metadata: authors: 0: author: Garlick, Robert
count: World
docna: 0: docna: Academic peer effects with different group
            assignment policies : residential tracking versus random assignment
docty: Policy Research Working Paper
theme: Other human development
majtheme: Human development
subtopic: Taxation & Subsidies,Demographics,Educational Sciences,Educational Institutions & Facilities,Educational Populations,Education for Development (superceded),Effective Schools and Teachers,Education For All
teratopic: Education
abstracts: cdata!: This paper studies the relative academic
            performance of students tracked or randomly assigned to
            South African university dormitories. Tracked or streamed
            assignment creates dormitories where all students obtained
            similar scores on high school graduation examinations.
            Random assignment creates dormitories that are approximately
            representative of the population of students. Tracking
            lowers students' mean grades in their first year of
            university and increases the variance or inequality of
            grades. This result is driven by a large negative effect of
            tracking on low-scoring students' grades and a
            near-zero effect on high-scoring students' grades.
            Low-scoring students are more sensitive to changes in their
            peer group composition and their grades suffer if they live
            only with low-scoring peers. In this setting, residential
            tracking has undesirable efficiency (lower mean) and equity
            (higher variance) effects. The result isolates a pure peer
            effect of tracking, whereas classroom tracking studies
            identify a combination of peer effects and differences in
            teacher behavior across tracked and untracked classrooms.
            The negative pure peer effect of residential tracking
            suggests that classroom tracking may also have negative
            effects unless teachers are more effective in homogeneous
            classrooms. Random variation in peer group composition under
            random dormitory assignment also generates peer effects.
            Living with higher-scoring peers increases students'
            grades and the effect is larger for low-scoring students.
            This is consistent with the aggregate effects of tracking
            relative to random assignment. However, using peer effects
            estimated in randomly assigned groups to predict outcomes in
            tracked groups yields unreliable predictions. This
            illustrates a more general risk that peer effects estimated
            under one peer group assignment policy provide limited
            information about how peer effects might work with a
            different peer group assignment policy.
repnme: repnme: Academic peer effects with different group
            assignment policies : residential tracking versus random assignment
display_title: Academic peer effects with different
            group assignment policies : residential tracking versus
            random assignment
listing_relative_url: /research/2014/02/19135855/academic-peer-effects-different-group-assignment-policies-residential-tracking-versus-random-assignment
topicv3: Teachers Management m1326119 1523,Demographic Change m1327040 1448,Education m1327048 470,Soft Skills m1327287 2137,Vouchers m1504820 3553
publishtoextweb_dt: 2014-02-01T00:00:00Z
historic_topic: Education
no_of_pages: 45
model_extractions: WPS6787 Policy Research Working Paper 6787 Academic Peer Effects with Different Group Assignment Policies Residential Tracking versus Random Assignment _Robert Garlick_ The World Bank Development Research Group Human Development and Public Services Team February 2014
Policy Research Working Paper 6787

# **Abstract**

This paper studies the relative academic performance of students tracked or randomly assigned to South African university dormitories. Tracked or streamed assignment creates dormitories where all students obtained similar scores on high school graduation examinations. Random assignment creates dormitories that are approximately representative of the population of students.

Tracking lowers students’ mean grades in their first year of university and increases the variance or inequality of grades. This result is driven by a large negative effect of tracking on low-scoring students’ grades and a near-zero effect on high-scoring students’ grades. Low-scoring students are more sensitive to changes in their peer group composition and their grades suffer if they live only with low-scoring peers. In this setting, residential tracking has undesirable efficiency (lower mean) and equity (higher variance) effects. The result isolates a pure peer effect of tracking, whereas classroom tracking studies identify a combination of peer effects and differences in teacher behavior across tracked and untracked classrooms. The negative pure peer effect of residential tracking suggests that classroom tracking may also have negative effects unless teachers are more effective in homogeneous classrooms.

Random variation in peer group composition under random dormitory assignment also generates peer effects. Living with higher-scoring peers increases students’ grades and the effect is larger for low-scoring students. This is consistent with the aggregate effects of tracking relative to random assignment. However, using peer effects estimated in randomly assigned groups to predict outcomes in tracked groups yields unreliable predictions. This illustrates a more general risk that peer effects estimated under one peer group assignment policy provide limited information about how peer effects might work with a different peer group assignment policy.

This paper is a product of the Human Development and Public Services Team, Development Research Group. It is part of a larger effort by the World Bank to provide open access to its research and make a contribution to development policy discussions around the world. Policy Research Working Papers are also posted on the Web at http://econ.worldbank.org. The author may be contacted at rgarlick@worldbank.org.

_The Policy Research Working Paper Series disseminates the findings of work in progress to encourage the exchange of ideas about development issues. An objective of the series is to get the findings out quickly, even if the presentations are less than fully polished. The papers carry the names of the authors and should be cited accordingly. The findings, interpretations, and conclusions expressed in this paper are entirely those of the authors. They do not necessarily represent the views of the International Bank for Reconstruction and Development/World Bank and its affiliated organizations, or those of the Executive Directors of the World Bank or the governments they represent._ Produced by the Research Support Team
# Academic Peer Effects with Different Group Assignment Policies: Residential Tracking versus Random Assignment<sup>_∗_</sup>

## Robert Garlick<sup>_†_</sup>

February 25, 2014

**Keywords:** education; inequality; peer effects; South Africa; tracking **JEL classification:** I25; I25; O15

> _∗_ This paper is a revised version of the first chapter of my dissertation. I am grateful to my advisors David Lam, Jeff Smith, Manuela Angelucci, John DiNardo, and Brian Jacob for their extensive guidance and support. I thank Raj Arunachalam, Emily Beam, John Bound, Tanya Byker, Scott Carrell, Julian Cristia, Susan Godlonton, Andrew Goodman-Bacon, Italo Gutierrez, Brad Hershbein, Claudia Martinez, David Slusky, Rebecca Thornton, Adam Wagstaff, and Dean Yang for helpful comments on earlier drafts of the paper, as well as conference and seminar participants at ASSA 2014, Chicago Harris School, Columbia, Columbia Teachers College, CSAE 2012, Cornell, Duke, EconCon 2012, ESSA 2011, Harvard Business School, LSE, Michigan, MIEDC 2012, Michigan State, NEUDC 2012, Northeastern, Notre Dame, PacDev 2011, SALDRU, Stanford SIEPR, SOLE 2012, UC Davis, the World Bank, and Yale School of Management, I received invaluable assistance with student data and institutional information from Jane Hendry, Josiah Mavundla, and Charmaine January at the University of Cape Town. I acknowledge financial support from the Gerald R. Ford School of Public Policy and Horace H. Rackham School of Graduate Studies at the University of Michigan. The findings, interpretations and conclusions are entirely those of the author. They do not necessarily represent the views of the World Bank, its Executive Directors, or the countries they represent.

> _†_ Postdoctoral Researcher in the World Bank Development Research Group and Assistant Professor in the Duke University Department of Economics; rob.garlick@gmail.com

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# **1 Introduction**

Group structures are ubiquitous in education and group composition may have important effects on education outcomes. Students in different classrooms, living environments, schools, and social groups are exposed to different peer groups, receive different education inputs, and face different institutional environments. A growing literature shows that students’ peer groups influence their education outcomes even without resource and institutional differences across groups.<sup>1</sup> Peer effects play a role in empirical and theoretical research on different ways of organizing students into classrooms and schools.<sup>2</sup> Most studies focus on the effect of assignment or selection into different peer groups for a given group assignment or selection process.<sup>3</sup> This paper advances the literature by asking a subtly different question: What are the – relative effects of two group assignment policies randomization and tracking or streaming – based on academic performance on the distribution of student outcomes? This contributes to a small but growing empirical literature on optimal group design. Comparison of different group assignment policies corresponds to a clear social planning problem: How should students be assigned to groups to maximize some target outcome, subject to a given distribution of student characteristics? Different group assignment policies leave the marginal distribution of education inputs unchanged. This raises the possibility of improving academic outcomes with few pecuniary costs. Such low cost education interventions are particularly attractive for resource-constrained education systems.

Studying peer effects under one group assignment policy provides limited information about the effect of changing the group assignment policy. Consider the comparison between

> 1Manski (1993) lays out the identification challenge in studying peer effects: do correlated outcomes within peer groups reflect correlated unobserved pre-determined characteristics, common institutional factors, or peer effects – causal relationships between students’ outcomes and their peers’ characteristics? Many papers address this challenge using randomized or controlled variation in peer group composition; peer effect have been documented on standardized test scores (Hoxby, 2000), college GPAs (Sacerdote, 2001), college entrance examination scores (Ding and Lehrer, 2007), cheating (Carrell, Malmstrom, and West, 2008), job search (Marmaros and Sacerdote, 2002), and major choices (Di Giorgi, Pellizzari, and Redaelli, 2010). Estimated peer effects may be sensitive to the definition of peer groups (Foster, 2006) and the measurement of peer characteristics (Stinebrickner and Stinebrickner, 2006).

> 2Examples include Arnott (1987) and Duflo, Dupas, and Kremer (2011) on classroom tracking, Benabou (1996) and Kling, Liebman, and Katz (2007) on neighborhood segregation, Epple and Romano (1998) and Hsieh and Urquiola (2006) on school choice and vouchers, and Angrist and Lang (2004) on school integration.

> 3See Sacerdote (2011) for a recent review that reaches a similar conclusion.

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random group assignment and academic tracking, in which students are assigned to academically homogeneous groups. First, tracking generates groups consisting of only high- or only low-performing students, which are unlikely to be observed under random assignment. Strong assumptions are required to extrapolate from small cross-group differences in mean scores observed under random assignment to large cross-group differences under that will be generated under tracking.<sup>4</sup> Second, student outcomes may depend on multiple dimensions of their peer group characteristics. Econometric models estimated under one assignment policy may omit characteristics that would be important under another assignment policy. For example, within-group variance in peer characteristics may appear unimportant in homogeneous groups under tracking but matter in heterogeneous groups under random assignment. Third, peer effects will not be policy-invariant if students’ interaction patterns change with group assignment policies. If, for example, students prefer homogeneous social groups, then the intensity of within-group interaction will be higher under tracking than random assignment. Peer effects estimated in “low-intensity” randomly assigned groups will then understate the strength of peer effects in “high-intensity” tracked groups.

I study peer effects under two different group assignment policies at the University of Cape Town in South Africa. First year students at the university were tracked into dormitories up to 2005 and randomly assigned from 2006 onward. This generated residential peer groups that were respectively homogeneous and heterogeneous in baseline academic performance. I contrast the distribution of first year students’ academic outcomes under the two policies. I use non-dormitory students as a control group in a difference-in-differences design to remove time trends and cohort I show that tracking leads to lower and more unequally distributed grade point averages (GPAs) than random assignment. Mean GPA is 0.13 standard deviations lower under tracking. Low-scoring students perform substantially worse under tracking than random assignment, while high-scoring students’ GPAs are approximately equal under the two policies. I adapt results from the econometric theory literature to estimate the effect of tracking on academic inequality. Standard measures of inequality are substantially higher under

> 4Random assignment may generate all possible types of groups if the groups are sufficiently small and group composition can be captured by a small number of summary statistics. I thank Todd Stinebrickner for this observation.

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tracking than random assignment. I explore a variety of alternative explanations for these results: time-varying student selection into dormitory or non-dormitory status, differential time trends in student performance between dormitory and non-dormitory students, limitations of GPA as an outcome measure, and direct effects of dormitory assignment on GPAs. I conclude that the results are not explained by these factors.

