Classroom Peer Effects and Student Achievement

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Classroom Peer Effects and Student AchievementAuthor(s): Mary A. Burke and Tim R. SassSource: Journal of Labor Economics, Vol. 31, No. 1 (January 2013), pp. 51-82Published by: The University of Chicago Press on behalf of the Society of Labor Economists and theNORC at the University of ChicagoStable URL: http://www.jstor.org/stable/10.1086/666653 .

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Classroom Peer Effects andStudent Achievement

Mary A. Burke, Federal Reserve Bank of Boston

Tim R. Sass, Georgia State University

Weanalyze the impact of classroompeers’ ability (measured by theirindividual fixed effects) on student achievement for all Florida pub-lic school students in grades 3–10 over a 6-year period. We controlfor both student and teacher fixed effects, thereby alleviating biasesdue to endogenous assignment of both peers and teachers. Underlinear-in-means specifications, estimated peer effects are small to non-existent, but we find some sizable and significant peer effects withinnonlinear models. We also find that classroom peers, as comparedwith the broader group of grade-level peers at the same school, exerta greater influence on individual achievement gains.

I. Introduction

The potential for peers to affect individual achievement is central to manyimportant policy issues in elementary and secondary education, including theimpacts of school choice programs, ability tracking within schools, “main-streaming” of special education students, and racial and economic desegre-gation. Vouchers, charter schools, and other school-choice programs maybenefit students who stay in traditional public schools by engendering com-

We wish to thank the staff of the Florida Department of Education’s K-20 Ed-ucation Data Warehouse for their assistance in obtaining and interpreting the dataused in this study. We are grateful to John Gibson and Kevin Todd for excellentresearch assistance. The views expressed in this article are solely our own and donot necessarily reflect the opinions of the Florida Department of Education. Con-tact the corresponding author, Tim R. Sass, at [email protected].

[ Journal of Labor Economics, 2013, vol. 31, no. 1]© 2013 by The University of Chicago. All rights reserved.0734-306X/2013/3101-0001$10.00

51



petition that leads to improvements in school quality, but such programsmay also harm those same students if they diminish the quality of the stu-dents’ classmates (Epple and Romano 1998; Caucutt 2002). Grouping stu-dents in classrooms by ability might likewise have significant impacts onstudent achievement, depending on the magnitude and shape of peer influ-ences (Epple, Newlon, and Romano 2002). The effect of desegregation pol-icies on achievement will depend not just on the average spillovers from peerability but also on whether students of different backgrounds and abilitylevels experience peer effects of different magnitudes and/or exert differentinfluences on their peers.1

Despite the by now extensive list of papers that estimate peer effects ofvarious stripes in academic settings, findings varywidely across studies, andconsistent policy implications are hard to extract.2 As is well known, iden-tification of peer effects faces steep challenges due to issues such as endog-enous peer selection, simultaneity of outcomes, and the presence of corre-lated inputs within peer groups. Significant progress has been made inrecent years as researchers have made clever use of available data. In partic-ular, a handful of recent papers appear to show broad agreement that dis-ruptive peer behavior has negative effects on individual achievement (Figlio2007; Aizer 2008; Carrell and Hoekstra 2010; and Neidell and Waldfogel2010). Consensus is still lacking, however, on achievement spillovers frompeer ability. Because many recurrent policy issues (charter schools, eco-nomic and racial desegregation, tracking/detracking) entail redistributionof students on the basis of ability measures or characteristics that correlatewith ability, the value of reliablemeasures of ability spillovers remains high.Given a unique panel data set encompassing all public school students in

grades 3–10 in the state of Florida over the period 1999–2000 to 2004–5, wehave unprecedented resources with which to test for peer effects in the ed-ucational context. Unlike any previous study, we simultaneously controlfor the fixed inputs of students, teachers, and schools in measuring peereffects on academic achievement at the classroom level.3 These controlssharply limit the scope for biases from endogenous selection of peers andteachers and permit a sharper estimate of the influence of classroom peer

1 Hoxby andWeingarth (2006), Lavy, Paserman, and Schlosser (2008), andCooley(2010) all find that peer effects may differ across students depending on their abilitylevels;Hoxby (2000), Angrist andLang (2004), Betts andZau (2004),Hanushek,Kain,andRivkin (2009),Hanushek andRivkin (2009), andFryer andTorelli (2010) find thatpeer effects may differ by race, ethnicity, and/or gender.

2 See Vigdor and Nechyba (2007), Aizer (2008), and Epple and Romano (2011)for more extensive discussions of the related literature.

3 Other papers that adopt a fixed effects strategy include Betts and Zau (2004),Kramarz, Machin, and Ouazad (2007), Carrell and Hoekstra (2010), and Neidelland Waldfogel (2010), among others. Papers that use fixed effects in conjunctionwith other strategies include Vigdor and Nechyba (2007) and Cooley (2010).

52 Burke/Sass



ability (as opposed to grade-level-at-school peer ability) than has been pos-sible in previous research.4While fixed effects cannot control for classroomassignment policies that depend on unobserved, time-varying factors—Rothstein’s (2010) “dynamic tracking” problem—we employ sample re-strictions that limit the risks posed by such policies and find our results tobe robust to such restrictions.Ours is the first study using US data to compare peer effects across three

levels of schooling—elementary school, middle school, and high school—for both mathematics achievement and reading achievement.5 In addition,the data enable us to estimate models involving nonlinear, heterogeneouspeer effects that depend on both individual ability and peer ability, in keep-ing with recent evidence that simpler specifications (such as the standard“linear-in-means” model) fail to capture important dimensions of peer ef-fects.6

In addition to exploiting a rich data set,we employ a newestimation tech-nique, adapted fromArcidiacono et al. (2010), in which peer effects operatethrough a measure of peer ability that captures observed as well as unob-served components. Thismethodmitigates the potentialmeasurement errorassociated with standard ability measures such as lagged test scores and de-mographic characteristics, and it greatly facilitates the estimation of modelsinvolving multiple levels of fixed effects.Wefind that peer effects are small, but statistically significant, in the linear-

in-means models, although these effects obscure more complex interactions.In the nonlinear models, peer effects are larger on average than in the linearmodels, and the effects are both statistically and economically significant.Wefind that the impact of peer ability depends on the student’s own ability andon the relationship between own ability and peer ability—for example, forlow-achieving students, having very-high-aptitude peers appears worse thanhaving peers of average ability. Such nonlinearities imply that there are op-portunities for redistribution of students across classrooms and/or schoolsthat may result in aggregate achievement gains.

4 Studies that estimate classroom-level peer effects in elementary school and/ormiddle school in the United States include Betts and Zau (2004), Lefgren (2004),Hoxby and Weingarth (2006), Vigdor and Nechyba (2007), Zabel (2008), Cooley(2010), and Neidell and Waldfogel (2010).

5 Vigdor and Nechyba (2007) study effects of fifth-grade peers and examine thepersistence of these effects through the eighth grade. Hoxby andWeingarth (2006)estimate effects on outcomes for fifth grade through eighth grade. Unlike the latterpaper, we allow coefficients to differ across schooling levels.

6 Hoxby and Weingarth (2006) find that models involving homogeneous treat-ment effects are dominated by models involving heterogeneous treatment effects.Lavy et al. (2008), Imberman, Kugler, and Sacerdote (2009), Cooley (2010), andCarrell, Sacerdote, andWest (2011) also find that peer effects depart from the simplelinear-in-means model, although the specifications differ across this set of papers.

