have partly converged since the 1980s. While New
York segregation has trended lower for longer than in Boston, in both cities, peer share minority is
recently around 75%, while intense segregation has fallen since the turn of the century. Both cities
have also seen a remarkable reduction in exposure to Black peers for both Black and Hispanic students, with a corresponding increase in Hispanic exposure. Motivated by these evolving patterns ofracial diversity, our investigation considers school distance and travel effects on Black and Hispanic
students separately as well as jointly.

2.2

Busing and Choice

Since the early 2000s, Boston has assigned seats centrally in a match that takes as inputs school
priorities over students and student preferences over schools, which students rank. From 200105, Boston assigned students using the immediate acceptance algorithm. Since 2006, the Boston
match has employed a version of DA, with priority given to siblings of enrolled students and to
students residing in a school’s designated walk zone. Appendix Figure A2 maps Boston geocodes,
originally defined in the Garrity era and used during our study period. Walk zones for each school
are determined by drawing a one-mile radius circle around the school; residents of any geocode
intersected by this circle live in the school’s walk zone (in what follows, we call these “Garrity walkzones”).9
The Boston match, which covers traditional and pilot schools, breaks ties using a single randomlottery number assigned to each student. Boston students may also attend publicly-funded charterschools and one of three public selective-enrollment exam schools. Boston charter schools run single8

Rising Hispanic exposure and declining exposure to Black peers are typical of America’s large urban districts,
especially from the point of view of Black students. This is documented in Appendix Figure A1, which reports
segregation trends in the largest 100 districts with minority enrollment shares comparable to those of Boston and
New York.
9
See Dur et al. (2018) for more on Boston’s walk-zone policy. Motivated by high transportation costs, Boston
adopted a “Home-Based plan” in 2014 limiting the set of schools each applicant might rank, while still including atleast some with good outcomes (Shi, 2015; Pathak and Shi, 2021).

6

school lotteries, while Boston exam schools run a separate DA match using a weighted average of
middle school GPA and an admissions exam score as tie-breaker period. While Boston charter andexam school students are eligible for transportation services, we focus on schools in the traditional
sector since effects of travel to schools outside the traditional sector are harder to interpret.10
New York centralized assignment is also based on student preferences, school-specific priorities,
and a DA match. New York priorities depend on many factors, including geography and attendanceat an open house prior to the match. Within New York priority groups, tie-breaking is based either
on a random lottery number or on school-specific non-lottery criteria like test scores, interviews,
and auditions. Schools using non-lottery tie-breakers are known as “screened schools,” while thoseusing lottery tie-breaking are said to be “unscreened.” The New York high school match excludes
charter schools and a few highly selective exam schools such as Stuyvesant and Bronx Science(these are called “specialized high schools” in New York vernacular). As in Boston, New York
exam schools run a separate match.
Sixth graders in Boston currently qualify for yellow school bus service if their home-school
walking distance exceeds 1.5 miles. All Boston students in grade 7 and higher qualify for passes
granting free use of public city transport from September through June (BPS, 2021).11 In New
York, all high school students who live farther than 0.5 miles from school are eligible for MetroCards
granting free use of city subways and buses (NYC, 2021).12

3

Data and Samples

We obtained BPS data on all applicants for 6th and 9th grade seats in the centralized middle
and high school matches covering the school years beginning fall 2002-13. Match files include
information on applicants’ preferences over schools, school priorities, and lottery tie-breakers. Data
on school enrollment comes from the Massachusetts Department of Elementary and Secondary
Education (DESE). DESE files contain school enrollment data, as well as demographic information
including race, subsidized lunch status, sex, special education status, and language proficiency
status. We also obtained DESE data from the Massachusetts Comprehensive Assessment System(MCAS), a standardized assessment taken by all Massachusetts public school students. MCAS tests
are taken in Grades 3-10. MCAS outcomes examined here are Grade 6 Math scores and Grade 7
ELA scores for Grade 6 applicants and Grade 10 scores for Grade 9 applicants. Baseline scoresare from 4th grade for middle school applicants and from Grades 7-8 for high school applicants.13
10
Boston’s three exam schools admit students mainly in 7th and 9th grade. Abdulkadiroğlu, Angrist and Pathak(2014) use the exam school match to estimate causal effects of exam school attendance on educational outcomesin Boston and New York. Abdulkadiroğlu et al. (2011) and Cohodes, Setren and Walters (2021) use single-school
charter lotteries to estimate Boston charter effects.
11
Boston 7th and 8th graders were bused until 2014-15 (BPS, 2014b).
12
Until 2019, students in grades 7-12 living between 0.5 and 1.5 qualified for half-fare bus-only MetroCards(Corcoran, 2018).
13
The ELA baseline changes because MCAS testing expanded during our sample period. Grade 7 ELA scores areused for applicants enrolled in Grade 9 in school years 2002-03 through 2005-06 and Grade 8 ELA scores are used
for applicants enrolled in Grade 9 in school years 2006-07 through 2013-2014.

7

Test scores are standardized by test-grade-year to have mean zero and unit variance within asubject-grade-year among enrolled students in Boston in our sample who are tested in a given year.
College outcomes for Boston high school students are measured using data from the National
Student Clearinghouse (NSC) database. NSC data were obtained by DESE, which aims to match
Massachusetts public school graduates to NSC every year and matches non-graduates every otheryear. The NSC records supplied by DESE are used to code dummies for any college enrollment
and for four-year college enrollment.
The New York Department of Education (DOE) provided data on applicants to 9th grade
public high school programs from fall 2012 to fall 2016.14 New York application files include
all information used in the high school match. The DOE also provided information on student
enrollment, residential location, and demographic characteristics.
New York test score data come from two sorts of assessments. SAT scores, from tests taken
mostly in 11th grade, provide achievement outcomes. Baseline test score data are from New YorkState standardized Math and ELA assessments taken in 6th grade. For purposes of our analysis,
all scores are standardized to have mean zero and unit variance in the population of New York
charter, traditional public school, and exam school students, separately by subject, grade, andyear. Data on New York graduates’ college enrollment data come from the DOE’s annual matchof its graduates to the NSC and were also provided by the DOE.
Our analysis examines two busing-related treatments, the first related to distance in the formof non-neighborhood schools, the second a measure of travel time. For Boston students, nonneighborhood assignment and enrollment are defined according to whether students live in a school’s
Garrity walk zone. For New York students, non-neighborhood schooling is defined according towhether students are assigned or enroll at a school outside their district of residence (The DOE
partitions New York city into 32 districts). In both cities, travel time to school is given by public
transit travel time between a student’s residence and school, setting an arrival time of 8:00 am
on January 31st, 2022. Travel time is the shortest combination of walking, local and express
bus, and subway modes, estimated using the HERE Public Transit API. Residential addresses areapproximate (for Boston, this is the centroid of the geocode of residence; for New York, this is
the centroid of the census tract of residence). A set of online appendices further detail the data,
sample, and variable construction.
Finally, as noted in the discussion of segregation trends, we focus on impacts on Black and Hispanic students as well as on students overall. This focus reflects public interest in school quality fordisadvantaged minorities and decades of scholarship documenting important changes in the qualityof schools minority students attend (see, e.g., Welch and Light (1987); Card and Krueger (1992);
Rivkin and Welch (2006)). Moreover, as in many large urban districts that pay for transportation,
the Boston and New York public schools population is predominantly Black or Hispanic. Because
most busing is within-district, we leave study of relatively rare inter-district busing programs (such14

Exam and charter schools do not participate in the centralized high school match. See Abdulkadiroğlu, Pathak
and Roth (2005) for a detailed description of New York’s exam-school match.

8

as the Massachusetts Metco program) for future work.

3.1

Sample Characteristics

Table 1 describes the students in our analysis samples. Over 70% of the Boston and New York
students bodies are Black or Hispanic, and three-fourths have household incomes low enough toqualify for a free or reduced-price lunch. Students in both districts travel on average between 33
and 36 minutes to school each way.15 Roughly three-quarters of Boston match applicants ranka non-neighborhood school first, and a similar fraction enroll outside their neighborhood. The
demand for non-neighborhood enrollment is almost as high in New York, where roughly two-thirds
of applicants rank a non-neighborhood option first with a similar proportion enrolling out of theirneighborhood.
As can be seen by comparing the first two columns in the table, Boston students who enroll in
non-neighborhood schools have demographic characteristics much like those in the overall sample.
The most noteworthy difference between the full and neighborhood-enrolled Boston samples ishigher baseline scores in the latter. This partly reflects enrollment in charter and exam schools,
which are defined as non-neighborhood for all applicants for purposes of this table. Exam schools
in particular tend to enroll higher achievers (Abdulkadiroğlu et al., 2011).
The IV strategy used to estimate causal effects looks at match participants only. Non-applicantsin Boston are mostly continuing 6th graders enrolled in K-8 schools or those applying to charterand exam schools only. The New York applicant sample excludes high-needs special education
students, who obtain assignments outside the match, as well as students who decide to enroll in
the city’s public schools after the match.16 Appendix Table A1 details the sample selection rules
used to define our analysis samples.
With a few exceptions, applicants have demographic characteristics broadly similar to thoseof the enrolled sample. In particular, Boston applicants are a little more likely to be low income:column 3 shows that 79% of applicants qualify for a subsidized lunch vs 75% of those enrolled
in Boston. Boston applicants also have lower baseline test scores. Again, this difference can be
explained, at least in part, by the fact that the applicant sample excludes students who applied
only to exam or charter schools.
The New York applicant and enrolled student samples likewise appear demographically similar.
At the same time, mean baseline scores for New York applicants exceed mean baseline scores in
the New York enrolled sample. This reflects the exclusion of many special education students fromthe former. Note also that while our applicant samples exclude those who apply to charter andexam schools only, they include match participants ultimately seated in a charter or exam school.
It’s important, therefore, that the instrumental variables used to identify causal effects of distance15
Elementary school students travel less. Focusing on Grades 3-6 in New York and using data from the NYC
Office of Pupil Transportation, Cordes, Rick and Schwartz (2022) report that the average home-to-school travel timeis 21.1 minutes.
16
Students whose individualized education program (IEP) places them in a designated special needs category are
assigned outside the match (NYC Match, 2021). Student who arrive over the summer are placed administratively.