The mean effect size of 0.13 standard deviations is substantial for an education intervention. McEwan (2013) conducts a meta-study of experimental primary school interventions in developing countries. He finds average effects across studies of 0.12 for class size and composition interventions and 0.06 for school management or supervision interventions. Replacing tracking with random assignment thus generates gains that compare favorably to many other education interventions, albeit in different settings. The direct pecuniary cost is almost zero, yielding a particularly high benefit to cost ratio.

I then use randomly assigned dormitory-level peer groups to estimate directly the effect of living with higher- or lower-scoring peers. I find that students’ GPAs are increasing in the mean high school test scores of their peers. Low-scoring students benefit more than high-scoring students from living with high-scoring peers. Equivalently, own and peer academic performance are substitutes, rather than complements, in GPA production. This is qualitatively consistent with the effects of tracking. Peer effects estimated under random assignment can quantitatively predict features of the GPA distribution under tracking. However, the predictions are sensitive to model specification choices over which economic theory and statistical model selection criteria provide little guidance. This prediction challenge reinforces the value of cross-policy evidence on peer effects. I go on to explore the mechanisms driving these peer effects. I find that peer effects operate largely within race groups. This suggests that peer effects only arise when residential peers are also socially proximate and likely to interact directly. However, peer effects do not appear to operate through direct academic collaboration. They may operate through spillovers on time use or through transfers of soft skills.

This paper makes four contributions. First, I contribute to the literature on optimal group design in the presence of peer effects. Models by Arnott (1987) and Benabou (1996) show that the effect of peers’ characteristics on agents’ outcomes influences optimal class4
room or neighborhood assignment policies.<sup>5</sup> Empirical evidence on this topic is very limited. My paper most closely relates to Carrell, Sacerdote, and West (2013), who use peer effects estimated under random group assignment to derive an “optimal” assignment policy. Mean outcomes are, however, worse under this policy than under random assignment. They ascribe this result to changes in the structure of within-group student interaction induced by the policy change. Bhattacharya (2009) and Graham, Imbens, and Ridder (2013) establish assumptions under which peer effects based on random group assignment can predict outcomes under a new group assignment policy. The assumptions are strong: that peer effects are policy-invariant, that no out-of-sample extrapolation is required, and that relevant peer characteristics have low dimension. These results emphasize the difficulty of using peer effects estimated under one group assignment policy to predict the effects of changing the policy.

Second, I contribute to the literature on peer effects in education.<sup>6</sup> I show that student outcomes are affected by residential peers’ characteristics and by changes in the peer group assignment policy. Both analyses show that low-scoring students are more sensitive to changes in peer group composition, implying that own and peer academic performance are substitutes in GPA production. This is the first finding of substitutability in the peer effects literature of which I am aware.<sup>7</sup> I find that peer effects operate almost entirely within race groups, suggesting that spatial proximity generates peer effects only between socially proximate students.<sup>8</sup> I also find that dormitory peer effects are not stronger within than across classes. An economics student, for example, is no more strongly affected by other economics students in her dormitory than by non-economics students in her dormitory. This suggests that peer effects do not operate through direct academic collaboration but may operate through channels such as time use or transfer of soft skills, consistent with Stinebrickner

> 5A closely related literature studies the efficiency implications of private schools and vouchers in the presence of peer effects (Epple and Romano, 1998; Nechyba, 2000).

> 6This paper most closely relates to the empirical literature studying randomized or controlled group assignments. Other related work studies the theoretical foundations of peer effects models and identification conditions for peer effects with endogenously formed groups (Blume, Brock, Durlauf, and Ioannides, 2011).

> 7Hoxby and Weingarth (2006) provide a general taxonomy of peer effects other than the linear-in-means model studied by Manski (1993). Burke and Sass (2013), Cooley (2013), Hoxby and Weingarth (2006), Imberman, Kugler, and Sacerdote (2012) and Lavy, Silva, and Weinhardt (2012) find evidence of nonlinear peer effects.

> 8Hanushek, Kain, and Rivkin (2009) and Hoxby (2000) document stronger within- than across-race classroom peer effects.

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# and Stinebrickner (2006).

Third, I contribute to the literature on academic tracking by isolating a peer effects mechanism. Most existing papers estimate the effect of school or classroom tracking relative to another assignment policy or of assignment to different tracks.<sup>9</sup> However, tracked and untracked groups may differ on multiple dimensions: peer group composition, instructor behavior, and school resources (Betts, 2011; Figlio and Page, 2002). Isolating the causal effect of tracking on student outcomes via peer group composition, net of these other factors, requires strong assumptions in standard research designs. I study a setting where instruction does not differ across tracked and untracked students or across students in different tracks. Students living in different dormitories take classes together from the same instructors. While variation in dormitory-level characteristics might in principle affect student outcomes, my results are entirely robust to conditioning on these characteristics. I thus ascribe the effect of tracking to peer effects. Studying dormitories as assignment units limits the generalizability of my results but allows me to focus on one mechanism at work in school or classroom tracking. My findings are consistent with the results from Duflo, Dupas, and Kremer (2011). They find that tracked Kenyan students in first grade classrooms obtain higher average test scores than untracked students. They ascribe this to a combination of targeted instruction (positive effect for all students) and peer effects (positive and negative effects for high- and low-track students respectively).

Fourth, I make a methodological contribution to the study of peer effects and of academic tracking. These literatures strongly emphasize inequality considerations but generally do not measure the effect of different group assignment policies on inequality (Betts, 2011; Epple and Romano, 2011). I note that an inequality treatment effect of tracking can be obtained by comparing inequality measures for the observed distribution of outcomes under tracking and the counterfactual distribution of outcomes that would have been obtained in the absence of tracking. This counterfactual distribution can be estimated using standard methods for quantile treatment effects (Firpo, 2007; Heckman, Smith, and Clements, 1997). Firpo 9Betts (2011) reviews the tracking literature, including cross-country (Hanushek and Woessmann, 2006), cross-cohort (Meghir and Palme, 2005), and cross-school (Slavin, 1987, 1990) comparisons. A smaller literature studies the effect of assignment to different tracks in an academic tracking system (Abdulkadiroglu, Angrist, and Pathak, 2011; Ding and Lehrer, 2007; Pop-Eleches and Urquiola, 2013).

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(2010) and, in a different context, Rothe (2010) establish formal identification, estimation, and inference results for inequality treatment effects. I use a difference-in-differences design to calculate the treatment effects of tracking net of time trends and cohort effects. I therefore combine a nonlinear difference-in-differences model (Athey and Imbens, 2006) with an inequality treatment effects framework (Firpo, 2010). I also propose a conditional nonlinear difference-in-differences model in the online appendix that extends the original Athey-Imbens model. This extension accounts flexibly for time trends or cohort effects using inverse probability weighting (DiNardo, Fortin, and Lemiuex, 1996; Hirano, Imbens, and Ridder, 2003).

I outline the setting, research design, and data in section 2. I present the average effects of tracking in section 3, for the entire sample and for students with different high school graduation test scores. In section 4, I discuss the effects of tracking on the entire GPA distribution. I show the resultant effects on academic inequality in section 5. I then discuss the effects of random assignment to live with higher- or lower-scoring peers in section 6. I present a framework to reconcile the cross-policy and cross-dormitory results in section 7. In section 8, I report a variety of robustness checks to verify the validity of the research design used to identify the effects of tracking. I conclude in section 9 and outline the conditional nonlinear difference-in-differences model in appendix A.

# **2 Research Design**

I study a natural experiment at the University of Cape Town in South Africa, where first-year students are allocated to dormitories using either random assignment or academic tracking. This is a selective research university. During the time period I study, admissions decisions employed affirmative action favoring low-income students. The student population is thus relatively heterogeneous but not representative of South Africa.

Approximately half of the 3500-4000 first-year students live in university dormitories.<sup>10</sup> The dormitories provide accommodation, meals, and some organized social activities. Classes and instructors are shared across students from dormitories and students who do

> 10The mean dormitory size is 123 students and the interdecile range is 50 – 216. There are 16 dormitories in total, one of which closes in 2006 and one of which opens in 2007. I exclude seven very small dormitories that each hold fewer than 10 first-year students.

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not live in dormitories. Dormitory assignment therefore determines the set of residentially proximate peers but not the set of classroom peers. Students are normally allowed to live in dormitories for at most two years. They can move out of their dormitory after one year but cannot change to another dormitory. Dormitory assignment thus determines students’ residential peer groups in their first year of university; the second year peer group depends on students’ location choices. Most students live in two-person rooms and the roommate assignment process varies across dormitories. I do not observe roommate assignments. The other half of the incoming first year students live in private accommodation, typically with family in the Cape Town region.

Incoming students were tracked into dormitories up until the 2005 academic year. Tracking was based on a set of national, content-based high school graduation tests taken by all South African grade 12 students.<sup>11</sup> Students with high scores on this examination were assigned to different dormitories than students with low scores. The resultant assignments do not partition the distribution of test scores for three reasons. First, assignment incorporated loose racial quotas, so the threshold score for assignment to the top dormitory was higher for white than black students. Second, most dormitories were single-sex, creating pairs of female and male dormitories at each track. Third, late applicants for admission were waitlisted and assigned to the first available dormitory slot created by an admitted student withdrawing. A small number of high-scoring students thus appear in low-track dormitories and vice versa. These factors generate substantial overlap across dormitories’ test scores.<sup>12</sup> However, the mean peer test score for a student in the top quartile of the high school test score distribution was still 0.93 standard deviations higher than for a student in the bottom quartile.

From 2006 onward, incoming students were randomly assigned to dormitories. The policy change reflected concern by university administrators that tracking was inegalitarian and

> 11These tests are developed and moderated by a statutory body reporting to the Minister of Education. The tests are nominally criterion-referenced. Students select six subjects in grade 10 in which they will be tested in grade 12. The university converts their subject-specific letter grades into a single score for admissions decisions. A time-invariant conversion scale is used to convert international students’ A-level or International Baccalaureate scores into a comparable metric.

> 12The overlap is such that it is not feasible to use a regression discontinuity design to study the effect of assignment to higher- or lower-track dormitories. The first stage of such a design does not pass standard instrument strength tests.

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contributed to social segregation by income.<sup>13</sup> Assignment used a random number generator with _ex post_ changes to ensure racial balance.<sup>14</sup> One small dormitory ( _≈_ 1 _._ 5% of the sample) was excluded from the randomization. This dormitory charged lower fees but did not provide meals. Students could request to live in this dormitory, resulting in a disproportionate number of low-scoring students under both tracking and randomization. Results are robust to excluding this dormitory.

The policy change induced a large change in students’ peer groups. Figure 1 shows how the relationship between students’ own high school graduation test scores and their peers’ test scores changed. For example, students in the top decile lived with peers who scored approximately 0.4 standard deviations higher under tracking than random assignment; students in the bottom decile lived with peers who scored approximately 0.4 standard deviations lower. This is the identifying variation I use to study the effect of tracking.

My research design compares the students’ first year GPAs between the tracking period (2004 and 2005) and the random assignment period (2007 and 2008). I define tracking as the “treatment” even though it is the earlier policy.<sup>15</sup> I omit 2006 because first year students were randomly assigned to dormitories while second year students continued to live in the dormitories into which they had been tracked. GPA differences between the two periods may reflect cohort effects as well as peer effects. In particular, benchmarking tests show a downward trend in the academic performance of incoming first year students at South African universities over this time period (Higher Education South Africa, 2009). I therefore use a difference-in-differences design that compares the time change in dormitory students’ GPAs with the time change in non-dormitory students’ GPAs over the same period: where _i_ and _d_ index students and dormitories, _Dorm_ and _Track_ are indicator variables

> 13This discussion draws on personal interviews with the university’s Director of Admissions and Director of Student Housing.

