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Teacher Merit Pay and Student Test Scores: A Meta-Analysis
Lam D. Pham
Tuan D. Nguyen
Matthew G. Springer
Vanderbilt University
April 3, 2017
Author Note
Lam D. Pham, Department of Leadership, Policy, & Organizations, Vanderbilt
University; Tuan D. Nguyen, Department of Leadership, Policy, & Organizations, Vanderbilt
University; Matthew G. Springer, Department of Leadership, Policy, & Organizations,
Vanderbilt University.
We appreciate helpful comments and suggestions from seminar participants at annual
meeting of the Association for Education Finance and Policy. We would also like to
acknowledge Emily Tanner-Smith and Carolyn Heinrich for their feedback. Any errors remain
the sole responsibility of the authors. The views expressed in this paper do not necessarily
reflect those of sponsoring agencies or individuals acknowledged.
Correspondence concerning this article should be addressed to Lam Pham, Department of
Leadership, Policy, & Organizations, Vanderbilt University, Nashville, TN 37203. Email:
In recent years, teacher merit pay programs have garnered considerable political and financial
support, spurring rapid growth in the number of research studies investigating the association
between teacher pay incentives and student test scores. The growing research literature on this
topic presents a novel opportunity to synthesize our understanding of merit pay and its influence
on student test scores. This study fills that role as a meta-analysis of reported findings from 44
primary studies. Our meta-analysis finds that the presence of a merit pay program is associated
with a modest, statistically significant, positive effect on student test scores (0.052 standard
deviations). We also find that effect sizes are highly sensitive to program design and study
context, which suggests that while some merit pay programs have the potential to improve
student test scores in some contexts, researchers and policymakers should pay close attention to
how the program is structured and implemented.
Keywords: meta-analysis, review, teacher merit pay, teacher pay for performance, teacher
incentive pay
Teacher Merit Pay and Student Test Scores: A Meta-Analysis
During the 2012-13 school year, the most recent year for which national finance data are
available, public schools in the United States spent more than $210 billion on salaries,
accounting for nearly 60 percent of school expenditures. The primary determinant of teachers’
pay is a single salary schedule that standardizes remuneration based on years of experience and
highest degree earned. According to the 2011-12 Schools and Staffing Survey, roughly 95
percent of public school districts in the U.S. use a single salary schedule in pay setting. Critics
of current teacher salary schedules highlight an incongruence between performance and
compensation because years of teaching experience and education level have low correlation
with student outcomes (Hanushek, 2003; Podgursky & Springer, 2007, 2010; Springer, 2010). In
response to criticisms of input-based salary schedules, more school leaders at the local-, state-,
and federal-levels are proposing merit pay systems to better couple teacher performance with
Teacher merit pay programs, also called incentive pay, performance pay, and pay for
performance, offer increased compensation to teachers who meet certain performance criteria,
usually involving improved student test scores (Podgursky & Springer, 2007; Springer 2010).
Merit pay offers a solution to concerns that compensation based solely on degree attainment and
seniority weaken teachers’ incentives to exert more effort. Situated in principal-agent theory, pay
incentives are designed to help employers motivate workers when individual effort and ability
are not easily measured (Dixit, 2002; Heinrich & Marschke, 2010; Holmstrom & Milgrom,
1991). Within education, merit pay offers a theoretically appropriate solution because
administrators have limited time and capacity to closely observe teachers’ performance in the
classroom. Moreover, theories of personnel economics suggest that compensation can: (a) serve
as a powerful motivational incentive to increase firm performance by encouraging employees to
improve their practice and (b) improve the composition of the workforce through the attraction
and retention of high performers and discouragement of lesser performers from entering or
staying in the profession (Lazear 1998; Lazear and Shaw, 2007; Springer, 2010).
In contrast, critics of merit pay contend that assumptions made by principal-agent theory
do not hold in teaching. They argue the difficulty inherent in creating a reliable process for
identifying effective teachers, measuring a teacher’s value-added contribution, eliminating
unprofessional preferential treatment during the evaluation process, and standardizing
assessment systems across schools (Hatry, Greiner, & Ashford, 1994; Murnane & Cohen, 1986).
These criticisms have stigmatized more recent attempts to devise and implement merit pay
programs claiming further that teachers do not support merit pay policy (Goldhaber et al., 2005;
Podgursky & Springer, 2007) and adding that recent high-profile experiments do not report a
statistically significant effect on teacher performance or behavior.