9and travel are uncorrelated with charter and exam-school enrollment in the sample used for causal
analysis (this is shown in Appendix Table A2).
The experimental samples used for causal inference, described in columns 4 and 8 of Table
1, consist of the set of applicants for whom school assignment is not deterministic given theirpreferences and priorities. In other words, this sample contains applicants whose assignments
can be changed by redrawing tie-breakers. Just over one-quarter of New York applicants androughly 38% of Boston applicants are subject to a tie-breaking experiment. In data from bothcities, minority and low income (defined by free or reduced-price lunch eligibility) applicants are
disproportionately likely to be subject to experimental variation in assignment. Baseline scoresfor the experimental samples are also lower than among all applicants, especially in New York.
The lower baseline scores in the New York experimental sample reflect New York’s many screened
schools: as we explain below, screened school tie-breaking generates experimental variation local
to screened school admissions cutoffs. Students with high baseline scores are therefore more likely
to be sure of obtaining a screened-school seat.

4

Econometric Framework

4.1

OLS Estimates

We are interested in the causal effects of school distance and travel on the school environment
and academic outcomes. Ordinary least squares (OLS) estimates of the relationship between nonneighborhood enrollment and academic achievement provide a natural benchmark for the IV estimates that follow. OLS estimates are generated by fitting a model that can be written:
Yi = αGi + Xi0 Γ + ηi ,(1)

where Gi indicates non-neighborhood school attendance, Xi is a vector of controls, and ηi is a regression residual. Coefficient α is the parameter of interest. In Boston data, Gi indicates enrollment
at a school outside a student’s Garrity walk zone. In New York data, Gi indicates out-of-district
enrollment.
Equation (1) is estimated on the sample of enrolled students (a subset of the enrolled sample
described in the first column of Table 1, limited to students with data on residential location andoutcomes). Covariate vector Xi includes dummies for race, gender, special needs status, free or
reduced-price lunch eligibility, and English proficiency status; along with grade and year dummies.
To control for differences across neighborhoods, equation (1) includes fixed effects for each walkzone in Boston and for each district in New York (these are determined by students’ residential
address). Given our focus on traditional public schools, OLS estimates come from models that
include dummies for exam and charter sector enrollment, and a dummy for match participation.
Models for New York add dummies for enrollment in District 75 or 79, district codes allocatedto high-needs special education students and students with other unique needs (e.g., incarcerated

10

youth or those pursuing a GED). The dependent variable, Yi , is a test score or a measure of college
enrollment. Boston test scores are from the MCAS (6th grade Math and 7th grade ELA for middle
school, 10th grade Math and ELA for high school). New York test scores are from the SAT, taken
by approximately 70% of students.
Boston students who enroll out-of-neighborhood tend to have higher average test scores and are
more likely to go to college than students who attend schools closer to home. This is documented
in the first three columns of Table 2, which reports estimates of α in equation (1) separately for all,Black, and Hispanic students. Specifically, Table 2 shows that Boston students who enroll beyond
their neighborhood score about 0.06σ higher on MCAS Math tests and roughly 0.05σ higher on
MCAS ELA tests. Boston students who enroll in non-neighborhood schools are also 4.3 percentage
points more likely to enroll in college and 3.6 percentage points more likely to enroll in a four-yearcollege. Estimates for subsamples of Black and Hispanic students are similar.
OLS estimates for New York also show a strong association between achievement and nonneighborhood enrollment. New York students attending non-neighborhood schools score roughly
0.07σ higher on SAT math and 0.08σ higher on SAT reading, results reported in column 4 of Table
2. The corresponding estimated achievement gains for minority New Yorkers at non-neighborhood
schools are a little smaller, though still substantial. And non-neighborhood enrollment in New
York is associated with higher rates of college attendance and four-year college enrollment, though
not as much as in Boston.17 It remains to be seen, however, whether the association between nonneighborhood schooling and educational outcomes documented in Table 2 reflects causal effects or
selection bias.

4.2

Identification and Estimation of Causal Effects

Tie-breaking in the Boston and New York school assignment algorithms generates a research designthat identifies causal effects. In both cities, applicants submit rank-order lists of preferences forschool programs and are granted priorities by each program (many New York schools run multiple
programs, each admitting separately). We refer to an applicant’s preferences and priorities theirtype, denoted θi for applicant i. School assignment differences for students with the same value ofθ are due solely to the tie-breaking embedded in the match.
Boston uses a single randomly-drawn lottery numbers tie-breaker. To see how lottery tiebreaking can be used to identify causal effects of school distance a travel, consider a constant-effects
model of the effects of non-neighborhood enrollment, indicated by dummy Gi as before. Potential
outcomes {Y0i , Y1i } are indexed against this. The constant causal effect of interest, β = Y1i − Y0i ,is identified by an IV estimand that uses non-neighborhood assignment, Zi , as an instrument for
Gi in a two-stage least squares (2SLS) procedure incorporating a control function derived from ourunderstanding of the Boston and New York matches.
The details behind this argument are fleshed out as follows. Let Di (s) indicate whether applicant
17

Blagg, Rosenboom and Chingos (2018) document a similar association between travel time and test scores in
Washington, DC.

11

i is offered a seat at school s ∈ S, where S denotes the set of schools in the match. Although Zi is
not randomly assigned, it’s a function of the set of conditionally randomized offers, {Di (s)}, and avector of covariates, gi . Specifically,Zi =X

Di (s)gi (s),(2)

swhere gi (s) indicates whether s is a non-neighborhood school for i. Collect the set of gi (s) for
applicant i in vector gi . With lottery tie-breaking, identification is a consequence of the following
conditional independence property:
E[Y0i |θi , gi , Zi ] = E(E[Y0i |θi , gi , {Di (s)}]|θi , gi , Zi ) = E[Y0i |θi , gi ].

(3)

The first equals sign uses (2); the second uses lottery tie-breaking, which says that, conditional ontype, offers of a seat at s are determined by lottery and therefore ignorable in the sense of being
independent of potential outcomes. Conditioning on gi is irrelevant for the ignorability of offers,
but necessary for ignorability of Zi .
This conditional independence property leads to the following identification result:
Proposition 1. Suppose the effect of Bernoulli treatment Gi is constant and given by β = Y1i −Y0i .
Given instrumental variable, Zi , defined in (2) and satisfying (3), we have that:β=E[(Zi − µi )Yi ],E[(Zi − µi )Gi ](4)

where µi ≡ E[Zi |θi , gi ] and the denominator is presumed to be non-zero. Moreover,µi =Xψs (θi )gi (s),

(5)

s

where
ψs (θi ) = E[Di (s)|θi ] = P [Di (s) = 1|θi ]is the DA propensity score derived in Abdulkadiroğlu et al. (2017).
Proposition 1 is a consequence of the fact that, by virtue of the conditional independence
characterized by (3), we can write
Yi = βIV Gi + h(θi , gi ) + εi ,(6)h(θi , gi ) ≡ E[Y0i |θi , gi ],

(7)

where

εi ≡ Y0i − h(θi , gi ),

12

(8)

and these two terms are mean-independent of centered instrument Zi − µi . Mean-independence ofZi − µi and h(θi , gi ) + εi is the orthogonality condition yielding (4).
The dimension reduction implied by (5) is also useful. Control function µi depends on θi solely
via the the profile of assignment risk, {ψs (θi )}. Although θi has many points of support (there
are almost as many types of applicants as there are applicants), DA propensity scores depend on
only a few characteristics of an applicant’s rank-order list and the associated school-specific (butnot applicant-specific) cutoffs determined by the match. Abdulkadiroğlu et al. (2017) use a largemarket approximation to derive this result, giving a formula for ψs (θi ) that’s employed here toestimate µi for each applicant.18
Let µ̂i denote consistent estimates of µi computed from large-market estimates of the profile ofassignment risk. Plugging these in to the sample analog of (4) gives an estimator,P(Zi − µ̂i )Yiβ̂IV = P s,(Zi − µ̂i )Gisthat converges to β by the continuous mapping theorem. ]β is also estimated consistently (andconveniently) via 2SLS with first and second stages:
Gi = γZi + κ1 µi + ν1i ,(9)

Yi = βGi + κ2 µi + ν2i .

