
\section{Study design}\label{s:design}

\subsection{Setting}

The first tier of the study took place during the actual recruitment for civil service teaching jobs in upper primary in six districts of Rwanda in 2016.\footnote{Upper primary refers to grades 4, 5, and 6; schools typically include grades 1 through 6.} To apply for a civil service teaching job, an individual needs to hold a Teacher Training College (TTC) degree. Eligibility is further defined by specialization. Districts solicit applications at the district-by-subject-family level, aggregating curricula subjects into three `families' that correspond to the degree types issued by TTCs: math and science (TMS); modern languages (TML); and social studies (TSS). Districts invite applications between November and December, for the academic year beginning in late January/early February. Individuals keen to teach in a particular district submit one application and are then considered for all eligible teaching posts in that district in that hiring round. 

Given this institutional setting, we can think of district-by-subject-family pairs as \emph{labor markets}. The subject-family boundaries of these labor markets are rigid; within each district, TTC degree holders are considered for jobs in pools alongside others with the same qualification. The district boundaries may be more porous, though three quarters of the new teaching jobs in our study were filled by recruits living within the district at the time of application. Since this is the majority of jobs, we proceed by treating these labor markets as distinct for our primary analysis and provide robustness checks for cross-district applications in Online Appendix C.\footnote{As we note in the appendix, cross-district applications would not lead us to find a selection effect where none existed but we might overstate the magnitude of any selection effect.}

There are 18 such labor markets in our study.\footnote{Inference based on asymptotics could easily be invalid with 18 randomizable markets.  We address this risk by committing to randomization inference for all aspects of statistical testing.}
This is a small number in terms of statistical power (as we address below) but not from a system-scale perspective. The study covers more than 600 hiring lines constituting over 60 percent of the country's planned recruitment in 2016. Importantly, it is not a foregone conclusion that TTC graduates will apply for these civil service teaching jobs. Data from the 2017 Rwanda Labour Force Survey indicate that only 37 percent of recent TTC graduates were in teaching jobs, with 15 percent in non-teaching, salaried employment \citep{nisr17laborsurvey}. This is not because the teacher labor market is tight; nationwide close to a quarter of vacancies created by a teacher leaving a school remain unfilled in the following school year \citep{Zei20turnover}. A more plausible explanation is that the recent graduates in the outside sector earned a premium of close to 30 percent, making occupational choice after TTC a meaningful decision.  

\subsection{Experiment}

\paragraph{Contract structure}
The experiment was built around the comparison of two contracts paying a bonus on top of teacher salaries in each of the 2016 and 2017 school years, and was managed by Innovations for Poverty Action (IPA) in coordination with REB. The first of these was a P4P contract, which paid RWF 100,000  (approximately 15 percent of annual salary) to the top 20 percent of upper-primary teachers within a district, as measured by a composite performance metric.\footnote{The exchange rate on January 1, 2016 was 734 RWF to 1 USD, so the RWF 100,000 bonus was worth roughly 136 USD.} This metric equally weighted student learning alongside three measures of teachers' inputs into the classroom (presence, lesson preparation, and observed pedagogy). The measure of learning was based on a pay-for-percentile scheme that makes student performance at all levels relevant to teacher rewards \citep{BarNea12aer}.\footnote{Student learning contributed to an individual teacher's score via percentiles within student-based brackets so that 
a teacher with a particular mix of low-performing and high-performing students was, in effect, competing with other teachers with similar mixes of students. The data used to construct this measure, and the measures of teachers' inputs, are described in Sections \ref{ss:data_assessments} and \ref{ss:data_inputs} respectively, and we explain the adaptation of the Barlevy-Neal measure of learning outcomes to a repeated cross-section of pupils in Online Appendix D.} The 2016 performance award was conditional on remaining in post during the entire 2016 school year, and was to be paid early in 2017. Likewise, the 2017 performance award was conditional on remaining in post during the entire 2017 school year, and was to be paid early in 2018. The second was a fixed-wage (FW) contract that paid RWF 20,000 to all upper-primary teachers. This bonus was paid at the same time as the performance award in the P4P contract. 

Although P4P contracts based on a composite metric of teacher inputs and student performance have been used in a number of policy settings in the US \citep{Stecheretal, Imb15iza}, such contracts have been relatively less studied in low- and middle-income countries. In their comprehensive review, \citet{GleMur16chapter} discuss several evaluations of teacher incentives based on student test scores or attendance checks, but none based on a combination of both. After extensive discussions with REB about what would be suitable in this policy setting, a decision was made to use the P4P contract described above, based on a composite metric.

\paragraph{Design overview}
The design, summarized visually in Figure A.1 in Online Appendix A,
draws on a two-tiered experiment, as used elsewhere (see \cite{KarZin09ecta}, \cite{AshBerSha10aer}, and \cite{CohDup10qje} in credit-market and public-health contexts). Both tiers employ the contract variation described above.

Potential applicants, not all of whom were observed, were assigned to either advertised FW or advertised P4P contracts, depending on the labor market in which they resided. Those who actually applied, and were placed into schools, fall into one of the four groups summarized in Figure \ref{f:twobytwo}. For example, group $a$ denotes teachers who applied to jobs advertised as FW, and who were placed in schools assigned to FW contracts, while group $c$ denotes teachers who applied to jobs advertised as FW and who were then placed in schools re-randomized to P4P contracts. Under this experimental design, comparisons between groups $a$ and $b$, and between groups $c$ and $d$, allow us to learn about a pure compositional effect of P4P contracts on teacher performance, whereas comparisons along the diagonal of $a$--$d$ are informative about the total effect of such contracts, along
both margins.

\begin{figure}[htbp]
    \begin{center}
      \begin{tabular}{l l c c}
        & & \multicolumn{2}{c}{Advertised} \\
            &  & FW & P4P \\
        \multirow{ 2}{*}{Experienced}& FW & $a$ & $b$ \\
        &  P4P & $c$ & $d$ \\
      \end{tabular}
    \end{center}
\caption{Treatment groups among recruits placed in study schools}\label{f:twobytwo}
\end{figure}

\paragraph{First tier randomization: Advertised contracts}\label{ss:2ndtx}

Our aim in the first tier was to randomize the 18 distinct labor markets to contracts, `treating' all potential applicants in a given market so that we could detect the supply-side response to a particular contract. The result of the randomized assignment is that 7 of these labor markets can be thought of as being in a `P4P only' advertised treatment, 7 in a `FW only' advertised treatment, and 4 in a `Mixed' advertised treatment.\footnote{This randomization was performed in MATLAB by the authors. The Mixed advertised treatment arose due to logistical challenges detailed in the pre-analysis plan: the first-tier randomization was carried out at the level of the subject rather than the subject-family. An example of a district-by-subject-family assigned to the Mixed treatment is Ngoma-TML. An individual living in Ngoma with a TML qualification could have applied for an advertised Ngoma post in English on a FW contract, or an advertised Ngoma post in Kinyarwanda on a P4P contract. In contrast, Kirehe-TML is in the P4P only treatment. So someone in Kirehe with a TML qualification could have applied for either an English or Kinyarwanda post, but both would have been on a P4P contract.}
Empirically, we consider the Mixed treatment as a separate arm; we estimate a corresponding advertisement effect only as an incidental parameter.

This first-tier randomization was accompanied by an advertising campaign to increase awareness of the new posts and their associated contracts.\footnote{Details of the promotional materials used in this campaign are provided in Online Appendix E.} In November 2015, as soon as districts revealed the positions to be filled, we announced the advertised contract assignment. In addition to radio, poster, and flyer advertisements, and the presence of a person to explain the advertised contracts at District Education Offices, we also held three job fairs at TTCs to promote the interventions. These job fairs were advertised through WhatsApp networks of TTC graduates. All advertisements emphasized that the contracts were available for recruits placed in the 2016 school year and that the payments would continue into the 2017 school year. Applications were then submitted in December 2015. In January 2016, all districts held screening examinations for potential candidates. Successful candidates were placed into schools by districts during February--March 2016, and were then assigned to particular grades, subjects, and streams by their head teachers. 

\paragraph{Second-tier randomization: Experienced contracts}

Our aim in the second tier was to randomize the schools to which REB had allocated the new posts to contracts. A school was included in the sample if it had at least one new post that was filled and assigned to an upper-primary grade.\footnote{Because schools could receive multiple recruits, for different teaching specializations, it was possible for enrolled schools to contain two recruits who had experienced distinct advertised treatments. Recruits hired under the mixed advertisement treatment, and the schools in which they were placed, also met our enrollment criteria.  These were similarly re-randomized to either experienced P4P or experienced FW in the second-tier randomization.} Following a full baseline survey, schools were randomly assigned to either P4P or FW. Of the 164 schools in the second tier of the experiment, 85 were assigned to P4P and 79 were assigned to FW contracts.