Despite substantial opposition, teacher merit pay programs are growing in popularity with
considerable political and financial support. The federal government has awarded over $2 billion
in over 100 grants to grantees in more than 30 states and the District of Columbia to design and
implement performance pay systems. In Florida, Texas, Colorado, and Minnesota alone, multiple
districts have allotted more $550 million to merit pay programs (Springer and Taylor, 2016).
Meaningful investigations into the effects of teacher merit pay programs are especially timely in
light of increasing financial investments and ongoing controversy over them. Responding to this
need, research on merit pay programs has also grown over the last ten years, encompassing both
evaluations of programs currently in operation and randomized controlled experiments of
discrete interventions.
The growing empirical research on teacher merit pay programs provides a novel
opportunity to consider these studies in light of each other. Taking this opportunity, we use a
meta-analysis to synthesize the accumulated findings on how merit pay programs influence
student test scores. Our meta-analytical approach systematically reviews primary studies in the
context of other studies, which has advantages over more traditional narrative reviews of merit
pay as in Chamberlin et al. (2002), Harvey-Beavis (2003), Umansky (2005), Podgursky and
Springer (2007), Podgursky and Springer (2011), Viscardi (2012), and Imberman and
Lovenheim (2015). First, a meta-analysis can investigate whether the effect of merit pay is
estimated consistently across the literature. Where the effect is not consistent, a meta-analysis
can quantify the extent of variance across studies. Second, a meta-analysis makes use of effect
sizes across studies rather than vote-counting methods (i.e., counting p values across studies) that
overly emphasize statistically significant results. Third, a meta-analysis is especially fitting in
light of wide variation in features of merit pay programs. For example, some studies investigate
rank-order tournaments where teachers compete for incentives whereas others use fixed
performance contracts where teachers receive pay as long as they meet pre-specified
performance targets.
With the goal of synthesizing effects from multiple studies, our investigation asks:
1. To what extent does teacher merit pay affect K-12 student test scores?
2. To what extent do results vary across study and program characteristics, such as
individual versus group incentives?
Our study is focused on student test score outcomes and the motivational effect hypothesis of
performance compensation, as suggested by personnel economic theories. As for compositional
effects, we include a brief descriptive summary of the relationship between incentive pay and
teacher labor market outcomes such as retention and recruitment because too few primary studies
exist on this topic to allow for a more rigorous meta-analytical investigation. Nevertheless, we
believe it is important to recognize this second mechanism through which anticipated benefits of
merit pay programs may be realized.
The rest of this paper proceeds as follows. In the next section, we explain the context and
theoretical framework behind merit pay. Then, we discuss our methodology, including the
literature search process, the study inclusion criteria, the coding of primary studies, and the
analytic approach. Next, we present results from the main analysis, sensitivity checks, subgroup
and moderator analyses, risk of bias assessments, and an analysis of publication bias. We end
with a discussion of our findings, their implications, and some preliminary recommendations for
future teacher merit pay programs.
Context and Theoretical Framework
History of Compensation in Public Schooling. Teacher compensation in the U.S. traces
back to the room and board compensation model common in early 19th century one-room
schoolhouses (Protsik, 1995). Under this model, teachers rotated their residence between
students’ homes and received a small stipend along with room and board. Industrialization in the
late 1800s meant greater need for a better educated work force resulting in increased demand for
more and better-trained teachers. To meet this need, teacher compensation was reconceptualized
to the grade-based model which sought to imitate factory production models by paying teachers
based on skill (Podgursky & Springer, 2007). Since it was believed that younger students were
easier to educate, secondary teachers were paid more than elementary school teachers (Guthrie,
Springer, Rolle, & Houck, 2007). By the beginning of the 20th century, teacher compensation
changed again as labor leaders used collective bargaining to advocate for better working
conditions and salaries. During this period, the single salary schedule emerged where teachers
were paid according to uniform pay steps that meant teachers with the same years of experience
and education level were paid equally (Podgursky & Springer, 2007). The single salary pay
system continues to be the dominant model of teacher compensation with 95 percent of public
school districts using a uniform salary schedule.