Classroom Peer Effects and Student Achievement 53



We also find that peer effects tend to be stronger at the classroom levelthan the grade level—in most cases we find no significant peer effects at thegrade-within-school level. This agrees with recent findings by Carrell, Ful-lerton, andWest (2009) that peer effects estimates can differ greatly depend-ing on the accuracy with which the econometrician identifies the set of rel-evant peers. In most specifications, estimated peer effects are smaller whenteacher fixed effects are included in the model than when they are omitted,reinforcing the importance of controlling for unobserved teacher inputswhen estimating classroom peer effects.While estimating models with multiple levels of fixed effects is both data

intensive and computationally demanding, our data resources and choice ofmethods greatly facilitate the estimation of such models. The ability toidentify peer effects using nonexperimental data represents an importantcontribution because truly random assignment to classrooms is quite rarein practice, especially in the United States.7 Further, the nature of peer in-fluences may differ depending on whether peers are chosen deliberately orat random (Foster 2006; Weinberg 2007; Duflo, Dupas, and Kremer 2011).In addition, Arcidiacono et al. (2010) show that a moderate degree of sort-ing on student ability enables more accurate estimates of peer effects thanobtain under purely random assignment because sorting generates greatervariation in peer group ability within students.The remainder of this article is organized as follows. Section II presents

the empirical model and identification and discusses the method of mea-suring peer ability through fixed effects. Section III discusses the data andthe computational methods. Section IV describes the study’s results, andSection V concludes.

II. Empirical Model and Identification Method

A. A Cumulative Model of Student Achievement

We begin by specifying the cumulative cognitive achievement produc-tion function developed by Boardman and Murnane (1979) and Todd andWolpin (2003):

7 Boozer and Cacciola (2001) and Graham (2008) exploit random assignment inthe Tennessee STAR experiment. Numerous studies, including Sacerdote (2001)and Zimmerman (2003), exploit random assignment of college roommates. Lyle(2007), Carrell, Fullerton, andWest (2009), and Carrell et al. (2011) exploit randomgroup assignment in military academies. Ding and Lehrer (2007), Carman andZhang (2008), Lai (2008), Jackson (2009), andDuflo et al. (2011), among others, ex-ploit random assignment policies among primary and/or secondary schools outsidethe United States.

54 Burke/Sass



Aiamt 5oa

h50

hXi;a2ha1h 1 a2hui 1 bhu∼ ikða2hÞ

1 Tjða2hÞ; t2hhh 1 dh; jða2hÞ 1 fhCkða2hÞ

i1 qm 1 vt 1 εia:

ð1Þ

Equation (1) relates the current achievement level, Aiamt, for individual i atage a in gradem in calendar year t to the entire history of educational inputs,applied at each age, from the current age, a, back to age 0. (The index h indi-cates years elapsed since the inputwas applied.) Inputs include a vector,Xi,a-h,of observed, age-varying characteristics of individual i; a composite of fixed(observed and unobserved) individual characteristics; ui (including the stu-dent’s ability endowment and the fixed portion of the flow of parental in-puts);8 the average, u ∼ ikða2hÞ, of the fixed (composite) characteristics of indi-vidual i’s peers (not including herself) in classroom k(a-h) at age a-h;9 avector of observed (time-varying) characteristics, Tj(a-h),t-h, such as years ofexperience, of teacher j(a-h)—the teacher assigned to the student at agea-h—as of time t-h; the combined impact of the fixed (observed and unob-served) characteristics of the age a-h classroom teacher, denoted dh;jða2hÞ, aneffect which depends on the teacher’s identity and on the time elapsed (h)since she taught the student; and the class size experienced by the student atage a-h, denoted Ck(a-h). Achievement also depends on the student’s gradelevel, m, which contributes the fixed effect qm, and on the calendar year t,which contributes the fixed effect vt. Finally, there is an age-a random dis-turbance, εia.10 The model assumes that the achievement function is linear,with separable inputs. The effects of inputs do not vary with the student’sage, but they may depend on the amount of time that has elapsed since theinputs were applied.11 We relax the age-independence assumption some-

8 We bundle observed and unobserved characteristics into a single term becausethe fixed effects estimation technique does not allow us to recover the effects of ob-served fixed characteristics, such as race and gender, separately. The same bundlingapplies to peers’ fixed characteristics.

9 The specification allows a student’s own time-varying and fixed characteristicsto influence her achievement level, but it assumes that only the fixed characteristicsof peers enter the equation. This is fairly standard in the empirical literature, asmostspecificationsmeasure peer attributes with fixed or quasi-fixed observable character-istics, such as lagged test scores, race, gender, disability status, and socioeconomicstatus.

10 Effectively, the model assumes that prior random disturbance terms, as well asprior grade-level and calendar-year effects, have zero persistence.

11 The notation of subscripts guarantees that effects of inputs depend only on thetime elapsed since they were applied and not on the student’s current age. For ex-ample, coefficients subscripted by h5 0 refer to marginal effects on current (age a)achievement of inputs applied at age a, those subscripted by h51 refer to effects oncurrent achievement of inputs applied at age a-1, etc.




what by estimating separate models for elementary school, middle school,and high school observations.12

To facilitate estimation of the model, additional assumptions are neces-sary. First, we assume that the impact of the fixed individual characteristicsis age-invariant—that is, a2h 5 a2. This implies that the net impact on theachievement level of the fixed idiosyncratic inputs is a constant or fixed ef-fect, which we denote as gi ; a2ui. In addition, we assume that the mar-ginal effect, bh, of the average of the fixed characteristics of the peer groupðu ∼ ikða2hÞÞ is some fraction, lh (where 0 < lh < 1), of the marginal effect of astudent’s own (fixed) characteristics on her achievement.13 That is, bh 5lha2, so we can express the total effect of peers (encountered at age a-h) aslhg ∼ ikða2hÞ.14 By bundling all mean peer characteristics into a single “meanpeer fixed-effect” regressor, we can estimate the impact on individualachievement of aspects of peer ability that are not captured by noisy abilitymeasures, such as a test score measured at a point in time. For computa-tional tractability, we assume that the impact on current achievement of in-puts applied at least two periods ago (i.e., twice-lagged, third-lagged, etc.)is negligible.15 As such, we estimate the impact of the current and once-lagged values of the inputs listed above.16 Incorporating these assumptions,the linear-in-means estimation model becomes:

12 A detailed discussion of the derivation of the achievement model is containedin Todd and Wolpin (2003) and Harris, Sass, and Semykina (2010).

13 These assumptions are simplified by the fact that we are bundling all fixed indi-vidual characteristics, whether observed or unobserved, into the term ui. The modelgeneralizes readily to the case in which the components of ui are unbundled, on theassumption that the marginal effect of any given peer characteristic equals lh timesthemarginal effect of the own characteristic. See Arcidiacono et al. (2010) for details.

14 The first assumption in this paragraph (regarding individual fixed effects) holdsfor all models we estimate. A version of the second assumption (concerning the im-pact of peers) applies to all models, with the exception of the “two-way interac-tions” model described below. In models with both current and lagged peer effects,the fraction lh varies with the time lag, h. In the “one-way interactions” model de-scribed below, this fraction varies further with an observable (fixed) characteristicof the individual. While the second assumption does not hold for the two-way in-teractions model, we show in app. B, available in the online version of this article,that our solution method still yields unbiased peer effects estimates provided cer-tain data conditions are met.

15 In a recent paper, Jacob, Lefgren, and Sims (2010) find that the impact of edu-cational inputs, particularly teacher quality, erodes quickly. The estimated 1-yearpersistence rate is in the range of one-fifth to one-third, suggesting that twice andgreater lagged inputs would have an impact of at most 0.11 times the impact of con-temporaneous inputs.

16 We estimate two (independent) fixed effects per teacher: one to capture thecontemporaneous effect of the given teacher on age-a achievement and another tocapture the once-lagged effect of the teacher on age-a achievement (e.g., when she isthe age a-1 teacher). The estimation method places no restrictions on the relation-ship between a teacher’s lagged effect and her contemporaneous effect.