(10)

To see why, suppose first that µi is known and recall that a just-identified 2SLS estimand withcovariate µi can be written as IV using instrument Z˜∗ , defined as the residual from a regression ofi

Zi on µi (see, e.g., Angrist and Pischke (2009)). Here, µi = E[Zi |θi , gi ], so E[Zi |µi ] = µi , a linear
function of µi . The population regression of Zi on µi therefore yields the CEF residual,Z̃i∗ = Zi − E[Zi |θi ] = Zi − µi .
In practice, µi must be estimated, but 2SLS estimates controlling for µ̂i (denoted β̂2SLS ), areconsistent for β as long as µ̂i converges to µi .19
Our 2SLS estimates incorporate two extensions to this framework. The first, relevant for both
Boston and New York, covers ordered treatments like travel time, Ti , rather than Bernoulli Gi .
Swapping Ti for Gi in (9) and (10), the instrument for Ti is an applicant’s travel time to the school
they’re offered in the match. Formally, let ti (s) denote the time it takes applicant i to travel to18

Since we focus on students who are assigned seats in the match, the relevant DA propensity score is normalizedby match participants’ probability of being assigned any school in the match.
19
Appendix A.2 derives the limiting distribution of β̂2SLS assuming match applicants constitute a random sample
from the population of interest. The estimation error in empirical propensity scores originates in the randomness oflottery draws rather than sampling variance. Even so, simulation evidence in Appendix A.7 of Abdulkadiroğlu et al.
(2017) suggests that conventional robust-standard-error-based p-values for score-controlled reduced-form estimates
match the corresponding randomization-based p-values closely. Angrist et al. (forthcoming) uses a similar 2SLS
estimator based on centralized assignment to estimate individual school value-added.

13

school s. The offered travel instrument can then be written:Zi =X

Di (s)ti (s),

(11)

s

where Di (s) is a school-specific offer dummy as before. The extension of Proposition 1 to this casesolves the problem of causal identification with an ordered treatment tackled previously by Imbens(2000). Derivation of the control function for an ordered treatment obviates the need to condition
on multiple conditional probabilities as in earlier work.
Second, because New York’s high school match employs a mix of lottery and non-lottery tie
breaking, the control function for New York uses the more elaborate characterization of assignment
risk derived in Abdulkadiroğlu et al. (2022). This local DA propensity score relies on the factthat in a shrinking bandwidth around DA admissions cutoffs, non-lottery tie-breakers behave likelottery numbers. The local DA propensity score, written ψs (θi , τi (δN )), depends on a collection ofindicators for cutoff proximity, denoted τi (δN ) and determined in part by a data-driven bandwidth,δN . The conditioning variables that define control function µi for New York applicants include
τi (δN ) as well as applicant type and the distance vector, ti . The control function for offered travel
time in New York is:µi = E[Zi |θi , ti , τi (δN )] ≈Xψs (θi , τi (δN ))ti (s),swhere school-specific travel times for applicant i are collected in vector ti and the assignment risk
profile, {ψs (θi , τi (δN ))}, allows for both lottery and non-lottery tie-breakers (this risk profile isapproximate, characterizing offer rates as δN → 0). Finally, 2SLS estimates for New York arecomputed using a version of (9) and (10) that adds design controls in the form of local-linear
functions of screened-school tie-breakers; these functions use the same bandwidth used in τi (δN ).20
The 2SLS estimator characterized by (9) and (10) is derived here under constant effects. In
reality, treatment effects may be heterogeneous. Extending results in Angrist and Imbens (1995)
and Angrist, Graddy and Imbens (2000), Borusyak and Hull (2021) show that a centered IV
estimand of the form (4) can be written as a weighted average of covariate-specific causal effects. For
example, when using a Bernoulli-distributed treatment and instrument, as in the non-neighborhood
schooling model, the IV-estimand is a weighted average of conditional-on-covariates treatment
effects for covariate-specific compliant subpopulations defined by the response of Gi to Zi .
Appendix Table A2 reports a set of results meant to validate our research design. Even when
instruments are randomly assigned, differential attrition may lead to selection bias. Roughly 80% of
Boston match applicants have an MCAS Math or ELA outcome. Columns 2 and 3 of Table A2 show
20

The bandwidths used here are estimated as suggested by Calonico, Cattaneo and Titiunik (2014). Bandwidths
are computed separately for each test score variable; we use the smallest of these for each program. We set δN = 0
for screened programs which have fewer than 5 applicants in the bandwidth who are either below or above thetie-breaker cutoff. Design controls are as specified in equation (12) of Abdulkadiroğlu et al. (2022). These include
dummies indicating applicants that applied to each program and dummies indicating applicants in each bandwidth.

14

that the likelihood of observing these outcomes is unrelated to both non-neighborhood-offer andoffered-travel instruments. Roughly 70% of New York students take the SAT. Students who travel
are slightly less likely to have SAT scores. College outcomes – which come from administrative datafrom the National Student Clearinghouse – are unlikely to be compromised by instrument-induced
differences in follow-up.
A second set of diagnostics evaluates covariate balance. Appendix Table A2 also reports coefficients on offer instruments from regressions of covariates on these instruments, controlling for
estimated µi . Balance regressions for Boston show no statistically significant relationship between
instruments and baseline covariates. This highlights the balancing property that motivates our µi controlled 2SLS strategy. Balance estimates for New York applicants show a few small marginallysignificant differences, but the magnitudes of these seem unlikely to lead to substantial omitted
variables bias. In any case, the 2SLS estimates discussed below are from models that include
the baseline covariates listed in these tables as controls. Control for covariates changes the 2SLS
estimates little, while improving precision.
Beyond the usual concerns with differential attrition and covariate balance, research designs
exploiting centralized school assignment may be compromised by spillover effects that lead toviolations of the IV exclusion restriction supporting a causal interpretation of 2SLS estimates.
When one applicant is offered a non-neighborhood seat, another may be offered the neighborhood
seat not taken. This in turn may change neighborhood peer composition even for those who don’t
travel. Spillovers of this sort can be seen as a violation of the non-interference or stable unit
treatment values (SUTVA) assumption that typically underpins causal inference (see, e.g., Imbens
and Rubin (2015)). In the large-market framework used to construct µi , however, an individual
applicant’s school assignment is determined solely by their own tie-breakers and type. Offers are
therefore theoretically uncorrelated across applicants. Our empirical exploration of possible SUTVA
violations (not reported) suggests spillover effects are indeed negligible.

5

IV Estimates

5.1

Integration Consequences of Non-neighborhood Enrollment

Minority students who enroll in non-neighborhood schools have fewer same-race classmates as aresult. This is documented in Table 3, which reports 2SLS estimates of non-neighborhood enrollment effects on peer composition, separately by city. The table shows estimates for all applicantswith experimental variation in neighborhood enrollment and for two applicant groups defined byrace. The corresponding first-stage estimates for all applicants imply that a non-neighborhood offer
increases rates of non-neighborhood enrollment by 0.43 in Boston and 0.66 in New York (estimatedfirst stages for Black and Hispanic only are similar).
In samples including all applicants, the impact of non-neighborhood schooling on the proportionof a student’s classmates who are Black or Hispanic is modest. Disaggregating by race, however,effects on Black applicants’ minority exposure are substantial. Specifically, non-neighborhood en-15

rollment in Boston causes Black students to attend schools with 9.4 percentage points fewer Blackpeers and 5.8 percentage points more Hispanic peers, resulting in a total decrease in Black or Hispanic peer share of about 3.6 percentage points. Non-neighborhood school enrollment also sharply
reduces minority isolation for Black Boston applicants, a fall of almost 17 percentage points compared to a mean of 43 points. We focus here and in the rest of the paper on minority isolation
defined by a 90% rather than an 80% cutoff since the higher threshold features in contemporary
discussions of segregation such as Cohen (2021) and Potter (2022).
Among Black New York applicants, non-neighborhood school enrollment results in a roughly 9
percentage point reduction in Black peers and a 5 point increase in Hispanic peers. Overall minority(Black or Hispanic) exposure falls by 3.6 percentage points for Black New Yorkers who attend nonneighborhood schools. Non-neighborhood enrollment also reduces minority isolation more sharply
for Hispanic New York students than for Blacks. The former effect is almost 8 percentage points,
while the latter is around 3 points, and not significantly different from zero.
Non-neighborhood school enrollment also integrates the peer environment of Boston’s Hispanic
applicants, though to a far lesser degree than for Black applicants. Specifically, non-neighborhood
enrollment reduces Hispanic applicant’s peer share Hispanic and increases Hispanics’ peer shareBlack, but neither of these effects (on the order of 2 points) are significantly different from zero.
Non-neighborhood school enrollment also likewise no significant effect on Hispanic minority isolationin Boston. Estimated integration effects for New York’s many Hispanic students are larger thanfor Hispanics in Boston. These estimates suggest that non-neighborhood enrollment decreases peer
share Hispanic by 5.9 percentage points, while boosting peer share Black by 1.2 percentage points.
On balance, the estimates in Table 3 indicate that non-neighborhood enrollment has substantial
integrating effects, especially for Black applicants. Non-neighborhood enrollment reduces same-race
exposure more for Hispanic New Yorkers than for Hispanics in Boston. At the same time, effects on
peer share Black and Hispanic tend to be offsetting, so that changes in overall minority exposuredue to non-neighborhood schooling are well below the corresponding changes in same-race exposure.

5.2

Non-Neighborhood Effects on Achievement and College AttendanceNon-neighborhood enrollment boosts integration in the sense of reducing minority applicants’ samerace exposure and, for Blacks in Boston and Hispanics in New York, by reducing minority isolation.
We might therefore expect non-neighborhood schooling to increase learning and college enrollment
as well. The 2SLS estimates reported in Table 4, however, show little evidence of non-neighborhood
schooling effects on achievement and college attendance to match the integration gains documented
in Table 3.
As can be seen in the first three columns of Table 4, Boston students who enroll out-ofneighborhood have test scores and college enrollment rates close to those of students who stayin-neighborhood. Among Black Boston applicants, for example, non-neighborhood enrollment generates only an estimated 0.024σ (se=0.06) improvement in Math scores. This estimate contrasts
with the much larger (and more precise) OLS estimate of roughly 0.09σ (se=0.01), suggesting that16

the latter reflects selection bias.
Most of the 2SLS estimates of the impact of non-neighborhood schooling on Boston students’achievement and college attendance rates are smaller than the corresponding OLS estimates. At
the same time, few of the 2SLS estimates for Boston are estimated precisely enough to be statistically distinct from the corresponding OLS estimates. 2SLS estimates for New York applicants
are considerably more precise than those for Boston. With estimated standard errors of around0.02 − 0.03, most of the 2SLS estimates for New York amount to reasonably precise null effects ofneighborhood schooling on test scores and college-going.