Despite its widespread acceptance, the single salary schedule has been criticized because
public school administrators could not adjust teacher pay to reflect either performance or labor
market realities. One prominent compensation reform model proposed to address this issue is
merit-based pay. Merit pay in education is an longstanding idea dating back to Great Britain in
the early 1700s (Stucker & Hall, 1971). In the United States, Evenden reported 48 percent of the
over 300 cities he studied in 1918 using merit pay of some sort (Evenden, 1919). In the 1920s,
when scientific management was common, administrators adapted evaluations from business
management to schools, leading to widespread use of merit pay (Johnson & Papay, 2010). These
programs quietly dissipated and merit pay faded from public interest between the 1930s and
1950s. Interest in merit pay re-emerged, driven by public concern with international competition
during the Cold War. Merit pay programs at the time made use of sophisticated evaluation
techniques, such as Teacher Observation Codes meant to aid observers in evaluating teachers
(Johnson & Papay, 2010). For all their sophistication, interest in merit pay programs developed
during the Cold War waned by the 1970s.
With the release of A Nation at Risk in 1983, school districts again revisited merit pay
models as alternatives or supplements to the single salary schedule (Podgursky & Springer,
2007). Distinct from knowledge- of skill-based compensation where teachers are paid based on
“inputs,” merit-based systems pay teachers, groups of teachers or schools based on outcomes
such student test scores, classroom observations, or teacher portfolios. National interest in merit-
based pay has steadily grown in recent years with well-known programs such as Denver Public
Schools’ Professional Compensation System for Teachers (ProComp), Florida’s Merit Award
Program (MAP), Minnesota’s Quality Compensation Program (Q-Comp), Texas’ Governor’s
Educator Excellence Award Programs, and national programs such as the Milken Family
Foundation’s Teacher Advancement Program (TAP) and the U.S. Department of Education’s
Teacher Incentive Fund (TIF). While interest in merit pay programs in K-12 public schools has
historically waxed and waned, current merit pay programs share at least one common theme with
these past movements: theoretical belief in the efficacy of incentives in motivating teachers.
Theoretical Framework. Proponents of merit pay programs often cite principal-agent
theory as a framework for understanding the benefits of incentive pay (Burgess & Ratto, 2003;
Dixit, 2002). Principal-agent theory predicts that incentives are useful when principals and
agents have different goals in the context of information asymmetry (Heinrich & Marschke,
2010). School administrators and teachers pose this principal-agent problem because
administrators often do not have the time or capacity to adequately observe what teachers
actually do in their classrooms. Also, principal-agent theory is particularly attractive in the
context of merit pay in public schools, because the model incorporates organizational structures
into an analysis of workers’ responsiveness to incentives. In particular, schools improve most
when incentives are closely coupled with important student learning outcomes, and teachers are
most responsive when they believe their work contributes to the school’s goals and when they
feel capable of meeting the incentive criteria.
Supporters of merit pay also argue merit pay allows flexibility such that exceptional
teachers are compensated for their performance. This argument situates merit pay programs
within principles of efficiency where greater effort and better service yield higher salary.
Another attractive feature of merit schedules is that employers do not need to specify details for
how the outcome is to be achieved (Asch, 2005). In this way, teachers can continue to choose
teaching methods they deem best as long as they and their students meet certain target criteria.
In light of these theoretical benefits, scholars in the incentive pay literature suggest two
high-level pathways by which incentive pay improves student outcomes, which is also supported
in the general personnel economics literature (Podgursky & Springer, 2007). First, merit pay
encourages and motivates teachers to improve because their increased efforts will be rewarded
(Springer and Taylor, 2016). This pathway is especially well supported by principal-agent
theory. Second, pay incentives can be used to attract and retain higher performing teachers who
would benefit most from the extra compensation (Ballou & Podgursky, 1998). More studies into
this promising pathway have been emerging over the last few years (e.g., Clotfelter, Ladd, &
Vigdor, 2011; Dee & Wyckoff, 2015; Fulbeck, 2014; Glazerman et al., 2013; Springer, Swain, &
Rodriguez, 2015; Steele, Murnane, & Willett, 2010; Taylor & Springer, 2009), but most of the
scholarship on teacher pay incentives has focused on how these programs influence student test
scores and emphasized how incentive pay can motivate teachers to improve. In this meta-
analysis, we review studies that link merit pay with student test scores through improved teacher
motivation and performance, while acknowledging that student test score gains can occur
through a combination of improved teacher performance and elevated quality in the teacher
Balancing voices of support for merit pay, opponents present multiple criticisms of merit
pay when applied to teachers, questioning the assumptions of principal-agent theory. First,
incentive pay programs assume that organizational goals and criteria for quality performance are
clearly defined, assumptions that may not hold for teachers (Dixit, 2002; Lazear, 2001; Mehta,
2013). Teachers and schools have multidimensional educational goals for students such as
academic mastery, citizenship, character development, and career preparation, and there is
neither agreement on which goals are most important nor are there clear definitions for what
makes teachers “good” at achieving these goals (Lazear, 2001). Second, incentive programs
assume teachers know how to improve and are simply unmotivated to do so, but researchers have
shown that teachers do not always know how to do a better job (Thoonen et al., 2011) and vary
in their sense of self-efficacy (Klassen & Chiu, 2011). Finally, critics point out the negative
implications of individual merit pay programs on school culture when some teachers receive
increased compensation, others do not, and administrators cannot clearly identify why. This
argument is especially germane with growing interest in supporting teacher development through
collaboration (LaFee, 2003).