> 14There is no official record of how often changes were made. In a 2009 interview, the staff member responsible for assignment recalled making only occasional changes.

> 15Defining random assignment as the treatment necessarily yields point estimates with identical magnitude and opposite sign.

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Figure 1: Effect of Tracking on Peer Group Composition <!-- Start of picture text --> 0.6<br>0.4<br>Mean change in peers'<br>HS grad. test scores<br>0.2<br>0<br>-0.2<br>-0.4<br>-0.6<br>-0.8<br>0 10 20 30 40 50 60 70 80 90 100<br>Dormmates' mean HS grad. test scores<br><!-- End of picture text -->

# **Percentiles of own HS grad. test scores**

_Notes:_ The curve is constructed in three steps. First, I estimate a student-level local linear regression of mean dormitory high school test scores on students’ own test scores, separately for tracked and randomly assigned dormitory students. Second, I evaluate the difference at each percentile of the test score distribution. Third, I use a percentile bootstrap with 1000 replications to construct the 95% confidence interval, stratifying by assignment policy.

equal to 1 for students living in dormitories and for students enrolled in the tracking period, _f_ ( _⃗Xid_ ) is a function of students’ demographic characteristics and high school graduation test scores,<sup>16</sup> and _⃗μd_ is a vector of dormitory fixed effects. _β_ 3 equals the average treatment effect of tracking on the tracked students under an “equal trends” assumption: that dormitory and non-dormitory students would have experienced the same mean time change in GPAs if the assignment policy had remained constant. The difference-in-differences model identifies only a “treatment on the treated” effect; caution should be exercised in extrapolating this

> 16I use a quadratic specification. The results are similar with linear or cubic _f_ ( _·_ ).

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to non-dormitory students. Model 1 requires only that the equal trends assumption holds conditional on student covariates and dormitory fixed effects. I also estimate model 1 with inverse probability weights that reweight each group of students to have the same distribution of covariates as the tracked dormitory students.<sup>17</sup> _β_ 3 does not equal the average treatment effect of tracking on the tracked students if dormitory and non-dormitory students have different counterfactual GPA time trends. If the assignment policy change affects students through channels other than peer effects, _β_ 3 recovers the correct treatment effect but its interpretation changes. I discuss these concerns in section 8.

The data on students’ demographic characteristics and high school test scores (reported in table 1) are broadly consistent with the assumption of equal time trends. Dormitory students have on average slightly higher and more dispersed scores than non-dormitory students on high school graduation tests (panel A).<sup>18</sup> They are more likely to be black, less likely to speak English as a home language, and more likely to be international students (panel B). However, the time changes between the tracking and random assignment periods are small and not significantly different between dormitory and non-dormitory students. The notable exception is that the proportion of English-speaking students moves in different directions. The proportion of students who graduated from high school early enough to enroll in university during the tracking period (2004 or earlier) but did not enroll until random assignment was introduced (2006 or later) is very small and not significantly different between dormitory and non-dormitory students (panel C). I interpret this as evidence that students did not strategically delay their entrance to university in order to avoid the tracking policy. Finally,

> 17Unlike the regression-adjusted model 1, reweighting estimators permit the treatment effect of tracking to vary across student covariates. This is potentially important in this study, where tracking is likely to have heterogeneous effects. However, the regression-adjusted and reweighted results in section 3 are very similar. DiNardo, Fortin, and Lemiuex (1996) and Hirano, Imbens, and Ridder (2003) discuss reweighting estimators with binary treatments. Reweighted difference-in-differences models are discussed in Abadie (2005) and Cattaneo (2010), who also derive appropriate weights for treatment-on-the-treated parameters. The reweighted and regression-adjusted model is robust to misspecification of either the regression or the propensity score model.

> 18I construct students’ high school graduation test scores from subject-specific letter grades, following the university’s admissions algorithm. I observe grades for all six tested subjects for 85% of the sample, for five subjects for 6% of the sample, and for four or fewer subjects for 9% of the sample. I treat the third group of students as having missing scores. I assign the second group of students the average of their five observed grades but omit them from analyses that sub-divide students by their grades.

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Table 1: Summary Statistics and Balance Tests

||(1)<br>(2)|(3)|(4)|(5)|(6)|
|---|---|---|---|---|---|
||Entire<br>Track<br>sample<br>dorm|Random<br>dorm|Track<br>non-dorm|Random<br>non-dorm|Balance<br>test _p_|
|_Panel A: High school gradu_|_ation test scores_|||||
|Mean score (standardized)|0.088<br>0.169|0.198|0.000|0.000|0.426|
|A on graduation test|0.278<br>0.320|0.325|0.222|0.253|0.108|
|_≤_C on graduation test|0.233<br>0.224|0.201|0.254|0.250|0.198|
|_Panel B: Demographic char_|_acteristics_|||||
|Female|0.513<br>0.499|0.517|0.523|0.514|0.103|
|Black|0.319<br>0.503|0.524|0.116|0.118|0.181|
|White|0.423<br>0.354|0.332|0.520|0.495|0.851|
|Other race|0.257<br>0.143|0.144|0.364|0.387|0.124|
|English-speaking|0.714<br>0.593|0.560|0.851|0.863|0.001|
|International|0.144<br>0.225|0.180|0.106|0.061|0.913|
|_Panel C: Graduated high sc_|_hool in 2004 or earlier, _|_necessary to e_|_nroll under tr_|_acking_||
|Eligible for tracking|0.516<br>1.000|0.027|1.000|0.033|0.124|
|Eligible _|_ A student|0.475<br>1.000|0.002|1.000|0.010|0.037|
|Eligible _| ≤_C student|0.527<br>1.000|0.039|1.000|0.050|0.330|
|_Panel D: High school locate_<br>|_d in Cape Town, proxy _|_for dormitory _|_eligibility_|||
|Cape Town high school|0.411<br>0.088|0.083|0.765|0.754|0.657|
|Cape Town _|_ A student|0.414<br>0.101|0.065|0.848|0.811|0.976|
|Cape Town _| ≤_C student|0.523<br>0.146|0.186|0.798|0.800|0.224|

_Notes:_ Table 1 reports summary statistics of student characteristics at the time of enrollment, for the entire sample (column 1), tracked dormitory students (column 2), randomly assigned dormitory students (column 3), tracked non-dormitory students (column 4), and randomly assigned non-dormitory students (column 5). The _p_ -values reported in column 6 are from testing whether the mean change in each variable between the tracking and random assignment periods is equal for dormitory and non-dormitory students.

there is a high and time-invariant correlation between living in a dormitory and graduating from a high school outside Cape Town. This relationship reflects the university’s policy of restricting the number of students who live in Cape Town who may be admitted to the dormitory system.<sup>19</sup> The fact that this relationship does not change through time provides some reassurance that students are not strategically choosing whether or not to live in dormitories in response to the dormitory assignment policy change. This pattern may in part reflect prospective students’ limited information about the dormitory assignment policy: the

> 19I do not observe students’ home addresses, which are used for the university’s dormitory admissions. Instead, I match records on students’ high schools to a public database of high school GIS codes. I then determine whether students attended high schools in or outside the Cape Town metropolitan area. This is an imperfect proxy of their home address for three reasons: long commutes and boarding schools are fairly common, the university allows students from very low-income neighborhoods on the outskirts of Cape Town to live in dormitories, and a small number of Cape Town students with medical conditions or exceptional academic records are permitted to live in the dormitories.

12
change was not announced in the university’s admissions materials or in internal, local, or national media. On balance, these descriptive statistics support the identifying assumption that dormitory and non-dormitory students’ mean GPAs would have experienced similar time changes if the assignment policy had remained constant.<sup>20</sup> The primary outcome variable is first-year students’ GPAs. The university did not at this time report students’ GPAs or any other measure of average grades. I instead observe students’ complete transcripts, which report percentage scores from 0 to 100 for each course. I construct a credit-weighted average score and then transform this to have mean zero and standard deviation one in the control group of non-dormitory students, separately by year. The effects of tracking discussed below should therefore be interpreted in standard deviations of GPA. The numerical scores are intended to be time-invariant measures of student performance and are not typically “curved.”<sup>21</sup> The nominal ceiling score of 100 does not bind: the highest score any student obtains averaged across her courses is 97 and the 99<sup>_th_</sup> percentile of student scores is 84. These features provide some reassurance that my results are not driven by time-varying grading standards or by ceiling effects on the grades of top students. I return to these potential concerns in section 8.

# **3 Effects of Tracking on Mean Outcomes**

Tracked dormitory students obtain GPAs 0.13 standard deviations lower than randomly assigned dormitory students (table 2 column 1). The 95% confidence interval is [-0.27, 0.01]. Controlling for dormitory fixed effects, student demographics, and high school graduation test scores yields a slightly smaller treatment effect of -0.11 standard deviations with a narrower 95% confidence interval of [-0.17, -0.04] (column 2).<sup>22</sup> The average effect of tracking is thus

> 20I also test the joint null hypothesis that the mean time changes in all the covariates are equal for dormitory and non-dormitory students. The bootstrap _p_ -value is 0.911.

> 21For example, mean percentage scores on Economics 1 and Mathematics 1 change by respectively six and nine points from year to year, roughly half of a standard deviation.

> 22The bootstrapped standard errors reported in table 2 allow clustering at the dormitory-year level. Nondormitory students are treated as individual clusters, yielding 60 large clusters and approximately 7000 singleton clusters. As a robustness check, I also use a wild cluster bootstrap (Cameron, Miller, and Gelbach, 2008). The _p_ -values are 0.090 for the basic regression model (column 1) and _<_ 0.001 for the model with dormitory fixed effects and student covariates (column 3). I also account for the possibility of persistent dormitory-level shocks with a wild bootstrap clustered at the dormitory level. The _p_ -values are 0.104 and 0.002 for the models in columns 1 and 3.

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Table 2: Average Treatment Effect of Tracking on Tracked Students

||(1)|(2)|(3)|(4)|(5)|
|---|---|---|---|---|---|
|Tracking _×_ Dormitory|-0.129|-0.107|-0.130|-0.144|-0.141|
||(0.073)|(0.040)|(0.042)|(0.073)|(0.069)|
|Tracking|0.000|0.002|-0.013|0.042|-0.009|
||(0.023)|(0.021)|(0.020)|(0.057)|(0.049)|
|Dormitory|0.172|0.138|0.173|0.221|0.245|
||(0.035)|(0.071)|(0.072)|(0.061)|(0.064)|
|Dormitory fxed efects||_×_|_×_|_×_|_×_|
|Student covariates||_×_|_×_|_×_|_×_|
|Missing data indicators|||_×_||_×_|
|Reweighting||||_×_|_×_|
|Adjusted _R_<sup>2</sup>|0.006|0.255|0.230|0.260|0.275|
|# dormitory-year clusters|60|60|60|60|60|
|# dormitory students|7480|6600|7480|6600|7480|
|# non-dormitory students|7188|6685|7188|6685|7188|

_Notes:_ Table 2 reports results from regressing GPA on indicators for living in a dormitory, the tracking period and their interaction. Columns 2-5 report results controlling for dormitory fixed effects and student covariates: gender, language, nationality, race, a quadratic in high school graduation test scores, and all pairwise interactions. Columns 2 and 4 report results excluding students with missing test scores from the sample. Columns 3 and 5 report results including all students, with missing test scores replaced with zeros and controlling for a missing test score indicator. Columns 4 and 5 report results from propensity score-weighted regressions that reweight all groups to have the same distribution of observed student covariates as tracked dormitory students. Standard errors in parentheses are from 1000 bootstrap replications clustering at the dormitory-year level, stratifying by dormitory status and assignment policy, and re-estimating the weights on each iteration.

negative and robust to accounting for dormitory fixed effects and student covariates.<sup>23</sup> This pattern holds for all results reported in the paper: accounting for student and dormitory characteristics yields narrower confidence intervals and unchanged treatment effect estimates.