All upper-primary teachers---placed recruit or incumbent---within each school received the new contract. At individual applicant level, this amounted to re-randomization and hence a change to the initial assignment for some new recruits. A natural concern is that individuals who applied under one contract, but who were eventually offered another contract, might have experienced disappointment (or other negative feelings) which then had a causal impact on their behavior. To mitigate this concern,  all new recruits were offered an \emph{end-of-year retention bonus} of RWF 80,000 on top of their school-randomized P4P or FW contract. An individual who applied under advertised P4P in the hope of receiving RWF 100,000 from the scheme, but who was subsequently re-randomized to experienced FW, was therefore still eligible to receive RWF 100,000 (RWF 20,000 from the FW contract plus RWF 80,000 as a retention bonus). Conversely, an individual who applied under advertised FW safe in the knowledge of receiving RWF 20,000 from the scheme, but who was subsequently re-randomized to experienced P4P, was still eligible for at least RWF 80,000. None of the recruits objected to the (re)randomization or turned down their re-randomized contract. 

Of course, surprise effects, disappointment or otherwise, may still be present in on-the-job performance. When testing hypotheses relating to student learning, we include a secondary specification with an interaction term to allow the estimated impact of experienced P4P to differ by advertised treatment. We also explore whether surprise effects are evident in either retention or job satisfaction. We find no evidence for any surprise effect. 
To ensure that teachers in P4P schools understood the new contract, we held a compulsory half-day briefing session in every P4P school to explain the intervention. This session was conducted by a team of qualified enumerators and District Education Office staff, who themselves received three days of training from the Principal Investigators in cooperation with IPA. Online Appendix E reproduces an extract of the English version of the enumerator manual, which was piloted before use. The sessions provided ample space for discussion and made use of practical examples. Teachers' understanding was tested informally at the end of the session. We also held a comparable (but simpler) half-day briefing session in every FW school.  

\subsection{Hypotheses}\label{ss:hypotheses}

Pre-commitment to an analytical approach can forestall $p$-hacking, but requires clear specification of both what to test and how to test it; this presents an opportunity, as we now discuss.
A theoretical model, discussed briefly below, and included in our pre-analysis plan and Online Appendix B, guides our choice of \emph{what} hypotheses to test. However, exactly \emph{how} to test these hypotheses in a way that maximizes statistical power is not fully determined by theory, as statistical power may depend on features of the data that could not be known in advance: the distribution of outcomes, their relationships with possible baseline predictors, and so on. We used blinded data to help decide how to test the hypotheses. In what follows we first briefly describe the theoretical model, and then discuss our statistical approach. 

\paragraph{Theory}

The model considers a fresh graduate from teacher training who decides whether to apply for a state school teaching post, or a job in another sector (a composite `outside sector'). The risk neutral individual cares about compensation $w$ and effort $e$. Her payoff is sector specific: in teaching it is $w - (e^2 - \tau \, e)$, while in the outside sector it is $w - e^2$. The parameter $\tau \geq 0 $ captures the individual's \emph{intrinsic motivation} to teach, which is perfectly observed by the individual herself but not by the employer at the time of hiring.\footnote{See  \citet{DelDur07ej} for a related approach to modeling differential worker motivation across sectors.} Effort generates a performance metric $m = e\, \theta + \e$, where $\theta \geq 1$ represents her \emph{ability}, which is also private information at the time of hiring. Compensation corresponds to one of the four cells in Figure \ref{f:twobytwo}. The timing is as follows. Teacher vacancies are advertised as either P4P or FW. The individual, of type $(\tau,\theta)$, applies either to a teaching job or to an outside job. Employers hire, at random, from the set of $(\tau,\theta)$ types that apply. Thereafter, contracts are re-randomized. If the individual applies to, and is placed in a school, she learns about her experienced contract and chooses her effort level, which results in performance $m$ at the end of the year. Compensation is paid according to the experienced contract. 

This model leads to the following hypotheses, as set out in our pre-analysis plan:
 
\begin{enumerate}[I.]
    \item Advertised P4P induces differential \emph{application} qualities;
    \item Advertised P4P affects the observable skills of recruits \emph{placed} in schools;
    \item Advertised P4P induces differentially intrinsically motivated recruits to be  \emph{placed} in schools;
    \item Advertised P4P induces the supply-side selection-in of higher- (or lower-) performing teachers, as measured by the learning outcomes of their students; 
    \item Experienced P4P creates effort incentives which contribute to higher (or lower) teacher performance, as measured by the learning outcomes of their students;
    \item These selection and incentive effects are apparent in the composite performance metric.
\end{enumerate}

\noindent The model predicts that the set of $(\tau,\theta)$ types preferring a teaching job advertised under P4P to a job in the outside sector is different from the set of types preferring a teaching job advertised under FW to a job in the outside sector. This gives Hypothesis I. Since the model abstracts from labor demand effects (by assuming employers hire at random from the set of $(\tau,\theta)$ types that apply), this prediction simply maps through to placed recruits; i.e. to Hypothesis II via $\theta$, Hypothesis III via $\tau$, and Hypotheses IV to VI via the effect of $\theta$ and $\tau$ on performance.\footnote{When mapping the theory to our empirical context, we distinguish between these hypotheses for two reasons: we have better data for placed recruits because we were able to administer detailed survey instruments to this well-defined sub-sample; and for placed recruits we can identify the advertised treatment effect from student learning outcomes, avoiding the use of proxies for $(\tau,\theta)$. A further consideration is that the impact of advertised treatment might differ between placed recruits and applicants due to labor-demand effects. We discuss this important issue in Section \ref{s:robustness}.} The model also predicts that any given $(\tau,\theta)$ type who applies to, and is placed in, a teaching job will exert more effort under experienced P4P than experienced FW. This gives Hypotheses V and VI via the effect of $e$ on performance.

\paragraph{Analysis of blinded data}
Combining several previously-known insights, we used blinded data to maximize statistical power for our main hypothesis tests.

The first insights, pertaining to simulation, are due to \citet{HumSanVan13politanalysis} and \citet{Olk15jep}.  Researchers can use actual outcome data with the treatment variable scrambled or removed to estimate specifications in `mock' data.  This permits navigation of an otherwise intractable `analysis tree'. They can also improve statistical power by simulating treatment effects and choosing the specification that minimizes the standard error.
Without true treatment assignments, the influence of any decision over eventual treatment effect estimates is unknown; thus, these benefits are garnered without risk of $p$-hacking.\footnote{This would not be true if, for example, an outcome in question was known to have different support as a function of treatment, allowing the `blinded' researcher to infer treatment from the outcome variable.  For our blinded pre-analysis, we only consider outcomes (TTC score, and student test scores) that are nearly continuously distributed and which we believe are likely to have the same support in all study arms.  To make this analysis possible, we drew inspiration from \citet{FafLab17polanalysis}, who suggest dividing labor within a research team. In our case, IPA oversaw the data-blinding process.
Results of the blinded analysis (for which IPA certified that we used only blinded data) are in our pre-analysis plan. Our RCT registry entry \citep[][AEARCTR-0002565]{LeaOziSerZei18rctregistry} is accompanied by IPA's letter specifying the date after which treatment was unblinded.}

The second set of insights pertain to randomization inference. Since the market-level randomization in our study involves 18 randomizable units, asymptotic inference is unsuitable, so we use randomization inference. It is known that any scalar function of treatment and comparison groups is a statistic upon which a (correctly-sized) randomization-inference-based test of the sharp null hypothesis could be built, but also that such statistics may vary in their statistical power in the face of any particular alternative hypothesis \citep{ImbRub15book}. We anticipated that, even with correctly-sized tests, the market-level portion of our design may present relatively low statistical power. Consequently, we conducted blinded analysis to choose, on the basis of statistical power, among testing approaches for several hypotheses: Hypothesis I, and a common framework for Hypotheses IV and V.\footnote{Hypotheses II and III employ data that our team collected, so did not have power concerns associated with them; Hypothesis VI offered fewer degrees of freedom.}

Hypothesis I is the test of whether applicants to different contracts vary in their TTC scores.  Blinded analysis, in which we simulated additive treatment effects and calculated the statistical power under different approaches, suggested that ordinary least squares regression (OLS) would yield lower statistical power than would a Kolmogorov-Smirnov (KS) test of the equality of two distributions.
Over a range of simulations, the KS test had between one and four times the power of OLS. 
We therefore committed to KS (over OLS and two other alternatives) as our primary test of this hypothesis.\footnote{This refers to \citet{LeaOziSerZei18rctregistry}, Table C.1, comparing the first and third rows.}
This prediction is borne out in Table C.1 in Online Appendix C.\footnote{The confidence interval for the KS test is roughly half the width of  the corresponding OLS confidence interval: a gain in precision commensurate with more than tripling the sample size.}

Hypotheses IV and V relate to the effects of advertised and experienced contracts on student test scores. Here, with the re-randomization taking place at the school level, we had many possible specifications to choose from.  We examined 14 specifications (modeling random effects or fixed effects at different levels), and committed to one with the highest power. Simulations suggested that this could produce a 20 to 25 percent narrower confidence interval than in a simple benchmark specification.\footnote{This refers to \citet{LeaOziSerZei18rctregistry}, Table C.3, comparing row 12 to row 1.} Comparing Table \ref{t:learning_fx} to Table A.4 in Online Appendix A, this was substantively borne out.\footnote{For the pooled advertised treatment effect, the pre-committed random effects model yields a confidence interval that is 67 percent as wide as the interval from OLS: a gain in precision commensurate with increasing the sample size by 125 percent. The gain in precision for the pooled experienced treatment effect is smaller and commensurate with increasing sample size by 22 percent.} 

On the basis of this theory and analysis of blinded data, we settled on six primary tests: an outcome, a sample, a specification and associated test statistic, and an inference procedure for each of Hypotheses I-VI, as set out in Table A.1 in Online Appendix A. We also included a small number of secondary tests based on different outcomes, samples, and/or specifications. In Section \ref{s:results}, we report results for every primary test; secondary tests are in Section \ref{s:results} or in an appendix. To aid interpretation, we also include a small amount of supplementary analysis that was not discussed in the pre-analysis plan---e.g. impacts of advertised P4P on teacher attributes beyond observable skill and intrinsic motivation, and estimates from a teacher value added model---but are cautious and make clear when this is post-hoc.