The periodic rise and fall of interest in merit pay throughout history along with vigorous
debate over its suitability in education suggest a need for careful synthesis of available research
findings on teacher merit pay programs. Responding to this need, we use meta-analytical
techniques to synthesize the available empirical literature on merit pay in order to provide
evidence of its influence on student test scores based on the accumulation of knowledge from
multiple studies.
Our study is designed to examine how the presence of a teacher merit pay program
affects student test scores and whether results vary across design characteristics of the study or
merit pay program. To define the eligibility criteria, literature search, data analysis, and reporting
conventions, we follow the Preferred Reporting Items for Systematic Reviews and Meta-
Analysis standards as defined by Moher et al. (2009).
Eligibility Criteria
Primary studies eligible for inclusion in this meta-analysis needed to meet the following
criteria: (a) the sample is comprised of teachers and students in K-12 education; (b) the teachers
are located in a school, district, state, or country with a teacher merit pay program; (c) the study
reports quantitative student test scores data such as student performance on math and reading
state exams;1 (d) there is a business-as-usual comparison group2; and (e) the study uses a
randomized control trial (RCT) or a quasi-experimental design (QED). We also excluded studies
that compared the effect of getting a bonus against failing to get a bonus (e.g., Jinnai, 2016).
Literature Search. We obtained primary studies from searching 20 commonly used
economic and general social science databases, including ERIC, WorldCat, ProQuest, JSTOR,
NBER and EconLit. Through an iterative process, we created the following search string: teach*
AND (pay OR incentive* OR salar* OR merit OR "performance pay" OR "pay-for-
performance" OR "career ladder"), which returned over 19,000 studies.3 We also searched for
“grey” literature using Dissertation and Thesis Repositories in WorldCat and ProQuest as well as
a general Google search for evaluation reports of well-known merit pay programs such as the
Teacher Advancement Program (TAP) and the Teacher Incentive Fund (TIF). In addition to
searching databases, our literature search also included an examination of reference lists and
1 We excluded studies that reported proficiency rates or percentage pass as their outcome (e.g., Choi (2015);
Dowling, Murphy, & Wang (2007); Ladd (1999) because these outcomes are not comparable to our outcome of
interest: average student test scores.
2 One study (Wellington et al., 2016) falls slightly outside of this scope as the comparison group has three out of
four components of a merit pay program without the merit pay component, but it was included due to its national
scope. The estimates are robust to the exclusion of this study however. Results are available upon request.
3 The numbers of returned results for each database are presented in Supplemental Table S1 (online only). We
should also note that both Google Scholar and JSTOR limited us to reviewing only 1,000 results each even though
more results were returned.
previous reviews of the merit pay literature (Chamberlin, Wragg, Haynes, & Wragg, 2002;
Harvey-Beavis, 2003; Imberman, 2015; Podgursky & Springer, 2007; Podgursky & Springer,
2011; Umansky, 2005; Viscardi, 2012).
We limited our focus to publication dates between January 1989 and October 2016. We
chose 1989 because of its historical importance in the education accountability movement – the
Charlottesville Education Summit where President Bush and most of the nation’s governors met
to outline education goals that shifted national focus to student outcomes rather than education
inputs. We did not limit our search based on language, publication status, or country.
We also included studies conducted outside of the United States (Atkinson et al., 2009;
Contreras & Rau, 2012; Glewwe, Ilias, & Kremer, 2010; Lavy, 2002, 2009; Martins, 2009;
Mizala & Romaguera, 2005; Muralidharan & Sundararaman, 2011; Santibañez et al., 2007;
Woessmann, 2011). Three factors informed this choice. First, almost all investigations in the
current literature on teacher merit pay draws on these international studies to inform their
methods and framing, and these studies are important voices in the academic conversation over
teacher merit pay which should not be ignored when analyzing between-study outcomes.