56 Burke/Sass



Aia 5o1

h50

�gi 1 lhg ∼ ikða2hÞ 1Xi;a2ha1h

1 Tjða2hÞ;t2hhh 1 dh;jða2hÞ 1 fhCkða2hÞ

�

1 qm 1 vt 1 εia:

ð2Þ

As described above, the individual fixed effect, gi, represents the student’sfixed achievement differential, reflecting innate intellectual ability and anyfixed contribution to achievement of family inputs such as monitoring andsupport. For shorthand, we will refer to this effect as “ability, “quality,” or“aptitude.” To the extent that student and family inputs—and their impacton cumulative achievement—vary over time, the deviations are embedded inεia and assumed to be random—specifically,mean zero and independent andidentically distributed (i.i.d.)—conditional on the vector of regressors, inaddition to being serially uncorrelated.17 However, because we estimateseparate models for each of elementary school, middle school, and high-school outcomes,we effectively allow for systematic variation in the contri-butions of unobserved student-level inputs across schooling levels, as wellas variation in the strength of peer effects.While we assume that student-level inputs contribute a fixed effect to the

achievement level, Todd andWolpin (2007) find evidence that family inputscontribute a constant gain effect on achievement. If there were indeed indi-vidual heterogeneity in achievement gains, then the divergence betweenhigh-achieving and low-achieving students should increase with age. How-ever, in an analysis of the Florida data (results available in app. A, availablein the online version of this article), we observe little systematic variation ingains with the initial achievement level. In fact, we find evidence that stu-dents initially in the lower tail of the distribution exhibit above-averagesubsequent gains, while those in the upper tail exhibit below-average gains.Thus, at least inFlorida,measuring peer ability as a fixed contribution to stu-dent achievement gains seems inappropriate, and we adhere to a model withstudent fixed effects in the achievement level in our analysis.For illustrative purposes, we have described a model in which peer ef-

fects operate linearly through average peer ability. It seems reasonable to

17 Evidence of systematic responses in parental inputs to changes in schooling in-puts reveals mixed results. See, e.g., Bonesrønning (2004) andHoutenville andCon-way (2008). If parents increase their nonschool inputs (e.g., spending more timehelping with homework or hiring a tutor) in response to a poor classroom peergroup, our peer effect estimates would be biased downward.




expect that students might benefit more from high-aptitude peers thanlow-aptitude peers (i.e., effects are monotonic in peer ability), for example,if high-aptitude peers ask penetrating questions and provide key insightsduring classroom discussions more frequently than do lower-aptitude stu-dents. However, it is not obvious that such benefits would be linear in peerability, nor that such benefits would accrue uniformly to all types of stu-dents. Even monotonicity is an empirical question. Indeed, a growing listof papers finds evidence of nonlinearities in peer effects (see notes 1 and 6for examples of such papers). Such findings constitute an important devel-opment because policy can hope to generate aggregate achievement gainsonly if peer effects are nonlinear and therefore non-zero-sum in their im-pact on achievement.Accordingly, we estimate two nonlinear models of peer effects. In the

first, the influence of the mean peer fixed effect is allowed to depend on aquintile ranking of the student’s initial achievement level (based on an ini-tial test score) relative to the entire population of students in Florida.18 Inthe second, peer effects again depend on the student’s initial-test-scorerank, but themeasure of peer quality is no longer themean peer fixed effect.Instead, similar to themodel of Carrell et al. (2011), students are influencedby the respective shares of peers in the bottom quintile and top quintile ofthe global distribution of student fixed effects, and in turn these effects de-pend on the student’s initial test-score ranking. The share of peers in themiddle of the distribution is omitted due to collinearity.

B. Identification of Peer Effects

The identification of peer effects at the classroom level poses somedaunt-ing challenges. Manski (1993) first articulated the essential identificationproblems for peer effects estimation. These include the reflection problem(or simultaneity), inwhich spillover effects frompeers’ characteristics (suchas gender or scholastic aptitude) cannot be identified separately from spill-over effects of peers’ endogenous outcomes (such as test scores). The reflec-tion problem also hinders identification of the effects of own characteristicson outcomes. A related problem concerns correlated effects, or commonunobserved factors within a peer group (such as teacher quality) that mayproduce spurious correlations in peer outcomes. These identification issuesare pertinent regardless of whether peers are randomly assigned or not.However, nonrandom assignment adds considerably to the difficulty of

18 In the elementary school estimation, we use the first available test score, thethird-grade national percentile ranking. For middle school, we use the last elemen-tary school score (fifth grade), and for high school, we use the last middle schoolscore (eighth grade).

58 Burke/Sass



surmounting them and, as such, constitutes a central concern in the empir-ical literature (Epple and Romano 2011).

1. Nonrandom Assignment and Correlated Effects

The main identification challenge we face emanates from potential non-random assignment of students to schools, classrooms, and teachers on thebasis of unobserved factors. As explained by Moffitt (2001), nonrandomassignment produces correlated effects—in this case, common unobservedfactors influencing achievement within a peer group—whichmay bias peereffects estimation. Tomeet this challenge,we estimate amodel that controlsfor unobserved heterogeneity in achievement contributions at multiplelevels: the individual student, the teacher-school pair (and lagged teacher-school pair), the grade level, and the calendar year. The model controls fornumerous time-varying observed factors as well, such as the teacher’s yearsof experience, class size, and whether the student is repeating the givengrade. This method isolates quasi-experimental variation in the distribu-tion of peer group ability (summarized by the mean or possibly other mo-ments) within a student over time (within each schooling level) that is in-dependent of the various controls.The inclusion of controls for unobserved teacher inputs, while simulta-

neously controlling for student fixed effects, marks a significant methodo-logical contribution, as we know of no previous study of classroom peereffects that controls for both of these levels of effects in the same model.The added level of control is important in light of research showing thatteacher quality matters a great deal for student achievement and yet is notstrongly linked to observed teacher characteristics (see, e.g., Rockoff 2004;Rivkin et al. 2005; and Kane, Rockoff, and Staiger 2008). Furthermore,there is abundant evidence that teacher assignments are nonrandomwithinschools (Oakes et al. 1990; Argys, Rees, and Brewer 1996; Clotfelter, Ladd,and Vigdor 2006; Vigdor and Nechyba 2007; Feng 2009).While student fixed effects control for average teacher quality by student

(and average peer groupquality), teacher qualitymay covarywith peer abil-itywithin a student over time. Thiswill occur, for example, if higher-abilitystudents are matched with higher-quality teachers on average and yet thereis some randomness in teacher assignments. If so, mean peer ability will bepositively correlatedwith contemporaneous teacher quality, even after con-ditioning on individual ability, andmeasured peer effects will be biased up-ward when teacher quality is not accounted for. Negative matching be-tween teacher and student ability is also a possibility.Despite our extensive controls, we cannot control for all possible corre-

lated effects at the classroom level. Common physical inputs such as com-puters, desks, and lighting are not likely to vary significantly across class-rooms within schools, and thus our school fixed effects (embedded in the




teacher-school spell effects) should capture these factors. Localized shocksare also possible—such as a classroom-specific outbreak of influenza—butthese will lead to biased estimation only if they are correlated with the peervariables.The success of our fixed effects approach also depends on certain fea-

tures of the data. First, there must be sufficient within-student variation inpeer group composition in order to identify peer effects. Second, this var-iationmust not be collinear with thewithin-student variation in the qualityof the teacher-school pair. Identification would not obtain, for example, ifschools practiced strict classroom tracking and strict matching betweenteacher and student ability and if there were no mobility of students acrossschools. In such a case, students could have the same teacher and same peersthroughout all grades in a school, or at least experience no variation in eitherpeer group quality or teacher quality. We eliminate these concerns by lim-iting our sample to observations inwhich students and teacher-school pairsare connected in a single group. In such a connected group, at least somestudents are taught by multiple teacher/school combinations, all studentsever taught by teachers in the group are included, and all teacher/schoolsever encountered by the students are included. In other words, there is stu-dent mobility within the group but no mobility across groups.19 Further-more, analysis of selection into classrooms on the basis of peer ability andteacher ability, discussed below and in appendix A, online, indicates thatthere is sufficient variation within our data to identify peer effects.A second caveat is that fixed effects only alleviate bias associated with

sorting on time-invariant student and teacher characteristics (i.e., “static”tracking). As Rothstein (2010) argues, if students are assigned to teacherson the basis of prior, unobserved shocks to achievement (“dynamic” track-ing) and these shocks are serially correlated, then models with student andteacher fixed effects can yield biased estimates of teacher quality.20 For ex-ample, if studentswho have an unusually high test score in one year are sys-tematically assigned to high-quality teachers the following year and then inthat year fall back toward their typical achievement level (a case of meanreversion), estimates of the effect of the second-year teacher on studentachievement would likely be biased downward.

