Extracted main text — title through conclusion, appendix excluded. This is what our citation measures are computed over, published so the extraction can be checked by eye.
113,771 characters · 28 sections · 52 citation commands
LARGE Teacher-to-classroom assignment and student achievement LARGE
\thispagestyle{empty}
{\bf JEL codes:} I20, I21, I24 \singlespacing {\bf Keywords:} teacher quality, teacher assignment, education production, student achievement, average reallocation effects, K--12
\setcounter{page}{1} \onehalfspacing
Approximately four million teachers work in the public elementary and secondary education system in the United States. These teachers provide instruction to almost fifty million students, enrolled in nearly one hundred thousand schools, across more than thirteen thousand school districts ConditionOfEducation_NCES2017,DigestOfEducationStatistics_NCES2017. Differences in measured student achievement are substantial across US schools as well as across classrooms within these schools. Beginning with Hanushek_AER1971, a large economics of education literature attributes cross-classroom variation in student achievement to corresponding variation in (largely) latent teacher attributes. These latent attributes are sometimes referred to as teacher quality or teacher value-added.
The implications of value-added measures (VAM) for education policy are controversial both within the academy and outside it.\footnote{See, for example, the March 2015 special issue of Educational Researcher on value-added research and policy or the American Statistical Association's statement on value-added measures Morganstein_Wasserstein_SPP2014. } The most contentious applications of VAM involve their use in teacher tenure and termination decisions Chetty_et_al_EN2012,Darling-Hammond_ER2015. The premise of such applications is that changes in the stock of existing teachers \textendash specifically rooting out teachers with low VAMs and retaining those with high ones \textendash could lead to large increases in student achievement and other life outcomes.
In this paper we pose an entirely different question: is it possible to raise student achievement, without changes to the existing pool of teachers, by changing who teaches whom? Schools and school districts are the loci of teacher employment. To keep our analysis policy-relevant, we therefore focus on the achievement effects of different within-school and within-district teacher-to-classroom assignment policies.
For teacher assignment policies to matter, teachers must vary in their effectiveness in teaching different types of students. For example, some teachers may be especially good at teaching English language learners, minority students, or accelerated learners Dee_RESTAT2004, Loeb_et_al_EEPA2014. Formally educational production must be non-separable in some teacher and student attributes Graham_Imbens_Ridder_USC2007,Graham_Imbens_Ridder_QE14,Graham_Imbens_Ridder_JBES18.
Using data collected in conjunction with the Measures of Effective Teaching (MET) project, we present experimental evidence of such non-separabilities. We expand upon standard models of educational production, which typically assume that the effects of teacher and student inputs are separable. Our identification strategy relies on the random assignment of teachers to classrooms in the MET project. Specifically, we study assignments based upon (i) an observation-based, pre-experiment measure of teaching practice \textendash Danielson's Danielson2011 Framework for Teaching (FFT) instrument \textendash and (ii) students' and classroom peers' baseline test scores, also measured pre-experiment.
Alternative teacher assignments change the joint distribution of these variables. When the educational production function is non-separable in these variables, these changes can affect average achievement. Focusing on assignments based on teacher FFT and student baseline achievement, we find that within-district changes in teacher-to-classroom assignments could increase average classroom student achievement by as much as 0.04 standard deviations. This effect corresponds to the estimated difference in average achievement across the teacher-to-classroom assignment which maximizes aggregate achievement versus the one which minimizes it. Perhaps more realistically, comparing the status quo assignment in MET schools \textendash which was generated by random assignment of teachers to classrooms \textendash with the optimal one generates an estimated increase in average test scores of 0.02 standard deviations.
To benchmark these effects consider a policy which removes the bottom $\tau \times 100$ percent of teachers from classrooms \textendash sorted according to their VAM \textendash and replaces them with average teachers (i.e., teachers with VAMs of zero). Assuming a Gaussian distribution for teacher value-added, the effect of such an intervention would be to increase the mean of the student test score distribution by
standard deviations.\footnote{As is common practice, we abstract from the effects of possible behavioral responses to VAM-guided teacher retention policies. For example, teachers might become demoralized by VAM retention systems and teach less effectively as a result; or they could be motivated to teach more effectively.} Here $\sigma$ corresponds to the standard deviation of teacher value-added and $q_{\tau}$ to its $\tau^{th}$ quantile.
Rockoff_AER04 and Rothstein_QJE2010 estimate a standard deviation of teacher value-added of between 0.10 and 0.15. Taking the larger estimate and setting $\tau=0.05$ $(0.10)$ generates an expected increase in student test scores of $0.015$ $(0.026)$ standard deviations; smaller than, albeit comparable to, our reallocation effects. We note that replacing five (ten) percent of teachers would be difficult to do in practice. It would be even more difficult to correctly identify the bottom five (ten) percent of teachers (according to VA) and replace them with average ones. We conclude that the achievement effects of teacher assignment policies are meaningful.
In contrast to policies which replace teachers, and/or require the hiring of new ones, the within-school and within-district teacher reassignment policies we explore in this paper are resource neutral. Districts require no new teachers or financial resources to implement them. Of course, reassigning teachers across classrooms, and especially across schools within a district, may involve other types of costs. For example, many school districts operate under collective bargaining agreements which give senior teachers partial control over their school assignment Cohen-Vogel_et_al_EEPA2013.\footnote{ Moreover, many teachers have preferences over school and student characteristics. Thus, one might need to pay bonuses to move teachers to certain schools or classrooms (e.g., classrooms with high fractions of disadvantaged students).}
Our decision to use teacher FFT, students' and peers' baseline test scores as assignment variables was driven by their availability in the MET dataset. Of course, observational measures of teaching practices, such as the FFT, are routinely used for teacher evaluation, promotion, and retention decisions. Its seems reasonable, therefore, to explore whether they might also aid in determining a teacher's classroom assignment.
It seems likely, however, that assignments based upon a different pair of teacher and classroom attributes would lead to greater achievement gains.\footnote{That is, we did not consider the universe of possible assignment variables.} Working with appropriately chosen linear combinations of multiple student and teacher attributes could generate even larger achievement gains. We leave explorations along these lines to future research.
Readers may reasonably raise questions about the external validity of the results reported below. We believe such skepticism is warranted and encourage readers to view what is reported below as provisional. We do, however, hope our results are sufficiently compelling to motivate additional research and experimentation with teacher-to-classroom assignment policies.
Work by Susanna Loeb and co-authors suggests that US school districts have de facto teacher-to-classroom assignment policies Loeb2011, Grissom2015. For example, they find that less experienced, minority, and female teachers are more likely to be assigned to predominantly minority classrooms. They also present evidence that principals use teacher assignments as mechanisms for retaining teachers \textendash as well as for encouraging less effective teachers to leave \textendash and that more experienced teachers exert more influence on classroom assignment decisions.
Our work helps researchers and policy-makers understand the achievement effects of such policies and the potential benefits of alternative ones. The findings presented below suggest that teacher-to-classroom assignment policies are consequential and that changes to them could meaningfully increase average student achievement.
In addition to our substantive results, we present new identification results for average reallocation effects (AREs). Identification and estimation of AREs under (conditional) exogeneity is considered by Graham_Imbens_Ridder_QE14,Graham_Imbens_Ridder_JBES18. Unfortunately these results do not apply directly here. Although teachers were randomly assigned to classrooms as part of the MET experiment, compliance was imperfect. Furthermore some students moved across classrooms after the random assignment of teachers, which raises concerns about bias due to endogenous student sorting. We develop a semiparametric instrumental variables estimator AiChen2003 which corrects for student and teacher non-compliance. Our analysis highlights how complex identification can be in the context of multi-population matching models where agents sort endogenously.
In independent work, Aucejo2019 also use the MET data to explore complementarity between student and teacher attributes in educational production. They do not focus on adjusting for teacher and student non-compliance as we do, emphasizing instead an intent-to-treat type analysis. Their paper includes an interesting analysis of the different sub-components of the FFT measure; something not done here. Despite these methodological differences, their results are qualitatively concordant with ours. In earlier work, Dee_RESTAT2004, Dee2005 uses Project STAR data to study complementarity between teacher and student minority status.
Our goal is to identify the average achievement effects of alternative assignments of teachers to MET classrooms. These are average reallocation effects (AREs), as introduced by Graham_Imbens_Ridder_USC2007, Graham_Imbens_Ridder_QE14. The identification challenge is to use the observed MET teacher-to-classroom assignments and outcomes to recover these AREs.