How large is a treatment effect of 0.11 to 0.13 standard deviations? This is substantially smaller than the black-white GPA gap at this university (0.46 standard deviations) but larger than the female-male GPA gap (0.09). The effect size is marginally larger than when students are strategically assigned to squadrons at the US Airforce Academy (Carrell, Sacerdote, and West, 2013) and marginally smaller than when Kenyan primary school students are tracked into classrooms (Duflo, Dupas, and Kremer, 2011). These results provide a consistent picture about the plausible average short-run effects of alternative group assignment policies. These effects are not “game-changers” but they are substantial relative to many other education

> 23The regression-adjusted results in column 2 exclude approximately 9% of students with missing high school graduation test scores. I also estimate the treatment effect for the entire sample with missing data indicators and find a very similar result (column 3). Effects estimated with both regression adjustment and inverse probability weighting are marginally larger (columns 4 and 5). Trimming propensity score outliers following Crump, Hotz, Imbens, and Mitnik (2009) yields similar but less precise point estimates. This verifies that the results are not driven by lack of common support on the four groups’ observed characteristics. However, the trimming rule is optimal for the average treatment effect with a two-group research design; this robustness check is not conclusive for the average treatment effect on the treated with a difference-indifferences design.

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interventions.

Tracking changes peer groups in different ways: high-scoring students live with higherscoring peers and low-scoring students live with lower-scoring peers. The effects of tracking are thus likely to vary systematically with students’ high school test scores. I explore this heterogeneity in two ways. I first estimate conditional average treatment effects for different subgroups of students. In section 4, I estimate quantile treatment effects of tracking, which show how tracking changes the full distribution of GPAs.

I begin by estimating equation 1 fully interacted with an indicator for students who score above the sample median on their high school graduation test. Above- and below-median students’ GPAs fall respectively 0.01 and 0.24 standard deviations under tracking (cluster bootstrap standard errors 0.06 and 0.07; _p_ -value of difference 0.014). These very different effects arise even though above- and below-median students experience “treatments” of similar magnitude. Above- and below-median scoring students have residential peers who score on average 0.20 standard deviations higher and 0.27 standard deviations lower under tracking. This is not consistent with a linear response to changes in mean peer quality.<sup>24</sup> Either low-scoring students are more sensitive to changes in their mean peer group composition or GPA depends on some measure of peer quality other than mean test scores.

The near-zero treatment effect on above-median students is perhaps surprising. Splitting the sample in two may be too coarse to discern positive effects on very high-scoring students. I therefore estimate treatment effects throughout the distribution of high school test scores. Figure 2 shows that tracking reduces GPA through more than half of the distribution. The negative effects in the left tail are considerably larger than the positive effects in the right tail, though they are not statistically different. I reject equality of the treatment effects and changes in mean peer high school test scores in the right but not the left tail. These results reinforce the finding that low-scoring students are substantially more sensitive to changes in peer group composition than high-scoring students. Tracking may have a small positive effect on students in the top quartile but this effect is imprecisely estimated.<sup>25</sup>

> 24I test whether the ratio of the treatment effect to the change in mean peer test scores is equal for aboveand below-median students. The cluster bootstrap _p_ -value is 0.070.

> 25A linear difference-in-differences model interacted with quartile or quintile indicators has positive but insignificant point estimates in the top quartile or quintile.

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Figure 2: Effects of Tracking on GPA by High School Test Scores <!-- Start of picture text --> 0.6<br>0.4<br>Mean change in peers' HS test scores<br>0.2<br>0<br>0 10 20 30 40 50 60 70 80 90 100<br>-0.2<br>Average treatment effect of tracking<br>-0.4<br>-0.6<br>-0.8<br>Percentiles of high school graduation test scores<br>University GPA / Dormmates' mean test scores<br><!-- End of picture text --> _Notes:_ Figure 2 is constructed by estimating a student-level local linear regression of GPA against high school graduation test scores. I estimate the regression separately for each of the four groups (tracking/randomization policy and dormitory/nondormitory status). I evaluate the second difference at each percentile of the high school test score distribution. The dotted lines show a 95% confidence interval constructed from a nonparametric percentile bootstrap clustering at the dormitory-year level and stratifying by assignment policy and dormitory status. The dashed line shows the effect of tracking on mean peer group composition, discussed in figure 1.

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There is stronger evidence of heterogeneity across high school test scores than demographic subgroups. Treatment effects are larger on black than white students: -0.20 versus -0.11 standard deviations. However, this difference is not significant (cluster bootstrap _p_ - value 0.488) and is almost zero after conditioning on high school test scores. I also estimate a quadruple-differences model allowing the effect of tracking to differ across four race/academic subgroups (black/white _×_ above/below median). The point estimates show that tracking affects below-median students more than above-median students within each race group and affects black students more than white within each test score group. However, neither pattern is significant at any conventional level. I thus lack the power to detect any heterogeneity by race conditional on test scores. There is no evidence of gender heterogeneity: tracking lowers female and male GPAs by 0.14 and 0.12 standard deviations respectively (cluster bootstrap _p_ -value 0.897). I conclude that high school test scores are the primary dimension of treatment effect heterogeneity.

# **4 Effects of Tracking on the Distribution of Outcomes**

I also estimate quantile treatment effects of tracking on the treated students, which show how tracking changes the full GPA distribution. I first construct the counterfactual GPA distribution that the tracked dormitory students would have obtained in the absence of tracking (figure 3, first panel). The horizontal distance between the observed and counterfactual GPA distributions at each quantile equals the quantile treatment effect of tracking on the treated students (figure 3, second panel). This provides substantially more information than the average treatment effect but requires stronger identifying assumptions. Specifically, the average effect is identified under the assumption that any time changes in the mean value of unobserved GPA determinants are common across dormitory and non-dormitory students. The quantile effects are identified under the assumption that there are no time changes in the distribution of unobserved student-level GPA determinants for either dormitory or nondormitory students. GPA may experience time trends or cohort-level shocks provided these are common across all students. I discuss the implementation of this model, developed by Athey and Imbens (2006), in appendix A. I propose an extension to account flexibly for time 17
trends in observed student characteristics.

Figure 3 shows that tracking affects mainly the left tail. The point estimates are large and negative in the first quintile (0.1 - 1.1 standard deviations), small and negative in the second to fourth quintiles ( _≤_ 0 _._ 2 standard deviations), and small and positive in the top quintile ( _≤_ 0 _._ 2 standard deviations). The estimates are relatively imprecise; the 95% confidence interval excludes zero only in the first quintile.<sup>26</sup> This reinforces the pattern that the negative average effect of tracking is driven by large negative effects on the left tail of the GPA or high school test score distribution.

There is no necessary relationship between figures 2 and 3. Figure 2 shows that the average treatment effect of tracking is large and negative for students with low high school graduation test scores. Figure 3 shows that the quantile treatment effect of tracking is large and negative on the left tail of the GPA distribution. The quantile results capture treatment effect heterogeneity between and within groups of students with similar high school test scores. However, they do not recover treatment effects on specific students or groups of students without additional assumptions. See Bitler, Gelbach, and Hoynes (2010) for further discussion on this relationship.<sup>27</sup>

# **5 Effects of Tracking on Inequality of Outcomes**

The counterfactual GPA distribution estimated above also provides information about the relationship between tracking and academic inequality. Specifically, I calculate several standard inequality measures on the observed and counterfactual distributions. The differences between these measures are the inequality treatment effects of tracking on the tracked students.<sup>28</sup> The literature on academic tracking emphasizes inequality concerns (Betts, 2011).

> 26I construct the 95% confidence interval at each half-percentile using a percentile cluster bootstrap. The validity of the bootstrap has not been formally established for the nonlinear difference-in-differences model. However, Athey and Imbens (2006) report that bootstrap confidence intervals have better coverage rates in a simulation study than confidence intervals based on plug-in estimators of the asymptotic covariance matrix. 27 Garlick (2012) presents an alternative approach to rank-based distributional analysis. Using this approach, I estimate the effect of tracking on the probability that students change their rank in the distribution of academic outcomes from high school to the first year of university. I find no effect on several measures of rank changes. Informally, this shows that random dormitory assignment, relative to tracking, helps lowscoring students to “catch-up” to their high-scoring peers but does not facilitate “overtaking.”

> 28I apply the same principle to calculate mean GPA for the counterfactual distribution. The observed mean is 0.16 standard deviations lower than the counterfactual mean (cluster bootstrap standard error 0.07).

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Figure 3: Quantile Treatment Effects of Tracking on the Tracked Students <!-- Start of picture text --> 100<br>80<br>Observed<br>distribution<br>60<br>40<br>Counterfactual<br>distribution<br>20<br>0<br>-4 -3 -2 -1 0 1 2 3<br>University GPA<br>0.6<br>0.4<br>0.2<br>0<br>0 10 20 30 40 50 60 70 80 90 100<br>-0.2<br>Quantile treatment effects of tracking<br>-0.4<br>-0.6<br>-0.8<br>-1<br>-1.2<br>-1.4<br>-1.6<br>Percentiles of university GPA<br>Percentiles<br>University GPA<br><!-- End of picture text --> _Notes:_ The first panel shows the observed GPA distribution for tracked dormitory students (solid line) and the counterfactual constructed using the reweighted nonlinear difference-in-differences model discussed in appendix A (dashed line). The propensity score weights are constructed from a model including student gender, language, nationality, race, a quadratic in high school graduation test scores, all pairwise interactions, and dormitory fixed effects. The second panel shows the horizontal distance between the observed and counterfactual GPA distributions evaluated at each half-percentile. The axes are reversed for ease of interpretation. The dotted lines show a 95% confidence interval constructed from a percentile bootstrap clustering at the dormitory-year level, stratifying by assignment policy and dormitory status, and re-estimating the weights on each iteration.

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Table 3: Inequality Treatment Effects of Tracking

||(1)<br>Observed<br>distribution|(2)<br>Counterfactual<br>distribution|(3)<br>Treatment<br>efect|(4)<br>Treatment efect<br>in % terms|
|---|---|---|---|---|
|Interquartile range|1.023|0.907|0.116|12.79|
||(0.043)|(0.047)|(0.062)|(6.8)|
|Interdecile range|2.238|1.857|0.381|20.52|
||(0.083)|(0.091)|(0.109)|(5.9)|
|Standard deviation|0.909|0.766|0.143|18.67|
||(0.027)|(0.032)|(0.037)|(4.8)|

_Notes:_ Table 3 reports summary measures of academic inequality for the observed distribution of tracked dormitory students’ GPA (column 1) and the counterfactual GPA distribution for the same students in the absence of tracking (column 2). The counterfactual GPA is constructed using the reweighted nonlinear difference-in-differences model described in appendix A. Column 3 shows the treatment effect of tracking on the tracked students. Column 4 shows the treatment effect expressed as a percentage of the counterfactual level. The standard deviation is estimated by (E<sup>ˆ</sup> [ _GPA_<sup>2</sup> ] _−{_ E<sup>ˆ</sup> [ _GPA_ ] _}_<sup>2</sup> )<sup>0</sup><sup>_._5</sup> , with the expectations constructed by integrating the area to the left of the relevant GPA distribution. The distribution is evaluated at half-percentiles to minimize measurement error due to the discreteness of the counterfactual distribution. Standard errors in parentheses are from 1000 bootstrap replications clustering at the dormitory-year level and stratifying by assignment policy and dormitory status.