19 See Abowd, Creecy, and Kramarz (2002) for a detailed discussion of intercon-nected groups and the implications for identification of student and teacher/schooleffects. We determine interconnected groups by employing the Abowd-Creecy-Kramarz algorithm that is embedded in the Stata program felsdvreg.

20 Kane and Staiger (2008) compare estimated teacher effects from a variety ofachievement models with later experimental evidence on the effectiveness of thesame teachers. Models that control for prior educational inputs (via inclusion oflagged test scores) yielded unbiased estimates of student achievement under ran-dom assignment of students to teachers.

60 Burke/Sass



Using data from a cohort of students in North Carolina, Rothstein con-ducts falsification tests that support the existence of dynamic tracking. Heshows that future teachers have spurious effects on current achievementgains, even when controlling for student fixed effects. By an analogous ar-gument, estimates of peer effects may also be biased in the presence of dy-namic tracking—for example, if a good shock last period results in a partic-ularly strong peer group in the current period and the student’s achievementalso mean-reverts.The issue of bias associatedwith dynamic tracking is unlikely to be ama-

jor concern in our case for a number of reasons. First, Koedel and Betts(2011) show that if dynamic sorting is transitory, then associated bias willbe mitigated by observing teachers over multiple time periods and control-ling for student fixed effects. In keeping with these findings, we employstudent fixed effects and restrict our analysis to teachers who taught at leasttwo classes of students during the sample period. To provide additional in-surance against dynamic-tracking bias, following Harris and Sass (2011),we further limit our analysis sample to those districts in Florida in whicha Rothstein-style test fails to reject the null of strict exogeneity at a 95%confidence level.21

2. Simultaneity, or the Reflection Problem

Concerning the problem of simultaneity, we adopt a model of cognitiveachievement in which peers influence each other’s outcomes (standardizedtest score) only through their (fixed) ability or aptitude and not alsothrough their test scores or variable effort. If valid, this assumption side-steps the problem of separately identifying exogenous and endogenousspillovers.With very few exceptions (e.g., Kinsler 2009; Cooley 2010), pre-vious studies of peer effects in education have not attempted to separatethese types of effects, and in most cases it has been assumed that only ex-ogenous effects were at work.However, we cannot rule out the possibility of endogenous peer effects.

Cooley (2009), for example, finds evidence of effort spillovers among stu-dents, and, as mentioned above, there is considerable evidence that “badbehavior” among peers can have a negative impact on achievement. Ourestimates of peer effects should therefore be viewed as reduced-form coef-ficients that comprise both direct spillovers from peer ability and any spill-overs from consistent behavior patterns that are predicted by peer ability.

21 We implement the Rothstein test using the methodology of Koedel and Betts(2011). The test checks for significant effects of future teachers on current achieve-ment levels—a violation of the null hypothesis of no relationship—through eitherteachers’ observed characteristics or teacher fixed effects. This test should not besubject to the bias, identified by Kinsler (2011), that may arise under Rothstein’s(2010) own version of the test. In table A1 in app. A, online, we show that modelestimates are very similar between the restricted and unrestricted samples.




3. Measurement Error in Peer Ability

Most existing studies measure peer ability on the basis of lagged testscores or various instruments for (current or lagged) test scores or on thebasis of various observable, predetermined characteristics.22 Suchmeasuresmay capture true peer ability with considerable error, resulting in a down-ward bias on estimated peer effects. By contrast, we measure peer abilitybased on the peers’ fixed effects. This measure of peer ability captures thecontribution of both observed and unobserved factors to the student’sachievement level and as such is designed tomitigate themeasurement errorbias associated with measures based on observed factors only.This method holds the major computational advantage of facilitating es-

timation of multiple levels of fixed effects using a numerical algorithm thatapproximates nonlinear least-squares estimation, where the least-squaresestimators of the peer effects are consistent in principle. In addition, it mit-igates the risk of bias caused by regression to the mean, a bias that may af-fect peer effects estimates based on lagged peer test scores, as explained inBetts and Zau (2004).One potential disadvantage of themethod is that our results cannot tell us

whether specific peer characteristics (such as race and gender) matter, be-cause these are bundled into the peer fixed effects together with unobserv-able inputs.However, recent evidence (Hoxby andWeingarth 2006;Cooley2010) suggests that race and gender effects serve mainly as proxies for abil-ity, indicating that policy should focus on finding the optimal ability mixrather than the optimal racial mix.

III. Data, Sample Selection, and Computational Issues

A. Data

In the present study wemake use of a unique panel data set of school ad-ministrative records from Florida.23 The data cover 6 school years, 1999–2000 through 2004–5, and include all public school students in the state ofFlorida. Achievement test scores (administered in March) are available forboth mathematics and reading in each of grades 3–10 for each of two dif-ferent achievement tests. One of these tests is the “Sunshine State Stan-dards” Florida Comprehensive Achievement Test (FCAT-SSS), a criterion-based exam designed to test for the skills that students are expected to mas-ter at each grade level. The FCAT-SSS is a “high-stakes” test, which is usedfor school and student accountability. Student retention decisions, highschool graduation requirements, and school grades are all based on theFCAT-SSS. The other test is the FCAT Norm-Referenced Test (FCAT-

22 Lavy et al. (2008) use grade repetition as a proxy for ability, and Neidell andWaldfogel (2010) use attendance in preschool.

23 A more detailed description of the data is provided in Sass (2006).

62 Burke/Sass



NRT), a version of the Stanford-9 achievement test used throughout thecountry. TheFCAT-NRTdoes not enter into any accountabilitymetrics andis thus a “low-stakes” test. We use the FCAT-NRT scores because these areavailable for one additional year and since, coming from a low-stakes test,they are not subject to potential bias from “teaching to the test” (i.e., effortexpended by some teachers on test-taking strategies that may raise scores ona particular exam but that do not enhance actual student learning of the ma-terial). Although the FCAT-NRT scores are vertically scaled,meaning a one-point difference in the scaled score should represent an equivalent achieve-ment difference beginning from anywhere on the scale, we norm the scoresby grade and year (i.e., the scores are subtracted from the population meanat each grade/year combination and divided by the population standard de-viation for the relevant grade/year). This normalization reduces noise in theachievement caused by changes in the test instrument as well as any othergrade-specific shocks over time. The reduction in noise facilitates conver-gence of the estimation procedure, as is discussed further below.

B. Sample Selection

To permit a flexible education production function, we divide the sam-ple into three groups: (1) elementary school observations, used to estimatethe model for the fourth and fifth grades; (2) middle school data, used toestimate the model for the sixth, seventh, and eighth grades; and (3) highschool data, used to estimate the model for the ninth and tenth grades.24

The drawback of estimating separate models is that we limit the number ofobservations per student to two in the cases of elementary school and highschool and to three per student for middle school. In a small number ofcases, students are observed more than twice (or, for middle school, morethan three times) because they repeated a grade one ormore times.25Withineach level of schooling, we observe five cohorts, covering the 5 academicyears beginning with 2000–2001 and ending with 2004–5. Descriptive sta-tistics within each schooling-level sample are given in table 1.In the regression analysis, we omit students with only a single test score

observation for a given schooling level because peer effects are not identifiedfor these students. However, wemust also omit these “singletons” from thepeer groups of others because the fixed effects of singletons are also notidentified. If peer influence does not depend on singleton status, and if sin-gletons are broadly representative of the ability distribution, these biasesshould not be a source of concern. Appendix A, online, presents evidence

24 While third-grade test scores are available, they must be excluded from thenonlinear models, as explained below, and so are excluded from all models for dataconsistency.