Second, restricting the sample to only studies in the United States would limit the sample
unnecessarily, reducing statistical power for meaningful analysis. Finally, many of these
international studies were randomized controlled experiments with strong internal validity,
making them high quality estimates of the effects of merit pay.
Studies Meeting Eligibility Criteria. Starting with the results returned from our search
of databases and previous reviews, we used a three-phase process to screen for primary studies
that met all eligibility criteria, as illustrated in Figure 1. First, we read the title, abstract, and
introduction for all studies obtained in our original search. We retained a study if the title,
abstract or introduction mentioned that the study contained empirical results pertaining to the
effect of a merit pay program on student test scores. Some examples of studies excluded in this
phase include qualitative reports describing only perceptions of merit pay, investigations that do
not mention student test scores as an outcome of interest, theoretical works on the application of
merit pay, case studies of fewer than five teachers, studies situated in higher education settings,
and multiple reports that mention merit pay without explicit study of its effects. In total, we
screened 19,908 records.
[Insert Figure 1 Here]
In phase two, we were left with 137 studies for full text reading where two coders
independently assessed whether each study fits the eligibility criteria outlined above. The coders
discussed any discrepancies and made exclusion decisions upon consensus or consulted with the
third author to resolve any discrepancies. Of the 137, we excluded 93 studies due to lack of
relevant student test scores outcomes, non-empirical results, and duplicate reports. For multiple
reports from the same study (e.g., a dissertation and corresponding journal article or reports from
multiple years for the same evaluation), we kept only the most current publication.
In phase three, we contacted authors to request information when eligible studies were
missing key information. We sent e-mails to lead authors requesting information and resent these
e-mails if we did not receive a response within three weeks. We excluded eligible studies if key
information such as standard errors for effect estimates could neither be calculated nor obtained
from the authors. If the standard error or the t statistic was not provided, but the significance
level was indicated, we used a conservative estimate of the standard error by calculating the t
statistics for the p value corresponding to reported significance levels. Further details on how we
calculate standard errors are included in the analysis section below. After screening, we were left
with a sample of 44 primary studies that met all eligibility criteria, 33 of which contained effect
estimates in mathematics and 27 in reading or English language arts.
Coding Reports
Two of the authors independently coded relevant information for each of the 44 eligible
studies using a taxonomy similar to that of Springer and Balch (2010). We describe relevant
items in greater detail below. Any discrepancy was resolved by consensus between the two
coders and remaining disagreements unresolved by consensus were decided by the third author.
Dependent variable. Our main outcomes of interest were standardized regression
coefficients and standard errors from regressing student test scores on an indicator for the
presence of merit pay. This index is interpreted as the average standard deviation unit change in
students’ test scores when their teacher was part of a merit pay program compared to students
whose teacher was not part of a merit pay program. To ensure comparability across studies, we
recorded standard deviations in the outcome measure in order to standardize regression
coefficients when they were not already reported in standardized form. Other coded outcome
characteristics include whether student test scores were measured for math, ELA, or a different
subject, the instrument used to measure student test scores (e.g., state exams), the unit of
analysis, the school level (e.g., elementary, middle, or high school), levels of statistical
significance, t-statistics, R2, sample size, and the covariates in each regression.
Moderating variables. We coded a series of a priori moderators for meta-regression
models where we examined how the effects of teacher merit pay varied by study- and program-
level characteristics. These moderators were selected based on our reading of the literature and
prior work we have conducted on merit pay programs. Specifically, we include the following
variables as moderators: (a) whether the study was an RCT; (b) the country where the study took
place; (c) whether the merit pay was a bonus or salary bracket increase; (d) whether there was
professional development available for the treatment group in addition to merit pay; (e) whether
there was a group incentive at the teacher-team or school level; (f) how long the merit pay
program was implemented; and (g) whether the study was peer-reviewed. We also coded other
study characteristics such as: (a) the identification strategy; (b) whether it was an evaluation of
an existing intervention; and (c) whether pre-treatment equivalence was established between
treatment and comparison groups. Finally, we coded characteristics of the merit pay program
studied in each report including: (a) criteria for receiving an merit pay award; (b) the minimum,
maximum, and average amount of the merit pay received; (c) whether merit pay was one
component of a larger program that includes additional interventions such as teacher training;
and (d) whether the teachers receiving a merit pay award also received recognition in the form of
a public announcement.4
Analytic Strategy
Analysis of these data follow methods as presented by Borenstein, Hedges, Higgins, &
Rothstein (2009). Since most studies reported effect sizes at multiple time points, with multiple
estimation techniques, for different subject areas, and at different levels of analysis, our synthesis
of 44 studies contains 287 effect sizes. Below, we describe analytical decisions in selecting
models, accounting for these multiple within-study outcomes, reconciling studies that use similar
data, and assessing risk of bias from differences in study quality.