Our analysis is based upon experimentally generated combinations of student and teacher attributes, that is, it exploits the random assignment of teachers to classrooms in the MET experiment.\footnote{To be precise, the randomization was carried out within schools. See Section (ref) for details.} Like in many other field experiments, various deviations from MET's intended protocol complicate our analysis. In this section we outline a semiparametric model of educational production and consider its identification based upon the MET project as implemented, using the MET data as collected.
It is useful, however, to first explore nonparametric identification of reallocation effects under an ideal implementation of the MET project (henceforth MET as designed). Such an approach clarifies how the extra restrictions introduced below allow for the identification of reallocation effects despite non-compliance, attrition, and other deviations from the intended experimental protocol.
Our setting features two populations, one of students and the other of teachers. Each student is distinguished by an observed attribute $X_{i}$, in our case a measure of baseline academic achievement, and an unobserved attribute, say “student ability,” $V_{i}$. Similarly, each teacher is characterized by an observed attribute $W_{i}$, in our case an observation-based measure of teaching pedagogy, and an unobserved attribute, say “teacher quality," $U_{i}$.\footnote{We use “ability" as a shorthand for latent student attributes associated with higher test scores; likewise we use “quality" as a shorthand for latent teacher attributes associated with higher test scores.}
Let $i=1,\ldots,N$ index students. Let $C$ be the total number of MET classrooms or equivalently teachers. We define $G_{i}$ to be a $C\times1$ vector of classroom assignment indicators. The $c^{th}$ element of $G_{i}$ equals one if student $i$ is in classroom $c \in \{1,\dots,C\}$ and zero otherwise. The indices of student $i's$ peers or classmates are therefore given by the index set \[ p\left(i\right)=\left\{ j\thinspace:\thinspace G_{i}=G_{j},\thinspace i\neq j\right\} . \] Next we define the peer average attribute as $\bar{X}_{p\left(i\right)}=\frac{1}{\left|p\left(i\right)\right|}\sum_{j\in p\left(i\right)}X_{j}$ (i.e., the average of the characteristic $X$ across student $i's$ peers). We define $\bar{V}_{p\left(i\right)}$ similarly.
The MET project protocol did not impose any requirements on how students, in a given school-by-grade cell, were divided into classrooms. Evidently schools followed their existing procedures for dividing students within a grade into separate classrooms. An implication of this observation is that the MET experiment implies no restrictions on the joint density
beyond the requirement that the density be feasible.\footnote{We cannot, for example, have an assignment which implies all students have above-average peers.} For example, if most schools tracked students by prior test scores, then we would expect $X_{i}$ and $\bar{X}_{p\left(i\right)}$ to positively covary. If, instead, students were randomly assigned to classrooms and hence peers, we would have, ignoring finite population issues, the factorization \[ f_{X_{i},V_{i},\bar{X}_{p\left(i\right)},\bar{V}_{p\left(i\right)}}(x,v,\bar{x},\bar{v}) = f_{X_{i},V_{i}}(x,v)f_{\bar{X}_{p\left(i\right)},\bar{V}_{p\left(i\right)}}(\bar{x},\bar{v}) .\footnote{Indeed additional restrictions on the second density to the right of the equality above would also hold; see \citealp{Graham_Imbens_Ridder_NBER10}, and \citealp{Graham_HSE11}, for additional discussion and details.}\] Our analysis allows for arbitrary dependence between own and peer attributes, both observed and unobserved, and consequently is agnostic regarding the protocol used to group students into classrooms.
Two implications of this agnosticism are (i) our analysis is necessarily silent about the presence and nature of any peer group effects, and (ii) it is likely that more complicated policies, involving simultaneously regrouping students into new classes and reassigning teachers to them, could raise achievement by more than what is feasible via reassignments of teachers to existing classrooms alone, which is the class of policies we consider.\footnote{Learning about the effects of policies which simultaneously regroup students and reassign teachers would require double randomization. See Graham_EM08 for an empirical example and Graham_Imbens_Ridder_NBER10,Graham_Imbens_Ridder_JBES18 for a formal development.}
Although nothing about the MET protocol generates restrictions on the joint density (ref), random assignment of teachers to classrooms \textendash however formed \textendash ensures that
Here $W_{i}$ and $U_{i}$ denote the observed and unobserved attributes of the teacher assigned to the classroom of student $i$. A perfect implementation of MET as designed would ensure that student and teacher attributes vary independently of each other. Our research design is fundamentally based upon restriction (ref).
Let $Y_{i}$ be an end-of-year measure of student achievement, generated according to
Other than the restriction that observed and unobserved peer attributes enter as means, equation (ref) imposes no restrictions on educational production.\footnote{A fully nonparametric model would allow achievement to vary with any exchangeable function of peer attributes; see Graham_Imbens_Ridder_NBER10 for more details.} Under restriction (ref) the conditional mean of the outcome given observed own, peer, and teacher attributes equals
Equation (ref) coincides with (a variant of) the Average Match Function (AMF) estimand discussed by Graham_Imbens_Ridder_QE14,Graham_Imbens_Ridder_JBES18. The AMF can be used to identify AREs. Our setting \textendash which involves multiple students being matched to a single teacher \textendash is somewhat more complicated than the one-to-one matching settings considered by Graham_Imbens_Ridder_QE14,Graham_Imbens_Ridder_JBES18. One solution to this “problem" would be to average equation (ref) across all students in the same classroom and work directly with those averages. As will become apparent below, however, working with a student-level model makes it easier to deal with non-compliance and attrition, which have distinctly student-level features. It also connects our results more directly with existing empirical work in the economics of K-to-12 education, where student-level modelling predominates, and results in greater statistical power.
The decision to model outcomes at the student level makes the analysis of teacher re-assignments a bit more complicated, at least superficially. To clarify the issues involved it is helpful to consider an extended example. Assume there are two types of students, $X_i \in \{0,1\}$, and two types of teachers, $W_i \in \{0,1\}$. For simplicity assume that the population fractions of type $X_i=1$ students and type $W_i=1$ teachers both equal one-half, that is, half of the students are of type 1 and half of the students are taught by a teacher of type 1. Assume, again to keep things simple, that classrooms consist of three students each.
Table (ref) summarizes this basic set-up. Column 1 lists classroom types. For example, a $000$ classroom consists of all type-0 students. There are four possible classroom types, each assumed to occur with a frequency of one-fourth.\footnote{Within classrooms students are exchangeable.} The status quo mechanism for grouping students into classrooms induces a joint distribution of own and peer average attributes. This joint distribution is given in the right-most column of Table (ref). For instance, $\frac{1}{4}$ (3 out of 12) of the students are in a classroom with two type-0 peers, so that $f_{X_{i},\bar{X}_{p\left(i\right)}}(0,0)=\frac{1}{4}$, and $\frac{1}{6}$ (2 out of 12) of the students are in a classroom with one type-0 and one type-1 peer, so that $f_{X_{i},\bar{X}_{p\left(i\right)}}(0,\frac{1}{2})=\frac{1}{6}$. The MET experiment implies no restrictions on the joint density $f_{X_{i},\bar{X}_{p\left(i\right)}}(x,\bar{x})$, consequently we only consider policies which leave it unchanged.
Next assume, as was the case in the MET experiment, that under the status quo teachers are randomly assigned to classrooms. This induces the conditional distribution of $W_i$ given $X_i$ and $\bar{X}_{p\left(i\right)}$ reported in column 2 of Table (ref). Of course, from this conditional distribution, and the marginal for $X_i$ and $\bar{X}_{p\left(i\right)}$, we can recover the joint distribution of own type, peer average type, and teacher type (i.e., of $X_i$, $\bar{X}_{p\left(i\right)}$ and $W_{i}$).
Now consider the AMF: $m^{\mathrm{amf}}\left(x,\bar{x},w\right)$. Consider the subpopulation of students with $X_{i}=1$ and $\bar{X}_{p\left(i\right)}=\frac{1}{2}$. Inspecting Table (ref), this subpopulation represents \( \frac{1}{6} \) of all students (right-most column of Table (ref)). If we assign to students in this subpopulation a teacher of type $W_{i}=1$, then the expected outcome coincides with $m^{\mathrm{amf}}\left(1,\frac{1}{2},1\right)$. Under random assignment of teachers the probability of assigning a type-1 teacher is the same for all subpopulations of students.