25 Our estimation models include repeater-by-grade indicators to allow for dif-ferential achievement of students who repeat a grade.




on the observable characteristics of singletons that offers reassurance thatthe singleton exclusion is not likely to significantly alter our results.In addition to linking students and teachers to specific classrooms, our

data indicate the (average) proportion of time each student spends in eachclassroom. We restrict our analysis to students who receive instruction inthe relevant subject area (mathematics or reading/language arts) in just asingle classroom.This exclusion allows us to avoid the problemof determin-ing the propermathematics or reading peer group and the proper teacher. Toavoid atypical classroom settings and jointly taught classes, we consideronly courses with 10–50 students and with only one “primary instructor”of record. Finally, we eliminate charter schools from the analysis sincethey may have different curricular emphases and because student-peer andstudent-teacher interactions may differ in fundamental ways from thosein traditional public schools. Details on these sample restrictions and theireffects on the size of the estimation sample are discussed in appendix Aonline.Previous work has shown that student performance suffers in the first

year following a move to a new school (see, e.g., Bifulco and Ladd 2006;Sass 2006). In light of this evidence, we include three measures of studentmobility among the set of regressors: the number of schools attended in thecurrent year and indicators of “structural” and “nonstructural” moves bythe student. A structural move is defined as amove inwhich at least 30%ofa student’s cohort in the same grade at the initial school makes the samemove. This variable captures the effects of normal transitions from elemen-tary school tomiddle school and frommiddle school to high school, as wellas the impact of significant school rezonings. Correspondingly, a non-structural move is defined as any change in school attendance between the

Table 1Mean Values for Florida Public School Students, 1999–2000 to 2003–4

Mathematics Reading

ElementarySchool(Grades3–5)

MiddleSchool(Grades6–8)

HighSchool(Grades9–10)




Normed achievementlevel .1817 .0222 .5944 .1795 .4330 .5998

Standard deviation ofachievement level .9323 .8741 .9940 .9290 .8556 .8249

No. schools attended 1.0263 1.0276 1.0134 1.0265 1.0199 1.0111“Structural” mover .0087 .2299 .3101 .0082 .1976 .3703“Nonstructural”mover .0871 .1165 .1240 .0880 .1024 .1313

Class size 25.6410 28.0467 27.8566 25.7417 26.6857 28.0044Teacher experience 11.6039 9.3570 11.8577 11.6231 10.5089 11.4237

NOTE.—The descriptive statistics are based on individual student/year observations in the estimationsample.

64 Burke/Sass



end of the preceding school year and the current school year that does notsatisfy the structural move condition. This variable captures the impact ofmoves due to events such as family relocations and parents exercisingschool choice options.Time-varying teacher attributes are captured by a set of four indicator

variables representing varying experience levels: zero years of experience(first-year teachers), 1–2 years of experience, 3–4 years of experience, and5–9 years of experience. Teachers with 10 or more years of experience arethe omitted category.26 In addition to the time-varying teacher and studentfactors, all of the remaining regressors represent fixed effects, which are es-timated directly using our iterative method.

C. Empirical Estimation Method

From Section II, recall the linear-in-means version of the cognitiveachievement production function that we wish to estimate:

Tia 5o1

h50

hgi 1 lhg ∼ ikða2hÞ 1Xi;a2ha1h

1 Tjða2hÞ;t2hhh 1 dh;jlða2hÞ 1 fhCkða2hÞ

i1 qm 1 vt 1 εia:

ð3Þ

In the equation above, we have substituted Tia,, the standardized test score(in either mathematics or language arts), for Aia, the true achievement level,and the disturbance εia now embeds measurement error imposed by the testinstrument with respect to the true achievement level. We now denoteteacher fixed effects as teacher-school spell effects, dh; jlða2hÞ, which refers tothe effect on the age a test score of having experienced teacher j at schooll at age a-h. The teacher-school “spell” fixed effect allows the combined ef-fect of the teacher-school pair to be nonadditive—for example, some teach-ers maymake more efficient use of a school’s resources than others, and thesame teacher may perform differently at different schools. As explicated inAndrews, Schank, andUpward (2006), themethoddoes not separately iden-tify school and teacher contributions to achievement.Arcidiacono et al. (2010) describe a similar achievement function, in

which achievement spillovers likewise operate through peers’ fixed effects.These authors show that, provided certain assumptions hold, the (nonlin-ear) least-squares estimators of the peer effect coefficients, lh, are consis-tent for a finite number of observations per student. Under the same set ofassumptions as given in Arcidiacono et al. (2010), we argue in appendix B,

26 Most longitudinal studies of student achievement find that the marginal effectof additional teacher experience approaches zero after 5 years of experience. See,e.g., Rockoff (2004), Rivkin et al. (2005), and Kane et al. (2008).




available in the online version of this article, that the consistency results ap-ply to the linear-in-means model with lagged effects, above, and also ex-tend to themodels of nonlinear peer effects described below.27We rely fur-ther on the results of Arcidiacono et al. (2010) in employing a numericalsolutionmethod that is shownbyArcidiacono et al. to converge to the non-linear least-squares estimators of peer effect coefficients under reasonableassumptions.28

Analytical estimation of the achievement function is computationallydifficult given the large number of fixed effects operating at multiple levelsof aggregation and the nonlinearity of the least-squares problem. Combin-ing teacher and school effects into teacher-school spell effects simplifies theestimation considerably, but even with this simplification we must esti-mate fixed effects for over 200,000 students, plus two or three grade levelsand 5 calendar years within each schooling-level model. Standard fixed ef-fects methods eliminate one level of effects by demeaning the data with re-spect to the variable of interest, but such a strategy (e.g., demeaning by stu-dent) is not only insufficient in our case but is not feasible when estimatingspillovers from peers’ fixed effects.To estimate the model, we adopt an approximate version of the iterative

estimation procedure proposed by Arcidiacono et al. (2010), which we de-scribe in detail in appendix B, available in the online version of this article.29

In a second key result, Arcidiacono et al. (2010) show that their procedureyields coefficient estimates that converge to the (consistent) nonlinearleast-squares estimators under relatively nonrestrictive assumptions.30 Un-fortunately, this estimation procedure fails to convergewhen applied to theFlorida education data, a problem that we attribute to a combination ofnoise in test scores and relatively few observations per student.In our approximate version of the procedure, which facilitates conver-

gence, estimates of current peer effects will be biased downward in expec-tation relative to the true least-squares estimators. The downward biasconstitutes an attenuation effect since in our approximate method the indi-

27 In app. B, online, we employ a combination of analytical arguments and nu-merical evidence to support the consistency claims. Intuitively, consistency derivesfrom the fact that our models constitute special cases of the heterogeneous peer ef-fects model of Arcidiacono et al. (2010).

28 As discussed below and in app. B, online, inmostmodelswe employ an approxi-mation of the numerical solution method given by Arcidiacono et al. (2010), which isshown in simulations to provide good approximations to the exact solution under rea-sonable data conditions.

29 We utilize a tolerance level of 0.001 for convergence of the iterative procedure,meaning that convergence is defined as the point at which no parameter estimatechanges more than 0.001 from one iteration to the next.

30 The fixed effects estimates under the iterative procedure also converge to theleast-squares solution, but in the case of the fixed effects, the least-squares estima-tors are not consistent.

66 Burke/Sass



vidual fixed effects aremeasuredwith error.We show through simulations,described in appendix B online, that the downward bias is likely to be smallto moderate given the conditions present in our data. In particular, our ap-proximate method produces estimates in which the downward bias on cur-rent peer effects varies from 4% to 19% under simulated data conditionsthat mirror those in the Florida data.31 Simulations indicate, further, thatour results should be fairly robust to noise. As discussed in appendix B on-line, thedownwardbias on current peer effects is likely tobe relativelyweakin the results for reading at the middle school and high school levels andstronger for mathematics in middle school and high school; elementaryschool results (whether mathematics or reading) constitute the intermedi-ate case.