5.3

Travel Time Effects

The non-neighborhood schooling treatment is defined in part by arbitrary neighborhood boundaries.
We therefore explore causal effects of a school-travel treatment that various continuously above zero.
Estimated effects on integration and education outcomes are similar when minutes of travel timeto school, Ti , replaces neighborhood schooling as a mediator of school distance and travel effects.
Table 5 presents 2SLS estimates of school travel effects. These are reported in terms of twenty
minute increments, a scaling that facilitates comparison to the non-neighborhood effects in the previous table. This scaling is also motivated by Figure 3, which plots the distribution of travel time for
non-neighborhood enrollment compliers. Among applicants induced to enroll out-of-neighborhoodby virtue of being offered a non-neighborhood seat in the match, travel times are roughly 16-21
minutes longer than they would have been in the absence of such an offer. This figure also highlights
the relative skewness of non-neighborhood commute times relative to the compressed distribution
for those enrolling close to home. Estimated travel-time effects reflect outcomes for students whoride an hour or more to school as well as outcomes for students whose commute is far shorter.
As with non-neighborhood enrollment, twenty minutes of additional travel integrates the school
environment, especially for Black applicants. The pattern of estimated effects of school travelon peer race and minority isolation, presented in Panel A of Table 5, mostly parallels that seen in
estimates of effects of non-neighborhood enrollment. For Black students, for example, 20 minutes oftravel reduces same-race exposure by about 6 points in Boston and by about 7 points in New York.
Travel effects on minority isolation are larger in magnitude than the effects of non-neighborhood
enrollment on minority isolation; the former are also consistently negative across all racial groups.
Large integration effects of travel notwithstanding, Panel B of Table 5 again shows little evidenceof a travel effect on achievement or college attendance. Most of the estimated travel effects on
education outcomes in Panel B are small and not significantly different from zero. Also noteworthy
is the fact that standard errors for estimated travel effects are markedly below the standard errorsof estimated non-neighborhood schooling effects in Table 4.
A few statistically significant estimates in Panel B of Table 5 hint at deleterious effects of travel
on Hispanic students in New York. Estimates for this group, reported in column 6, suggest twentyminutes of additional travel reduces college-going by 4 points and four-year college attendance by 3
points. Estimated travel effects on Black college-going are also negative, though only one (for any

17college attendance in Boston) is (marginally) significantly different from zero.21

5.4

Value-Added and Other Mediators

Minority families who opt for a longer ride to school benefit from a more integrated school environment as a result. Yet, the absence of travel effects on educational outcomes suggests the schools
travelers travel to are no better than those they might attend nearby. Are neighborhood schools
really no worse than schools farther away? We explore this hypothesis using a measure of school
quality, rather than racial integration, as the principal mediator of distance and travel effects.
Schools differ in many ways, but a school’s causal value added offers a parsimonious summary ofschool quality that should reflect the cumulative impact of education inputs like class size, teacher
skills, and peers on student achievement. This observation motivates an investigation of the extent
to which effects of travel on school value added–or lack thereof–can account for the mostly absent
effects of travel on education-related outcomes.22
For purposes of this investigation, value added is estimated using a risk-controlled value-added
model (RC VAM). Introduced in Angrist et al. (forthcoming), RC VAM measures causal effects
of individual schools on achievement by controlling for student characteristics, including lagged
test scores, and for the probability a student is seated at each of the schools in their rank-orderlist. Angrist et al. (forthcoming) validate RC VAM using the subset of students and schools whereseats are randomly assigned. As in Angrist et al. (forthcoming), we focus on test-score value added
rather than college value added because lagged test-score controls enhance the predictive validityof test-score VAM estimates.23
Our investigation of value added as a mediator of travel effects is motivated by a version of (10)in which the RC VAM-derived value added of the school student i attends, denoted by Vi , replaces
non-neighborhood enrollment. The VAM second stage can be written:
Yi = βv Vi + κ2 µji + ν2i ,(12)

where βv is the causal effect of attendance at a higher-value-added school and µji is an instrumentspecific control function defined below. In the VAM literature, causal parameter βv is a forecast
coefficient gauging the extent to which students randomized to attend higher-value-added schools
learn more as a result (see, e.g., Angrist et al. (2016b)).
21
Distance and travel have little effect on absences, suspensions, or a composite disciplinary index in Boston. In
New York, twenty-minutes travel increases days absent by 0.8, but the corresponding estimated non-neighborhood
effect is not significantly different from zero. These and other estimates of travel effects on behavioral outcomes arereported in Appendix Table A3.
22
Appendix Table A4 summarizes direct estimates of distance and travel effects on school inputs in the form ofstudent-teacher ratios and two measures of teacher qualifications. These rely on the same causal framework used toestimate travel effects on peer race and minority isolation. Although non-neighborhood schooling and school travelappear to increase average class size, these changes are likely too small to have measurable downstream consequences(Krueger (1999) estimates a 0.2σ increase in achievement from a 10-student reduction in class size, while effects here
are at most a 0.7 increase in size). Effects on teacher qualifications are even smaller.
23
Chetty, Friedman and Rockoff (2014) argue that VAM assumptions are more plausible for test scores than for
longer-run outcomes where lagged measures of the dependent variable are unavailable.

18

The first of two instruments used to estimate (12) is offered value added, defined by:
Z1i =

X

Di (s)vi (s),swhere vi (s) is value added by school s in applicant i’s cohort. The second instrument is offered
travel, defined as before by:
Z2i =

X

Di (s)ti (s),sthough now written Z2i to distinguish this instrument from the first. Analogous to (9) and (10),control function µji is defined byµji ≡ E[Zji |θi , ti , vi ]; j = 1, 2;(13)

where vi is the vector of school value-added and ti is again the vector of travel times. The firststage equation in this setup regresses Vi on one or both instruments and the corresponding µji .
As a benchmark for first-stage estimates of travel effects on value added, Columns 1, 4, and 7
in Panel A of Table 6a (for Boston) and Table 6b (for New York) show that offered value added(instrument Z1i ) is a strong predictor of value added at the school an applicant attends. Moreover,as can be seen in Panel B of the table, 2SLS using offered value added to instrument value added at
the school attended generates precise estimates of βv of around 0.8 or higher. These high estimatesvalidate the predictive value of RC VAM estimates of value added in our samples.
In contrast with offered value added, offered school travel (instrument Z2i ) changes value added
little. This is documented in columns 2, 5, and 8 in Panel A of Tables 6a and 6b. An additional 20
minutes of offered travel time leads Boston travellers to enroll at schools with only slightly higher
value-added, a gain ranging from just under 0.01σ for Hispanic applicants to 0.016σ for Blacks.
The corresponding estimates for New York applicants, shown in the same columns in Panel A of
Table 6b, are even smaller: the largest quality increase due to school travel in New York is 0.009σ
for Blacks.24 Unsurprisingly, weak first-stage effects of travel on value added lead to imprecise andessentially uninformative second stage estimates (these appear in Panel B of the two tables in thecolumns containing the first-stage estimates for offered travel).
The results in Tables 6a and 6b suggest that weak effects of travel on education outcomescan be explained by small effects of travel on school quality. But perhaps travel affects outcomesthrough channels other than value added. For instance, a long commute requires earlier mornings,
potentially reducing sleep (Carrell, Maghakian and West, 2011). Commuting time might also eat
into study time.25 These considerations raise the possibility that negative aspects of travel offset
any gains due to integration.
The precisely-estimated forecast coefficients reported in Panel B of these tables imply that24

Effects of non-neighborhood enrollment on value added (not reported in the tables) are even smaller.
The US Department of Transportation’s Safe Routes to School Program cites other potential benefits of shortschool commutes (USDOT, 2021).
25

19

instrument Z1i is sufficient to identify and reliably estimate βv . Identification of βv by Z1i alone
allows us to test whether value-added satisfies the exclusion restriction implied by our explanationof null travel effects on achievement and college-going. The argument here can be boiled down to
two statements: (A) Value added mediates travel effects; (B) Travel changes value added little.
This restriction is tested by asking whether whether the offered-travel instrument, Z2i , predicts
outcomes net of the value-added effects captured by βv Vi . In other words, in a regression of 2SLS
residual Yi − βv Vi on both instruments, does Z2i matter? This test is implemented as the testof over-identifying restrictions obtained when using both offered travel and offered value added to
instrument Vi in equation (12).26
The results of this test, along with the associated first- and second-stage estimates, appear incolumns 3, 6, and 9 in Tables 6a and 6b. Over-identified estimates of the value-added forecast
coefficient, βv , are similar to the just-identified estimates obtained using Z1i only. Unsurprisingly,
therefore, statistics testing over-identifying restrictions, shown at the bottom of Panel B, offer noevidence against an exclusion restriction attributing all travel effects to changes in school quality
as measured by school value added. These findings therefore support our claim that that small
effects of travel on education outcomes are explained by small travel effects on school quality.27

6Conclusion: Busing Trade-Offs
We can no longer afford to spend millions a year to bus children across Boston to schoolsthat are not demonstrably better than schools near their homes.
Theodore Landsmark, The Boston Globe, January 2009
The estimates reported here align with longtime Boston schools observer Ted Landsmark’s

contention that busing today is of little educational consequence. At the same time, while reduced
travel seems likely to leave education outcomes unchanged, a shift to proximity-based assignment,
effectively, “neighborhood schools,” may increase segregation. By how much? We gauge this bysimulating a match in which both students and schools rank one another in order of proximity.
This imagined neighborhood assignment scenario uses information on the residential location ofeach student (geocode in Boston, census tract in New York), the location of each school, andthe school capacities. Because neighborhood schools are typically expected to accommodate allneighboring families, the simulation raises each school’s capacity to the maximum enrolled there
during the years for which we have data.
Our simulation results compare status quo enrollment patterns with patterns under binding
neighborhood assignment for all students enrolled in match-participating schools (not just those26

Over-identified models control for both µ1i and µ2i . Hausman (1983) shows that the Sargan over-identification
test statistic can be computed as sample size times the R2 from a regression of 2SLS residuals on excluded instruments,
partialing out any controls.
27
Cordes, Rick and Schwartz (2022) argue that long bus rides increase absenteeism, while also noting that controlling for student distance from school, within-route effects on absenteeism largely disappear. These results therefore
seem consistent with our estimated null effects of travel, which likewise control for student-school distance.