\section{Data}\label{s:data}

The primary analyses make use of several distinct types of data. Conceptually, these trace out the causal chain from the advertisement intervention to a sequence of outcomes: that is, from the candidates' application decisions, to the set (and attributes) of candidates hired into schools, to the learning outcomes that they deliver, and, finally, to the teachers' decisions to remain in the schools.  In this section, we describe the administrative, survey, and assessment data available for each of these steps in the causal chain.\footnote{All data generated by the study and used in this paper are made available in the replication materials \citep{LeaOziSerZei20icpsr}.} Our understanding of these data informs our choices of specification for analysis, as discussed in detail in the pre-analysis plan.

\subsection{Applications}\label{ss:data_applications}

Table \ref{t:applications} summarizes the applications for the newly advertised jobs, submitted in January 2016, across the six districts.\footnote{These data were obtained from the six district offices and represent a census of applications for the new posts across these districts.}  Of the 2,184 applications, 1,962 come from candidates with a TTC degree---we term these \emph{qualified} since a TTC degree is required for the placements at stake. In the table, we present TTC scores, genders, and ages---the other observed CV characteristics---for all qualified applicants. Besides these two demographic variables, TTC scores are the only consistently measured characteristics of all applicants. 

\begin{table}[!htbp]
    \caption{Application characteristics, by district}
    \label{t:applications}
    \begin{footnotesize}
    \input{tables/applications.tex}
    \end{footnotesize}
\end{table}

The 2,184 applications come from 1,424 unique individuals, of whom 1,246 have a TTC qualification. The majority (62 percent) of qualified applicants complete only one application, with 22 percent applying to two districts and 16 percent applying to three or more. Multiple applications are possible but not the norm, most likely because each district requires its own exam. Of those applying twice, 92 percent applied to adjacent pairs of districts. In Online Appendix C, we use this geographical feature of applications to test for cross-district labor-supply effects and fail to reject the null that these effects are zero. 

\subsection{Teacher attributes}\label{ss:data_teachers}

During February and March 2016, we visited schools soon after they were enrolled in the study to collect baseline data using surveys and `lab-in-the-field' instruments. School surveys were administered to head teachers or their deputies, and included a variety of data on management practices---not documented here---as well as administrative records of teacher attributes, including age, gender, and qualifications.  The data cover all teachers in the school, regardless of their eligibility for the intervention. Teacher surveys were administered to all teachers responsible for at least one upper-primary, core-curricular subject and included questions about demographics, training, qualifications and experience, earnings, and other characteristics. 

The `lab-in-the-field' instruments were administered to the same set of teachers, and were intended to measure the two characteristics introduced in the theory: intrinsic motivation and ability. In the model, more intrinsically motivated teachers derive a higher benefit (or lower cost) from their efforts to promote learning. To capture this idea of other-regarding preferences towards students, taking inspiration from the work of \citet{AshBanJack14jpube}, we used a framed version of the \emph{Dictator Game} \citep{EckGross96geb}.\footnote{Previous work shows the reliability of the DG as a measure of other-regarding preferences related to intrinsic motivation \citep{BrockLanLeon16jhr, BanKeef16eer, Des19aejapp}.} Teachers were  given 2,000 Rwandan francs (RWF) and asked how much of this money they wished to allocate to the provision of school supply packets for students in their schools, and how much they wished to keep for themselves. Each packet contained one notebook and pen and was worth 200 RWF. Teachers could decide to allocate any amount, from zero to all 2,000 RWF, which would supply ten randomly chosen students with a packet. 

We also asked teachers to undertake a \emph{Grading Task} which measured their mastery of the curriculum in the main subject that they teach.\footnote{See \cite{Bol17jep} who use a similar approach to assess teacher content knowledge.} Teachers were asked to grade a student examination script, and had 5 minutes to determine if a series of student answers were correct or incorrect. They received a fixed payment for participation. Performance on this task was used to estimate a measure of teacher skill based on a two-parameter item response theory (IRT) model.%

\subsection{Student learning}\label{ss:data_assessments}

Student learning was measured in three rounds of assessment: baseline, the end of the 2016 school year, and the end of the 2017 school year (indexed by $r=0,1,2$). These student assessments play a dual role in our study:  they provide the primary measure of learning for analysis of program impacts, and they were used in the experienced P4P arm for purposes of performance awards.

Working with the Ministry of Education, we developed comprehensive subject- and grade-specific, competency-based assessments for grades 4, 5 and 6. These assessments were based on the new Rwanda national curriculum and covered the five core subjects: Kinyarwanda, English, Mathematics, Sciences, and Social Studies. There was one assessment per grade-subject, with students at the beginning of the year being assessed on the prior year's material. Each test aimed to cover the entire curriculum for the corresponding subject and year, with questions becoming progressively more difficult as a student advanced in the test. The questions were a combination of multiple choice and fill-in diagrams. The tests were piloted extensively; they have no ceiling effects while floor effects are limited.\footnote{Test scores are approximately normally distributed with a mean of close to 50 percent of questions answered correctly. A validation exercise of the test at baseline found its scores to be predictive of the national Primary Leaving Exam scores (both measured in school averages).} In each round, we randomly sampled a subset of students from each grade to take the test. In Year 1, both baseline and endline student samples were drawn from the official school register of enrolled students compiled by the head teacher at the beginning of the year. This ensured that the sampling protocol did not create incentives for strategic exclusion of students. In Year 2, students were assessed at the end of the year only, and were sampled from a listing that we collected in the second trimester.

Student samples were stratified by teaching \emph{streams} (subgroups of students taught together for all subjects). In Round 0, we sampled a minimum of 5 pupils per stream, and oversampled streams taught in at least one subject by a new recruit to fill available spaces, up to a maximum of 20 pupils per stream and 40 per grade.  In rare cases of grades with more than 8 streams, we sampled 5 pupils from all streams.  In Round 1, we sampled 10 pupils from each stream: 5 pupils retained from the baseline (if the stream was sampled at baseline) and 5 randomly sampled new pupils. We included the new students to alleviate concerns that teachers in P4P schools might teach (only) to previously sampled students. In Round 2, we randomly sampled 10 pupils from each stream using the listing for that year.\footnote{Consequently, the number of pupils assessed in Year 2 who have also been assessed in Year 1 is limited.  Because streams are reshuffled across years and because we were not able to match Year 2 pupil registers to Year 1 registers in advance of the assessment, it was not possible to sample pupils to maintain a panel across years while continuing to stratify by stream.}  

The tests were orally administered by trained enumerators. Students listened to an enumerator as he/she read through the instructions and test questions, prompting students to answer. The exam was timed for 50 minutes, allowing for 10 minutes per section. Enumerators administered the exam using a timed proctoring video on electronic tablets, which further ensured consistency in test administration. Individual student test results were kept confidential from teachers, parents, head teachers, and Ministry of Education officials, and have only been used for performance award and evaluation purposes in this study.

Responses were used to estimate a measure of student learning (for a given student in a given round and given subject in a given grade) based on a two-parameter IRT model. We use empirical Bayes estimates of student ability from this model as our measure of a student's learning level in a particular grade.

\subsection{Teacher inputs}\label{ss:data_inputs}

We collected data on several dimensions of teachers' inputs into the classroom.  This was undertaken in P4P schools only during Year 1, and in both P4P and FW schools in Year 2. This composite metric is based on three teacher input measures (presence, lesson preparation, and observed pedagogy), and one output measure (pupil learning)---the `4Ps'.  Here we describe the input components measured. 

To assess the three inputs, P4P schools received three unannounced surprise visits: two spot checks during Summer 2016, and one spot check in Summer 2017. During these visits, Sector Education Officers (SEOs) from the District Education Offices (in Year 1) or IPA staff (for logistical reasons, in Year 2) observed teachers and monitored their presence, preparation and pedagogy with the aid of specially designed tools.\footnote{Training of SEOs took place over two days. Day 1 consisted of an overview of the study and its objectives and focused on how to explain the intervention (in particular the 4Ps) to teachers in P4P schools using the enumerator manual in Online Appendix E. During Day 2, SEOs learned how to use the teacher monitoring tools and how to conduct unannounced school visits. SEOs were shown videos recorded during pilot visits. SEOs were briefed on the importance of not informing teachers or head teachers ahead of the visits. Field staff monitored the SEOs' adherence to protocol.}  FW schools also received an unannounced visit in Year 2, at the same time as the P4P schools. Table A.2 in Online Appendix A shows summary statistics for each of these three input measures over the three rounds of the study. 

\emph{Presence} is defined as the fraction of spot-check days that the teacher is present at the start of the school day. For the SEO to record a teacher present, the head teacher had to physically show the SEO that the teacher was in school. 