IV. Results

A. Mean Peer Effects

We first discuss results under linear-in-means specifications. In thesemodels, we estimate the effects on current achievement of the average abil-ity (as measured by our fixed effects) of current classroom peers as well asthe average ability (fixed effects) of once-lagged classroom peers (not in-cluding the student herself in the peer means).32 Table 2 reports coefficientestimates for the covariates of interest under our preferred model specifi-cation, in which we account for multiple levels of fixed effects, includingteacher-school spell effects.We find positive and highly significant effects of current peer ability

within every level of schooling and subject, with the exception of middleschool mathematics. These effects are quite small in magnitude, however.For elementary school mathematics—the largest estimated effect—an in-crease in current peer ability from the populationmean to 0.25 standard de-viations above the mean (about 10 percentile points) would yield an in-crease in own achievement of 0.007 standard deviation units, or aboutone-quarter of a percentile point. For comparison, this effect is equal to thegain (also in elementary mathematics) from reducing class size by threestudents, and it amounts to about half the gain from having a teacher with1–2 years of experience rather than a novice teacher. For both mathematicsand reading, current peer effects are substantially larger at the elementaryschool level than at themiddle school or high school level. These results areconsistent with the fact that elementary school students typically spend the

31 The relevant data conditions concern the degree of sorting into classrooms bystudent ability and the degree of matching between student ability and teacher abil-ity. These issues are discussed in detail in app. B, online.

32 For comparison, we also estimate models in which the peer group—whethercurrent or lagged—consists of all others in the same grade level and school in a givenyear. Unless specified otherwise, results pertain to classroom peer effects.




Table 2Estimates of the Determinants of Mathematics and Reading Achievement inFlorida, 1999–2000 to 2003–4

Mathematics Reading







Mean peerfixed effect .0292*** 2.0013 .0088** .0271*** .0087* .0124***

(.0029) (.0026) (.0037) (.0021) (.0048) (.0044)Mean laggedpeer fixedeffect 2.0033** .0083*** .0145*** 2.0031*** 2.0039* .0027

(.0013) (.0012) (.0013) (.0011) (.0022) (.0022)Number ofschoolsattended 2.0255** 2.0645*** 2.2955*** 2.0215* 2.0708*** 2.0343**

(.0113) (.0053) (.0144) (.0114) (.0123) (.0165)Structuralmover .0642* 2.0285*** .0405*** .0333 2.0128 2.1332***

(.0384) (.0073) (.0097) (.0357) (.0139) (.0487)Nonstructuralmover 2.0015 2.0173*** .0465*** 2.0063 2.0028 2.0264

(.0077) (.0039) (.0088) (.0061) (.0087) (.0171)Class size 2.0022*** 2.0014*** 2.0057*** 2.0013** 2.0005 2.0004

(.0008) (.0002) (.0005) (.0006) (.0005) (.0005)Teacher with0 years ofexperience .0499* .0535*** .0897*** .0275 .0221 .0478

(.0262) (.0123) (.0223) (.0283) (.0241) (.0599)Teacher with1–2 years ofexperience .0661*** .0606*** .0796*** .0483** .0429* .0175

(.0187) (.0086) (.0162) (.0212) (.0228) (.0493)Teacher with3–4 years ofexperience .0759*** .0451*** .0569*** .0563*** .0268 2.0035

(.0200) (.0079) (.0150) (.0196) (.0182) (.0412)Teacher with5–9 years ofexperience .0410*** .0286*** .0214* .0425*** .0184 2.0019

(.0144) (.0068) (.0112) (.0142) (.0142) (.0285)No. ofstudents 156,526 231,082 160,400 172,770 88,181 93,123

No. ofobservations 315,566 542,650 363,901 348,378 212,281 186,452

NOTE.—Models also include year, grade-level, and repeater-by-grade indicators, as well as lagged stu-dent mobility, class size, and teacher experiencemeasures. Bootstrapped standard errors are in parentheses.

* Significant at the .10 level (two-tailed test).** Significant at the .05 level (two-tailed test).*** Significant at the .01 level (two-tailed test).



entire school daywith the same peer groupwhereasmiddle school and highschool students experience multiple peer groups during the typical six-period or seven-period school day.As expected, in all but one case, the coefficient on lagged peer ability is

smaller in magnitude than that on current peer ability. In all cases excepthigh school reading, lagged peer effects are at least marginally significant(10% level or better), indicating that peers have persistent effects on achieve-ment levels.While the presence of some negative lagged peer effectsmay ap-pear puzzling, the sizes of the negative effects are an order of magnitudesmaller than the contemporaneous peer effects. Further, results from non-linear models (discussed below) suggest that negative peer influences neednot be perverse.Notice that the signs on most of the time-varying regressors are as we

would expect: achievement declines with the number of schools attendedin a year for all grades and subjects. Larger class size has a uniformly neg-ative impact on outcomes. The class size effects are significant for all gradelevels in the case of mathematics and for elementary school only in the caseof reading. Notice also that within-teacher variation in years of experiencehas fairly small effects on achievement, with most of the gain coming in theearly years, consistent with the findings of Rivkin et al. (2005) and Harrisand Sass (2011).Table 3 gives results for a model that is similar to that reported in table 2,

but where student observations from elementary school andmiddle schoolare pooled. With this pooling, we can restrict the minimum observationsper student to three rather than two in order to reduce noise in estimatesof student fixed effects and assess robustness of results to this refinement.The trade-off is that coefficients can no longer vary between elementaryschool and middle school. As expected, the estimated current peer effectsare roughly intermediate between the elementary school–only and middleschool–only estimates. For mathematics achievement, the current peer ef-fect becomes very small and statistically insignificant. For reading, the cur-rent peer effect is positive and statistically significant. Within-year studentmoves have a negative effect on student performance in both subjects, andclass size continues to be negatively correlated with mathematics achieve-ment. The point estimates on specific levels of teacher experience vary fromthose in the disaggregated models, but payoffs to experience remain rela-tively small and occur mainly in the first years of teaching.Table 4 shows how different model specifications influence the current

peer effect estimates.33 The coefficients in the first row correspond to thosereported in table 2, from our preferred specification. The coefficients in the

33 Unless otherwise specified, all models reported in this table include the sameset of controls as the baseline model presented in table 2.




second row come from amodel in which we do not control for unobservedteacher effects—we use school fixed effects rather than teacher-school spelleffects. In the third row, the peer group is defined as all others in the samegrade level (within the same school and year), but the specification is other-wise identical to the preferred one.Observe first that estimated peer effects are generally larger in the ab-

sence of teacher fixed effects. At the elementary level, the (current) peer ef-fect inmathematics without teacher controls, at 0.0635, ismore than doublethe estimated effect with the controls. Similarly, in elementary reading thepeer coefficient increases by more than 50% in the absence of teacher con-trols. This coefficient difference is at least marginally significant in all cases

Table 3Estimates of the Determinants of Mathematics and Reading Achievement inFlorida, 1999–2000 to 2003–4 (Minimum of Three Observations per Student)

MathematicsElementary School/

Middle School(Grades 4–8)

ReadingElementary School/

Middle School(Grades 4–8)

Mean peer fixed effect .0014 .0154**(.0010) (.0067)

Mean lagged peer fixed effect 2.0041*** 2.0094***(.0014) (.0029)

No. of schools attended 2.1366*** 2.0348*(.0224) (.0196)

Structural mover 2.0084 2.0140(.0089) (.0173)

Nonstructural mover .0041 2.0009(.0070) (.0141)

Class size 2.0037*** .0004(.0008) (.0006)

Teacher with 0 years ofexperience 2.0832*** .0474

(.0315) (.0378)Teacher with 1–2 years ofexperience 2.0597** .0670**

(.0296) (.0327)Teacher with 3–4 years ofexperience 2.0599** .0284

(.0276) (.0257)Teacher with 5–9 years ofexperience 2.0437** .0119

(.0211) (.0206)No. of students 109,507 38,982No. of observations 370,841 133,189



70 Burke/Sass



except high school reading and high school mathematics. On the whole, theresults suggest a positive correlation between average current peer abilityand teacher quality—current and/or lagged—controlling for individual abil-ity. This correlationproduces an upwardbias on estimated peer effectswhenteacher fixed effects are omitted.The second important finding is that positive peer effects largely disap-

pear whenmeasuring peer influences at the (within-school) grade level. Es-timated grade-level peer effects are statistically insignificant at all schoolinglevels in mathematics and in elementary school reading. The only case inwhich there is a positive and even marginally significant effect is for highschool mathematics. Taking these results at face value, a natural interpreta-tion is that the classroom setting facilitates learning spillovers in a way thatnonclassroom interactions do not. Taking a skeptical view, we are alsomore likely to obtain spurious peer effects at the classroom level than at thegrade level due to endogenous classroom assignment and/or classroom-wide unobserved shocks, despite our efforts to avoid such pitfalls.