20

participating in the match). Table 7 reports simulated neighborhood assignment impacts on average
travel time, the share of students eligible for publicly funded school transportation (“busing”), andmeasures of segregation. Simulated neighborhood assignment reduces travel time by about 13
minutes for Boston middle and high-schoolers and by as much as 17 minutes for New York highschool students. The share eligible for school transportation falls sharply in Boston, a decline ofabout 50 percentage points, with more modest though still substantial declines in New York.28
Black New York 9th graders are estimated to see the largest increase in same-race exposure fromthe shift to neighborhood schools, a change of 5.4 points. And minority isolation (that is, enrollment
in a school with a student body 90 or more percent minority) is predicted to jump sharply for Black
students in Boston. For others, neighborhood assignment affects integration much less. Remarkably,for Hispanics, our simulation predicts no change in minority isolation and only small changes insame-race exposure (for Boston Hispanics, this falls slightly). Consequently, under neighborhood
assignment, minority students as a group enroll in schools with shares of same-race peers matching
those experienced today. These patterns reflect the fact that the reassignment scenario puts every
student in play: when students who used to travel are pulled back to neighborhood schools, some
now attending these schools are displaced.
Sharp drops in busing eligibility can be expected to reduce school transportation costs markedly.
As with changes in transportation usage, precise savings from reduced busing are hard to pin down.
We can get a rough idea of possible savings, however, by using average yellow-bus transportation
costs for Boston 6th graders and the value of public transportation passes for high school students inBoston and New York. Boston public school student CharlieCards cost $90 / month (in 2022) andare issued for 10 months; averaging yellow-bus costs for 6th graders with this amount (estimated ataround $1,732 in 2014) results in an average annual savings of around $1020 (in 2022 dollars) per
formerly-transported-student in Boston (BPS, 2014a).29 New York MetroCards cost $127 a monthin 2022 and are valid only on days when school is in session, implying an annual savings of roughly$1,300 per formerly-transported student in New York (NYCDOE, 2022).30
These savings could be used to improve school quality. A recent meta-analysis of school expenditure effects by Jackson and Mackevicius (2021) suggests that, over the course of four years, $1,000of additional annual spending might boost test scores by about 0.044σ and increase college attendance rates by approximately 3.9 percentage points. In practice, we can’t say how transportation
savings might be allocated over students. It seems reasonable to imagine, however, that additional
spending would likely target high-need students. In any case, the possibility of such gains highlights
the value of a fresh look at busing-resource trade-offs.
A complete analysis of busing trade-offs should include the effect of neighborhood school assignment on overall district enrollment. Some families may be attracted by neighborhood schools,
but others may leave in response to limits on choice (Epple et al. (2014) explores these issues).
28

Boston eligibility criteria are those for 6th grade.
Costs are adjusted to May 2022 dollars using Consumer Price Index (Series ID = CUUR0000SA0).
30
These calculations differ from the sums reported in Figure 1, which include fixed costs and costs for elementary
school students.
29

21

Neighborhood assignment might also dilute incentives for school effectiveness, an issue consideredin, e.g., Card, Dooley and Payne (2010) and Campos and Kearns (2022). Shi (2015) and Pathak
and Shi (2021) examine recent efforts to reduce transportation costs in Boston by limiting choicewithout a full return to neighborhood schools. The Covid pandemic has also spurred efforts to
reduce school transportation services across the country (see, for example, Washington (2021) and
Russell (2021)). We expect to leverage quasi-experimental student assignment to generate further
evidence on the causal connections between school choice, racial integration, and human capital in
the near future.

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Figure 1: Per-Pupil Annual Expenditures on Student Transportation

1800
1500
1200
900
600
300
0

Per-pupil expenditure on transportation ($)

2100

Top 100 School Districts by Enrollment, FY 1997-2017

1997

2002

2007

Fiscal year

Top 100 Districts by Enrollment

2012

Boston2017

New York

Source: National Center for Education Statistics (NCES) Common Core of Data.
Notes: Transportation expenditure corresponds to the amount spent on the transportation of public school students,
including vehicle operation, monitoring riders, and vehicle servicing and maintenance. Per-capita amounts are computed by dividing total costs by total district enrollment. Enrollment data are from the NCES and count the numberof students for which the district is financially responsible. Fiscal year t is defined as the school year ending in t.
Expenditure data is adjusted to June 2017 dollars using the Consumer Price Index (Series ID = CUUR0000SA0).
Top 100 districts by enrollment is a within-year designation.

29

100%

Figure 2: Racial Exposure in Boston and New York Public Schools, 1988-2018(a) Boston Public Schools

75%

100%

100%

75%

75%

50%

50%

25%

25%

50%

0%

0%

1988 1993 1998 2003 2008 2013 20181988 1993 1998 2003 2008 2013 2018Black students

Hispanic students(b) New York Public Schools

25%

0%

100%

100%

75%

75%

50%

50%

25%

25%

1988 1993 1998 2003 2008 2013 20180%0%1988 1993 1998 2003 2008 2013 2018Black students
Racial exposure
Peer share
Black

Peer share
Hispanic

1988 1993 1998 2003 2008 2013 2018

Hispanic students
Minority isolation schools

Peer shareBlack or Hispanic

Proportion enrolled at schools>90% Black or Hispanic

Proportion enrolled at schools>80% Black or Hispanic

Source: Common Core Public Elementary and Secondary School Universe Survey, documented in https://nces.ed.
gov/ccd/pubschuniv.asp.
Notes: Solid lines plot the proportion of a student’s peers falling into various race groups. Dotted and dashed lines
plot the proportion of students enrolled at schools with a student body that’s either over 80% or over 90% Blackor Hispanic. Year t on the x-axis marks the school year ending in t. Schools with missing race data are omitted.
New York Public Schools consist of schools in the aggregated New York City district code and the New York City
community districts. Virtual, future, closed, or inactive schools are not included in the sample. The sample includes
all grades, but does not include students in adult education. Black is defined as “non-Hispanic, Black.”

30

.05

.04

Figure 3: Travel Time Distributions for Non-Neighborhood Compliers

Difference in means = 21.2 (0.8).03.02

Density

.03

0

0

.01

.01

.02

Density.04

Difference in means = 15.5 (0.3)

0

20

40

60

Enrolled travel time

31

Neighborhood offer(i) Boston

80

0

20

40

60

80

100

Enrolled travel time
Non-neighborhood offer

Neighborhood offer

Non-neighborhood offer(ii) New York

Notes: This figure plots the distributions of travel time (in minutes) for Boston and New York neighborhood compliers. Densities for non-neighborhood compliers
are estimated using 2SLS regressions of the interaction of a kernel density function and a non-neighborhood enrollment indicator on the enrollment indicator,
instrumented by a non-neighborhood assignment indicator, controlling for student demographics, baseline achievement, and offer risk. Densities for non-offeredcompliers are estimated by replacing enrollment with one minus enrollment in this 2SLS procedure. The model uses a Gaussian kernel and the Silverman (1986)
rule of thumb bandwidth. Vertical dashed lines indicate mean potential outcomes.

Table 1: Boston and New York Analysis Samples
Boston (6th and 9th grade)

New York (9th grade)

EnrolledsampleEnrolled (nonnbhd) sample

ApplicantsampleExperimental
sampleEnrolledsampleEnrolled (nonnbhd) sample

ApplicantsampleExperimental
sample

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

A: Race
Black
Hispanic
White or Asian
N

0.43
0.34
0.22

0.45
0.31
0.22

0.44
0.37
0.18

0.48
0.37
0.13

0.29
0.40
0.29

0.33
0.40
0.25

0.27
0.39
0.33

0.30
0.44
0.24

119,915

82,03166,801

24,879394,777

250,254

298,840

75,686

0.76
0.50
0.19
0.12
0.03
0.02

0.73
0.51
0.07
0.09
0.18
0.18

0.78
0.52
0.08
0.05
0.04
0.04

0.05
0.06

0.08
0.09

0.04
0.07
0.77

0.04
0.05
0.74

B: Other covariates
0.73
0.49
0.18
0.16
0.01
0.01

Free and reduced-price lunch
FemaleSpecial education
Limited English proficiency
Baseline mathBaseline English

0.73
0.50
0.19
0.12
0.07
0.06

0.79
0.50
0.17
0.14
-0.10
-0.07

0.80
0.51
0.18
0.11
-0.14
-0.11

0.75
0.49
0.18
0.14
-0.01
-0.02

32

C: School sectors
0.13
0.10

Enrolled in charter
Enrolled in exam
Enrolled in offered school

0.19
0.15

0.08
0.03
0.69

0.09
0.04
0.62
D: Travel

Ranked a non-nbhd school first
Enrolled in a non-nbhd school
Enrolled travel time
Enrolled distance
Eligible for busing
N