Lesson \emph{preparation} is defined as the planning involved with daily lessons, and is measured through a review of teachers' weekly lesson plans. Prior to any spot checks, teachers in grades 4, 5, and 6 in P4P schools were reminded how to fill out a lesson plan in accordance with REB guidelines. Specifically, SEOs provided teachers with a template to record their lesson preparation, focusing on three key components of a lesson---the lesson objective, the instructional activities, and the types of assessment to be used. A `hands-on' session enabled teachers to practice using this template. During the SEO's unannounced visit, he/she collected the daily lesson plans (if any had been prepared) from each teacher. Field staff subsequently used a lesson-planning scoring rubric to provide a subjective measure of quality.  Because a substantial share of upper-primary teachers did not have a lesson plan on a randomly chosen audit day, we used the presence of such a lesson plan as a summary measure in both the incentivized contracts and as an outcome for analysis.

\emph{Pedagogy} is defined as the practices and methods that teachers use in order to impact student learning. We collaborated with both the Ministry of Education and REB to develop a monitoring instrument to measure teacher pedagogy through classroom observation. Our classroom observation instrument measured objective teacher actions and skills as an input into scoring teachers' pedagogical performance.  Our rubric was adapted from the Danielson Framework for Teaching, which is widely used in the U.S. \citep{Dan07book}. The observer evaluated the teachers' effective use of 21 different activities over the course of a full 45-minute lesson. Based on these observations and a detailed rubric, the observer provided a subjective score, on a scale from zero to three, of four components of the lesson: communication of lesson objectives, delivery of material, use of assessment, and  student engagement. The teacher's incentivized score, as well the measure of pedagogy used in our analysis, is defined as the average of these ratings across the four domains.   

\subsection{Balance}

We use the baseline data described in this section to check whether the second-tier randomization produced an appropriately `balanced' experienced treatment assignment. Table \ref{t:balance} confirms that across a wide range of school, teacher, and student characteristics there are no statistically significant differences in means between the experienced P4P and FW treatment arms.\footnote{Since the teacher inputs described in Section \ref{ss:data_inputs} were collected \emph{after} the second-tier randomization, they are not included in Table \ref{t:balance}. See instead Table A.2 in Online Appendix A.}  

\begin{table}[!thbp]
\caption{Baseline characteristics and balance of experienced P4P assignment}
\label{t:balance}
\begin{footnotesize}
\input{tables/Balance}
\floatfoot{
The table provides summary statistics for attributes of schools, teachers (new recruits placed in upper primary only), and students collected at baseline.  The first column presents means in FW schools, (with standard deviations in brackets); the second column presents estimated differences between FW and P4P schools (with randomization inference $p$-values in parentheses).  
The sample in Panel B consists of new recruits placed in upper-primary classrooms at baseline, who undertook the lab-in-the-field exercises.
In Panel B, Grading Task IRT scores are standardized based on the distribution among incumbent teachers. In Panel C, student learning IRT scores are standardized based on the distribution in the experienced FW arm.
}
\end{footnotesize}
\end{table}

\section{Results}\label{s:results}

Our two-tiered experiment allows us to estimate impacts of pay-for-performance on the type of individuals applying to, and being placed in, primary teaching posts (the compositional margin), and on the activities undertaken by these new recruits (the effort margin). We report these results in Sections \ref{ss:composition_fx} and \ref{ss:ExperiencedP4P} respectively. Of course, the long-run effects of pay-for-performance will depend not only on selection-in, but also selection-\emph{out}, as well as the dynamics of the behavioral response on the part of teachers who stay. We address dynamic issues in Section \ref{ss:dynamics}, and postpone a substantive discussion of results until Section \ref{s:robustness}.  All statistical tests are conducted via randomization inference with 2,000 permutations of the experienced treatment.

\subsection{Compositional margin of pay-for-performance}\label{ss:composition_fx}

We study three types of compositional effect of pay-for-performance. These are impacts on: the quality of applicants; the observable skill and motivation of placed recruits on arrival; and the student learning induced by these placed recruits during their first and second year on the job.  

\paragraph{Quality of applicants} Motivated by the theoretical model sketched in Section \ref{ss:hypotheses}, we begin by testing for impacts of advertised P4P on the quality of applicants to a given district-by-qualification pool (Hypothesis I).
We focus on Teacher Training College final exam score since this is the only consistently measured quality-related characteristic we observe for all applicants. 

Our primary test uses a Kolmogorov-Smirnov (henceforth, KS) statistic to test the null that there is no difference in the distribution of TTC scores across advertised P4P and advertised FW labor markets. This test statistic can be written as
\begin{equation}\label{eq:KSstat}
    T^{KS} = \sup_{y} \left| \hat{F}_{P4P}(y) - \hat{F}_{FW}(y)\right| = \max_{i=1,\ldots,N} \left| \hat{F}_{P4P}(y_i) - \hat{F}_{FW}(y_i) \right|.
\end{equation}
Here, $\hat{F}_{P4P}(y)$ denotes the empirical cumulative distribution function of TTC scores among applicants who applied under advertised P4P, evaluated at some specific TTC score $y$. Likewise, $\hat{F}_{FW}(y)$ denotes the empirical cumulative distribution function of TTC scores among applicants who applied under advertised FW, evaluated at the same TTC score $y$.             
We test the statistical significance of this difference in distributions by randomization inference. To do so, we repeatedly sample from the set of potential (advertised) treatment assignments $\mathcal{T}^A$ and, for each such permutation, calculate the KS test statistic. The  $p$-value is then the share of such test statistics larger in absolute value than the statistic calculated from the actual assignment. 

\begin{figure}[!hbtp]
\includegraphics[width=0.65\textwidth]{figures/ttcscore_outcomes.pdf}
\caption{Distribution of applicant TTC score, by advertised treatment arm \label{f:apps}}
\begin{footnotesize}
\floatfoot{
 KS test statistic is 0.026, with a $p$-value of 0.909. 
}
\end{footnotesize}
\end{figure}

Figure \ref{f:apps} depicts the distribution of applicant TTC score, by advertised treatment arm.  These distributions are statistically indistinguishable between advertised P4P and advertised FW. The KS test-statistic has a value of 0.026, with a $p$-value of 0.909. Randomization inference is well-powered, meaning that we can rule out even small effects on the TTC score distribution:  a 95 percent confidence interval based on inversion of the randomization inference test rules out additive treatment effects outside of the range $[-0.020, 0.020]$. (The OLS estimate of this additive treatment effect is -0.001, as reported in Table C.1 in Online Appendix C.) We therefore conclude that there was no meaningful impact of advertised P4P on the TTC final exam scores of applicants.\footnote{This conclusion is further substantiated by the battery of secondary tests in Online Appendix C.} 

Below, we move on to consider impacts of advertised P4P on the quality of applicants who were offered a post and chose to accept it---a subset that we term \emph{placed recruits}. It is worth emphasizing that we may find results here even though there is no evidence of an impact on the distribution of TTC score of applicants. This is because, for this well-defined set of placed recruits, we have access to far richer data: lab-in-the-field instruments measuring attributes on arrival, as well as measures of student learning in the first and second years on the job.

\paragraph{Skill and motivation of placed recruits}\label{ss:hires_fx} Along the lines suggested by \citet{Dalfin16}, we explore whether institutions can attract the most capable or the most intrinsically motivated into public service. We include multidimensional skill and motivation types in the theoretical model and test the resulting hypotheses (Hypotheses II and III) using the data described in Section \ref{ss:data_teachers}. Specifically, we use the Grading Task IRT score to measure a placed recruit's skill on arrival, and the framed Dictator Game share sent to capture  baseline intrinsic motivation. 

Our primary tests use these baseline attributes of placed recruits as outcomes.  For attribute $x$ of teacher $j$ with qualification $q$ in district $d$, we estimate a regression of the form 
        \begin{equation}\label{eq:baseline_chars}
        x_{jqd} = \tau_A T^A_{qd} + \gamma_q + \delta_d + e_{jqd},
        \end{equation}
where treatment $T^A_{qd}$ denotes the contractual condition under which a candidate applied.\footnote{Here and throughout the empirical specifications, we will define $T^A_{qd}$ as a \emph{vector} that includes indicators for both the P4P and mixed-treatment advertisement condition. However, for hypothesis testing, we are interested only in the coefficient on the pure P4P treatment. Defining treatment in this way ensures that only candidates who applied (and were placed) under the pure FW treatment are considered as the omitted category here, to which P4P recruits will be compared.} Our test of the null hypothesis is the $t$ statistic associated with coefficient $\tau_A$. We obtain a randomization distribution for this $t$ statistic under the sharp null of no effects for any hire by estimating equation \eqref{eq:baseline_chars} under the set of feasible randomizations of advertised treatments, $T^A \in \mathcal{T}^A$.