Table 4Comparison of Estimated Effects of Mean Peer Fixed Effects on Mathematicsand Reading Achievement in Florida from Models with Varying Peer GroupLevels and Varying Teacher Controls, 1999–2000 to 2003–4

Mathematics Reading

Peer Group/TeacherControls







Classroompeers/withteacher fixedeffects .0292*** 2.0013 .0088** .0271*** .0087* .0124***

(.0029) (.0026) (.0037) (.0021) (.0048) (.0044)Classroompeers/noteacher fixedeffect .0635*** .0126*** .0019 .0424*** .0176*** .0150***

(.0035) (.0018) (.0030) (.0031) (.0035) (.0051)Grade-levelpeers/withteacherfixed effects .0044 2.0003 2.0012 2.0031 2.0315** .0100*

(.0111) (.0062) (.0054) (.0143) (.0131) (.0054)No. ofstudents 156,526 231,082 160,400 172,770 88,181 93,123

No. ofobservations 315,566 542,650 363,901 348,378 212,281 186,452






B. Nonlinear Peer Effects

As a first step in relaxing the linear-in-means specification, we allow theimpact of mean peer ability to depend on the student’s own “type,” wheretype is simply an indicator of baseline achievement within the schoolinglevel. In particular, we take the national percentile rank of the student’s ini-tial score on the FCAT-NRT test—in the grade preceding the estimationsample—and place it within the distribution of these ranks among her Flor-ida public school cohort (defined by grade level and year).34 The student is a“low” type if her initial percentile rank falls in the bottom quintile of theFlorida distribution, a “middle” type if it falls between the 20th and 80thpercentiles, and a “high” type if it lies in the top quintile.35 Current andlagged peer variables are constructed as in the linear-in-means model. Re-sults are reported in table 5.36

Among elementary school students, middle- and high-type students gainabout equally (in either subject area) from an improvement in average cur-rent peer ability, whereas low-type students are either unaffected (mathe-matics) or are made worse off by a small margin (reading). The magnitudeof the positive spillovers for middle- and high-type students is roughlytwice the size of the effect averaged over all students (i.e., the estimates intable 2). Inmiddle school and high schoolmathematics, all types of studentsgain from an improvement in average (current) peer quality, but the gainsare two to three times larger for high-type students than for middle-typestudents. In middle school reading we find no significant (current) peer ef-fects. For high school reading, middle and high types both benefit signifi-cantly (and roughly equally) from an improvement in average current peerability, while low types are made significantly worse off.Looking at lagged peer effects in the one-way heterogeneity model, we

find that the negative impact of lagged peers observed, for example, in thecase of elementary school mathematics, is driven by the (negative) impactof lagged mean peer ability on low-type students. More in line with ex-pectations, middling and high types each experience positive spillovers

34 In elementary school, the earliest score observed is for third grade. Because weuse third-grade scores to define (predetermined) type, we must omit third-gradeoutcomes from the estimation sample.

35 While this type of indicator is an imperfect measure of ability, identifying het-erogeneity in peer effects along an observable dimension has at least two distinctadvantages: first, policy recommendations that apply to a given type will be imple-mentable (in principle); second, according to Arcidiacono et al. (2010), types mustbe based on observed factors in order to guarantee consistency of least-squares es-timators of the heterogeneous (type-specific) peer effects.

36 Due to the computational costs of estimating the nonlinear models, we esti-mate only our preferred specification (including teacher effects, no singleton stu-dents, classroom level effects). We assume that the impact of changes in specifica-tion would be similar qualitatively to the impact on the results in the linear models.

72 Burke/Sass



(on elementary school mathematics scores) from lagged mean peer abil-ity, spillovers that are smaller than the respective spillovers from currentpeer ability.To allow for an even more complex set of peer influences, we estimate

a two-way interaction model, similar to those of Hoxby and Weingarth(2006) andCarrell et al. (2011). In this model, the achievement level of eachstudent type (low, middle, and high, as defined above) is influenced by the(respective) shares of peers (either current or lagged) in each of three re-gions of the sample-wide distribution of individual fixed effects: the bot-tom quintile, the middle three quintiles, and the top quintile. To estimatethese effects, we construct six peer variables, each the product of a binary(own) type indicator and the proportion of peers of a given ability rank: forexample, “individual of low type × fraction of (current/lagged) peers inlowest ability quintile,” “individual of low type × fraction of (current/lagged) peers in highest quintile,” and similarly for middle- and high-typeindividuals. Due to collinearity of the proportions, we omit the effect ofthe proportion of middle-ability peers on each individual type. Therefore,the marginal effect (on a given type) of an increase in the proportion ofhigh-ability peers (alternatively, low-ability peers) represents the net effectof increasing the high-ability (low-ability) proportion and reducing the

Table 5Estimates of the Effect of Mean Classroom Peer Fixed Effects by Own InitialTest Score Quintile on Mathematics and Reading Achievement in Florida,1999–2000 to 2003–4

Mathematics Reading







Lowest test scorequintile × meanpeer fixed effect .0170 .0235*** .2681*** 2.0223* 2.0021 2.0613**

(.0134) (.0072) (.0175) (.0124) (.0127) (.0241)Middle test scorequintiles × meanpeer fixed effect .0670*** .0278*** .0532*** .0462*** 2.0071 .0352***

(.0092) (.0027) (.0060) (.0078) (.0079) (.0095)Highest test scorequintile × meanpeer fixed effect .0640*** .0807*** .1657*** .0384*** .0187 .0377***

(.0130) (.0075) (.0093) (.0111) (.0133) (.0141)No. of students 154,397 169,446 158,939 170,565 153,781 92,945No. ofobservations 311,260 413,979 360,814 343,917 59,724 186,066






middle-ability proportion, since the low-ability (high-ability) proportionand class size are being held constant.Table 6 reports the current peer effect coefficients for each of the six

subject-by-schooling level models. Among the elementary school results,all effects are highly significant and are consistent across mathematics andreading. For both subjects, we observe considerable heterogeneity in the na-ture of effects by own type and segment of peer group. Low-type studentsare made worse off by increases in the fraction of peers at either extremeof the ability distribution—that is, they reap greater benefits from peers ofmiddling ability than from either high- or low-ability peers. Middle-typestudents are made worse off by an increase in the fraction of low-abilityclassmates and better off by an increase in the share of high-ability peers—suggesting that they rank peers directly in accordance with their ability.High-type students benefit froman increase in the share of peers in the low-est ability quintile, as well as from an increase in the proportion of high-ability peers.The magnitudes of these latter peer effects are economically significant.

For example, amonghigh-initial-score students (high types) inmathematics,an increase in the proportion of top-quintile peers from 0.2 to 0.4 is asso-ciated with an increase of 0.03 standard deviations in achievement (1.2 per-centiles in the achievement distribution), or about twice the impact of hav-ing a teacher with 1–2 years of experience rather being taught by a noviceteacher.At the middle school and high school levels, current peer effects are

qualitatively similar to those at the elementary level, with an exception inthe case of middle school mathematics—middling types benefit marginallyfrom a higher share of low-ability peers—and with the qualification thateffects are statistically insignificant in a few cases. In most cases, laggedpeer effects in the two-way interaction model have the same sign as thecoefficients on the corresponding current peer variables and yet are smallerin magnitude.One explanation for heterogeneous peer effects by own type and peer

ability could be that teachers tend to target the instructional level towardthe better students in a given class. When ability differentials in a class arelarge and teachers target the top students, the weakest students might feellost or overwhelmed. When ability differentials within a class are moremoderate, the goals set by the teacher may seem at least within reach of theweaker students, who may be inspired to do better than if expectationswere set very low. In addition, the ability to learn from peers may dependon their relative ability rather than their absolute ability, since relative abil-ity likely influences the potential for communication and friendship be-tween peers. In the case of high and low achievers, the intellectual distancebetween the two groups may be so great that there is little or no between-group interactionwithin the classroom. If true, this could explainwhy high