0.77
32.9
3.63
0.71

1.00
38.3
4.43
0.88

0.72
0.74
32.9
3.61
0.70

0.79
0.79
35.3
4.01
0.76

0.64
36.4
4.48
0.96

1.00
43.2
5.85
0.99

0.66
0.65
37.5
4.70
0.96

0.73
0.69
38.3
4.76
0.97

98,37973,803

66,281

24,879389,284

250,135

297,734

75,686

Notes: Statistics for Boston use data on middle school students enrolled in 6th grade and high school students enrolled in 9th grade in 2002-03 to 2013-14. Statistics for
New York use data on high school students enrolled in 9th grade in 2012-13 to 2016-17. Columns 1 and 5 report descriptive statistics for the sample of enrolled students
who have demographic information. Columns 2 and 6 restrict the sample to students who enroll in a non-neighborhood school. Columns 3 and 7 report statistics for the
sample of match applicants who have demographic information. The experimental samples in columns 4 and 8 restrict the applicant sample to offered students who have (i)non-degenerate risk of school assignment, (ii) non-missing baseline test scores, and (iii) non-missing geographic information (residential geocodes in Boston and census tracts
or districts in New York). Boston baseline test scores are from the MCAS (4th grade Math and ELA for middle school, 8th grade Math and 7th/8th grade ELA for highschool); New York baseline scores are 6th grade scores from the NY state standardized assessments. Charter and exam schools are considered to lie outside of a student’s
neighborhood. Travel time and distance are by public transit; units are in minutes and miles, respectively. Busing eligibility is defined as being enrolled at a school that hasa driving distance of more than 1.5 miles in Boston and more than 0.5 miles in New York. The sample sizes after Panel A count students with demographic information;
the sample sizes after Panel D count students who also have geographic information.

Table 2: OLS Estimates of Non-Neighborhood Schooling Effects
Non-neighborhood enrollment
Boston
New York
All students

Black
students

Hispanic
students

All students

Black
students

Hispanic
students

(1)

(2)

(3)

(4)

(5)

(6)

Mean

0.0646(0.0071)-0.0000.0870(0.0107)-0.2580.0694(0.0117)-0.1510.0737(0.0033)
0.002

0.0507(0.0062)-0.416

0.0542(0.0048)-0.334Mean

0.0458(0.0070)0.015

0.0719(0.0109)-0.1550.0360(0.0114)-0.1320.0846(0.0034)
0.002

0.0596(0.0067)-0.3060.0700(0.0050)-0.295

N

83,221

34,93627,965259,224

67,27894,742Mean

0.0432(0.0063)0.427

0.0453(0.0097)
0.388

0.0399(0.0098)
0.365

0.0065(0.0020)0.520

0.0061(0.0039)0.430-0.0052(0.0031)
0.446

Mean

0.0364(0.0055)
0.324

0.0353(0.0084)
0.277

0.0360(0.0084)
0.253

0.0220(0.0018)
0.335

0.0127(0.0034)
0.246

0.0135(0.0026)0.232

N40,91817,41614,154

303,975

89,375

121,046MCAS Math /SAT Math
MCAS ELA /SAT Reading

Any college

Four-year
college

Notes: This table reports OLS estimates of the relationship between non-neighborhood school enrollment and achievement or college-going. The Boston sample includes students enrolled in the 2002-13 school years; the New York sample
cover the population enrolled in the 2012-16 school years. All models control for student demographic characteristics,
match participation, charter school enrollment, and exam school enrollment. The models also include fixed effects forschool walk zone in Boston and residential school district in New York. The New York specification also includes anindicator for district 75 schools (serving only special education students) and district 79 schools (serving specialized
student populations such as incarcerated youth or adults pursuing a GED). Boston test scores are from the MCAS
(6th grade Math and 7th grade ELA for middle school, 10th grade Math and ELA for high school); New York testscores are from the SAT. Approximately 70% of New York students take the SAT.

Table 3: 2SLS Estimates of Non-Neighborhood Schooling Effects on Peer Race
Non-neighborhood enrollment
Boston

New YorkAllapplicantsBlackapplicants

Hispanic
applicantsAllapplicantsBlackapplicants

Hispanic
applicants

(1)

(2)

(3)

(4)

(5)

(6)

Mean
SD

-0.0259(0.0094)
0.452
0.171

-0.0938(0.0143)
0.505
0.160

0.0230(0.0155)
0.412
0.166

-0.0073(0.0039)
0.297
0.226

-0.0874(0.0122)
0.458
0.255

0.0116(0.0049)
0.260
0.170

Mean
SD

0.0251(0.0086)
0.378
0.150

0.0583(0.0123)
0.347
0.136

-0.0204(0.0140)
0.423
0.151

-0.0246(0.0039)
0.426
0.222

0.0514(0.0094)
0.372
0.218

-0.0590(0.0056)
0.532
0.192

Mean
SD

-0.0008(0.0078)
0.830
0.128

-0.0355(0.0109)
0.852
0.114

0.0026(0.0113)
0.835
0.114

-0.0320(0.0041)
0.724
0.260

-0.0360(0.0090)
0.830
0.197

-0.0474(0.0055)
0.793
0.210

Mean

-0.0618(0.0289)
0.367-0.1650(0.0449)
0.433

0.0222(0.0488)0.366-0.0436(0.0086)
0.394-0.0325(0.0236)0.572-0.0780(0.0131)0.459

N24,87911,984

9,103

75,686

23,07733,436Peer share Black

Peer share Hispanic

Peer share Blackor Hispanic

Minority isolation

Notes: This table reports 2SLS estimates of non-neighborhood enrollment effects on peer racial composition, computed in samples of Boston middle and high school applicants and New York high school applicants. The sample isrestricted to offered applicants with non-degenerate risk of school assignment. The instrument is non-neighborhood
assignment. The endogenous variable is 6th or 9th grade non-neighborhood enrollment. The non-neighborhood firststages are approximately 0.43 for Boston and 0.66 for New York; race-specific first stages are similar. Models include
control function µi , defined in Equation 5, as well as student demographic variables and baseline achievement. School
peer shares are computed using samples of all enrolled students in 6th or 9th grade. Minority isolation is defined asenrolled at a school where the proportion of Black or Hispanic exceeds 90%.

34

Table 4: 2SLS Estimates of Non-Neighborhood Schooling on Test Scores and College AttendanceNon-neighborhood enrollment
Boston
New YorkAllapplicantsBlackapplicants

Hispanic
applicantsAllapplicantsBlackapplicants

Hispanic
applicants

(1)

(2)

(3)

(4)

(5)

(6)

Mean

0.0368(0.0424)-0.1150.0244(0.0600)-0.276-0.0322(0.0719)-0.126-0.0094(0.0147)-0.0220.0050(0.0314)-0.3750.0045(0.0202)-0.259Mean

0.0301(0.0419)-0.0780.0565(0.0603)-0.1600.0314(0.0702)-0.1000.0146(0.0153)-0.0000.0416(0.0347)-0.2550.0384(0.0211)-0.208N

21,24010,348

7,637

55,43015,54823,345Mean

0.0194(0.0419)0.391-0.0129(0.0649)0.380

0.0015(0.0603)
0.372-0.0168(0.0127)0.570-0.0405(0.0300)
0.488-0.0221(0.0192)
0.522

Mean

0.0099(0.0369)
0.271

0.0477(0.0563)0.261-0.0300(0.0520)0.245-0.0094(0.0119)0.358-0.0093(0.0267)
0.281-0.0040(0.0167)
0.276

N14,492

6,872

5,572

58,597

18,19926,173MCAS Math /SAT Math
MCAS ELA /SAT Verbal

Any college

Four-year
college

Notes: This table reports 2SLS estimates of non-neighborhood enrollment effects on student achievement and college
enrollment, computed in samples of Boston middle and high school applicants and New York high school applicants.
The sample, instrument, endogenous variable, and controls are as described in Table 3. Standardized test outcomesare as described in Table 2.

35

Table 5: 2SLS Estimates of School Travel Effects on Peer Race and Education Outcomes
Travel time
Boston

New YorkAllapplicantsBlackapplicants

Hispanic
applicantsAllapplicantsBlackapplicants

Hispanic
applicants

(1)

(2)

(3)

(4)

(5)

(6)

A: Peer race and minority isolation
Peer share Black-0.0272(0.0057)-0.0602(0.0076)-0.0006(0.0096)-0.0133(0.0029)-0.0698(0.0064)0.0165(0.0039)

Peer share Hispanic

0.0026(0.0050)

0.0221(0.0065)-0.0199(0.0084)-0.0161(0.0026)

0.0242(0.0050)-0.0478(0.0040)

Minority isolation-0.1551(0.0169)-0.2084(0.0239)-0.1352(0.0287)-0.0555(0.0059)-0.1012(0.0123)-0.0581(0.0099)

24,833

11,953

9,089

74,93622,82933,124N

B: Test scores and college attendance
MCAS Math /SAT Math

0.0246(0.0254)0.0229(0.0357)-0.0107(0.0421)-0.0011(0.0095)-0.0007(0.0165)

0.0063(0.0145)

21,200

10,3207,626

55,04915,44523,173

Any college-0.0146(0.0217)-0.0612(0.0303)

0.0048(0.0344)-0.0252(0.0082)-0.0187(0.0155)-0.0421(0.0135)

Four-year
college-0.0060(0.0190)-0.0262(0.0262)-0.0012(0.0298)-0.0209(0.0075)-0.0037(0.0137)-0.0314(0.0116)

14,450

6,843

5,559

57,97917,99625,907

N

N

Notes: This table reports 2SLS estimates of travel time effects on the variables at left, computed in the samples of
Boston middle and high school applicants and New York high school applicants. The sample is as described in Table
3. Travel time effects are per 20 minutes of travel. The instrument is travel time offered. The endogenous variable is
6th or 9th grade enrolled travel time. Travel time first stages are around 0.40 for Boston and 0.57 for New York. The
sample is as described in Table 3. Models include a control function – analogous to µi , defined in Equation 5 – that
controls for the expected offered travel time across possible lottery draws, as well as student demographic variables
and baseline achievement. Minority isolation is defined as in Table 3. Standardized test outcomes are as describedin Table 2.