Before reporting these $t$ statistics, it is instructive to view the data graphically. Figure \ref{f:placedrecruits}a shows the distribution of Grading Task IRT score, and Figure \ref{f:placedrecruits}b the framed Dictator Game share sent, by advertised treatment arm and measured on placed recruits' arrival in schools. A difference in the distributions across treatment arms is clearly visible for the measure of intrinsic motivation but not for the measure of skill. Our regression results tell the same story. In the Grading Task IRT score specification, our estimate of $\tau_A$ is $-0.184$, with a (randomization inference) $p$-value of $0.367$. In the Dictator Game share sent specification, our estimate of $\tau_A$ is $-0.100$, with a $p$-value of $0.029$. It follows that we cannot reject the sharp null of no advertised P4P treatment effect on the measured skill of placed recruits, but we can reject the sharp null of no advertised P4P treatment effect on their measured intrinsic motivation (at the 5 percent level). Teachers recruited under advertised P4P allocated approximately 10 percentage points \emph{less} to the students on average.

\begin{figure}[!hbtp]
\begin{minipage}{0.49\textwidth}
\begin{center}
\includegraphics[width=\textwidth]{figures/PlacedTeacherAbility_outcomes.pdf} \\
{\footnotesize (a) Grading task score}
\end{center}
\end{minipage} %
\begin{minipage}{0.49\textwidth}
\begin{center}
\includegraphics[width=\textwidth]{figures/PlacedDGsend_outcomes.pdf} \\
{\footnotesize (b) Dictator Game contribution}
\end{center}
\end{minipage}

\caption{Distribution of placed recruit attributes on arrival, by advertised treatment arm}
\label{f:placedrecruits}
\begin{footnotesize}
\floatfoot{
In Figure 3a, the $t$ statistic for a difference in mean Grading Task IRT score across the P4P and FW treatments is $-0.184$, with a $p$-value of $0.367$. In Figure 3b, the $t$ statistic for a difference in mean DG share sent across the P4P and FW treatments is $-0.100$, with a $p$-value of $0.029$. 
}
\end{footnotesize}
\end{figure}

We chose not to include additional teacher attributes in the theoretical model, or in the list of pre-specified hypotheses to avoid multiple hypothesis testing concerns. Notwithstanding this decision, we did collect additional data on placed recruits at baseline, meaning that we can use our two-tiered experimental design to conduct further \emph{exploratory} analysis of the impact of advertised P4P. Specifically, we estimate regressions of the form given in equation \eqref{eq:baseline_chars} for four additional teacher attributes: age, gender, risk aversion, and an index capturing the Big Five personality traits.\footnote{Here we follow \citet{DalFinRos13qje} who measure the risk preferences and Big Five personality traits of applicants for civil service jobs in Mexico, and \citet{CallenNBER} who study the relevance of Big Five personality traits for the performance of health workers in Pakistan.} Results are reported in Table A.3 in Online Appendix A, with details of the variable construction provided in the table-note. We are unable to reject the sharp null of no advertised P4P treatment effect for any of these exploratory outcomes.      

\paragraph{Student learning induced by placed recruits}\label{ss:learning_fx} The skill and motivation of placed recruits on arrival are policy relevant insofar as these attributes translate into teacher effectiveness.  To assess this, we combine experimental variation in the advertised contracts to which recruits applied, with the second-stage randomization in experienced contracts under which they worked.  This allows us to estimate the impact of advertised P4P on the student learning induced by these recruits, holding constant the experienced contract---a pure compositional effect (Hypothesis IV).

Our primary test is derived from estimates on student-subject-year level data.  The advertised treatment about which a given student's performance is informative depends on the identity of the placed recruit teaching that particular subject via qualification type and district. We denote this by $T^A_{qd}$ for teacher $j$ with qualification type $q$ in district $d$, and suppress the dependence of the teacher's qualification $q$ on the subject $b$, stream $k$, school $s$, and round $r$, which implies that $q=q(bksr)$. The experienced treatment is assigned at the school level, and is denoted by $T^E_s$. We pool data across the two years of intervention to estimate a specification of the type
    %
    \begin{equation}
    \label{eq:assessments_pooled}
    z_{ibksr} = \tau_A T^A_{qd} + \tau_E T^E_s + \lambda_I I_j + \lambda_E T_s^E I_j + \rho_{br} \bar{z}_{ks,r-1} + \delta_d + \psi_r + e_{ibksr}
    \end{equation}
    %
for the learning outcome of student $i$ in subject $b$, stream $k$, school $s$, and round $r$.  We define $j=j(bksr)$ as an identifier for the teacher assigned to that subject-stream-school-round. The variable $I_j$ is an indicator for whether the teacher is an incumbent, and the index $q=q(j)$ denotes the qualification type of teacher $j$ if that teacher is a recruit (and is undefined if the teacher is an incumbent, so that $T^A_{qd}$ is always zero for incumbents). Drawing on the pseudo-panel of student outcomes, the variable $\bar{z}_{ks,r-1}$ denotes the vector of average outcomes in the once-lagged assessment among students placed in that stream, and its coefficient, $\rho_{br}$, is subject- and round-specific. The coefficient of interest is $\tau_A$: the average of the within-year effect of advertised P4P on pupil learning in Year 1 and the within-year effect of advertised P4P on pupil learning in Year 2.\footnote{We focus on \emph{within-year} impacts because there is not a well-defined cumulative treatment effect. Individual students receive differing degrees of exposure to the advertised treatments depending on their path through streams (and hence teachers) over Years 1 and 2.}  

The theoretical model of Online Appendix B, as well as empirical evidence from other contractual settings \citep{EinFinRyaSchCul13aer}, suggests that pay-for-performance may induce selection on the \emph{responsiveness} to performance incentives. If so, then the impact of advertised treatment will depend on the contractual environment into which recruits are placed. Consequently, we also estimate a specification that allows advertised treatment effects to differ by experienced treatment, including an interaction term between the two treatments. This interacted model takes the form
    \begin{align}\label{eq:assessments_interacted}
    z_{ibksr}  = \tau_A T^A_{qd} + \tau_E T^E_s & + \tau_{AE} T^A_{qd} T^E_s 
    + \lambda_I I_j \notag \\
   & + \lambda_E T^E_s I_j + \rho_{bgr} \bar{z}_{ks,r-1} + \delta_d  + \psi_r +e_{ibksr}.
    \end{align}
    %
Here, the compositional effect of advertised P4P among recruits placed in FW schools is given by $\tau_A$ (a comparison of on-the-job performance across groups $a$ and $b$, as defined in Figure \ref{f:twobytwo}). Likewise, the compositional effect of advertised P4P among recruits placed in P4P schools is given by $\tau_A + \tau_{AE}$ (a comparison of groups $c$ and $d$). 
If $\tau_{AE}$ is not zero, then this interacted model yields the more policy relevant estimands \citep{MurRomWut20nber}. Noting the distinction between estimands and test statistics \citep{ImbRub15book}, we pre-specified the pooled coefficient $\tau_A$ from equation \eqref{eq:assessments_pooled} as the primary test statistic for the presence of compositional effects. Our simulations, using blinded data, show that this pooled test is better powered under circumstances where the interaction term, $\tau_{AE}$, is small.  

We estimate equations \eqref{eq:assessments_pooled} and \eqref{eq:assessments_interacted} by a linear mixed effects model, allowing for normally distributed random effects at the student-round level.\footnote{In our pre-analysis plan, simulations using the blinded data indicated that the linear mixed effects model with a student-round normal random effects would maximize statistical power. We found precisely this in the unblinded data. For completeness, and purely as supplementary analysis, we also present estimates and hypotheses tests via ordinary least squares. See Table A.4 in Online Appendix A. These OLS estimates are generally larger in magnitude and stronger in statistical significance.} Randomization inference is used throughout.  To do so, we focus on the distribution of the estimated $z$-statistic (i.e., the coefficient divided by its estimated standard error), which allows rejections of the sharp null of no effect on any student's performance to be interpreted, asymptotically, as rejection of the non-sharp null that the coefficient is equal to zero \citep{DicRom17jasa}.  Inference for $\tau_A$ is undertaken by permutation of the advertised treatment, $T^A \in\mathcal{T^A}$, while inference for $\tau_E$ likewise proceeds by permuting the experienced treatment $T^E\in\mathcal{T^E}$. To conduct inference about the interaction term, $\tau_{AE}$ in equation \eqref{eq:assessments_interacted}, we simultaneously permute both dimensions of the treatment, considering pairs $(T^A,T^E)$ from the set $\mathcal{T^A}\times \mathcal{T^E}$.

\begin{table}[!hbtp]
\caption{Impacts on student learning, linear mixed effects model\label{t:learning_fx}}
\begin{footnotesize}
\input{tables/LearningImpacts_LME}
\floatfoot{
For each estimated parameter, or combination of parameters, the table reports the point estimate (stated in standard deviations of student learning), 95 percent confidence interval in brackets, and $p$-value in parentheses. Randomization inference is conducted on the associated $z$ statistic. The measure of student learning is based on the empirical Bayes estimate of student ability from a two-parameter IRT model, as described in Section \ref{ss:data_assessments}. 
}
\end{footnotesize}
\end{table}
    
Results are presented in Table \ref{t:learning_fx}. Pooling across years, the compositional effect of advertised P4P is small in point-estimate terms, and statistically indistinguishable from zero (Model A, first row). We do not find evidence of selection on responsiveness to incentives; if anything, the effect of P4P is stronger among recruits who applied under advertised FW contracts, although the difference is not statistically significant and the 95 percent confidence interval for this estimate is wide (Model B, third row). The effect of advertised P4P on student learning does, however, appear to strengthen over time. By the second year of the study, the within-year compositional effect of P4P was 0.04 standard deviations of pupil learning. OLS estimates of this effect are larger, at 0.08 standard deviations, with a $p$-value of 0.10, as shown in Table A.4. 