This is the first study of which I am aware to measure explicitly the effect of tracking on inequality. Existing results from the econometric theory literature can be applied directly to this problem (Firpo, 2007, 2010; Rothe, 2010). Identification of these inequality effects requires no additional assumptions beyond those already imposed in the quantile analysis.

Table 3 shows inequality measures for the observed and counterfactual GPA distributions. The standard deviation and interquartile and interdecile ranges are all significantly higher under tracking than under the counterfactual.<sup>29</sup> Tracking increases the interquartile range by approximately 12% of its baseline level and the other measures by approximately 20%. This reflects the particularly large negative effect of tracking on the lowest quantiles of the GPA distribution. Tracking thus decreases mean academic outcomes and increases academic inequality. Knowledge of the quantile and inequality treatment effects permits a more comprehensive evaluation of the welfare consequences of tracking. These parameters might inform an inequality-averse social planner’s optimal trade-off between efficiency and equity if the mean effect of tracking were positive, as found in some other contexts.

> This is consistent with the average effect from the linear difference-in-differences models in section 3.

> 29I do not calculate other common inequality measures such as the Gini coefficient and Theil index because standardized GPA is not a strictly positive variable.

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# **6 Effects of Random Variation in Dormitory Composi-**

# **tion**

The principal research design uses cross-policy variation by comparing tracked and randomly assigned dormitory students. My second research design uses cross-dormitory variation in peer group composition induced by random assignment. I first use a standard test to confirm the presence of residential peer effects, providing additional evidence that the main results are not driven by confounding factors. I document differences in dormitory-level peer effects within and between demographic and academic subgroups, providing some information about mechanisms. In section 7, I explore whether peer effects estimated using random dormitory assignment can predict the distributional effects of tracking. I find that low-scoring students are more sensitive to changes in peer group composition than high-scoring students, which is qualitatively consistent with the effect of tracking. Quantitative predictions are, however, sensitive to model specification choices.

I first estimate the standard linear-in-means model (Manski, 1993): where _HSid_ and _HSd_ are individual and mean dormitory high school graduation test scores, _Xid_ is a vector of student demographic characteristics, and _⃗μ_ is a vector of dormitory fixed effects. _α_ 2 measures the average gain in GPA from a one standard deviation increase in the mean high school graduation test scores of one’s residential peers.<sup>30</sup> Random dormitory assignment ensures that _HSd_ is uncorrelated with individual students’ unobserved characteristics so _α_ 2 can be consistently estimated by least squares.<sup>31</sup> However, random assignment also means that average high school graduation test scores are equal in expectation. _α_ 2 is identified using sample variation in scores across dormitories due to finite numbers of

> 30 _α_ 2 captures both “endogenous” effects of peers’ GPA and “exogenous” effects of peers’ high school graduation test scores, using Manski’s terminology. Following the bulk of the peer effects literature, I do not attempt to separate these effects.

> 31The observed dormitory assignments are consistent with randomization. I fail to reject equality of dormitory means for high school graduation test scores (bootstrap _p_ -value 0.762), proportion black (0.857), proportion white (0.917), proportion other races (0.963), proportion English-speaking (0.895), proportion international (0.812), and for all covariates jointly (0.886).

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Table 4: Peer Effects from Random Assignment to Dormitories

||(1)|(2)|(3)|(4)|(5)|(6)|
|---|---|---|---|---|---|---|
|Own HS graduation|0.362|0.332|0.331|0.400|0.373|0.373|
|test score|(0.014)|(0.014)|(0.014)|(0.024)|(0.023)|(0.023)|
|Own HS graduation||||0.137|0.144|0.142|
|test score squared||||(0.017)|(0.017)|(0.017)|
|Mean dorm HS graduation|0.241|0.222|0.220|0.221|0.208|0.316|
|test score|(0.093)|(0.098)|(0.121)|(0.095)|(0.103)|(0.161)|
|Mean dorm HS graduation||||0.306|0.311|-0.159|
|test score squared||||(0.189)|(0.207)|(0.316)|
|Own _×_ mean dorm HS||||-0.129|-0.132|-0.132|
|graduation test score||||(0.073)|(0.069)|(0.069)|
|_p_-value of test against||||0.000|0.000|0.000|
|equivalent linear model|||||||
|Adjusted _R_<sup>2</sup>|0.213|0.236|0.248|0.244|0.270|0.278|
|# students|3068|3068|3068|3068|3068|3068|
|# dormitory-year clusters|30|30|30|30|30|30|

_Notes:_ Table 4 reports results from estimating equations 2 (columns 1-3) and 4 (columns 4-6). Columns 2, 3, 5, and 6 control for students’ gender, language, nationality and race. Columns 3 and 6 include dormitory fixed effects. The sample is all dormitory students in the random assignment period with non-missing high school graduation test scores. Standard errors in parentheses are from 1000 bootstrap replications clustering at the dormitory-year level.

students in each dormitory. This variation is relatively low: the range and variance of dormitory means are approximately 10% of the range and variance of individual scores. Given this limited variation, the results should be interpreted with caution.

I report estimates of equation 2 in table 4, using the sample of all dormitory students in the ˆ random assignment period. I find that _α_ 2 = 0 _._ 22, which is robust to conditioning on student demographics and dormitory fixed effects. Hence, moving a student from the dormitory with the lowest observed mean high school graduation test score to the highest would increase her GPA by 0 _._ 18 standard deviations. These effects are large relative to existing estimates (Sacerdote, 2011). Stinebrickner and Stinebrickner (2006) suggest a possible reason for this pattern. They document that peers’ study time is an important driver of peer effects and that peer effects are larger using a measure that attaches more weight to prior study behavior: high school GPA instead of SAT scores. I measure peer characteristics using scores on a content-based high school graduation test, while SAT scores are a common measure in existing research. However, the coefficient from the dormitory fixed effects regression is fairly imprecisely estimated (90% confidence interval from 0 _._ 02 to 0 _._ 42) so the magnitude should be interpreted with caution.<sup>32</sup> This may reflect the limited variation in _HSd_ .

> 32As a robustness check, I use a wild cluster bootstrap to approximate the distribution of the test statistic under the null hypothesis of zero peer effect. This yields _p_ -values of 0.088 using dormitory-year clusters and

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Table 5: Subgroup Peer Effects from Random Assignment to Dormitories

||(1)|(2)|(3)|(4)|
|---|---|---|---|---|
|Own HS graduation|0.327|0.327|0.369|0.322|
|test score|(0.016)|(0.016)|(0.017)|(0.017)|
|Mean dorm HS graduation test|0.203|0.162|||
|score for own race|(0.059)|(0.083)|||
|Mean dorm HS graduation test|-0.007|-0.035|||
|score for other races|(0.055)|(0.091)|||
|Mean dorm HS graduation test|||0.050|0.099|
|score for own faculty|||(0.045)|(0.048)|
|Mean dorm HS graduation test|||0.198|0.190|
|score for other faculties|||(0.062)|(0.083)|
|Adjusted _R_<sup>2</sup>|0.219|0.243|0.214|0.249|
|# students|3068|3068|3068|3068|
|# dormitory-year clusters|30|30|30|30|

_Notes:_ Table 5 reports results from estimating equation 3 using race subgroups (columns 1-2) and faculty subgroups (columns 3- 4). “Faculty” refers to colleges/schools within the university such as commerce and science. Columns 2 and 4 include dormitory fixed effects and control for students’ gender, language, nationality and race. The sample is all dormitory students in the random assignment period with non-missing high school graduation test scores. Standard errors in parentheses are from 1000 bootstrap replications clustering at the dormitory-year level.

The linear-in-means model can be augmented to allow the effect of residential peers to vary within and across sub-dormitory groups. Specifically, I explore within- and across-race peer effects by estimating: For student _i_ of race _r_ in dormitory _d_ , _HSrd_ and _HS−rd_ denote the mean high school graduation test scores for other students in dormitory _d_ of, respectively, race _r_ and all other race ˆ ˆ groups. _β_ 2 and _β_ 3 equal 0 _._ 16 and _−_ 0 _._ 04 respectively (table 5, column 2). The difference strongly suggests that peer effects operate primarily within race groups but it is quite imprecisely estimated (bootstrap _p_ -value 0.110). I interpret this as evidence that spatial proximity does not automatically generate peer effects. Instead, peer groups are formed through a combination of spatial proximity and proximity along other dimensions such as race, which remains highly salient in South Africa.<sup>33</sup> This indicates that interaction patterns by students may mediate residential peer effects, meaning that estimates are not policy-invariant.

> 0.186 using dormitory clusters.

> 33I find a similar result using language instead of race to define subgroups. This pattern could also arise if students sort into racially homogeneous geographic units by choosing rooms within their assigned dormitories. As I do not observe roommate assignments, I cannot test this mechanism.

23
I also explore the content of the interaction patterns that generate residential peer effects by estimating equation 3 using faculty/school/college groups instead of race groups. The estimated within- and across-faculty peer effects are respectively 0 _._ 10 and 0 _._ 19 (cluster bootstrap standard errors 0 _._ 05 and 0 _._ 08). Despite their relative imprecision, these results suggests that within-faculty peer effects are not systematically stronger than cross-faculty peer effects.<sup>34</sup> This result is not consistent with peer effects being driven by direct academic collaboration such as joint work on problem sets or joint studying for examinations. Interviews with students at the university suggest two channels through which peer effects operate: time allocation over study and leisure activities, and transfers of tacit knowledge such as study skills, norms about how to interact with faculty, and strategies for navigating academic bureaucracy. This is consistent with prior findings of strong peer effects on study time (Stinebrickner and Stinebrickner, 2006) and social activities (Duncan, Boisjoly, Kremer, Levy, and Eccles, 2005).

Combining the race- and faculty-level peer effects results indicates that spatial proximity alone does not generate peer effects. Some direct interaction is also necessary and is more likely when students are also socially proximate. However, the relevant form of the interaction is not direct academic collaboration. The research design and data cannot conclusively determine what interactions do generate the estimated peer effects.

34 Each student at the University of Cape Town is registered in one of six faculties: commerce, engineering, health sciences, humanities and social sciences, law, and science. Some students take courses exclusively within their faculty (engineering, health sciences) while some courses overlap across multiple faculties (introductory statistics is offered in commerce and science, for example). I obtain similar results using coursespecific grades as the outcome and allowing residential peer effects to differ at the course level. For example, I estimate equations 2 and 3 with Introductory Microeconomics grades as an outcome. I find that there are strong peer effects on grades in this course (ˆ _α_ 2 = 0 _._ 34 with cluster bootstrap standard error 0 _._ 15) but they are not driven primarily by other students in the same course ( _β_<sup>ˆ</sup> 2 = 0 _._ 06 and _β_<sup>ˆ</sup> 3 = 0 _._ 17 with cluster bootstrap standard errors 0 _._ 17 and 0 _._ 15). This, and other course-level regressions, are consistent with the main results but the smaller sample sizes yield relatively imprecise estimates that are somewhat sensitive to the inclusion of covariates.