One important choice for this meta-analysis was the decision between a fixed-effect
versus a random-effects model. The fixed-effect model assumes a common true effect size across
all studies, whereas the random-effects model allows the true effect size to vary across studies
4 All coded variables and their descriptions can be found in Supplemental Table S2 (online only).
(Borenstein, et al, 2009). Mechanically, the fixed-effect model assigns weights ( to each
study (i) using the inverse of each within-study variance 
In contrast, the random-effects model weights studies using both the within-study variance and
the estimated between-study variance ):
 (2)
For this investigation, a random-effects model is most fitting because substantial
variation exists across studies in terms of intervention characteristics such as the amount of
incentive pay offered, how long the programs were implemented, and the criteria teachers must
meet in order to receive the incentive. Moreover, we do not expect the effect of teacher merit pay
programs to be homogenous across different populations and settings. Below, we also present
quantitative evidence that a random-effects model is more appropriate than the fixed-effect
In order to account for multiple outcomes and time points within a study, we chose not to
treat each within-study outcome as separate, because this method unfairly assigns more weight to
studies with more reported outcomes, and it assumes within-study outcomes are independent. For
example, math and reading scores within a study of teachers in the same district receiving similar
pay incentives will have some amount of correlation. To account for multiple within-study
outcomes, we computed the mean of all outcomes within each study and used this average as the
unit of analysis. To calculate standard errors for each study, we used the variance formula
presented by Borenstein et al. (2009), which has the advantage of taking covariance between
different outcomes (i, j) into account:
One drawback to this variance formula is that it requires correlations between each
outcome, , a measure rarely reported. Without access to this information, we estimate a
correlation of 0.5 between each outcome as a median measure between  0, which will
certainly underestimate the variance, and  1, which will overestimate the variance. We also
check this variance at different correlations below. Our results are fairly robust across a wide
range of .
An alternative method is to use a robust variance estimation to account for the non-
independence of effect sizes (Hedges et al., 2010). This method adjusts the standard errors to
account for the shared variance due to the study-level characteristics for a given value of , the
expected correlation among the dependent effects. Following Tanner-Smith and Tipton (2013),
we tested values of ranging from 0 to 0.9 in increments of 0.1. The results using robust
variance estimation are similar across different values of and the point estimate and standard
error is the same as the our estimate with  0.5 to the third decimal place. However, a
drawback of robust variance estimation is that traditional measures of heterogeneity such as I2 or
Q are not available for analysis. Consequently, we use the variance formula presented in
Borenstein et al. (2009) as the main analytical technique.
Our search strategy sometimes yielded multiple policy reports and research articles
studying the same merit pay program. To avoid overweighting results from almost identical data,
we only kept the most recent results if multiple versions of a study were published by the same
authors. If different groups of researchers investigated the same merit pay program and its effects
on the same sample of students in overlapping years, we averaged their results, giving each study
equal weight. Following this method, we averaged together four primary studies utilizing data
from the School-wide Performance Bonus Program (SPBP) in New York City Public Schools.5
Also, two reports evaluated the Teacher Advancement Program (TAP) in the same district with
overlapping time periods and were also averaged together.6 After combining these reports, we
were left with a final analysis sample of 40 studies.7
Risk of Bias Analysis
The process of selecting studies for a meta-analysis presents a number of challenges, with
competing schools of thought on the optimal approach. The selection process is important
because inclusion or exclusion of studies determines the scope and validity of meta-analytic
results. We opted to use an inclusive approach which may make the comparison and synthesis of
studies questionable given that studies included in the analysis are decidedly different and poorly
produced studies may inject considerable bias. To address this concern, we consider two separate
approaches: the critical evaluation approach as defined by Lam and Kennedy (2005) and the
quality rating approach as defined by Lipsey and Wilson (2001).