Finally consider a counterfactual assignment of teachers to classrooms. Since we leave the composition of classrooms unchanged, $f_{X_{i},\bar{X}_{p\left(i\right)}}(x,\bar{x})$ is left unmodified. The counterfactual assignment therefore corresponds to a conditional distribution for teacher type, $\tilde{f}_{\left. \tilde{W}_{i} \right| X_{i},\bar{X}_{p\left(i\right)}} \left(\left. w \right| x,\bar{x}\right)$ which satisfies the feasibility condition:
for all $w \in \mathbb{W}$. Here $\tilde{f}$ denotes a counterfactual distribution, while $f$ denotes a status quo one. We use $\tilde{W}_{i}$ to denote an assignment from the counterfactual distribution. Note that by feasibility of an assignment $\tilde{W}_{i}\stackrel{D}{=}W_{i}$ marginally, but will differ conditional on student attributes. Condition (ref), as discussed by Graham_Imbens_Ridder_QE14, allows for degenerate conditional distributions, as might occur under a perfectly positive assortative matching.
Average achievement under a counterfactual teacher-to-classroom assignment equals:
Since all the terms to the right of the equality are identified, so too is the ARE. Conceptually we first \textendash see the inner integral in equation (ref) \textendash compute the expected outcome in each type of classroom (e.g., $X_{i}=x$ and $\bar{X}_{p\left(i\right)}=\bar{x}$) given its new teacher assignment (e.g., to type $\tilde{W}_{i}=w$). We then \textendash see the outer two integrals in equation (ref) \textendash average over the status quo distribution of $X_{i},\bar{X}_{p\left(i\right)}$, which is left unchanged. This yields average student achievement under the new assignment of teachers to classrooms.
In addition to the feasibility condition (ref) we need to also rule out allocations that assign different teachers to students in the same classrooms. Note that $m^{\mathrm{amf}}\left(x,\bar{x},w\right)$ is the average outcome for the subpopulation of students of type $X_i=x$ with peers $\bar{X}_{p(i)}=\bar{x}$. For example, in Table (ref) classroom 001 has students from two subpopulations so defined. Assignment of teachers to subpopulations of students opens up the possibility that a classroom is assigned to teachers of different types for its constituent subgroups of students. If, as indicated in Table (ref), the teacher-type assignment probability is the same for all subpopulations of students represented in a classroom, then the ARE in equation (ref) coincides with one based on direct assignment of teachers to classrooms. This implicit restriction on teacher assignments provides a link between models for individual outcomes and classroom-level reallocations.
In the MET experiment as implemented not all teachers and students appear in their assigned classrooms. This occurs both due to attrition (e.g., when a student changes schools prior to follow-up) as well as actual non-compliance (e.g., when a teacher teaches in a classroom different from their randomly assigned one).
In this section we describe our approach to identifying AREs in MET as implemented. Relative to the idealized analysis of the previous subsection we impose two types of additional restrictions. First, we work with a semiparametric, as opposed to a nonparametric, educational production function. Second, we make behavorial assumptions regarding the nature of non-compliance. Both sets of assumptions are (partially) testable.
Our first set of restrictions involve the form of the educational production function. A key restriction we impose is that unobserved student, peer, and teacher attributes enter separably. Although this assumption features in the majority of economics of education empirical work Chetty_et_al_AER2014a,Chetty_et_al_AER2014b, it is restrictive. We also discretize the observed student and teacher attribute. This allows us to work with a parsimonously parameterized educational production function that nevertheless accommodates complex patterns of complementarity between student and teacher attributes. Discretization also allows us to apply linear programming methods to study counterfactual assigments Graham_Imbens_Ridder_USC2007, Bhattacharya_JASA2009.
Specifically we let $X_{i}$ be a vector of indicators for each of $K$ “types" of students. Types correspond to intervals of baseline test scores. Our preferred specification works with $K=3$ types of students: those with low, medium, and high baseline test scores.\footnote{Precise variable definitions are given below.} In this case $X_{i}$ is a $2 \times 1$ vector of dummies for whether student $i$'s baseline test score was in the medium or high range (with the low range being the omitted group). This definition of $X_{i}$ means that $\bar{X}_{p(i)}$ equals the $2 \times 1$ vector of fractions of peers in the medium and high baseline categories (with the fraction low range omitted).
We discretize the distribution of the teacher attribute similarly: $W_{i}$ is a vector of indicators for $L$ different ranges of FFT scores. In our preferred specification we also work with $L=3$ types of teachers: those with low, medium, and high FFT scores. Hence $W_{i}$ is again a $2 \times 1$ vector of dummies for whether the teacher of student $i$'s FFT score was in the medium or high range (with the low range again being the omitted group).
We assess the sensitivity of our results to coarser and finer discretizations of the baseline test score and FFT distributions. Specifically we look at $K=L=2$ and $K=L=4$ dicretizations.
We posit that end-of-school year achievement for student $i$ is generated according to
Observe that \textendash as noted above \textendash own, $V_i$, peer, $\bar{V}_{p(i)}$, and teacher, $U_{i}$, unobservables enter equation (ref) additively. The labelled grouping of terms in equation (ref) highlights the flexibility of our model relative to those typically employed by researchers. As in traditional models, observed and unobserved student and teacher attributes are posited to directly influence achievement. We add to this standard set-up the possibility of complementarity between own and peer attributes, and complementarity between own and teacher attributes. Additionally our model allows for both observed and unobserved peer attributes to influence achievement.
Conditional on working with a discrete student and teacher type space, equation (ref) is unrestrictive in how own and teacher attributes interact to generate achievement. In contrast, equation (ref) restricts the effect of peers' observed composition on the outcome. Partition $\zeta=\left(\zeta_{1},\dots,\zeta_{K-1}\right)$ and similarly partition $\lambda=\left(\lambda_{1},\dots,\lambda_{L-1}\right)$. The $(K-1)\times1$ gradient of student $i$'s outcome with respect to peer composition is
which is constant in $\bar{X}_{p\left(i\right)}$, although varying heterogenously with student and teacher type. Put differently convexity/concavity in $\bar{X}_{p\left(i\right)}$ is ruled out by equation (ref). It should be noted that the MET data, in which the assignment of peers is not random, are not suitable for estimating peer effects (non-linear or otherwise).
For completeness we also include the interaction of teacher type with peer composition \textendash the $\left(W_{i}\otimes\bar{X}_{p\left(i\right)}\right)$ regressor in equation (ref) \textendash although $\lambda$ is poorly identified in practice.\footnote{Admittedly, the $\left(W_{i}\otimes\bar{X}_{p\left(i\right)}\right)$ term is not entirely straightforward to interpret; however it seemed ad hoc to include some second-order interactions while a priori excluding others. We also report specifications which exclude this term below (as its coefficient is always insignificantly different from zero).} Due to our limited sample size, we do not include the third order interactions of own, peer, and teacher types.\footnote{The educational production function in equation (ref) includes $J=\mathrm{dim}(\alpha)+\mathrm{dim}(\beta)+\mathrm{dim}(\gamma)+\mathrm{dim}(\delta)+\mathrm{dim}(\zeta)+\mathrm{dim}(\eta)+\mathrm{dim}(\lambda)=1+2+2+2+4+4+4=19$ parameters. A fully interacted model would introduce $8$ additional parameters, for $3 \times 3 \times 3 = 27$ in total. Even this model would not be fully flexible since, although constructed from averages of binary indicators, $\bar{X}_{p(i)}$ is not binary-valued. A more flexible model would therefore also include, for example, interactions of $X_i$ with the squares of the elements of $\bar{X}_{p(i)}$ (and so on.)}
Relative to a standard “linear-in-means" type model typically fitted to datasets like ours HanushekKainRivkin2004:
equation (ref) is rather flexible. It allows for rich interactions in observed own, peer, and teacher attributes and is explicit in that both observed and unobserved peer attributes may influence own achievement. The “linear-in-means" model (ref) presumes homogenous effects and does not explicitly incorporate unobserved peer attributes.\footnote{Manski_ReStud93 did allow for unobserved peer attributes as did Graham_EM08; but these cases are exceptional.}
As mentioned above, a student's assigned teacher and peers may deviate from her realized ones due to attrition and non-compliance. To coherently discuss our assumptions about these issues we require some additional notation. Let $W_{i}^{*}$ and $\bar{X}_{p^*\left(i\right)}$ denote student $i's$ assigned teacher and peer attribute (here $p^{*}\left(i\right)$ is the index set of $i's$ assigned classmates). Random assignment of teachers to classrooms ensures that a student's assigned teacher's attributes are independent of her own unobservables:
Here $g_{1}(x,\bar{x})$ is unrestricted. Under double randomization, with students additionally grouped into classes at random, we would have the further restriction \[ \mathbb{E}\left[\left.V_{i}\right|X_{i},\bar{X}_{p^{*}\left(i\right)}\right]=\mathbb{E}\left[\left.V_{i}\right|X_{i}\right]. \] However, since the MET experiment placed no restrictions on how students were grouped into classrooms, we cannot rule out the possibility that a student's peer characteristics, $\bar{X}_{p^{*}\left(i\right)}$, predict her own unobserved ability, $V_i$. Consequently our data are necessarily silent about the presence and nature of any peer group effects in learning. This limitation does not limit our ability to study the effects of teacher reallocations, because we leave the student composition of classrooms \textendash and hence the “peer effect" \textendash fixed in our counterfactual experiments.