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# **7 Reconciling Cross-Policy and Cross-Dormitory Results**

The linear-in-means model restricts average GPA to be invariant to any group reassignment: moving a strong student to a new group has equal but oppositely signed effects on her old and new peers’ average GPA. If the true GPA production function is linear, then the average treatment effect of tracking relative to random assignment must be zero. I therefore estimate a more general production function that permits nonlinear peer effects: This is a parsimonious specification that permits average outcomes to vary over assignment processes but may not be a perfect description of the GPA production process. In particular, I use only the mean as a summary of peer group characteristics.<sup>35</sup> _γ_ 12 and _γ_ 22 are the key parameters of the model. _γ_ 12 indicates whether own and peer high school graduation test scores are complements or substitutes in GPA production, and whether GPA is super- or submodular in own and peer test scores. If _γ_ 12 _<_ 0, the GPA gain from high-scoring peers is larger for low-scoring students. In classic binary matching models, this parameter governs whether positive or negative assortative matching is output-maximizing (Becker, 1973). In matching models with more than two agents, _γ_ 12 is not sufficient to characterize the outputmaximizing set of matches. _γ_ 22 indicates whether GPA is a concave or convex function of peers’ mean high school graduation test scores. If _γ_ 22 _<_ 0, total output is higher when mean test scores are identical in all groups. If _γ_ 22 _>_ 0, total output is higher when some groups have very high means and some groups have very low means. This parameter has received relatively little attention in the peer effects literature but features prominently in some models of neighborhood effects (Benabou, 1996; Graham, Imbens, and Ridder, 2013). Tracking will deliver higher total GPA than random assignment if both parameters are positive and vice

> 35See Carrell, Sacerdote, and West (2013) for an alternative parameterization and Graham (2011) for background discussion. Equation 4 has the attractive feature of aligning with theoretical literatures on binary matching and on neighborhood segregation. The results are qualitatively similar if dormitory-year means are replaced with medians.

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versa. If the parameters have different signs, the average effect of tracking is ambiguous.<sup>36</sup> Estimates from equation 4 are shown in table 4 columns 4, 5 (controlling for student demographics) and 6 (with dormitory fixed effects). _γ_ ˆ12 is negative and marginally statistically significant across all specifications. The point estimate of _−_ 0 _._ 13 (cluster bootstrap standard error 0 _._ 07) implies the GPA gain from an increase in peers’ mean test scores is 0.2 standard deviations larger for students at the 25<sup>th</sup> percentile of the high school test score distribution than students at the 75<sup>th</sup> percentile. This is consistent with the section 4 result that low-scoring students are hurt more by tracking than high-scoring students are helped. However, the sign of _γ_ ˆ22 flips from positive to negative with the inclusion of dormitory fixed effects. It is thus unclear whether GPA is concave or convex in mean peer group test scores.

I draw three conclusions from these results. First, there is clear evidence of nonlinear peer effects from the cross-dormitory variation generated under random assignment. Likelihood ratio tests prefer the nonlinear models in columns 4-6 to the corresponding linear models in columns 1-3. Second, peer effects estimates using randomly induced cross-dormitory variation may be sensitive to the support of the data. Using dormitory fixed effects reduces the variance of _HSd_ from 0 _._ 19 to 0 _._ 11. This leads to different conclusions about the curvature of the GPA production function in columns 5 and 6. Third, the results from the fixed effects specification (column 6) are qualitatively consistent with the negative average treatment effect of tracking.

Are the coefficient estimates from equation 4 quantitatively, as well as qualitatively, consistent with the observed treatment effects of tracking? I combine coefficients from estimating equation 4 for randomly assigned dormitory students with observed values of individual- and dormitory-level regressors for tracked dormitory students. I then predict the level of GPA and the treatment effect of tracking for students in the first and fourth quartiles of the high school graduation test score distribution. I compare these predictions to observed GPA for tracked dormitory students and to the difference-in-differences treatment effect of tracking.

The results in table 6 show that the predictions are sensitive to specification of equation

> 36To derive this result, note that E[ _HSd|HSid_ ] = _HSid_ under tracking and E[ _HSid_ ] under random as- ~~2~~ signment. Hence, E[ _HSidHSd_ ] and E[ _HSd_<sup>]bothequalE[</sup><sup>_HS_</sup> _id_<sup>2]undertrackingandE[</sup><sup>_HSid_]2underran-</sup> dom assignment. Plugging these results into equation 4 for each assignment policy yields E[ _Yid|_ Tracking] _−_ E[ _Yid|_ Randomization] = _σHS_<sup>2(</sup><sup>_γ_22 +</sup><sup>_γ_12).Thissimpledemonstrationassumesaninfinitenumberofstudents</sup> and dormitories. This assumption is not necessary but simplifies the exposition.

26
Table 6: Observed and Predicted GPA Using Different Production Function Specifications

||(1)<br>Quartile 4|(2)<br>Quartile 1|
|---|---|---|
|Panel A: Mean GPA|||
|Observed|0.761|-0.486|
|Predicted, without dormitory fxed efects|0.889|-0.345|
|Predicted, least squares with dormitory dummies|0.698|-0.433|
|Predicted, within-group transformation|0.689|-0.503|
|Panel B: Mean treatment efect of tracking|||
|Estimated from diference-in-diferences design|0.032|-0.225|
|Predicted, without dormitory fxed efects|0.223|-0.050|
|Predicted, least squares with dormitory dummies|0.041|-0.139|
|Predicted, within-group transformation|0.032|-0.195|

_Notes:_ Table 6 panel A reports observed GPA (row 1) and predicted GPA from three different models. All predictions use observed regressor values from tracked dormitory students and estimated coefficients from randomly assigned dormitory students. The first prediction uses coefficients generated by estimating equation 4 without dormitory fixed effects (shown in column 5 of table 4). The second prediction uses coefficients generated by estimating equation 4 with dormitory indicator variables (shown in column 6 of table 4). The third prediction uses coefficients generated by estimating equation 4 with data from a withindormitory transformation (shown in column 6 of table 4). The second and third predictions differ because the values of the dormitory fixed effects respectively are and are not used in the prediction.

4. Excluding dormitory fixed effects (row 2) yields very inaccurate predictions, with GPA and treatment effects too high for students in the top and bottom quartiles. This reflects the estimated convexity of the GPA production function without dormitory fixed effects (ˆ _γ_ 22 = 0 _._ 31 but insignificant). With dormitory fixed effects included, the production function is not convex (ˆ _γ_ 22 = _−_ 0 _._ 16 but insignificant) and own and peer test scores are substitutes (ˆ _γ_ 12 = 0 _._ 13). The fixed effects estimates thus predict negative and zero treatment effects on the first and fourth quartiles respectively, matching the difference-in-differences estimates. However, the first quartile estimates are quite sensitive to specifying the fixed effects with dormitory dummies (row 3) or using a within-group data transformation (row 4).

This exercise illustrates that a simple reduced form GPA production function can come close to predicting the treatment effects of tracking. However, the predictions are very sensitive to specification choices regarding covariates and group fixed effects, which in turn influence the support of the data. These are precisely the choices for which economic theory is likely to provide little guidance. Statistical model selection criteria are also inconclusive in this setting.<sup>37</sup> This sensitivity may be due to out-of-sample extrapolation, dependence of GPA on group-level statistics other than the mean, or behavioral responses by students that

> 37For example, the Akaike and Bayesian information criteria are lower for the models respectively with and without dormitory fixed effects, while a likelihood ratio test for equality of the models has _p_ -value 0.083. Hurder (2012) finds that model selection criteria are also inconclusive in a similar application.

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make peer effects policy-sensitive.

# **8 Alternative Explanations for the Effects of Tracking**

I consider four alternative explanations that might have generated the observed GPA difference between tracked and randomly assigned dormitory students. The first two explanations are violations of the “parallel time changes” assumption: time-varying student selection regarding whether or not to live in a dormitory and differential time trends in dormitory and non-dormitory students’ characteristics. The third explanation is that the treatment effects are an artefact of the grading system and do not reflect any real effect on learning. The fourth explanation is that dormitory assignment affects GPA through a mechanism other than peer effects; this would not invalidate the results but would change their interpretation.

## **8.1 Selection into Dormitory Status**

The research design assumes that non-dormitory students are an appropriate control group for any time trends or cohort effects on dormitory students’ outcomes. This assumption may fail if students select whether or not to live in a dormitory based on the assignment policy. I argue that such behavior is unlikely and that my results are robust to accounting for selection. First, the change in dormitory assignment policy was not officially announced or widely publicized, limiting students’ ability to respond. Second, table 1 shows that there are approximately equal time changes in dormitory and non-dormitory students’ demographic characteristics and high school graduation test scores. Third, the results are robust to accounting for small differences in these time changes using regression or reweighting.

Fourth, admission rules cap the number of students from Cape Town who may be admitted to the dormitory system. Given this rule, I use an indicator for whether each student attended a high school outside Cape Town as an instrument for whether the student lives in a dormitory. High school location is an imperfect proxy for home address, which I do not observe. Nonetheless, the instrument strongly predicts dormitory status: 76% of non-Cape Town students and 8% of Cape Town students live in dormitories. The intention-to-treat and instrumented treatment effects (table 7, columns 2 and 3) are very similar to the treatment 28
effects without instruments (table 2).

# **8.2 Time Trends in Student Characteristics**

The research design assumes that dormitory and non-dormitory students’ GPAs do not have different time trends for reasons unrelated to the change in assignment policy. I present three arguments against this concern. First, I extend the analysis to include data from the 2001–2002 academic years (“early tracking”), in addition to 2004–2005 (“late tracking”) and 2007–2008 (random assignment). I do not observe dormitory assignments in 2001–2002 so I report only intention-to-treat effects.<sup>38</sup> The raw data are shown in the first panel of figure 4. I estimate the effect of tracking under several possible violations of the parallel trends assumption. The average effect of tracking comparing 2001-2005 to 2007-2008 is -0.09 with standard error 0.04 (table 7, column 4). This estimate is appropriate if one group of students experiences a transitory shock in 2004/2005. A placebo test comparing the difference between Cape Town and non-Cape Town students’ GPAs in 2001-2002 and 2004-2005 yields a small positive but insignificant effect of 0.06 (standard error 0.05). I subtract the placebo test result from the original treatment effect estimate to obtain a “trend-adjusted” treatment effect of -0.18 with standard error 0.10 (table 7, column 6). This estimate is appropriate if the two groups of students have linear but non-parallel time trends and are subject to common transitory shocks (Heckman and Hotz, 1989). Finally, I estimate a linear time trend in the GPA gap between Cape Town and non-Cape Town students from 2001 to 2005. I then project that trend into 2007–2008 and estimate the deviation of the GPA gap from its predicted level. This method yields a treatment effect of random assignment relative to tracking of 0.14 with standard error 0.09 (table 7, column 5). This estimate is appropriate if the two groups of students have non-parallel time trends whose difference is linear. The effect of tracking is relatively robust across the standard difference-in-differences model and all three models estimated under weaker assumptions. However, there is some within-policy

> 38The cluster bootstrap standard errors do not take into account potential clustering within (unobserved) dormitories in 2001–2002 and so may be downward-biased. I omit the 2003 academic year because the data extract I received from the university had missing identifiers for approximately 80% of students in that year. I omit 2006 because first year students were randomly assigned to dormitories that still contained tracked second year students. The results are robust to including 2006.