\begin{figure}[!hb]
\begin{minipage}{0.49\textwidth}
\begin{center}
\includegraphics[width=\textwidth]{figures/Recruits_TVA_byTx_yr1.pdf} \\
{\footnotesize (a) Year 1}
\end{center}
\end{minipage} %
\begin{minipage}{0.49\textwidth}
\begin{center}
\includegraphics[width=\textwidth]{figures/Recruits_TVA_byTx_yr2.pdf} \\
{\footnotesize (b) Year 2}
\end{center}
\end{minipage}

\caption{Teacher value added among recruits, by advertised treatment and year}
\label{f:TVA_Recruits_byTx}
\begin{footnotesize}
\floatfoot{
The figures plot distributions of teacher value added under advertised P4P and advertised FW in Years 1 and 2. Value-added models estimated with school fixed effects. Randomization inference $p$-value for equality in distributions between P4P and FW applicants, based on one-sided KS test, is 0.796 using Year 1 data; 0.123 using Year 2 data; and 0.097 using pooled estimates of teacher value added (not pre-specified). 
}
\end{footnotesize}
\end{figure}

For the purposes of interpretation, it is useful to recast the data in terms of teacher value added. As detailed in Online Appendix D, we do so by estimating a teacher valued-added (TVA) model that controls for students' lagged test scores, as well as school fixed effects, with the latter absorbing differences across schools attributable to the experienced P4P treatment. This TVA model gives a sense of magnitude to the student learning estimates in Table \ref{t:learning_fx}. Applying the Year 2 point estimate for the effect of advertised P4P would raise a teacher from the 50th to above the 73rd percentile in the distribution of (empirical Bayes estimates of) teacher value added for placed recruits who applied under FW. The TVA model also reveals the impact of advertised P4P on the distribution of teacher effectiveness. Figure \ref{f:TVA_Recruits_byTx}b shows that the distribution of teacher value added among recruits in their second year on the job is better, by first order stochastic dominance, under advertised P4P than advertised FW. This finding is consistent with the view that a contract that rewards the top quintile of teachers attracts individuals who deliver greater learning. 

\subsection{Effort margin of pay-for-performance}\label{ss:ExperiencedP4P}

Having studied the type of individuals applying to, and being placed in, upper-primary posts, we now consider the activities undertaken by these new recruits.

\paragraph{Student learning induced by placed recruits} We start by using the two-tiered experimental variation to estimate the impact of experienced P4P on the student learning induced by the placed recruits, holding constant the advertised contract---a pure effort effect (Hypothesis V). Our primary test uses the specification in equation  \eqref{eq:assessments_pooled}, again estimated by a linear mixed effects model. The coefficient of interest is now $\tau_E$. To investigate possible `surprise effects' from the re-randomization, we also consider the interacted specification of equation \eqref{eq:assessments_interacted}. In this model, $\tau_E$ gives the effect of experienced P4P among recruits who applied under FW contractual conditions (a comparison of groups a and c, as defined in Figure 1), while $\tau_E+\tau_{AE}$ gives the effect of experienced P4P among recruits who applied under P4P contractual conditions (a comparison of groups b and d). If recruits are disappointed, because it is groups b and c who received the ‘surprise’, $\tau_E$ should be smaller than $\tau_E+\tau_{AE}$.\footnote{We are grateful to a referee for highlighting a further interpretation: $\tau_E$ in Model B is the policy-relevant estimate of experienced P4P at the start of any unexpected transition to P4P, while $\tau_E+\tau_{AE}$ is the policy-relevant estimate for that effect slightly further into a transition---the effect of P4P on a cohort anticipating P4P.} 

Results are presented in Table \ref{t:learning_fx}. Pooling across years, the within-year effect of experienced P4P is $0.11$ standard deviations of pupil learning (Model A, second row). The randomization inference $p$-value is $0.02$, implying that we can reject the sharp null of no experienced P4P treatment effect on placed recruits at the 5 percent level. We do not find evidence of disappointment caused by the re-randomization. The interaction term is insignificant (Model B, third row) and, in point-estimate terms, $\tau_E$ is larger than $\tau_E+\tau_{AE}$. As was the case for the compositional margin, the effort effect of experienced P4P on student learning appears to strengthen over time. By the second year of the study, the within-year effort effect of P4P was $0.16$ standard deviations of pupil learning.\footnote{Across all specifications, the interaction term between experienced P4P and an indicator for incumbent teachers is negative, though statistically insignificant, and smaller in magnitude than the direct effect of experienced P4P, implying a weaker---though still positive---effect of P4P on incumbents in point-estimate terms.}

To put this in perspective, we compare the magnitude of this effort effect to impacts in similar studies in the US, and beyond. \citet{SojMykWes14jhr} study pay-for-performance schemes in Minnesota, typically based on a composite metric of subjective teacher evaluation and student performance, and find an effect of 0.03 standard deviations of pupil learning. \citet{DeeWyc15jpam} study a high-stakes incentive over a composite metric in Washington, DC, and find effects consistent with those of \citet{SojMykWes14jhr} in terms of the implied magnitude of effects on pupil learning. \citet{GleMur16chapter} review a range of studies, including several in Benin, China, India and Kenya that employ incentives for either students or teachers based solely on student performance; effect sizes are larger, typically above 0.2 standard deviations of pupil learning. Our effort effect falls within this range and is of a comparable magnitude to the impact in \citet{DufHanRya12}, who study incentives for teacher attendance in India.

\paragraph{Dimensions of the composite performance metric}\label{s:4Ps}

The results in Table \ref{t:learning_fx} speak to the obvious policy question, namely whether there are impacts of advertised and experienced P4P contracts on student learning. For completeness, and to gain an understanding into mechanisms, we complete our analysis by studying whether there are impacts on the \emph{contracted} metrics which are calculated at teacher-level (Hypothesis VI). For these tests, we use the following specifications:
\begin{equation}\label{eq:spec_inputs}
 m_{jqsdr} = \tau_A T^A_{qd} + \tau_E T^E_{s}  + \lambda_I I_j + \lambda_E T_s^E I_j  + \gamma_q + \delta_d  + \psi_r + e_{jqsdr}
\end{equation}
\begin{equation}\label{eq:spec_inputs_split}
m_{jqsdr} = \tau_A T^A_{qd} + \tau_E T^E_{s} + \tau_{AE} T^A_{qd} T^E_{s} + \lambda_I I_j + \lambda_E T_s^E I_j+ \gamma_q + \delta_d + \psi_r  + e_{jqsdr},
\end{equation}
for the metric of teacher $j$ with qualification $q$ in school $s$ of district $d$, as observed in post-treatment round $r$. As above, the variable $I_j$ is an indicator for whether the teacher is an incumbent (recall that $T^A_{qd}$ is always zero for incumbents).\footnote{Note that any attribute of recruits themselves, even if observed at baseline, suffers from the `bad controls' problem, as the observed values of this covariate could be an outcome of the advertised treatment. These variables are therefore not included as independent variables.} A linear mixed effects model with student-level random effects is no longer applicable; outcomes are constructed at the teacher-level, and given their rank-based construction, normality does not seem a helpful approximation to the distribution of error terms. As stated in our pre-analysis plan, we therefore estimate equations \eqref{eq:spec_inputs} and \eqref{eq:spec_inputs_split} with a round-school random-effects estimator to improve efficiency. The permutations of treatments used for inferential purposes mirror those above.  

\begin{table}[!hpt]
\caption{Estimated effects on dimensions of the composite 4P performance metric\label{t:inputs}}
\begin{footnotesize}
\input{tables/4Ps}
\end{footnotesize}
\floatfoot{
For each estimated parameter, the table reports the point estimate, 95 percent confidence interval in brackets, and $p$-value (or for FW means, standard deviations) in parentheses.  Randomization inference is conducted on the associated $t$ statistic. All estimates are pooled across years, but outcomes are observed in the FW arm during the second year only. Outcomes are constructed at teacher-round-level as follows: \emph{preparation} is a binary indicator for existence of a lesson plan on a randomly chosen spot-check day; \emph{presence} is the fraction of spot-check days present at the start of the school day; \emph{pedagogy} is the classroom observation score, measured on a four-point scale; and \emph{pupil learning} is the  Barlevy-Neal percentile rank. The \emph{summary metric} places 50 percent weight on learning and 50 percent on teacher inputs, and is measured in percentile ranks.
}
\end{table}

Results are reported in Table \ref{t:inputs} and, to the extent available, are based on pooled data.\footnote{As discussed in Section \ref{ss:data_inputs}, FW schools only received unannounced visits to measure teacher inputs in Year 2.} Consistent with the pooled results in Table \ref{t:learning_fx}, we see a positive and significant impact of experienced P4P on both the summary metric and the learning sub-component. The specifications with teacher inputs as dependent variables suggest that this impact on student learning is driven, at least in part, by improvements in teacher presence and pedagogy. Teacher presence was 8 percentage points higher among recruits who experienced the P4P contract compared to recruits who experienced the FW contract; an impact that is statistically significant at the 1 percent level and sizeable in economic terms given that baseline teacher presence was already nearly 90 percent. Recruits who experienced P4P were 0.10 points more effective in their classroom practices than recruits receiving FW, although it is possible that this improvement occurred only during the observation. We find no evidence of impacts on lesson planning.