36

Table 6a: Estimates of School Value-Added Effects on MCAS Math in Boston
All applicantsJust-ID(1)

Black applicantsOver-ID(2)(3)

Just-ID(4)

Hispanic applicantsOver-ID(5)(6)

Just-ID(7)

Over-ID(8)(9)

A: First-stage effects on value-added

Instrumental variable:
Offered school MCAS Mathvalue-added

0.434(0.018)Offered travel time

0.431
(0.018)0.014(0.003)0.455(0.024)0.007(0.003)0.450(0.024)0.016(0.004)0.400(0.031)

0.009(0.004)0.397(0.031)37

0.009(0.005)0.007(0.005)-0.329(1.429)0.803(0.172)

B: 2SLS estimates of value-added effects
Endogenous variable:
MCAS Math value-added
Over-ID

0.814(0.100)0.589(0.579)test statistic
p-valueN

0.810(0.099)0.738(0.136)0.518(0.788)0.015
0.90
20,222

21,216

20,1140.747(0.134)0.825(0.173)

0.006
0.94
9,798

10,331

9,742

0.277
0.60
7,315

7,633

7,276

Notes: This table shows 2SLS estimates of the effects of enrolled school Math value-added on 6th and 10th grade MCAS test scores (for 6th and 9th grade
applicants, respectively). Columns 1, 4, and 7 report estimates from a just-identified model that instruments enrolled value-added with offered travel time, scaledin 20 minute increments. Columns 2, 5, and 8 report the results of instrumenting enrolled value-added with offered value-added. Remaining columns report theresults of instrumenting enrolled value-added with both offered travel time and offered value-added. Estimates are computed in the sample of offered applicantsfor Boston middle and high school, with non-degenerate risk of school assignment. The sample is as described in Table 3. Models include control functions µ1
and µ2 , as defined in Equation 13, as well as student demographic variables and baseline achievement. Value-added is computed using 6th and 10th grade MCAS
math test scores (for 6th and 9th grade applicants, respectively). The risk-controlled value-added computation follows that in Angrist et al. (forthcoming).

Table 6b: Estimates of School Value-Added Effects on SAT Math in New YorkAll applicantsJust-ID(1)

Black applicantsOver-ID(2)(3)

Just-ID(4)

Hispanic applicantsOver-ID(5)(6)

Just-ID(7)

Over-ID(8)(9)

A: First-stage effects on value-added
Instrumental variable:
Offered school SAT Mathvalue-added

0.607(0.018)Offered travel time

0.608
(0.018)0.006(0.002)0.589(0.025)-0.002(0.002)0.590(0.026)0.009(0.003)0.649(0.033)0.000(0.003)0.649(0.033)0.003(0.003)-0.001(0.002)0.693(1.715)0.793(0.059)

B: 2SLS estimates of value-added effects

38

Endogenous variable:
SAT Math value-added
Over-ID

0.818(0.042)-0.100(0.578)test statistic
p-valueN

0.819(0.042)0.948(0.082)-0.106(0.855)2.923
0.09
55,42855,13055,1280.954(0.082)

0.792(0.059)2.108
0.15
15,54815,47815,4780.005
0.94
23,34523,19923,199Notes: This table shows 2SLS estimates of the effects of enrolled school Math value-added on SAT math scores. The specifications follow those in Table 6a.
Estimates are computed in the sample of offered applicants for New York high school, with non-degenerate risk of school assignment. The sample is as describedin Table 3. Models include control functions µ1 and µ2 , as defined in Equation 13, as well as student demographic variables and baseline achievement. Mathvalue-added corresponds to contemporaneous-year risk-controlled school value-added model estimates. Value-added is computed using SAT math test scores. The
risk-controlled value-added computation follows that in Angrist et al. (forthcoming).

Table 7: Neighborhood Reassignment with Increased School Capacities
Baseline scenario

Change relative to baseline

Time

Busingeligibility

Same-race
exposure

Minority
isolation

Time

Busingeligibility

Same-race
exposure

Minority
isolation

(1)

(2)

(3)

(4)

(5)

(6)

(7)

(8)

A: Boston (6th and 9th grade)
Black students

34.0

0.73

0.489

0.430

-13.1

-0.48

0.019

0.105

Hispanic students

31.1

0.66

0.478

0.365

-13.4

-0.47

-0.0150.003

Black or Hispanic students

32.6

0.70

0.834

0.398

-13.2

-0.47

0.002

0.055

-0.23
-0.23
-0.23

0.054
0.012
0.006

0.040
0.000
0.016

B: New York (9th grade)
Black students
Hispanic students
Black or Hispanic students

39.8
33.7
36.2

0.97
0.95
0.96

0.468
0.532
0.790

0.493
0.406
0.442

-17.0
-13.6
-15.0

39

Notes: The Boston sample includes students enrolled in the 2006-13 school years; the New York sample includes students enrolled in the 2012-16 school years.
Baseline statistics in columns 1-4 show student-weighted average enrolled school characteristics. Statistics are for students who: (i) participate in the matchand enroll in a match school, or (ii) do not participate in the match but enroll in a match school and have non-missing geographic information. Columns 5-8
characterize simulated alternative assignments generated by a match in which students and schools rank each other by proximity (where proximity is defined interms of driving distance). School capacities in this simulation are set to equal maximum observed enrollment (in 2001-2016 for Boston and in 2009-2019 for
New York). The statistics in columns 5-8 are changes relative to columns 1-4. Travel time is by public transit. Same-race exposure is defined as the proportion
same-race in the assigned school (in the same grade). Minority isolation is defined as in Table 3. Students are deemed busing-eligible when their driving distanceis at least 1.5 miles in Boston and at least 0.5 miles in New York.

75%
A

Appendix50%
A.1 Additional Figures and Tables
Figure A1: Racial Exposure in 100 High-Minority-Share Districts, 1988-2018

25%

0%

100%

100%

75%

75%

50%

50%

25%

25%

1988 1993 1998 2003 2008 2013 20180%0%1988 1993 1998 2003 2008 2013 2018Black students
Racial exposure
Peer share
Black

Peer share
Hispanic

1988 1993 1998 2003 2008 2013 2018

Hispanic students
Minority isolation schools

Peer shareBlack or Hispanic

Proportion enrolled at schools>90% Black or Hispanic

Proportion enrolled at schools>80% Black or Hispanic

Source: Common Core Public Elementary and Secondary School Universe Survey, documented in https://nces.ed.
gov/ccd/pubschuniv.asp.
Notes: The sample used here consists of schools in the 100 largest districts by enrollment, drawn from the set of
districts with 60-80% minority enrollment. The set of districts meeting these criteria varies by year. School districts
with less than 10 years of data are excluded. Other variable definitions and sample restrictions are as described in
Figure 2.

40

Boston 2013 Middle and High Schools

Figure A2: Boston Geocodes and Walk Zones

Fenway High School

New Mission High SchoolsizeaTechBoston Academy

0

1

2mi

West Roxbury Academy

Notes: Lines mark geocode boundaries. Blue shading marks a few school walk zones. Blue dots mark Boston highschools in 2013. Red dots mark Boston middle schools in 2013.

41

5

Table A1: OLS and 2SLS Sample Construction
Boston

New York

6th grade

9th grade

9th grade

(1)

(2)

(3)

56,827
48,14363,08850,236

394,777
389,284

32,80032,661
27,22415,15912,958
11,746
11,35810,35034,001
33,62029,766
20,475
17,922
16,556
15,818
14,529298,840
297,734
269,734
172,040
101,960
90,03083,97075,686

A: OLSAll enrolled students with demographic information
With geographic information
B: 2SLS
Applicants in the match with demographic information
With geographic information
Ranked at least two programs, the first over-subscribed
Is not guaranteed assignment at first choiceHas non-degenerate risk of school assignment
Who are offered a seat
Enroll in a school
With baseline scores

Notes: This table illustrates the construction of the OLS and 2SLS samples. The OLS sample start from the sample
of all enrolled students with demographic information and excludes students with missing geographic information(geocodes in Boston and residential districts in New York). The 2SLS sample starts with the subset of all match
applicants with demographic information and ends with the final row after implementing the sample restrictions
described in the rows of the table.