In the critical evaluation approach, each study included in our review was given a score
from 0 to 15 based on the number of minimum quality criteria met. Table 1 presents the fifteen
quality criteria. We included only studies with a threshold score of 13 or higher out of 15 and
then compared whether our summary effect including all studies differed from our estimate when
we included only studies meeting the minimum quality threshold.
[Insert Table 1 Here]
5 The four reports/articles on SPBP include Fryer (2013), Goodman & Turner (2011) Marsh et al., (2011), and
Springer & Winters (2009).
6 The two TAP reports include Schacter & Thum (2005) and Schacter, Thum, Reifsneider, & Schiff (2004).
7 The results remain qualitatively and quantitatively similar if we treat these reports as individual studies. For the
remainder of this paper, we refer to 40 “studies” as our primary analysis sample, recognizing that one such “study”
is an average of four reports or articles on SPBP and another is an average of two reports on TAP.
In the quality rating approach, each of the study authors independently rated each study
holistically using our professional judgment of the quality of the study on a scale of 1 to 5 where
1 has high risk of bias and 5 has low risk of bias. Table 1 also presents some criteria we
considered when determining our ratings. After independently rating each study, we discussed
our individual scores until we obtained consensus on a final quality rating for each study. We
note that the vast majority of our independent quality ratings were either exactly the same or
differed by one point. There were two cases where the independent ratings differed by two points
for two observers, but differences were not due to disagreements about quality of analysis;
rather, they were due to differences in how strongly we believed the primary studies’ argument
that their sample of teachers working under merit pay programs were comparable to the
comparison group teachers. Our individual ratings never varied by more than two points.
Our goal was twofold. First, we analyzed the extent to which teacher merit pay affects
student test scores. Second, we investigated how the results vary across both study- and program-
level characteristics. In this section, we present our findings on how merit pay is associated with
student test scores, how results vary across study and program characteristics, and whether the
effect estimates are robust to different decision rules. We conclude with a qualitative
presentation of what previous studies have concluded about the effects of merit pay on the
recruitment and retention of teachers.
Table 2 presents descriptive information about primary studies included in the analysis.
Effect sizes ranged from -0.366 to 0.690 with a mean value of 0.084. Approximately 74 percent
of the effect sizes recorded in our review are positive, with one study reporting a significant
negative effect (Martins, 2009).8
[Insert Table 2 Here]
In terms of study characteristics, almost half of the studies are peer-reviewed
publications, where peer-review is defined as the peer-review journal publication process or a
peer-review process at a large research firm. Twenty-five percent of the studies in our sample
used a randomized control study design, most of which were published post-2005. Sample sizes
ranged from 323 to 8,561,194 students or 92 to 43,251 schools with an average sample size of
approximately 594,751 student or 8,254 school observations.
The merit pay treatment duration ranged between one and twelve years with an average
treatment length of approximately four years. The type of awards received by teachers included
gifts, one-time bonuses, and permanent salary increases, ranging in value from approximately
$26 to $20,000 US. The smallest award amounts are from merit pay programs implemented in
developing countries or those programs that offered gifts as awards (Glewwe et al., 2010). About
one in five of the primary studies evaluated a merit pay program with a job-training component,
a feature that has become a requirement of the federal Teacher Incentive Fund program.
Effect of Merit Pay on Student Test scores
Table 3 presents random-effects estimates of the association between the presence of a
teacher merit pay program and student test scores for all studies meeting our inclusion criteria.
As reported in Panel B, the overall effect estimates indicate that, on average, teacher
participation in a merit pay program was associated with a 0.052 standard deviation increase in
student test scores and a fairly precise standard error of 0.008, with lower and upper bound
8 Martins explains the negative finding by stating that the results “are consistent with incentives-related disruption in
collaborative work in schools” (p. 17), suggesting that pay incentives led to decreased student test scores because the
competition for bonuses had adverse effects on collegial support among teachers.
estimates of 0.037 and 0.068, respectively. Based on empirical benchmarks established by Hill
and colleagues (2008), an effect size of 0.052 is roughly equivalent to 4 additional weeks of
learning assuming a standard deviation of 0.40 per year and 36 weeks in a school year. When we
subset our analysis to only studies conducted in the United States, the summary effect estimate
decreases to 0.035, or about 3 additional weeks of learning, but remains significant. While we
believe the strong internal validity of international studies warrant their inclusion, the subset of
studies conducted in the U.S. contains less variation in economic and social contexts, and we
continue to find evidence of significant effects. The smaller summary effect size suggests that
merit pay may have a smaller influence in U.S. schools compared to other countries and
illustrates how implementation of merit pay can vary depending on school context.