\subsection{Dynamic effects}\label{ss:dynamics}

Our two-tiered experiment was designed to evaluate the impact of pay-for-performance and, in particular, to quantify the relative importance of a compositional margin at the recruitment stage versus an effort margin on the job. The hypotheses specified in our pre-analysis plan refer to selection-in and incentives among placed recruits. Since within-year teacher turnover was limited by design and within-year changes in teacher skill and motivation are likely small, the total effect of P4P in Year 1 can plausibly only be driven by a change in the type of teachers recruited and/or a change in effort resulting from the provision of extrinsic incentives. 

Interpreting the total effect of P4P in Year 2 is more complex, however. First, we made no attempt to discourage \emph{between}-year teacher turnover, and so there is the possibility of a further compositional margin at the retention stage (c.f. \citeauthor{MurSun11jpe} 2011). Experienced P4P may have selected-out the low skilled \citep{Laz00aer} or, more pessimistically, the highly intrinsically motivated. Second, given the longer time frame, teacher characteristics could have changed. Experienced P4P may have eroded a given teacher's intrinsic motivation (as hypothesized in the largely theoretical literature on motivational crowding out) or, more optimistically, encouraged a given teacher to improve her classroom skills. In this section, we conduct an exploratory analysis of these dynamic effects.\footnote{We emphasize that this material is exploratory; the hypotheses tested in this section were not part of our pre-analysis plan. That said, the structure of the analysis in this section does follow a related pre-analysis plan (intended for a companion paper) which we uploaded to our trial registry on October 3, 2018, \emph{prior} to unblinding of our data.} 

\paragraph{Retention effects}\label{ss:retention}

We begin by exploring whether experienced P4P affects retention rates among recruits. Specifically, we look for an impact on the likelihood that a recruit is still employed at midline in February 2017 at the start of the Year 2; i.e. after experiencing pay-for-performance in Year 1, although before the performance awards were announced. To do so, we use a linear probability model of the form
\begin{equation}\label{eq:retentionprob}
\Pr[employed_{iqd2} =1] = \tau_E T_s^E + \gamma_q + \delta_d,
\end{equation}
where $employed_{iqd2}$ is an indicator for whether teacher $i$ with subject-family qualification $q$ in district $d$ is still employed by the school at the start of Year 2, and $\gamma_q$ and $\delta_d$ are the usual subject-family qualification and district indicators.

As the first column of Table \ref{t:retention} reports, our estimate of $\tau_E$ is zero with a randomization inference $p$-value of 0.94. There is no statistically significant impact of experienced P4P on retention of recruits; the retention rate is practically identical---at around 80 percent---among recruits experiencing P4P and those experiencing FW.  

\begin{table}[!hbtp]
    \caption{Retention of placed recruits} 
    \label{t:retention}
    \begin{footnotesize}
    \input{tables/retention}
    \end{footnotesize}
    \floatfoot{
   For each estimated parameter, the table reports the point estimate and $p$-value in parentheses. Randomization inference is conducted on the associated $t$ statistic. In each column, the outcome is an indicator for whether the teacher is still employed at the start of Year 2. The mean of this dependent variable for FW recruits is 0.80. In the second column, the specification includes an interaction of experienced treatment with the teacher's baseline Grading Task IRT score (not de-meaned); in the third column, the interaction is with the teacher's share sent in the baseline framed Dictator Game (again not de-meaned). All specifications include controls for districts and subjects of teacher qualification.
   }
\end{table}

It is worth noting that there is also no impact of experienced P4P on \emph{intentions} to leave in Year 3. In the endline survey in November 2017, we asked teachers the question:``How likely is it that you will leave your job at this school over the coming year?''. Answers were given on a 5-point scale. For analytical purposes we collapse these answers into a binary indicator coded to 1 for `very likely' or `likely' and 0 otherwise, and estimate specifications analogous to equations (\ref{eq:spec_inputs}) and (\ref{eq:spec_inputs_split}). As the second column of Table A.5 in Online Appendix A shows, there is no statistically significant impact of experienced P4P on recruits' self-reported likelihood of leaving in Year 3. Our estimate of $\tau_E$ is $-0.06$ with a randomization inference $p$-value of 0.39.

Of course, a retention rate of 80 percent implies 20 percent attrition from Year 1 to Year 2, which is non-negligible. And the fact that retention \emph{rates} are similar does not rule out the possibility of an impact of experienced P4P on the \emph{type} of recruits retained. To explore this, we test whether experienced P4P induces differentially skilled recruits to be retained. Here, we use teachers' performance on the baseline Grading Task in the primary subject they teach to obtain an IRT estimate of their ability in this subject, denoted $z_i$, and estimate an interacted model of the form
\begin{equation}\label{eq:placed_skill}
\Pr[employed_{iqd2} =1] = \tau_E T_s^E + \zeta T_s^E z_i + \beta z_i + \gamma_q  + \delta_d .
\end{equation}
Inference for the key parameter, $\zeta$, is undertaken by performing randomization inference for alternative assignments of the school-level experienced treatment indicator. As the second column of Table \ref{t:retention} reports, our estimate of $\zeta$ is $-0.05$, with a randomization inference $p$-value of $0.39$. There is not a significant difference in selection-out on baseline teacher skill across the experienced treatments. Hence, there is no evidence that experienced P4P induces differentially skilled recruits to be retained. 

We also test whether experienced P4P induces differentially intrinsically motivated recruits to be retained. Here, we use the contribution sent in the framed Dictator Game played by all recruits at baseline, denoted $x_i$, and re-estimate the interacted model in equation (\ref{eq:placed_skill}), replacing $z_i$ with $x_i$. As the third column of Table \ref{t:retention} reports, our estimate of $\zeta$ in this specification is $0.15$, with a randomization inference $p$-value of $0.37$. There is not a significant difference in selection-out on baseline teacher intrinsic motivation across the experienced treatments. Hence, there is also no evidence that experienced P4P induces differentially intrinsically motivated recruits to be retained. 

\paragraph{Changes in retained teacher characteristics}\label{ss:endline}

To assess whether experienced P4P changes within-retained-recruit teacher skill or intrinsic motivation from baseline to endline, we estimate the following ANCOVA specification
\begin{equation}\label{eq:placed_motivation_diff}
y_{isd2} = \tau_E T^E_{s} + \rho y_{isd0} + \gamma_q + \delta_d + e_{isd}, 
\end{equation}
where $y_{iqsd2}$ is the characteristic (raw Grading Task score or framed Dictator Game contribution) of retained recruit $i$ with qualification $q$ in school $s$ and district $d$ at endline (round 2), and $y_{iqsd0}$ is this characteristic of retained recruit $i$ at baseline (round 0). As the first column of Table \ref{t:round2chars} reports, our estimate of $\tau_E$ in the Grading Task specification is $0.68$, with a randomization inference $p$-value of 0.57. Our estimate of $\tau_E$ in the Dictator Game specification is $-0.04$, with a randomization inference $p$-value of 0.06. Both estimates are small in magnitude and, in the case of the Dictator Game share sent, we reject the sharp null only at the 10 percent level. Hence, to the extent that contributions in the Dictator Game are positively associated with teachers' intrinsic motivation, we find no evidence that the \emph{rising} effects of experienced P4P from Year 1 to Year 2 are driven by \emph{positive} changes in our measures of within-retained-recruit teacher skill or intrinsic motivation.\footnote{Although repeated play of lab experimental games may complicate interpretation in some contexts, several factors allay this concern here.  First, unlike strategic games, the `Dictator Game' has no second `player' about whom to learn. Second, the two rounds of play were fully two years apart.} 

\begin{table}
\caption{Characteristics of retained recruits at endline}
\label{t:round2chars}
\begin{footnotesize}
\input{tables/round2chars}

\floatfoot{
For each estimated parameter, the table reports the point estimate and $p$-value in parentheses. Randomization inference is conducted on the associated $t$ statistic. In the first column, the outcome is the Grading Task score of the teacher at endline on a (raw) scale from $0$ to $30$; in the second column, it is the teacher's share sent in the framed Dictator Game played at endline. All specifications include the outcome measured at baseline and controls for district and subject-of-qualification.
}
\end{footnotesize}

\end{table}

Before moving on, it is worth noting that the Dictator Game result could be interpreted as weak evidence that the experience of P4P contracts crowded out the intrinsic motivation of recruits. We do not have any related measures observed at both baseline and endline with which to further probe \emph{changes} in motivation. However, we do have a range of related measures at endline: job satisfaction, likelihood of leaving, and positive/negative affect.\footnote{We follow \cite{Bloomqje15} in using the Maslach Burnout Index to capture job satisfaction and the Clark-Tellgen Index of positive and negative affect to capture the overall attitude of teachers.} As Table A.5 shows, there is no statistically significant impact of experienced P4P on any of these measures. 