42

Table A2: Attrition and Covariate Balance
BostonMean(1)

New York

Non-nbhd
Travel timeassignment
(2)

(3)

Mean
(4)

Non-nbhd
Travel timeassignment
(5)

(5)

A: Attrition and selection into other sectors
Has outcome MCAS Math /SAT Math

0.837

0.0059(0.0087)

0.0033(0.0052)0.68-0.0120(0.0065)-0.0083(0.0036)

Has outcome MCAS ELA /SAT Reading

0.820

0.0011(0.0092)

0.0026(0.0054)0.68-0.0120(0.0065)-0.0083(0.0036)

28,344

28,341

90,06389,4510.0140(0.0069)

0.0070(0.0039)0.0011(0.0028)

0.0030(0.0017)

27,17627,173

83,97083,5020.0047(0.0081)0.0059(0.0042)-0.0016(0.0032)-0.0019(0.0017)

15,81815,81883,97083,5020.0014(0.0062)0.0047(0.0072)-0.0034(0.0074)
0.0023(0.0040)0.0006(0.0033)-0.0028(0.0066)0.0016(0.0037)
0.0050(0.0040)-0.0038(0.0040)-0.0001(0.0023)-0.0035(0.0016)-0.0072(0.0037)-0.0082(0.0109)-0.0087(0.0118)

0.0024(0.0060)
0.0030(0.0064)

75,68674,936N
Charter enrolled

0.091
N

Exam enrolled

0.065
N

0.043

0.043

B: Baseline covariates
Black

0.482

Hispanic

0.366

Female0.505

Special education

0.182

Limited English proficiency

0.114

Free and reduced-price lunch

0.805

Baseline math

-0.145Baseline English-0.112
N

24,8790.0019(0.0131)0.0013(0.0126)0.0207(0.0132)-0.0044(0.0104)
0.0035(0.0081)-0.0035(0.0103)

0.0040(0.0073)-0.0064(0.0070)-0.0008(0.0073)-0.0075(0.0057)-0.0014(0.0043)0.0011(0.0058)

0.305

0.0033(0.0232)-0.0144(0.0243)0.0043(0.0127)-0.0084(0.0136)0.045

24,87924,83375,686

0.442
0.515
0.079
0.049
0.779

0.036

Notes: This table reports coefficients from regressions of the variables listed in each row on distance and travel
instruments. Column 1 and 4 report sample means for each dependent variable. The independent variable incolumns 2 and 5 is a non-neighborhood school assignment. The independent variable in columns 3 and 6 is offered
travel time. Estimates are computed in the samples of Boston middle and high school applicants and New Yorkhigh school applicants. For columns 2 and 4, the sample, instrument (non-neighborhood assignment), and controls
are as in Table 3. For columns 3 and 5, the sample instrument (travel-time offered), and controls are as in Table
5. Travel time effects are per 20 minutes of travel. Exam school enrollment is restricted to the sample of 9th
grade applicants in Boston.

43

Table A3: 2SLS Estimates of School Travel Effects on Behavioral Outcomes
Boston

New YorkAllapplicantsBlackapplicants

Hispanic
applicantsAllapplicantsBlackapplicants

Hispanic
applicants

(1)

(2)

(3)

(4)

(5)

(6)

A: Non-neighborhood enrollment
Days absent
MeanSD-2.1073(2.4686)26.11842.20-2.5351(3.5440)
25.40541.91-4.2450(3.9591)
27.34841.35

0.2248(0.4278)13.08620.00

0.1439(1.1200)
14.87521.64

0.6216(0.6878)
14.985
21.11

N24,62911,882

9,006

75,57023,05333,403Mean
SD

0.0732(0.0675)
0.303
1.608

0.0060(0.1105)
0.375
1.374

0.1460(0.1070)
0.269
1.991

Mean
SD

-0.0087(0.0526)
0.007
1.011

-0.0413(0.0778)-0.002
0.983

0.0391(0.0895)
0.069
1.069

N

22,90910,921

8,498

Number of suspensions

Disciplinary index

B: Travel timeDays absent
MeanSD

0.5319(1.5096)26.10242.16

1.3816(2.0779)
25.40341.91-0.8008(2.4337)27.30341.26

0.7848(0.2894)13.01119.92

0.4354(0.5961)
14.76721.54

1.4132(0.4975)
14.93021.04

N24,583

11,851

8,992

74,93522,82933,124Mean
SD

0.0444(0.0425)
0.300
1.602

0.0536(0.0618)
0.370
1.358

0.0354(0.0740)
0.269
1.992

Mean
SD

0.0295(0.0314)
0.005
1.009

0.0372(0.0454)-0.0050.979

0.0321(0.0510)
0.068
1.070

N

22,863

10,8908,484

Number of suspensions

Disciplinary index

Notes: This table reports 2SLS estimates of distance and travel effects on behavioral outcomes,
computed in the samples of Boston middle and high school applicants and New York high school
applicants. For Panel A, the sample, instrument (non-neighborhood assignment), and controls are
as in Table 3. In Panel B, the sample instrument (travel-time offered), and controls are as in Table
5. The corresponding endogenous variables are 6th or 9th grade non-neighborhood enrollment andenrolled travel time. Travel time effects are per 20 minutes of travel. Outcomes are measured ineither 6th or 9th grade. Following Jackson (2018), the disciplinary index equals the first principal
component of the following outcomes: ever being suspended, number of suspensions, ever being
truant, number of days truant, ever attending a DYS school, and number of days absent. The
index is standardized to have mean zero and standard deviation one among all enrolled students.
When constructing the index, outcomes are coded so that a positive estimate reflects an increasein discipline.

44

Table A4: 2SLS Estimates of School Travel Effects on School Characteristics
Boston

New YorkAllapplicantsBlackapplicants

Hispanic
applicantsAllapplicantsBlackapplicants

Hispanic
applicants

(1)

(2)

(3)

(4)

(5)

(6)

A: Non-neighborhood enrollment
Student-teacher ratio

0.176(0.155)
Mean
13.11
SD S 3.10

0.514(0.246)
13.00
3.20

0.295
(0.233)
13.02
2.92

0.183
(0.031)
4.43
1.37

0.022
(0.082)
4.34
1.53

0.264
(0.045)4.30
1.36

Percent of teachers licensed inteaching assignment

0.009(0.008)Mean
0.90
SD S 0.14

0.012(0.012)
0.89
0.15

0.004
(0.012)
0.91
0.12

0.012
(0.003)
0.79
0.16

0.022
(0.008)
0.77
0.17

0.016
(0.005)0.77
0.17

Percent of core academic classes taught
by highly-qualified teachers

0.027(0.005)Mean
0.88
SD S 0.11

0.031(0.008)
0.88
0.12

0.026
(0.008)
0.88
0.11

0.006
(0.003)0.86
0.11-0.001(0.006)
0.85
0.11

0.017
(0.004)0.84
0.11

10,888

8,353

56,871

17,30025,194

N

22,709

B: Travel time
Student-teacher ratio

0.500(0.110)
Mean
13.11
SD S 3.10

0.726(0.159)
13.00
3.20

0.561
(0.168)
13.02
2.92

0.208
(0.022)
4.44
1.37

0.113
(0.048)
4.34
1.52

0.326
(0.032)4.30
1.36

Percent of teachers licensed inteaching assignment

0.001(0.005)Mean
0.90
SD S 0.14-0.004(0.007)
0.89
0.15

0.006
(0.007)
0.91
0.12

0.015
(0.002)
0.79
0.16

0.015
(0.004)
0.77
0.17

0.020
(0.004)0.77
0.17

Percent of core academic classes taught
by highly-qualified teachers

0.010(0.003)Mean
0.88
SD S 0.11

0.016(0.005)
0.88
0.12

0.002
(0.005)
0.88
0.11

0.010
(0.002)
0.86
0.11

0.004
(0.003)
0.85
0.11

0.017
(0.003)0.84
0.11

10,886

8,353

56,492

17,19925,011

N

22,706

Notes: This table reports 2SLS estimates of distance and travel effects on school characteristics, computed in
the samples of Boston middle and high school applicants and New York high school applicants. For Panel A,
the sample, instrument (non-neighborhood assignment), and controls are as in Table 3. In Panel B, the sample
instrument (travel-time offered), and controls are as in Table 5. The corresponding endogenous variables are 6th
or 9th grade non-neighborhood enrollment and enrolled travel time. Travel time effects are per 20 minutes oftravel. The sample is limited to offered applicants with non-degenerate risk of school assignment.

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A.2

2SLS Inference with an Estimated Control Function

Section 4.2 discusses 2SLS estimates of distance and travel effects with first and second stages thatcan be written:
Gi = γZi + κ1 µi + ν1i ,Yi = βGi + κ2 µi + ν2i .
This appendix derives the limiting distribution of a 2SLS estimator, denoted β̂2SLS , computed byreplacing the control function, µi , with an estimate, µ̂i .
Replacing µi with µ̂i in the second stage equation, we have:
Yi = βGi + κ2 µ̂i + (ν2i + κ2 (µi − µ̂i )).
DefineZ̃i = (I − Pµ̂ )Zi ,P
where Pµ̂ is the matrix that projects onto µ̂i , so that i Z̃i µ̂i = 0 by construction. Then, β̂2SLS
can be written:P
Z̃i Yiβ̂2SLS = P ii Z̃i GiPZ̃i (ν2i + κ2 (µi − µ̂i ))=β+ i
Pi Z̃i GiPZ̃i (ν2i + κ2 µi )=β+ i Pi Z̃i GiP
Z̃i ui,= β + Pii Z̃i Gi
where ui = ν2i + κ2 µi . Given random sampling, the limiting distribution of our 2SLS estimator has
sampling variance proportional to E[Z̃i2 u2i ].
Note that the residual needed for this formula is consistently estimated by ûi = Yi − β̂2SLS .
Our calculation uses the residual generated by 2SLS, however, that is, ν̂2i = Yi − β̂2SLS − κ2 µ̂i .
In practice, the distinction between the two residuals matters little for estimated standard errors.
This is apparent from a comparison of the standard deviation of the two residuals. These estimatedstandard deviations are less than 1% apart for both test scores and college enrollment outcomes in
Boston and New York.

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