74 Burke/Sass



Tab

le6

Estim

ates

oftheEffects

ofPe

erAbilityQuintile

byOwnInitialT

estScoreQuintile

onMathe

maticsan

dReading

Ach

ievemen

tin

Florida,

1999–2000

to2003–4

Mathem

atics

Reading

Elementary

School

(Grades

4–5)

Middle

School

(Grades

6–8)

High

School

(Grades

9–10)

Elementary

School

(Grades

4–5)

Middle

School

(Grades

6–8)

High

School

(Grades

9–10)

Lowestquintile

×fractionofpeers

inlowestquintile

2.2638***

2.1263***

2.4089***

2.2325***

2.2643***

2.3156***

(.0238)

(.0113)

(.0165)

(.0230)

(.0173)

(.0316)

Lowestquintile

×fractionofpeers

inhighestquintile

2.2398***

2.2074***

2.4553***

2.2759***

2.3698***

2.3976***

(.0351)

(.0241)

(.0540)

(.0347)

(.0532)

(.0654)

Middle

threequintiles×fractionofpeers

inlowestquintile

2.0482**

.0172**

2.1287***

2.0434***

2.0138

2.0256

(.0199)

(.0069)

(.0081)

(.0150)

(.0138)

(.0157)

Middle

threequintiles×fractionofpeers

inhighestquintile

.1059***

.0698***

2.0210

.0615***

2.0011

2.0338*

(.0165)

(.0067)

(.0129)

(.0212)

(.0174)

(.0197)

Highestquintile

×fractionofpeers

inlowestquintile

.1487***

.1667***

.0874***

.1144***

.2106***

.0824***

(.0340)

(.0242)

(.0240)

(.0290)

(.0319)

(.0253)

Highestquintile

×fractionofpeers

inhighestquintile

.1437***

.1614***

.2346***

.0662***

.0780***

.0133

(.0313)

(.0101)

(.0116)

(.0238)

(.0291)

(.0267)

No.ofstudents

154,397

169,446

158,939

170,565

59,724

92,945

No.ofobservations

311,260

413,979

360,814

343,917

153,781

186,066

NOTE.—

Modelsalso

includeyear,grade-level,andrepeater-by-gradeindicators,aswellaslagged

studentmobility,classsize,andteacher

experience

measures.Bootstrapped

stan-

darderrors

arein

parentheses.

*Sign

ificantat

the.10level(two-tailedtest).

**Sign

ificantat


***

Sign

ificantat




achievers appear to benefit from an increase in low-achieving classmates;they are better having no interaction with low-achieving peers than moresignificant interaction with middling peers.37

If initial achievement is a reasonable (if noisy) proxy for ability as mea-sured by fixed effects, these results can be used to guide policy, althoughthe implications are not clear-cut. For example, middling-ability studentswould like to be placed with high-ability peers, but high-ability types preferother high types (or even low-ability peers) tomiddling peers. The results dosuggest that some degree of tracking should be preferred to a policy of uni-formly mixed classrooms. For example, dividing students into two tracks,one for below-median ability and another for above-median ability, and cre-ating mixed classrooms within each track would maximize peer benefits forlow-ability students andwould allowat least somemiddling-ability studentsto benefit from having higher-ability peers, although high-ability studentswould prefer a policy involving stricter segregation by ability. In the school-ing experiment in Kenya described in Duflo et al. (2011), a simple two-trackpolicy, enacted in second-grade classrooms in a random sample of schools,was found to have significant benefits to students across all quantiles of thebaseline score distribution.The effects in our two-way interaction model agree in some respects

with the findings of Hoxby and Weingarth (2006), who estimate a similarmodel (on elementary school and middle school grades combined), but inwhich the peer group segments are more finely subdivided. They find, forexample, that low-initial-score students prefer peers of slightly higher abil-ity than themselves and are made worse off by an increase in the share ofpeers of very high ability. They also find that high-scoring students do bestwhen matched with other high-scoring students. In contrast, using data onAir Force Academy students, Carrell et al. (2009) find that low-ability stu-dents are helped, rather than hurt, by an increase in the share of high-ability(based on verbal SAT score) peers. This alternative finding for higher ed-ucation—the Air Force Academy in particular—may reflect differences inthat institutional setting compared to primary and secondary education.For example, disparities in ability among Air Force students are likely tobe smaller than those present in our data.

V. Summary and Conclusions

This article adds to a growing list of studies that use matched panel datato estimate peer effects in academic achievement. As in earlier studies, thepanel data facilitate the identification of peer effects on academic achieve-ment by enabling control for endogenous variation in peer groups. Unlikemany earlier studies, we are able to place students within classroom groups

37 It is also possible that high achievers may simply get an increase in self-esteemby feeling superior to the low achievers in the classroom.

76 Burke/Sass



with specific teachers, and we observe each teacher with more than onegroup of students. Accordingly, ours is the first study to control simulta-neously for unobserved heterogeneity in both student ability and teachereffectiveness, among other unobserved effects, and the first to estimateclassroom-level peer effects at the elementary school, middle school, andhigh school levels for the same school system and to compare these tograde-level effects. While not the first to do so, we add further value byadopting an innovative computational technique that aims both to facilitatefixed effects estimation and to minimize measurement error in peer ability,and we estimate nonlinear peer effects models that allow for non-zero-sumpolicy implications.We observe many instances of significant peer effects at the classroom

level, but rarely are effects significant at the general grade level. Such resultsunderscore the importance of identifying the salient peer group. In addi-tion, estimated peer effects are generallyweakerwhenwe control for unob-served inputs at the teacher-school level. This result indicates that teacherability may vary systematically with peer ability, even controlling for in-dividual student ability, and that it is therefore important to control forteacher effectiveness, ideally through teacher fixed effects. This findingmay also help to account for the fact that we observe smaller peer effects(comparing linear-in-means models) than have been found in some pre-vious studies that did not control for teacher effects.We find that peer effects exhibit subtleties not captured by the linear-in-

means specification. For example, students with low initial achievementlevels appear to benefit less, andmay even experience negative effects, froman increase in the average ability of their peer group than do those withhigher initial scores. Our richest model of peer interactions indicates, fur-ther, that these initially weak students prefer to interact with peers in themiddle of the ability distribution than with peers in the very top tier. Stu-dents with middling initial achievement levels experience effects that aremonotonic in peer ability, and therefore they do best when placed withhigh-ability peers. High achievers prefer high-ability peers to middlingpeers, yet they also prefer low-ability peers tomiddling peers. Thus,mono-tonicity is violated for both low and high initial scorers, but most of the ev-idence supports the single-crossing property, whereby high-ability stu-dents benefit more than others from increases in the share of high-abilitypeers.These preferences over peer ability do not point to a single, optimal pol-

icy prescription since the diverse peer rankings cannot be simultaneouslysatisfied for all types of students. However, they do suggest that classroomassignment policies involving some degree of tracking by ability—such assplitting students into two tracks—should be preferred to policies in whichall classrooms contain a broad mix of students. Taking the single-crossingproperty seriously would call for segregating high-ability students in a sep-




arate track. However, the desirability of such a policy—which could in-crease inequality of outcomes—depends on whether achievement gains (orlosses) are weighted equally regardless of the student’s initial achievementlevel and whether achievement disparities should matter in addition to av-erage achievement. If the goal is to raise achievement among the lowestscorers, focus should be placed on matching such students with others ofmodestly higher ability rather than with the top students.Any implementation of conscious peer group management should pro-

ceed in modest steps. Our tentative policy recommendations are based onrelatively small differences in peer composition resulting from natural var-iation in classroomassignments. Extreme changes in classroomcompositionmight not have the anticipated effects, as recently noted by Carrell et al.(2011). Further, while our findings suggest that the distribution of studentability may influence teaching strategies in ways that benefit some studentsbut not others,more research is needed to reveal the nature of such strategiesand how teacher resources might be best exploited in light of classroom as-signment policies.

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Classroom Peer Effects and Student Achievement