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|GPA _|_ non-<br>exclusion<br>(11)<br>-0.077<br>(0.050)<br>_×_<br>_×_<br>_×_<br>0.302<br>60<br>7449<br>7043<br>(outcome), whether<br>is on the treatment<br>te, column 2 shows<br>e. Columns 4–6 use<br>ng all four observed<br>redicted GPA from<br>king to the last two<br>s estimate with the<br> only one period or<br>rence-in-diferences<br>diferences estimate<br>fying by assignment<br>ts are not observed.|
|---|
|% credits<br>excluded<br>(10)<br>0.027<br>(0.005)<br>_×_<br>_×_<br>_×_<br>0.052<br>60<br>7480<br>7188<br>udents’ GPA <br>nt of interest <br>t stage estima<br> stage outcom<br>mate compari<br>ignment and p<br>o years of trac<br>e-in-diference<br>er observed in <br> reports a dife<br> diference-in-<br>ications, strati<br>ory assignmen|
|(9)<br>-0.165<br>(0.044)<br>_×_<br>_×_<br>_×_<br>_×_<br>0.229<br>60<br>7480<br>7188<br>p between st<br>The coefcie<br>hows the frs<br>ith the frst <br>ferences esti<br> random ass<br> the frst tw<br>ts a diferenc<br>that are eith<br> Column 10 <br> 11 reports a<br>otstrap repl<br>hich dormit|
|(8)<br>-0.139<br>(0.043)<br>_×_<br>_×_<br>_×_<br>0.242<br>52<br>6795<br>7188<br>relationshi<br>rument). <br>olumn 1 s<br> colinear w<br>rence-in-di<br>GPA under<br> comparing <br>mn 7 repor<br>rmitories <br>xed efects.<br>e. Column <br>om 1000 bo<br>s 4-6, for w|
|No. of<br>credits<br>(7)<br>-0.013<br>(0.038)<br>_×_<br>_×_<br>_×_<br>0.127<br>60<br>7480<br>7188<br>1–3 show the <br>pe Town (inst<br>king period. C<br>cause they are<br>reports a dife<br>een observed <br>iferences test <br> (1989). Colu<br>e excluding do<br>ulty/school f<br>as the outcom<br>entheses are fr<br>ata in column|
|(6)<br>-0.115<br>(0.055)<br>0.058<br>(0.052)<br>-0.175<br>(0.100)<br>2001-<br>-2008<br>0.000<br>60<br>8509<br>14203<br> Columns <br>outside Ca<br>ng the trac<br>xcluded be<br>Column 4 <br>rence betw<br>erence-in-d<br> and Hotz <br>ces estimat<br> college/fac<br> excluded <br>rors in par<br>2001-2002 d|
|(5)<br>0.141<br>(0.093)<br>2001-<br>-2008<br>_×_<br>0.000<br>60<br>8509<br>14203<br>ns 8.1 - 8.3. <br>ols located <br>iversity duri<br> efects are e<br>ssumption. <br>orts the dife<br> placebo dif<br>ng Heckman<br>e-in-diferen<br>te including<br>academically<br> Standard er<br>cept for the|
|(4)<br>-0.090<br>(0.044)<br>2001-<br>-2008<br>0.002<br>60<br>8509<br>14203<br> in subsectio<br>om high scho<br>nded the un<br>mitory fxed <br>ime trends a<br>olumn 5 rep<br> reports the <br>fects followi<br>s a diferenc<br>ences estima<br>tudents are <br>he outcome. <br>r clusters ex|
|(3)<br>-0.133<br>(0.050)<br>_×_<br>_×_<br>_×_<br>0.231<br>60<br>6915<br>6466<br>ks discussed <br>raduated fr<br>tudents atte<br>timate. Dor<br>he parallel t<br>signment. C<br>d. Column 6<br>nd placebo e<br>mn 8 report<br>ence-in-difer<br>from which s<br>d courses as t<br>ormitory-yea|
|(2)<br>-0.093<br>(0.034)<br>_×_<br>_×_<br>0.231<br>60<br>6915<br>6466<br>ustness chec<br>ether they g<br>or whether s<br>ws the IV es<br>008 to test t<br>f random as<br>acking perio<br> the main a<br>tcome. Colu<br>orts a difer<br>e of courses <br>non-exclude<br> resamples d|
|Outcome<br>Dorm<br>(default is GPA)<br>student<br>(1)<br>Cape Town high school<br>0.601<br>(0.019)<br>Cape Town high school<br>_×_ tracking period<br>Dormitory _×_<br>tracking period<br>Cape Town high school<br>_×_ randomization period<br>Placebo pre-treatment<br>dif-in-dif<br>Trend-corrected<br>treatment efect<br>Sample period (default<br>is 2004-2008)<br>Dormitory fxed efects<br>Student covariates<br>_×_<br>Missing data indicators<br>_×_<br>Instruments<br>Faculty fxed efects<br>Pre-treatment time trend<br>Adjusted _R_2<br>0.525<br># dorm-year clusters<br>60<br># dormitory students<br>6915<br># non-dorm students<br>6466<br>_Notes:_ Table 7 reports results from the rob<br>they live in dormitories (treatment) and wh<br>or instrument interacted with an indicator f<br>the reduced form estimate, and column sho<br>data from 2001-2002, 2004-2005, and 2007-2<br>years of tracking to the two observed years o<br>a linear time trend extrapolated from the tr<br>years of tracking and the diference between<br>credit-weighted number of courses as the ou<br>use a diferent admission rule. Column 9 rep<br>estimate with the credit-weighted percentag<br>with GPA calculated using only grades from<br>policy and dormitory status. The bootstrap|

30
GPA variation through time: intention-to-treat students (those from high schools outside Cape Town) strongly outperform control students in 2006 and 2007 but not 2008. The reason for this divergence is unclear.

Second, the time trends in the proportion of graduating high school students who qualify for admission to university are very similar for Cape Town and non-Cape Town high schools between 2001 and 2008 (shown in the second panel of figure 4). Hence, the pools of potential dormitory and non-dormitory students do not have different time trends. This helps to address any concern that students make different decisions about whether to attend the University of Cape Town due to the change in the dormitory assignment policy. However, the set of students who qualify for university admission is an imperfect proxy for the set of potential students at this university. Many students whose high school graduation test scores qualify them for admission to a university may not qualify for admission to this relatively selective university.

Third, the results are not driven by two approximately simultaneous policy changes at the university. The university charged a flat tuition fee up to 2005 and per-credit fees from 2006. This may have changed the number of courses for which students registered. However, the credit-weighted number of courses remained constant for dormitory and non-dormitory students, with a difference-in-differences estimate of 0.013, less than 0.4% of the mean (table 7 column 7). The university also closed one dormitory in 2006 and opened a new dormitory in 2007, as well as reserving one cheaper dormitory for low-income students under both policies. The estimated treatment effect is robust to excluding all three dormitories (table 7 column 8).

# **8.3 Limitations of GPA as an Outcome Measure**

I explore four ways in which the grading system might pose a problem for validity or interpretation of the results: curving, ceiling effects, course choices, and course exclusions. First, instructors may use “curves” that keep features of the grade distribution constant through time within each course. Under this hypothesis, the effects of tracking may be negative effects on dormitory students relative to non-dormitory students, rather than negative effects on absolute performance. This would not invalidate the main result but would certainly 31
Figure 4: Long-term Trends in Student Academic Performance <!-- Start of picture text --> 0.4<br>0.3<br>0.2<br>GPA for students from non-<br>Cape Town high schools<br>0.1<br>0<br>2001 2002 2003 2004 2005 2006 2007 2008<br>Linear prediction<br>-0.1 using 2001-2005 data<br>-0.2<br>-0.3<br>0.3<br>High schools in Cape Town<br>0.25<br>0.2<br>0.15<br>High schools not in Cape Town<br>0.1<br>0.05<br>0<br>2001 2002 2003 2004 2005 2006 2007 2008<br>University GPA<br>Rate of qualification for university admission<br><!-- End of picture text --> _Notes:_ The first panel shows mean GPA for first year university students from high schools outside Cape Town. The time series covers the tracking period (2001-2005) and the random assignment period (2006-2008). Mean GPA for students from Cape Town high schools is, by construction, zero in each year. Data for 2003 is missing and replaced by a linear imputation. The dotted lines show a 95% confidence interval constructed from 1000 replications of a percentile bootstrap stratifying by assignment policy and dormitory status. The bootstrap resamples dormitory-year clusters for 2004-2008, the only years in which dormitory assignments are observed. The second panel shows the proportion of grade 12 students whose score on the high school graduation examination qualified them for admission to university. The mean qualification rate for high schools in Cape Town is 0.138 in the tracking period (2001 - 2005) and 0.133 in the random assignment period (2007 - 2008). The mean qualification rate for high schools outside Cape Town is 0.250 in the tracking period (2001 - 2005) and 0.245 in the random assignment period (2007 - 2008). The second difference is 0.001 (bootstrap standard error 0.009) or, after weighting by the number of grade 12 students enrolled in each school, 0.007 (standard error 0.009).

32
change its interpretation. This is a concern for most test score measures but I argue that it is less pressing in this context. Instructors at this university are not encouraged to use grading curves and many examinations are subject to external moderation intended to maintain an approximately time-consistent standard. I observe several patterns in the data that are not consistent with curving. Mean grades in the three largest introductory courses at the university (microeconomics, management, information systems) show year-on-year changes within an assignment policy period of up to 6 points (on a 0 to 100 scale, approximately 1/3 of a standard deviation). Similarly, the 75<sup>th</sup> and 25<sup>th</sup> percentiles of the grades within these large first-year courses show year-on-year changes of up to 8 and 7 points respectively. This demonstrates that grades are not strictly curved in at least some large courses. I also examine the treatment effect of tracking on grades in the introductory accounting course, which builds toward an external qualifying examination administered by South Africa’s Independent Regulatory Board for Auditors. This external assessment for accounting students, although it is only administered only after they graduate, reduces the scope for internal assessment to change through time. Tracking reduces mean grades in the introductory accounting course by 0.11 standard deviations (cluster bootstrap standard error 0.12, sample size 2107 students). This provides some reassurance that tracking reduces the academic competence of low-scoring students.

Second, tracking may have no effect on high-scoring students if they already obtain near the maximum GPA and are constrained by ceiling effects. I cannot rule out this concern completely but I argue that it is unlikely to be central. The nominal grade ceiling of 100 does not bind for any student: the highest grade observed in the dataset is 97/100 and the 99<sup>th</sup> percentile is 84/100. Some courses may impose ceilings below the maximum grade, which will not be visible in my data. However, the course convenors for Introductory Microeconomics, the largest first-year course at the university, confirmed that they used no such ceilings. The treatment effect of tracking on grades in this course is 0.13 standard deviations (cluster bootstrap standard error 0.06), so the average effect across all courses is at least similar to the average effect in a course without grade ceilings.

Third, dormitory students may take different classes, with different grading standards, in the tracking and random assignment periods. There are some changes in the type of courses 33
students take: dormitory students take slightly fewer commerce and science classes in the tracking than random assignment period, relative to non-dormitory students. However, the effect of tracking is consistently negative within each type of class. The treatment effects for each faculty/school/college range between -0.23 for engineering and -0.04 for medicine. The average treatment effect with faculty fixed effects is -0.17 with standard error 0.04 (table 7, column 9). I conclude that the main results are not driven by time-varying course-taking behavior.

Fourth, the university employs an unusual two-stage grading system which does explain part of the treatment effect of tracking. Students are graded on final exams, class tests, homework assignments, essays, and class participation and attendance, with the relative weights varying across classes. Students whose weighted scores before the exam are below a course-specific threshold are excluded from the course and do not write the final exam. These students receive a grade of zero in the main data, on a 0-100 scale. I also estimate the treatment effect of tracking on the credit-weighted percentage of courses from which students are excluded and on GPA calculated using only non-excluded courses (table 7, columns 10 and 11). Tracking substantially increases the exclusion rate from 3.7 to 6.4% and reduces GPA in non-excluded courses by 0.08 standard deviations, though the latter effect is imprecisely estimated. I cannot calculate the hypothetical effect of tracking if all students were permitted to write exams but these results show that tracking reduces grades at both the intensive and extensive margins. This finding is consistent with the negative effect of tracking being concentrated on low-scoring students, who are most at risk of course exclusion. The importance of course exclusions also suggests that peer effects operate from early in the semester, rather than being concentrated during final exams.