Finally, even with double randomization, we would still have $\mathbb{E}\left[\left.V_{i}\right|X_{i}\right]\neq 0$. Observed and unobserved attributes may naturally covary in any population (e.g., for example, average hours of sleep, which is latent in our setting, plausibly covaries with baseline achievement and also influences the outcome). Such covariance is only a problem if, as is true in the traditional program evaluation setting, the policies of interest induce changes in the marginal distribution of $X_i$ \textendash and hence the joint distribution of $X_i$ and $V_i$.\footnote{A prototypical example is a policy which increases years of completed schooling. Such a policy necessarily changes the joint distribution of schooling and unobserved labor market ability relative to its status quo distribution.} This is not the case here: any reallocations leave the joint distribution of $X_{i}$ and $V_{i}$ unchanged.
The MET protocol also ensures that assigned peer unobservables, $\bar{V}_{p^*(i)}$, are independent of the observed attributes of one's assigned teacher:
with $g_{2}\left(X_{i},\bar{X}_{p^{*}\left(i\right)}\right)$, like $g_{1}\left(X_{i},\bar{X}_{p^{*}\left(i\right)}\right)$, unrestricted.
Random assignment of teachers to classrooms also ensures independence of the unobserved attribute of a student's assigned teacher and observed student and peer characteristics:
The second equality is just a normalization.\footnote{Reallocations leave the joint distribution of $U_{i}$ and $W_{i}$ unchanged, so we are free to normalize this mean to zero.}
Under MET as designed we could identify AREs using equations (ref), (ref), and (ref). To see this let, as would be true under perfect compliance, $W_{i}=W_{i}^{*}$ and $\bar{X}_{p\left(i\right)}=\bar{X}_{p^{*}\left(i\right)}$ for all $i=1,\dots,N$. Using equations (ref), (ref), and (ref) yields, after some manipulation, the partially linear regression model Robinson_EM88:
with $\mathbb{E}\left[\left.A_{i}\right|X_{i},\bar{X}_{p\left(i\right)},W_{i}\right]=0$ for
and where the nonparametric regression component equals
Note, even under this perfect experiment, we cannot identify $\beta$, $\gamma$, and $\zeta$; these terms are confounded by $g_{1}\left(X_{i},\bar{X}_{p\left(i\right)}\right)$ and $g_{2}\left(X_{i},\bar{X}_{p\left(i\right)}\right)$ and hence absorbed into the nonparametric component of the regression model. This lack of identification reflects the inherent inability of the MET experiment to tell us anything about peer group effects. Nevertheless, as detailed below, knowledge of $\delta$, $\eta$, and $\lambda$ is sufficient to identify the class of reallocation effects we focus upon.
Unfortunately, we do not observe student outcomes under full compliance. Non-compliance may induce correlation between $A_i$ and $X_i$, $\bar{X}_{p\left(i\right)}$ and $W_i$ in regression model (ref). Our solution to this problem is to construct instrumental variables for observed teacher and peer attributes, $W_i$ and $\bar{X}_{p\left(i\right)}$ \textendash which necessarily reflect any non-compliance and attrition on the part of teachers and students \textendash from the assigned values, $W^{*}_{i}$ and $\bar{X}_{p^{*}\left(i\right)}$.
Rigorously justifying this approach requires imposing restrictions on how, for example, realized and assigned teacher quality relate to one another. The first assumption we make along these lines is:
Assumption (ref) implies that the difference between realized and assigned (unobserved) teacher “quality” cannot be predicted by own and assigned peer and teacher observables. While Assumption (ref) is not directly testable, we can perform the following plausibility test. Let $R_{i}-R_{i}^{*}$ be the difference between the realized and assigned value of some observed teacher attribute other than $W_i$ (e.g., years of teaching experience). Under equation (ref), if we compute the OLS fit of this difference onto $1$, $X_{i}$, $W_{i}^{*}$, and $\bar{X}_{p^{*}\left(i\right)}$, a test for the joint significance of the non-constant regressors should accept the null of no effect. Finding that, for example, students assigned to classrooms with low average peer prior-year achievement, tend to move into classrooms with more experienced teachers suggests that Assumption (ref) may be implausible.
Assumption (ref) and equation (ref) above yield the mean independence restriction
This equation imposes restrictions on the unobserved attribute of student $i$'s realized teacher. It is this latent variable which drives the student outcome actually observed.
Our second assumption involves the relationship between the unobserved attributes of a student's assigned peers and those of her realized peers. These two variables will differ if some students switch out of their assigned classrooms.
Assumption (ref) implies that the difference between realized and assigned unobserved peer “quality” cannot be predicted by assigned teacher observables. We do allow for these deviations to covary with a student's type and the assigned composition of her peers. Assumption (ref) and equation (ref) yield a second mean independence restriction of
where $g^{*}_{2}\left(X_{i},\bar{X}_{p^{*}\left(i\right)}\right) \stackrel{def}{\equiv} \mathbb{E}\left[\left.\bar{V}_{p(i)}-\bar{V}_{p^{*}(i)}\right|X_{i},\bar{X}_{p^{*}\left(i\right)}\right] + g_{2}\left(X_{i},\bar{X}_{p^{*}\left(i\right)}\right)$ is unrestricted. We can also pseudo-test Assumption (ref) using observed peer attributes. Finding, for example, that \textendash conditional on own type, $X_i$, and assigned peers' average type, $\bar{X}^{*}_{p(i)}$ \textendash assigned teacher quality, $W^{*}_{i}$, predicts differences between the realized and assigned values of other observed peer attributes provides evidence against Assumption (ref).
The experiment-generated restrictions \textendash equations (ref), (ref), and (ref) above \textendash in conjunction with our two (informally testable) assumptions about deviations from the experiment protocol \textendash Assumptions (ref) and (ref) above \textendash together imply the following conditional moment restriction:
We wish to emphasize two features of restriction (ref). First, the conditioning variables are assigned peer and teacher attributes, not their realized counterparts. This reflects our strategy of using assignment constructs as instruments. Second, any function of $W^{*}_{i}$, as well as interactions of such functions with functions of $X_i$ and $\bar{X}_{p^{*}\left(i\right)}$ do not predict the composite error $U_{i}+V_{i}+\rho\bar{V}_{p\left(i\right)}$ conditional on $X_i$ and $\bar{X}_{p^{*}\left(i\right)}$; hence such terms are valid instrumental variables.
More specifically we redefine $h$ to equal
and $A_{i}$ to equal
Equations (ref), (ref), and (ref) yield an outcome equation of
Condition (ref) implies that $A_i$ is conditionally mean zero given $X_i$, $\bar{X}_{p^{*}\left(i\right)}$ and $W^{*}_{i}$.
Summarizing, the experimentally-induced restrictions (ref), (ref), and (ref), and our Assumptions (ref) and (ref) together imply that:
The estimation simplifies if we impose a restriction on the peer attrition/non-compliance that is similar to Assumption (ref), but is on the observable peer average:
This restriction is directly testable. By equation (ref), \[ \mathbb{E}\left[\left.\bar{X}_{p(i)}\right|X_{i},\bar{X}_{p^{*}\left(i\right)},W_{i}^{*}\right]=\mathbb{E}\left[\left.\bar{X}_{p(i)}\right|X_{i},\bar{X}_{p^{*}\left(i\right)}\right]. \] If this restriction holds the outcome equation is as in (ref), but with a redefined nonparametric $h$ that is a function of $X_{i}$ and $\bar{X}_{p^{*}\left(i\right)}$ only,
and $A_{i}$ is
The conditional moment restriction in equation (ref) also holds for this error.
Equations (ref) and (ref) jointly define a partially linear model with an endogenous parametric component. This is a well-studied semiparametric model (see, for example, Chen_et_al_EM2003). The parameters $\delta$, $\eta$, and $\lambda$ are identified; $h\left(X_{i},\bar{X}_{p^{*}\left(i\right)}\right)$ is a nonparametric nuisance function.