Further substantiating this point, Table A.6 in Online Appendix A shows the distribution of answers to the endline survey question: ``What is your overall opinion about the idea of providing high-performing teachers with bonus payments on the basis of objective measures of student performance improvement?''\footnote{We follow the phrasing used in the surveys run by \cite{MurSun11eer}.} The proportion giving a favorable answer exceeds 75 percent in every study arm. In terms of Figure \ref{f:twobytwo}, group $a$ (recruits who both applied for and experienced FW) had the most negative view of pay-for-performance, while group $c$ (who applied for FW but experienced P4P) had the most positive view. Hence it seems that it was the idea, rather than the reality, of pay-for-performance that was unpopular with (a minority of) recruits.\footnote{Consistent with our failure to find `surprise effects' in student learning, there is no evidence that the re-randomization resulted in hostility toward pay-for-performance; if anything the reverse.} 

\section{Discussion}\label{s:robustness}

\paragraph{Compositional margin} To recap from Section \ref{ss:composition_fx}, we find no evidence of an advertised treatment impact on the measured quality of applicants for upper-primary teaching posts in study districts, but we do find evidence of an advertised treatment impact on the measured intrinsic motivation of individuals who are placed into study schools. We draw three conclusions from these results. 

First, potential applicants were aware of, and responded to, the labor market intervention. The differences in distributions across advertised treatment arms in Figure \ref{f:placedrecruits}b (Dictator Game share sent) and Figure \ref{f:TVA_Recruits_byTx}b (teacher valued added in Year 2) show that the intervention changed behavior. Since these differences are for placed recruits not applicants, it could be that this behavior change was on the labor demand rather than supply side. In Figure A.2 in Online Appendix A, we plot the empirical probability of hiring as a quadratic function of the rank of an applicant's TTC score within the set of applicants in their district.
It is clear from the figure that the predicted probabilities are similar across P4P and FW labor markets. We also test formally whether the probability of hiring, as a function of  CV characteristics (TTC score, age and gender), is the same under both P4P and FW advertisements.\footnote{Note that this is a sufficient but not necessary test of the absence of a demand-side response. It is sufficient because districts do not interview applicants, so CVs give us the full set of characteristics that could determine hiring. It is not necessary, however, because we observe hires rather than offers. The probability that an offer is accepted could be affected by the advertised contract associated with that post, even if applicants apply to jobs of both types and even if DEOs do not take contract offer types into account when selecting the individuals to whom they would like to make offers.} We find no statistically significantly differences across advertised treatment arms. 

Second, the supply-side response was, if anything, beneficial for student learning. The P4P contract negatively selected-in the attribute measured by the baseline Dictator Game. However, Table D.1 in Online Appendix D shows that the rank correlation between the baseline DG share sent by recruits and their teacher value added is small and not statistically significant. Consistent with this, our primary test rules out meaningful negative effects of advertised P4P on student learning. In fact, our supplementary analyses---the OLS estimates in Table A.4 and the distributions of teacher value added in Figure \ref{f:TVA_Recruits_byTx}---point to \emph{positive} effects on learning by recruits' second year on the job. It therefore appears that only positively selected attribute(s) mattered, at least in the five core subjects that we assessed. 

Finally, districts would struggle to achieve this compositional effect directly via the hiring process. The positively selected attribute(s) were not evident  in the metrics observed at baseline---either in TTC scores, or in the Grading Task scores that districts could in principle adopt.\footnote{An alternative explanation for the null KS test on applicant TTC scores is that individuals applied everywhere. If this were true, we would expect to see most candidates make multiple applications, and a rejection of the null in a KS test on \emph{placed recruits'} TTC scores (if the supply-side response occurred at  acceptance rather than application). We do not see either in the data.} This suggests that there is not an obvious demand-side policy alternative to contractually induced supply-side selection.

\paragraph{Effort margin}  To recap from Section \ref{ss:ExperiencedP4P}, we find evidence of a positive impact of experienced P4P on student learning, which is considerably larger (almost tripling in magnitude) in recruits' second year on the job. In light of Section \ref{ss:dynamics}, we draw the following conclusions from these results. 

The additional learning achieved by recruits working under P4P, relative to recruits working under FW, is unlikely to be due to selection-out---the compositional margin famously highlighted by \citet{Laz00aer}. Within-year teacher turnover was limited by design. Between-year turnover did happen but cannot explain the experienced P4P effect. In Online Appendix D, we show that the rank correlation between recruits' baseline Grading Task IRT score and their teacher value added is positive. However, in Section \ref{ss:dynamics} we reported that, if anything, selection-out on baseline teacher skill runs the wrong way to explain the experienced P4P effect. 

Neither is the experienced P4P effect likely to be due to within-teacher changes in skill or motivation. We find no evidence that recruits working under P4P made greater gains on the Grading Task from baseline to endline than did recruits working under FW. As already noted, recruits' Dictator Game share sent is not a good predictor of teacher value added. But even if it were, we find no evidence that recruits working under P4P contributed more from baseline to endline than did recruits working under FW, if anything the reverse.  

Instead, the experienced P4P effect is most plausibly driven by teacher effort. This conclusion follows  from the arguments above and the direct evidence that recruits working under P4P provided greater inputs than did recruits working under FW. Specifically, the P4P contract encouraged recruits to be present in school more often and to use better pedagogy in the classroom, behaviors that were incentivized components of the 4P performance metric.

\paragraph{Total effect} The total effect of the P4P contract combines both the advertised and experienced impacts: $\tau_A + \tau_E$. By the second year of the study, the within-year total effect of P4P is $0.04 + 0.16= 0.20$ standard deviations of pupil learning, which is statistically significant at the one percent level.
Roughly four fifths of the total effect can thus be attributed to increased teacher effort, while the remainder arises from supply-side selection during recruitment. At a minimum, our results suggest that in relation to positive effort-margin effects, fears of pay-for-performance causing motivational crowd-out among new public-sector employees may be overstated.  

Our estimates raise the question of why this effect is so much stronger in Year 2 compared to Year 1, particularly on the effort margin. One interpretation is that this is because it takes time for recruits to settle into the job and for the signal to noise ratio in our student learning measures to improve \citep{StaRoc10jep}. Consistent with this interpretation, we note that the impact of experienced P4P on incumbents did not increase in the second year.  
This interpretation suggests that Year 2 effects are the best available estimates of longer-term impacts.

\section{Conclusion}\label{s:conclusion}

This two-tier, two-year, randomized controlled trial featuring extensive data on teachers---their skills and motivations before starting work, multiple dimensions of their on-the-job performance, and whether they left their jobs---offers new insights into the compositional and effort margins of pay-for-performance. We found that potential applicants were aware of, and responded to, the first-tier labor market intervention. This supply-side response to advertised P4P was, if anything, beneficial for student learning. We also found a positive impact of experienced P4P that appears to stem from increased teacher effort, rather than selection-out or changes in measured skill or intrinsic motivation. 

Given these encouraging results, it is natural to ask whether it would be feasible and cost effective to implement this P4P contract at scale. We worked closely with the government to design a contract that was contextually feasible and well-grounded in theory. A composite P4P metric was used to avoid narrowly emphasizing any single aspect of teacher performance and, when measuring learning, we followed the pay-for-percentile approach that aims to give all teachers a fair chance, regardless of the composition of the students they teach. We also took care to ensure that the P4P contract, if successful, could be built into the growth path of teacher wages. While a larger bonus might have elicited stronger impacts, the expected value of the P4P bonus was set at three percent of teacher salaries to be commensurate with annual teacher salary increments (and discretionary pay in other sectors under Rwanda's \emph{imihigo} system of performance contracts for civil servants). 

The fact that we compared a P4P contract with an expenditure-equivalent fixed wage alternative that is equal in magnitude to annual teacher salary increments means that it is reasonable to think about cost effectiveness primarily in terms of measurement. For pupil learning, the minimum requirement for the P4P contract we study is a system of repeated annual assessments across grades and key subjects.\footnote{Such a system may  soon be a part of Rwanda's `comprehensive assessment' program. See, e.g., https://www.newtimes.co.rw/opinions/mineducs-new-guide-student-assessment-triggers-debate.} Measurement of the other aspects of performance---teacher presence, preparation, and pedagogy---can in principle be conducted by head teachers or district staff (who are increasingly being asked to monitor teacher performance) at modest cost.     

There are nonetheless limitations of our work. Inasmuch as the impacts on either the compositional or effort margin might differ after five or ten years, there is certainly scope for further study of this topic in low- and middle-income countries. For instance, it would be interesting to explore whether long-term P4P commitments influence early-career decisions to train as a teacher; our study restricts attention to employment choices by individuals who have already received TTC degrees. 

Another set of issues relate to unintended consequences of pay-for-performance. We found that advertised P4P attracted teachers with lower intrinsic motivation, as measured by the share sent in the framed baseline Dictator Game. It is possible that the students taught by these more self-regarding teachers became more self-regarding themselves or otherwise developed different soft skills. We also found that experienced P4P improved performance on three of the four incentivized dimensions of the composite metric: teacher presence and pedagogy, and pupil learning. It is conceivable that the students in P4P schools may have been impacted by `multi-tasking' as teachers focused on these dimensions to the detriment of others. Since we did not measure aspects of student development beyond test score gains, it would be interesting to explore these issues in future work.

Rwanda's labor market has a characteristic that is unusual for low- and middle-income countries: it has no public sector pay premium, and consequently many of those qualified to teach choose not to, making it more similar to high- income country labor markets in this regard. Whether the positive effects we find in Rwanda of a multidimensional, pay-for-percentile contract---improving performance without dampening employee satisfaction---will generalize to settings where public-sector wage premiums differ remains an open question, for the education sector and beyond.

\cleardoublepage 
