# **8.4 Other Channels Linking Dormitory Assignment to GPA**

I ascribe the effect of tracking on dormitory students’ GPAs to changes in the distribution of peer groups. However, some other feature of the dormitories or assignment policy may account for this difference. Dormitories differ in some of their time-invariant characteristics such as proximity to the main university campus and within-dormitory study space. The negative treatment effect of tracking is robust to dormitory fixed effects, which account for 34
any relationship between dormitory features and GPA that is common across all types of students. Dormitory fixed effects do not account for potential interactions between student and dormitory characteristics. In particular, tracking would have a negative effect on lowscoring students’ GPAs even without peer effects if there is a negative interaction effect between high school graduation test scores and the characteristics of low-track dormitories. I test this hypothesis by estimating equation 2 with an interaction between _HSid_ and the rank of dormitory _d_ during the tracking period. The interaction term has a small and insignificant coefficient: 0.003, cluster bootstrap standard error 0.006. Hence, low-scoring students do not have systematically lower GPAs when randomly assigned to previously low-track dormitories. This result is robust to replacing the continuous rank measure with an indicator for belowmedian-rank dormitories. I conclude that the results are not explained by time-invariant dormitory characteristics.

This does not rule out the possibility of time-varying effects of dormitory characteristics or of effects of time-varying characteristics. I conducted informal interviews with staff in the university’s Office of Student Housing and Residence Life to explore this possibility. There were no substantial changes to dormitories’ physical facilities but there was some routine staff turnover, which I do not observe in my data. It is also possible that assignment to a lowtrack dormitory may directly harm low-scoring students through stereotype threat. Their dormitory assignment might continuously remind them of their low high school graduation test score and undermine their confidence or motivation (Steele and Aronson, 1995). I cannot directly test this explanation and so cannot rule it out. However, the consistent results from the cross-policy and cross-dormitory analyses suggest that peer effects explain the bulk of the observed treatment effect of tracking, Wei (2009) also notes that evidence of stereotype threat outside laboratory conditions is rare.

# **9 Conclusion**

This paper describes the effect of tracked relative to random dormitory assignment on student GPAs at the University of Cape Town in South Africa. I show that tracking lowered mean GPA and increased GPA inequality. This result occurs because living with high-scoring peers 35
has a larger positive effect on low-scoring students’ GPAs than on high-scoring students’ GPAs. These peer effects arise largely through interaction with own-race peers and the relevant form of interaction does not appear to be direct academic collaboration. I present an extensive set of robustness checks supporting a causal interpretation for these results.

My findings show that different peer group assignment policies can have substantial effects on students’ academic outcomes. Academic tracking into residential groups, and perhaps other noninstructional groups, may generate a substantially worse distribution of academic performance than random assignment. However, my results do not permit a comprehensive evaluation of the relative merits of the two policies. Tracking clearly harms low-scoring students but some (imprecise) results suggest a positive effect on high-scoring students. Changing the assignment policy may thus entail a transfer from one group of students to another and, as academic outputs are not directly tradeable, Pareto-ranking the two policies may not be possible. Non-measured student outcomes may also be affected by different group assignment policies. For example, high-scoring students’ GPAs may be unaffected by tracking because the rise in their peers’ academic proficiency induces them to substitute time away from studying toward leisure. In future work I plan to study the long-term effects of tracking on graduation rates, time-to-degree, and labor market outcomes. This will permit a more comprehensive evaluation of the two group assignment policies. One simple revealed preference measure of student welfare under the two policies is the proportion of dormitory students who stay in their dormitory for a second year. Tracking reduces this rate for students with above- and below-median high school test scores by 0.4 percentage points and 6.7 percentage points respectively (cluster bootstrap standard errors 3.5 and 3.8 respectively). Low-scoring dormitory students may thus be aware of the negative effect of tracking and respond by leaving the dormitory system early.

Despite these provisos, my findings shed light on the importance of peer group assignment policies. I provide what appears to be the first cleanly identified evidence on the effects of noninstructional tracking. This complements the small literature that cleanly identifies the effect of instructional tracking. For example, Duflo, Dupas, and Kremer (2011) suggest that a positive total effect of instructional tracking may combine a negative peer effect of tracking on low-scoring students with a positive effect due to changes in instructor behavior. My findings 36
suggest that policymakers can change the distribution of students’ academic performance by rearranging the groups in which these students interact without changing the marginal distribution of inputs into the education production function. This is attractive in any setting but particularly in resource-constrained developing countries. While the external validity of any result is always questionable, my findings may be particularly relevant to universities serving a diverse student body that includes both high performing and academically underprepared students. This is particularly relevant to selective universities with active affirmative action programs (Bertrand, Hanna, and Mullainathan, 2010).

The examination of peer effects under random assignment also points to fruitful avenues for future research. As in Carrell, Sacerdote, and West (2013), peer effects estimated under random assignment do not robustly predict the effects of a new assignment policy and residential peer effects appear to be mediated by students’ patterns of interaction. This highlights the risk of relying on reduced form estimates that do not capture the behavioral content of peer effects. Combining peer effects estimated under different group assignment policies with detailed data on social interactions and explicit models of network formation may provide additional insights.

# **References**

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# **A Reweighted Nonlinear Difference-in-Differences Model**

Athey and Imbens (2006) establish a model for recovering quantile treatment on the treated effects in a difference-in-differences setting. This provides substantially more information than the standard linear difference-in-differences model, which recovers only the average treatment effect on the treated. However, the model requires stronger identifying assumptions.

The original model is identified under five assumptions. Define _T_ as an indicator variable equal to one in the tracking period and zero in the random assignment period and _D_ as an indicator variable equal to one for dormitory students and zero for non-dormitory students. The assumptions are:

- _A1_ GPA in the absence of tracking is generated by the unknown production function _GPA_ = _h_ ( _U, T_ ), where _U_ is an unobserved scalar random variable. GPA does not depend directly on _D_ .

- _A2_ The production function _h_ ( _u, t_ ) is strictly increasing in _u_ for _t ∈{_ 0 _,_ 1 _}_ .

- _A3_ The distribution of _U_ is constant through time for each group, in this case dormitory and non-dormitory students: _U ⊥ T |D_ .

- _A4_ The support of dormitory students’ GPA is contained in that of non-dormitory students’ GPA: _supp_ ( _GPA|D_ = 1) _⊆ supp_ ( _GPA|D_ = 0).<sup>39</sup>

- _A5_ The distribution of GPA is strictly continuous.<sup>40</sup>

These assumptions are sufficient to identify the counterfactual distribution of tracked dormitory students’ GPAs in the absence of tracking, _FGPA_<sup>_CF_</sup> _|D_ =1 _,T_ =1<sup>(</sup><sup>_·_) =</sup><sup>_FGPA_10 �</sup> _FGPA_<sup>_−_100 (</sup><sup>_FGPA_01 (</sup><sup>_·_))</sup> �. These are the outcomes that tracked students would have obtained if they had been randomly assigned. The _q_<sup>_th_</sup> quantile treatment effect of tracking on the treated students is defined as the horizontal difference between the observed and counterfactual distributions at quantile _q_ : _FGPA_<sup>_−_1</sup> _|D_ =1 _,T_ =1<sup>(</sup><sup>_q_)</sup><sup>_−F_</sup> _GPA_<sup>_CF,−_</sup> _|D_<sup>1</sup> =1 _,T_ =1<sup>(</sup><sup>_q_).</sup>

> 39This assumption is testable and holds in my data.

> 40This assumption is testable and holds approximately in my data. There are 5505 unique GPA values for 14668 observations. No value accounts for more than 0.3% of the observations.

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These identifying assumptions may hold conditional on some covariate vector _X_ but not unconditionally. In my application, some of the demographic characteristics show time trends (table 1). If these characteristics are subsumed in _U_ and in turn influence GPA, then the stationarity assumption _A3_ will fail. The assumption may, however, hold after conditioning on _X_ .

Athey and Imbens discuss two ways to include observed covariates in the model. First, a fully nonparametric method that applies the model separately to each value of the covariates. This is feasible only if the dimension of _X_ is low. Second, a parametric method that applies the model to the residuals from a regression of GPA on _X_ . This is valid only under the strong assumption that the observed covariates _X_ and unobserved scalar _U_ are independent (conditional on _D_ ) and additively separable in the GPA production function. Substantively, the additively separable model is misspecified if the treatment effect of tracking at any quantile varies with _X_ . For example, different treatment effects on students with high and low high school graduation test scores would violate this restriction.

I instead use a reweighting scheme that avoids the assumption of additive separability and may be more robust to specification errors. Specifically, I define the reweighted counterfactual distribution at each value _g_ as where _FGPAdω_ 0<sup>(</sup><sup>_·_)isthedistributionfunctionof</sup><sup>_GPA × Pr_(</sup><sup>_T_= 1</sup><sup>_|D_=</sup><sup>_d, X_)</sup><sup>_/Pr_(</sup><sup>_T_= 0</sup><sup>_|D_=</sup> _d, X_ ). Intuitively, this scheme assigns high weight to students in the random assignment period whose observed characteristics are similar to those in the tracking period.<sup>41</sup> This is a straightforward adaptation of the reweighting techniques used in wage decompositions and program evaluation (DiNardo, Fortin, and Lemiuex, 1996; Hirano, Imbens, and Ridder, 2003). The counterfactual distribution is identified under conditional analogues of assumptions _A_ 1 _−_

> 41 I could instead use _FGP A_<sup>_RW,CF_11(</sup><sup>_g_)=</sup><sup>_FGP A_10</sup> _ω_ � _FGP A_<sup>_−_100</sup> _ω_ � _FGP A_ 01 _ω_<sup>(</sup><sup>_g_)</sup> �<sup>�</sup> as the counterfactual distribution, with weights _Pr_ ( _T_ = 1 _, D_ = 1 _|X_ ) _/Pr_ ( _T_ = _t, D_ = _d|X_ ) for ( _d, t_ ) _∈{_ 0 _,_ 1 _}_<sup>2</sup> . This reweights all four groups of students to have the same distribution of observed characteristics. Balancing the distributions may increase the plausibility of the assumption that dormitory and non-dormitory students share the same production function _h_ ( _x, u, t_ ). Results from this model are similar, but with larger negative effects in the left tail.

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_A_ 5.<sup>42</sup> Hence, the _q_<sup>_th_</sup> quantile treatment effect on the tracked students is I do not formally establish conditions for consistent estimation. Firpo (2007) recommends a series logit model for the propensity score _Pr_ ( _T_ = 1 _|D_ = _d, X_ ) with the polynomial order chosen using cross-validation. I report results with a quadratic function; the treatment effects are similar with linear, cubic, and quartic specifications. I implement the estimator in four steps:

1. For _D ∈{_ 0 _,_ 1 _}_ , I regress _T_ on student gender, language, nationality, race, a quadratic in high school graduation test scores and all pairwise interactions. I construct the predicted probability _Pr_<sup>ˆ</sup> ( _T_ = 1 _|D, X_ ).

2. I evaluate equation 5 at each half-percentile of the GPA distribution (i.e. quantiles 0.5 to 99.5). I plot this counterfactual GPA distribution for tracked students in the first panel of figure 3, along with the observed GPA distribution.

3. I plot the difference between observed and counterfactual distributions at each halfpercentile in the second panel of figure 3.

4. I construct a 95% bootstrap confidence interval at each half-percentile, clustering at the dormitory-year level and stratifying by ( _D, T_ ).

The Stata code for implementing this estimator is available on my website.

> 42Note that the conditional analogues of assumptions _A_ 4 and _A_ 5 are more restrictive. For example, the common support assumption _A_ 4 may hold for the marginal distribution _FGP A_ ( _·_ ) but not for the conditional distribution _FGP A|X_ ( _·|x_ ) for some value of _x_ .

43