We implement the partial linear IV estimator using the following approximation for $h(x,\bar{x})$: \[ h\left(X_{i},\bar{X}_{p^{*}\left(i\right)}\right)\approx X_{i}'b+\bar{X}_{p^{*}\left(i\right)}'d+\left(X_{i}\otimes\bar{X}_{p^{*}\left(i\right)}\right)'f. \] For this approximation we estimate $\delta$, $\eta$, and $\lambda$ by linear IV fit of $Y_{i}$ onto a constant, $X_{i}$, $\bar{X}_{p^{*}\left(i\right)},$ $\left(X_{i}\otimes\bar{X}_{p^{*}\left(i\right)}\right)$, $W_{i}$, $\left(X_{i}\otimes W_{i}\right)$, and $\left(W_{i}\otimes\bar{X}_{p\left(i\right)}\right)$ using the excluded instruments $W_{i}^{*},\left(X_{i}\otimes W_{i}^{*}\right)$, and $\left(W_{i}^{*}\otimes\bar{X}_{p^{*}\left(i\right)}\right)$. Note that both assigned and realized peer groups enter the main equation.
As in the case with perfect compliance, we do not identify $\beta$, $\gamma$, and $\zeta$, again reflecting the inherent inability of the MET experiment to tell us anything about peer group effects. Nevertheless knowledge of $\delta$, $\eta$, and $\lambda$ is sufficient to identify the class of reallocation effects we focus upon.
The MET study was conducted during the 2009/10 and 2010/11 school years in elementary, middle, and high schools located in six large urban school districts in the United States.\footnote{The school districts are: Charlotte-Mecklenburg (North Carolina), Dallas Independent School District (Texas), Denver Public Schools (Colorado), Hillsborough County Public Schools (Florida), Memphis City Schools (Tennessee), and the New York City Department of Education (New York). The participation of school districts and schools in the MET study was voluntary.} The goal of the study was to examine determinants and consequences of teacher quality and teaching practices. In the first year of the study, the MET researchers collected detailed background information on teaching practices for each teacher as well as background performance measures for each student. In the second year of the study, MET researchers conducted a field experiment, randomly assigning teachers to classrooms within school-by-grade-by-subject cells (“randomization blocks”). The randomization blocks typically consisted of two to three classrooms each. Classroom composition was not manipulated as part of the study. For more details about the study design, see WhiteRowan2018 and Kaneetal2013.
The dataset contains detailed information on the students, their classroom teachers, and their classroom peers. As our key measure of teaching practices, we use Danielson's Danielson2011 “Framework for Teaching” (FFT) measure, collected at baseline (school year 2009/10). The FFT is designed to provide feedback to teachers, but has also been used to study the impact of teaching practices on student outcomes (c.f., GarrettSteinberg2015,Aucejo2019). The FFT is an observational measure: teachers are video-taped several times during a school year and subsequently rated \textendash using a specially designed rubric \textendash by trained raters (often former teachers).
For our main outcome measure we use students' 2010/11 end-of-year standardized state test scores in the subjects mathematics and English language arts (ELA). The dataset also includes background characteristics from school district records for students (age, gender, race/ethnicity, special-education status, free/reduced-price lunch eligibility, gifted status, and whether a student is an English language learner) and for teachers (education, teaching experience in the district). Through a section identifier, we can match a student to her classroom peers.
In constructing our estimation sample, we closely follow GarrettSteinberg2015, who investigate the impact of FFT on students' test score outcomes in the MET study. We restrict our sample to all elementary- and middle-school students (grades 4--8) who took part in the randomization. Furthermore, we only include students with non-missing information on baseline and final test score outcomes as well as students with non-missing information on the characteristics of the assigned and realized teacher, and the characteristics of the assigned and realized classroom peers. Details of the data construction from the MET data files are provided in Appendix {(ref)}.
Our final sample consists of about 8,500 students and 614 teachers in math and of about 9,600 students and 649 teachers in ELA.\footnote{Appendix Table (ref) summarizes all student and teacher variables.} The majority of the students (60 percent) are elementary school students (grades 4--5), and the remaining students are middle school students (grades 6--8). Nearly 60 percent of the students are economically disadvantaged, that is, eligible for free/reduced-price lunch.\footnote{This variable is missing for 30 percent of the students in the math sample and for 25 percent of students in the ELA sample.} The student sample is diverse, with equal proportions of white, black, and Hispanic students.
Student test scores are centered at the relevant district-level mean and standardized by the relevant district-level standard deviation. MET students exceed their district average test score by about 0.15 standard deviations on average. The majority of the teachers are female (about 85 percent), and about two-thirds of them are white. Most of the teachers have substantial teaching experience \textendash seven years on average \textendash and about 40 percent of the teachers have graduated from a Master's program.\footnote{Teaching experience and teacher education are missing for about 30 percent of teachers.}
The MET data includes ratings of teaching practices for two domains of the FFT, “Classroom Environment” and “Instruction.” These domains are divided into four components each,\footnote{The components of the domain “Classroom Environment” are: creating an environment of respect and rapport; establishing a culture for learning; managing classroom procedures; managing student behavior. The components of the domain “Instruction” are: communicating with students; using questioning and discussion techniques; engaging students in learning; using assessment in instruction.} and each component is rated on a four-point scale by each rater (unsatisfactory, basic, proficient, distinguished), with high scores in a category indicating that a teacher is closer to an ideal teaching practice according to the FFT. The teachers are video-taped at least twice during the school year during lessons, and each video is rated independently by at least two raters. In our analysis, we average the scores across all videos, raters, components, and domains. This aggregation of the scores is the most common one in the literature (cf., GarrettSteinberg2015,Aucejo2019).
The FFT is on average 2.5 in math and 2.6 in ELA, which corresponds to a rating between “basic” and “proficient”; for the purpose of our analysis, we create three categories of FFT (see Appendix Figure (ref)). We set the cutoffs at FFTs of 2.25 and 2.75. In our sample, low-FFT teachers have “basic” teaching practices on average (average FFT of 2.1 in both math and ELA), and high-FFT teachers have “proficient” teaching practices on average (average FFT of 2.9 in both math and ELA); 18 percent of the teachers in math and 14 percent of the teachers in ELA are classified as having a low FFT, 62 percent of the teachers in math and 58 percent of the teachers in ELA are classified as having a middle FFT, and 20 percent of the teachers in math and 28 percent of the teachers in ELA are classified as having a high FFT. Our results are not sensitive to the exact position of the cutoffs, and we investigate a model with two or four, instead of three, FFT categories in our sensitivity checks below. This categorization also creates variation in FFT levels within randomization blocks: in our sample, 65 percent of randomization blocks in math, and 70 percent of randomization blocks in ELA include teachers with different levels of FFT (for example, both a low- and a middle-FFT teacher).
The end-of-year test scores provided in the MET data are $z$-scores, i.e., they are standardized such that district-wide, they will be mean zero with unit standard deviation. Since MET schools are not representative at the district level, the mean test scores may \textendash and do \textendash deviate from zero. We use the 2010/11 $z$-score as our outcome variable.
To identify reallocation effects, we split 2009/10 baseline test scores into three bins, corresponding to terciles of the within-district $z$-score distribution. In our estimation sample, 27 percent of the students in math, and 26 percent in ELA, have “low” baseline test scores, 36 percent of the students in math, and 35 percent of the students in ELA, have “middle” baseline test scores, and 36 percent of the students in math, and 39 percent of the students in ELA, have “high” baseline test scores.\footnote{These numbers are not exactly 33 percent in each category, because the students in our sample have on average higher baseline test scores than the full student population in a district.} To include classroom peers into the analysis, we compute the fraction of each student's classmates with high, middle, and low baseline test scores (leave-own-out means).
As outlined in Section (ref), some teachers and students switched classrooms or schools before the start of the school year, which we take into account in our identification strategy. In our sample, 69 percent of the students in math, and 73 percent of the students in ELA, are actually taught by their randomly assigned teachers. This level of non-compliance is high enough to make analyses which ignore it potentially problematic.
We also observe changes in classroom peers after the randomization but before the beginning of the school year. Changes in assigned peers were driven by students who leave schools, repeat a grade or, in some cases, by the need to adjust their schedule. On average, students' realized peers, however, are not appreciably different from their assigned ones. The difference in baseline $z$-scores between the assigned and the realized peers amounts to just 0.02 standard deviations on average both in math and in ELA.
In this section, we report the results of the series of specification tests discussed earlier; specifically tests designed to assess the plausibility of Assumptions (ref) and (ref). These two assumptions impose restrictions on the nature of non-compliance by students and teachers. We further directly test restriction (ref), which is a restriction on the nature of non-compliance by peers. We also assess the quality of the initial MET randomization of teachers to classrooms.
To test whether the randomization was successful in balancing student characteristics across teachers with different levels of FFT we regress the FFT of a student's assigned teacher on the student's own characteristics, controlling for randomization block fixed effects. None of the student characteristics predict assigned teacher's FFT, individually or jointly, which confirms that the randomization indeed “worked” (see Appendix Table (ref)).
Covariate balance, however, is not a sufficient condition to identify reallocation effects under non-compliance by both students and teachers (see Section (ref)). Assumption (ref) requires that own and assigned peer and teacher observables should not predict the difference between realized and assigned unobserved teacher quality. Since this assumption involves a statement about unobserved variables, we cannot test it directly. Instead we “test" it indirectly as described in Section (ref). Specifically we use those teacher background characteristics that are not part of the the model as replacements for the unobserved quality of a teacher: a teacher's demographics, experience, and education. We regress the difference between realized and assigned teacher characteristics on the student's baseline test score, the FFT of the assigned teacher, and the average baseline test score of the assigned peers. Consistent with Assumption (ref), these variables do not jointly predict differences between the characteristics of the assigned and realized teacher in any of the regression fits (see Appendix Table (ref)).
Assumption (ref) states that differences between realized and assigned unobserved peer quality cannot be predicted by assigned teacher observables, conditional on own baseline achievement and the baseline achievement of assigned peers. Again, we can only perform an indirect test of this assumption. To do so we regress differences between the assigned and realized characteristics of classroom peers onto the FFT of the assigned teacher, controlling for own baseline test scores and assigned peers' average baseline test scores. We do not find, consistent with Assumption (ref), that teacher FFT predicts differences between the characteristics of the assigned and realized peers (see Appendix Tables (ref) and (ref)).
Finally, we directly assess restriction (ref), which implies that the baseline test scores of realized peers cannot be predicted by assigned teacher FFT. We test this restriction by regressing the baseline test scores of realized peers onto a student's baseline test score, the baseline test scores of her assigned peers, as well as the FFT of her assigned teacher. We find that this restriction also holds in our data (see Appendix Table (ref)).
To construct estimates of the average effect of reassigning teachers across classrooms we proceed in three steps. First, as outlined in Section (ref), we estimate (a subset of) the parameters of the educational production function. Second, we feed these parameters into a linear programming problem to compute an optimal assignment (i.e., an assignment that maximizes aggregate achievement). Third, we compare the aggregate outcome under the optimal assignment to the aggregate outcome under the status quo assignment, as well as to that under the worst assignment (i.e., the one which minimizes aggregate achievement). These comparisons provide a sense of the magnitude of achievement gains available from improved teacher assignment policies.
The specification that we use to estimate the parameters of the educational production function coincides with equation (ref). Since randomization was carried out within randomization blocks, we additionally include randomization block fixed effects in this regression model. We then estimate the model's parameters by the method of instrumental variables (IV) as described in Section (ref). Tests for instrument relevance following Sanderson2016 confirm that our IV estimates are unlikely to suffer from weak-instrument bias (see Appendix Table (ref)).
The aim of the analysis is to find an assignment of teachers to classrooms that improves student outcomes. What is meant by an “optimal" assignment depends, of course, on the objective function.
In this paper we choose to maximize aggregate outcomes (i.e., the sum of all students' test scores). This is the “simplest” objective we can consider, it is straightforward to compute, justifiable from a utilitarian perspective, and easy to interpret. We would like to emphasize, however, that our analysis can be modified to accommodate other objective functions \textendash in some cases easily, in others with more difficulty. In practice, for example, the social planner may care about both the aggregate outcome as well as inequality, especially across identifiable subgroups.
Our intention is not to advocate for maximization of the aggregate outcome in practice, although doing so is appropriate in some circumstances; rather this objective provides a convenient starting point and makes our analysis comparable to that of other educational policy evaluations (e.g., the typical regression-based class-size analysis provides an estimate of the effect of class-size on average achievement).
To determine the optimal allocation, we feed the estimated parameters from equation ((ref)), specifically $\hat{\delta}$, $\hat{\eta}$, and $\hat{\lambda}$, into a linear program. Given these parameters, we can compute, for each student, her predicted outcome when taught by a low-, middle-, or high-FFT teacher, leaving the original classroom composition unchanged.
Formally, for each student $i$, we compute three counterfactual outcomes $\widehat{Y}_{i}(w)$, $w \in \{w_L, w_M, w_H\}$, corresponding to an assignment to a low-, middle- or high-FFT teacher. Aggregated to the classroom level this yields, in an abuse of notation, three counterfactual classroom-level test score aggregates, $\widehat{{Y}}_{c}(w)=\sum_{i\in s\left(c\right)}\widehat{Y}_{i}(w)$, with $w \in \{w_L, w_M, w_H\}$ (here $s\left(c\right)$ denotes the set of indices for students in classroom $c$).
By aggregating the counterfactual outcomes to the classroom level, we transform the assignment problem from a many-to-one matching problem to a one-to-one matching problem. This approach is only suitable because the configuration of students across classrooms remains fixed; we only consider the effects of reassigning teachers across existing classrooms of students.\footnote{As noted earlier the effects of classroom composition changes on student achievement are unidentifiable here in any case.} The one-to-one matching problem is a special linear program, a transportation problem, which is easily solvable.\footnote{Appendix (ref) contains the details on how we specify the transportation problem. To compute the optimal assignment, we use the function \tt{lpSolve} in $R$.}
There are a few additional constraints we impose to make the reallocation exercise realistic. First, we do not allow teachers to be reassigned across districts or across school types (i.e., elementary or middle school). We also present, as a sensitivity check, a version of the allocation where we only allow teachers to be reassigned within their randomization block. Second, there are a few teachers that teach several sections of a class. In this case, we treat these sections as clusters, and allocate one teacher to all sections in each such cluster.
When computing counterfactual outcomes for each student, we omit the nonparametric component, $h(x,\bar{x})$, as well as the randomization block fixed effects and the main effects of own baseline achievement. This is appropriate because we report the difference between the sum of aggregate outcomes for two allocations where the nonparametric component, the fixed effects, and the main effects of own baseline achievement cancel out.
In addition to the optimal assignment, we also compute a “worst” possible assignment, i.e., the assignment that minimizes aggregate test scores. The difference between the aggregate outcome for the best and worst assignment is the maximal reallocation gain. This provides an upper bound on the magnitude of student achievement gains that teacher reassignments might yield in practice.
An individual reallocation effect, or reallocation gain, is defined as the difference between an individual student's outcome under two assignments. For example, one can compute, for each student, $\widehat{Y}_{i}(\tilde{W}_{i}^{opt})$, i.e., the predicted outcome under the optimal allocation, where $\tilde{W}_{i}^{opt}$ takes the values $w_L$, $w_M$, or $w_H$, depending on whether the student would be assigned to a low-, middle-, or high-FFT teacher in an optimal allocation. Similarly, one can compute the same parameter for each student under the status quo, which we denote as $\widehat{Y}_{i}(W_{i})$. In MET schools the status quo assignment was induced by random assignment of teachers to classrooms within randomization blocks. The allocation of teachers across schools within a given district was, of course, non-random, and possibly non-optimal from the standpoint of maximizing the aggregate outcome. An individual reallocation gain can then be computed as the difference between these two outcomes, $\widehat{Y}_{i}(\tilde{W}_{i}^{opt})-\widehat{Y}_{i}(W_{i})$. The optimal assignment is not the assignment that maximizes the predicted outcome for student $i$, but the assignment that maximizes the aggregate outcome across all the classrooms in the sample (subject to the various constraints we impose on the problem \textendash like ruling out reassignments across school districts).
These individual gains can be aggregated in many ways in order to create policy-relevant parameters. We start by defining our key parameter of interest, the average reallocation effect, as
We also consider conditional average reallocation effects, that is, average reallocation effects for students with varying baseline characteristic $x$ (e.g., students with low, middle, and high baseline test scores):
Below we show that only about one-half of MET students would experience a teacher change when switching from the status quo teacher assignment to an optimal one. The reallocation effect for students in classrooms not assigned a different teacher is, of course, zero. This motivates a focus on the average achievement gain among those students who are assigned a different teacher. We define the reallocation effect conditional on being reassigned as:
We can, of course, not condition on $x$ as well.
Finally, the maximal reallocation gain is obtained if we compare the average outcome under an optimal assignment with that under a worst assignment
where $\widehat{Y}_{i}(\tilde{W}_{i}^{worst})$ is the predicted outcome for student $i$ under an allocation that minimizes aggregate test scores.
We use the Bayesian bootstrap to quantify our (posterior) uncertainty about AREs. We treat each teacher-classroom pair as an i.i.d. draw from some unknown (population) distribution. Following Chamberlain_Imbens_JBES03, we approximate this unknown population by a multinomial, to which we assign an improper Dirichlet prior. This leads to a posterior distribution which (i) is also Dirichlet and (ii) conveniently only places probability mass on data points observed in our sample.
Mechanically, we draw $C$ standard exponential random variables and weigh each student in section/classroom $c=1, \dots, C$ with the $c^{th}$ weight (i.e., all students in the same section have the same weight). Using this weighted sample, we compute the IV regression fit, solve for the optimal (worst) assignment, and compute the various reallocation effects. We repeat this procedure 1,000 times. This generates 1,000 independent draws from the posterior distribution of the ARE.
Formally this approach to inference is Bayesian. Consequently the “standard errors" we present for our ARE estimates summarize dispersion in the relevant posterior distribution (not variability across repeated samples).\footnote{The “standard errors" for the AREs are constructed as follows. Let $\hat{\theta}^{(b)}$ be the estimate of the reallocation effect in $b^{th}$ the bootstrap sample (or equivalently the $b^{th}$ draw from the posterior distribution for $\theta$) and $\hat{\theta}$ the reallocation effect in the original sample. Consider the centered statistic $\hat{\theta}^{(b)} - \hat{\theta}$; let $q(0.025)$ and $q(0.975)$ be the 0.025 and 0.975 quantiles of its bootstrap/posterior distribution. We then construct the interval $[\hat{\theta} - q(0.975), \hat{\theta} - q(0.025)]$ (see Hansen:2018). We compute the corresponding standard error by dividing this interval by $2\Phi^{-1}(0.975) \approx 3.92$, where $\Phi(.)$ is the standard normal CDF.} An alternative, frequentist, approach to inference is provided by Hsieh2018. They transform the problem of inference on the solution to a linear program into inference on a set of linear moment inequalities. If the binding constraints are the same over the bootstrap distribution, then inference based on the Bayesian bootstrap will be similar to that based on moment inequalities (see also Graham_Imbens_Ridder_USC2007 and Bhattacharya_JASA2009).
Before reporting parameter estimates for our preferred model \textendash equation (ref) above with three categories of FFT, own and peer baseline achievement each \textendash we present those for a more conventional model with teacher FFT, student and peer average baseline test scores all entering linearly. For this specification we leave the FFT and baseline test scores undiscretized. These initial results replicate and expand upon the prior work of GarrettSteinberg2015, who study the impact of FFT on student achievement in (approximately) the same sample.\footnote{Aucejo2019 study the impact of FFT in the MET data, but focus on math classrooms in elementary schools.}
These initial results indicate that teacher FFT does not affect students' test scores on average (see Table (ref), Panel A). This is consistent with the findings of GarrettSteinberg2015. Table (ref) presents estimates, using the instrumental variables described in Section (ref). Here this involves using the FFT score of a student's randomly assigned teacher as an instrument for that of her realized teacher (Panels A--C), and the average baseline test score of her assigned peers as an instrument for the average baseline test score of her realized peers (Panel B).
OLS estimates of the same model are reported in Appendix Table (ref). The coefficient on FFT is statistically significant and positive in the OLS results. The discrepancy between the OLS and IV results may reflect the impact of correcting for non-compliance, as described above, or simply reflect the greater sampling variability of the IV estimates.
Next we add the interactions of teacher FFT with both the baseline student, and peer average, test scores. This provides an initial indication of whether any complementarity between teacher FFT and student baseline achievement is present. These results suggest that high-FFT teachers are more effective at teaching students with higher baseline scores (see Table (ref), Panels B and C). This result is significant at the 5-percent level in the math sample, but only weakly significant in the ELA sample. The magnitudes and precision of the teacher-student match effects are similar across the IV and OLS estimates (the latter reported in Appendix Table (ref)). The coefficient on the interaction between teacher FFT and peer average baseline achievement (Panel B) is poorly determined (whether estimated by IV or OLS).
In Table (ref) we report IV estimates of our preferred $3 \times 3$ model. This corresponds to equation (ref) with both $W_i$ and $X_i$ consisting of dummy variables for middle and high FFT and baseline test scores respectively. In this specification, the teacher FFT main effects remain insignificant. We do, however, find positive match effects between teacher FFT and student baseline scores. These are significant for the high-FFT teachers (i.e., teachers with a “proficient” score on average). Students with middle or high baseline test score levels score significantly higher on end-of-year achievement tests when matched with a high-FFT teacher, compared to students with low baseline test scores (see Table (ref), Panels B and C).\footnote{In contrast, the coefficients on interactions of the teacher FFT dummy variables with the peer composition variables are imprecisely determined.} The OLS estimation results, reported in the appendix, are qualitatively similar to the IV ones; although the interactions of the middle-FFT dummy variable with the middle- and high-baseline student test score dummies are also significant when estimated by OLS (see Appendix Table (ref)).
To compute optimal assignments and average reallocation effects, we use the IV estimates presented in columns 5--6 of Table (ref). These specifications omit the FFT-by-peer composition interaction terms, whose coefficients are poorly determined in all specifications (whether fitted by IV or OLS). Omitting these terms has little effect on either the location or the precision of the coefficients on the FFT-by-baseline interactions. In Appendix Tables (ref) and (ref) we also present average rellocation effects based upon the specifications in columns 3--4 of Table (ref). These ARE estimates are larger, albeit less precisely determined.
If an optimal assignment is similar to the status quo one, then large reallocation effects are unlikely. Therefore, before quantifying any reallocation effects, we first discuss how an optimal assignment and a worst assignment differ from the status quo.
Our primary reassignment policy considers reassignments of teachers across classrooms district-wide (that is, we allow teachers to move to a different school within their district). We do restrict teachers to teach at the same level (e.g., elementary school teachers do not move to middle school classrooms). Under this scenario we find that, when moving from the status quo to an optimal assignment, 49 percent of the students in the math sample, and 47 percent of the students in the ELA sample, are assigned to a new teacher. The balance of students remain with their status quo teacher.
It is interesting to examine how the reallocation changes the “assortativeness” of the assignment. An assignment is characterized as positive assortative if students with higher baseline test scores are more frequently matched with higher-FFT teachers, compared to a random assignment. Indeed, we observe this in our data for the optimal assignment. Figure (ref) displays, for each level of FFT, the distribution of student baseline test scores in the average class a teacher of that FFT level is assigned to. In both the math and in the ELA sample, the optimal allocation is more assortative than the status quo. In the status quo in math, for instance, a high-FFT teacher has on average 23 percent of students with low baseline test scores and 40 percent of students with high baseline test scores. In the optimal allocation, the fraction of students with low baseline test scores drops to 9 percent, and the fraction of students with high baseline test scores increases to 61 percent on average. The optimal allocation in the ELA sample displays a similar pattern. The positive assortativeness arises in the optimal allocation because students with high baseline test scores benefit more from a high-FFT teacher, compared to students with low baseline test scores (see Table (ref)). The worst allocation displays negative assortativeness (see Appendix Figure (ref)).
Tables (ref) and (ref) present ARE estimates. In Panel A an optimal assignment is compared with the status quo; while in Panel B optimal assignments are compared with “worst" assignments. We presents results for all students (Panels A.I and B.I), as well as for just those students who experience a teacher change as part of the reallocation (Panels A.II and B.II).
In the math sample (Table (ref)), the optimal allocation improves average test scores by 1.7 percent of a test score standard deviation compared to the status quo. This effect is precisely determined with a Bayesian bootstrap standard error of 0.6 percent. The reported effects are largely driven by students with high baseline test scores. These students gain 2.8 percent of a test score standard deviation on average; students with middle and low baseline test scores, in contrast, gain only 1.2 and 1.4 percent of a test score standard deviation, respectively (on average).
Since only half of the students experience a change in their teacher, the average effect represents an equal-weighted mixture of a zero effect and a positive effect on those students who do experience a change in teachers. The average effect for the latter group is 3.6 percent of a test score standard deviation (Panel A.II, SE = 1.2 percent).
The comparison of an optimal allocation with a worst allocation yields improvements that are about twice as large. Relative to a worst allocation, an optimal allocation improves test scores by 4.0 percent of a standard deviation on average (SE = 1.2 percent). The gains are 7.2 percent of a standard deviation for students with high baseline test scores, and 1.9 and 3.8 percent of a standard deviation for students with middle and low baseline test scores, respectively. If one considers only those students who are reassigned to a new teacher, the reallocation effect amounts 6.0 percent of a standard deviation on average (Panel B.II, SE = 1.9 percent).
One way to benchmark the magnitude of these AREs is to compare them with the effects of hypothetical policies aimed at improving teacher value-added measures (VAMs). As noted in the introduction, such policies are controversial, as is the evidence marshalled to support them. Here we offer no commentary on the advisability of actually adopting VAM-guided teacher personnel policies; nor do we offer an assessment of VAM studies. Rather we simply use these studies, and the policy thought experiments they motivate, to benchmark our ARE findings.
Teacher value-added is typically conceptualized as an invariant intercept-shifter, which uniformly raises or lowers the achievement of all students in a classroom. In this framework replacing a low value-added teacher with a high one will raise achievement for all students in a classroom. Rockoff_AER04 estimates that the standard deviation of the population distribution of teacher value-added (in a New Jersey school district) is around 0.10 test score standard deviations in both math and reading. Recent studies find somewhat higher estimates: Chetty_et_al_AER2014a estimates that the standard deviation of teacher value-added is 0.16 in math and 0.12 in reading; similarly, Rothstein2017 finds values of 0.19 in math and 0.12 in reading.
Using a standard deviation of 0.15 we can consider the effect of a policy which removes the bottom $\tau \times 100$ percent of teachers, sorted by VAM, and replaces them with teachers at the $\tilde{\tau}^{th}$ quantile of the VAM distribution. Under normality the effect of such a policy on average student achievement is to increase test scores by
standard deviations. Setting $\tau = 0.05$ and $\tilde{\tau} = 0.75$ this expression gives an estimate of the policy effect of 0.021 (i.e., 2.1 percent of a test score standard deviation). This is comparable to the average effect on math achievement associated with moving from the status quo MET assignment to an optimal one. In practice correctly identifying, and removing from classrooms, the bottom five percent of teachers would be difficult to do. Replacing them with teachers in the top quartile of the VAM distribution perhaps even more so. Contextualized in this way the AREs we find are large.
An attractive feature of the policies we consider is that they are based on measurable student and teacher attributes, not noisily measured latent ones. At the same time we are mindful that most school districts would not find it costless to reallocate teachers freely across classrooms and schools.
Another way to calibrate the size of the effects we find is as follows. We find that when implementing an optimal teacher-to-classroom assignment, only about one half of students experience a change in teachers. We find that test scores increase by about 3.6 percent of a standard deviation for these students. This is comparable to increasing the average VAM of these students' teachers from zero (i.e., the median) to the 0.6 quantile of the teacher VAM distribution. Again, increasing the VAM of half of all teachers by such an amount may be difficult to do in practice.\footnote{One may also use effect sizes of educational interventions in general as point of comparison. Based on a meta-study by Kraft2020, an effect size of 4 percent of a standard deviation in math qualifies as a “medium effect,” corresponding to the 40th percentile of effect sizes found across 750 educational interventions in pre-K--12 settings in the US (see Table 1 in Kraft2020).}
For English language arts (ELA) achievement we find smaller reallocation effects. Moving from the status quo to an optimal allocation is estimated to raise achievement by 0.8 percent of a test score standard deviation (SE = 0.6 percent). As with math, these gains are concentrated among students with high baseline scores who are assigned a new teacher. These students experience an average gain of 5 percent of a test score standard deviation (SE = 2.5 percent).
In sum implementing an optimal assignment generates improvements in test score outcomes across the distribution of baseline achievement. Yet, while the gains are large for students with high baseline test scores \textendash up to 10 percent of a standard deviation for students with high baseline test scores in math \textendash for students with middle and low baseline test scores, the gains are smaller. Our results suggest that reallocations matter more in math, compared to ELA. This is in line with the value-added literature, which consistently reports higher value-added in math compared to ELA.
Our results provide strong evidence of complementarity between student baseline test scores and teacher practices. This complementarity, if taken into account when assigning teachers to classrooms, appears to make a difference in students' performance across the distribution of baseline achievement. Teacher reassignments that maximize the average test score, however, will not close the achievement gap between students with low versus high baseline achievement levels. They actually widen this achievement gap. A different objective function, one that values equity as well as “efficiency," may be preferred in practice.
It is also possible that assignments based on other student/teacher attributes might both raise average achievement and narrow achievement gaps. For example, if literacy in a student's native language helps develop literacy in English, then perhaps bilingual teachers could help to raise the achievement levels of English language learners. Many other examples might merit exploration.
Working with a discrete categorization of baseline achievement and teacher FFT provides a simple, but also highly flexible, way of capturing non-linearities in educational production. We tested the sensitivity of our results to alternative categorizations of teachers and students. Specifically, we test (a) a coarser specification with two levels of teacher FFT (cutoff point at 2.5) and two levels of student baseline test scores and (b) a finer specification with four levels of teacher FFT (cutoff points at 2.25, 2.5, and 2.75) and four levels of student baseline test scores.
In the coarser specification, we do not detect any significant match effects between teacher FFT and student baseline test scores (see Appendix Table (ref)): the model with only two levels of teacher FFT does not capture the positive effect of the high-FFT teachers on students with middle or high baseline test scores. By contrast, the results of the finer specification, with four levels of FFT, are very similar to the results of our preferred specification (see Appendix Table (ref)).
We also assess the sensitivity of our results to the measure of teaching practices that we use in the analysis. The MET data also contains an alternative measure, the CLASS (Classroom Assessment Scoring System), for a subset of the sample (6,320 observations in the math sample and 6,999 observations in the ELA sample). The CLASS is a teacher observation protocol that uses different domains and evaluation criteria than the FFT (see Section (ref) in the Data Appendix for details on the observation protocol and on how we process the data). The CLASS is also widely used in research on teacher quality (e.g. Carneiro2016). We find that our results are similar when using the CLASS instead of the FFT (see Appendix Table (ref)).
In our preferred optimization procedure, we optimize the assignment of teachers to classrooms within types of schools (elementary or middle school) and school districts. We choose these restrictions because teachers might not be willing or able to teach in a different school type or a different school district. As a sensitivity check, we also calculated the results of both a more restrictive and a less restrictive optimization procedure.
Our least restrictive allocation optimizes the assignment within school types, but allows for reassignments across districts. The magnitudes of the reallocation effects in this case are only slightly larger than those where reallocations are within districts (see Appendix Tables (ref) and (ref), columns 1--4). This finding may reflect the similarity of the distributions of baseline student achievement and teacher FFT in MET school districts. It would be interesting to repeat our analysis in a metro area consisting of an urban core district and multiple suburban ones. In such a setting is it seems plausible that moving teachers across school districts might raise average achievement.
Our most restrictive allocation reassigns teachers only within school-grade-subject cells (i.e., randomization blocks). This restriction is strong because each randomization block typically contains only two or three sections. Under this restriction, the reallocation gains are overall negligible (see Appendix Tables (ref) and (ref), columns 5--8).
Our main results for the reallocation effects are based on a model without teacher-to-peer match effects (i.e., in a model which imposes the restriction that $\lambda = 0$), since these effects are very noisily estimated using our data. Using a model which does not impose this restriction generates reallocation effects about twice as large. These effects are also more noisily measured (see Appendix Tables (ref) and (ref)).
We provide an econometric framework that allows us to semiparametrically characterize complementarity between teaching practices and student baseline test scores. Our framework exploits the random assignment of teachers to classrooms available in the MET dataset, while formally dealing with non-compliance by both teachers and students.
Our results show that the potential gains associated with an outcome-maximizing assignment of teachers to classrooms are large. They are comparable to fairly large (hypothetical) interventions to raise teacher VAM. An attractive feature is that they are, at least in theory, resource neutral. No new teachers are required to implement the policies we consider.
Our focus on the objective of maximizing the population average test score leads to an optimal assignment that increases the gap between less and more prepared students. We could also consider objective functions that do no focus on average test scores, but instead on test score gaps or proficiency levels. We could, for instance, choose an assignment which maximizes the number of students who reach a “proficient" level on their end-of-year assessment. It is possible that this objective function would suggest a less assortative assignment: students with high baseline scores would likely reach the proficient level regardless of their teacher's FFT, while the incremental effect of having a high-FFT teacher on the probability of attaining proficiency may be larger for students with lower baseline test scores. Outcomes other than math and ELA achievement (e.g., socio-emotional skills) may also be of interest.
We consider this paper as a first pass that establishes the feasibility of recovering match effects from imperfect experimental data and shows that the resulting reallocation effects that depend upon these match effects and the supply of teachers are substantial.