[Insert Table 3 Here]
We also produce estimates by two subject areas most reported in the literature,
mathematics and reading/English language arts (ELA). We find that, on average, the influence
of merit pay on student test scores is relatively similar across the two subject areas. The average
effect for math and ELA test score outcomes are 0.066 and 0.037, respectively. These estimates
are not statistically different from the overall effect.
The random-effects model is the most conceptually appropriate model due to substantial
variations across studies in terms of study- and program-level characteristics. However, we also
present empirical evidence that a random-effects model is more appropriate than a fixed-effect
model. Panel B of Table 2 includes three statistics relevant to the heterogeneity of study effects
for both the main effect and by subject. The proportion of observed variance that reflects true
heterogeneity in effect sizes (I2) is 89.564, indicating that less than 11 percent of the total
variation can be attributed to random error. Cochrane’s Q statistic, which is a classical measure
of heterogeneity used in the meta-analytic literature, tests the null hypothesis of homogeneity
across studies. With a less than .001, we find evidence to reject the null hypothesis that the
true dispersion of effect sizes is zero. In other words, effect sizes are heterogeneous across
studies. Relatedly, the estimated variance of the distribution of true effect size parameters across
studies () is 0.001, suggesting a tight distribution of effect sizes across studies. Together,
these three measures suggest that there is heterogeneity in effect sizes, justifying the random
effects model; however, the effects from different studies are not widely dispersed.
Moderators of the Effect of Merit Pay on Student
While our results indicate that merit pay has a modest, statistically significant effect on
student test scores, these estimates vary depending on the context and implementation of the
incentive program. To illustrate, Figure 2 presents a forest plot of the overall random-effects
model. Each row represents a primary study in our meta-analysis, plotted according to the
standardized effect estimates, or roughly the difference between the average score of students
enrolled in a classroom taught by a teacher eligible for merit pay and the average score of
students in the control or comparison condition used by the study authors after controlling for
various student, teacher, and school characteristics. The dotted vertical line intersecting with the
black diamond at the bottom of the graph shows the average effect size across all 40 studies,
assuming a correlation of 0.05 between multiple within-study outcomes.
[Insert Figure 2 Here]
We explore how these results vary across both study- and program-level characteristics
using a number of potential moderators of the effect of merit pay on student test scores. Study-
level characteristics include whether the study was peer-reviewed or randomly assigned units to
a control or treatment condition. Program-level characteristics include whether the incentive
structure was a rank-order tournament, rewarded teachers at the group level, or included merit
pay plus some other reform component such as job training. As displayed in Table 4, we find
that peer-reviewed studies and studies employing a randomized research design have slightly
larger effects than those reported for the complete sample. In terms of program-level
characteristics, we find that incentive pay programs employing a group incentive design produce
an effect over two times the average study in our sample (0.111 vs. 0.052), which lends support
to the shared nature of teaching and learning hypothesis. Interestingly, the studies conducted on
merit pay programs that include an on-the-job training component show no statistically
significant difference in effect.
[Insert Table 4 Here]
Sensitivity and Robustness Checks
We examine the robustness of our findings to a number of common threats identified in
the meta-analytic literature, including publication bias, risk of bias, non-independence of effect
sizes, and the unit of analysis used in the evaluation of the merit pay program.
Publication Bias. A common threat in the meta-analytic literature is publication bias.
That is, the literature included in our study may be systematically unrepresentative of the true
population of completed studies on merit pay. To explore this threat, Figure 3 presents a
contour-enhanced funnel plot, which is designed to aid in differentiating asymmetry due to
publication bias from that due to other factors. The contour overlay shows if studies appear to be
missing in areas of statistical non-significance (the area inside the inner most funnel) or in the
areas of higher statistical significance (the area outside the inner funnel). If studies are missing
in areas of statistical non-significance, this adds credence to the possibility that the asymmetry is
due to publication bias. Studies missing in the area of high statistical significance suggest the
cause of the asymmetry may be more likely due to factors other than publication bias, such as
variable study quality. Asymmetry to the left or right of the center indicates that studies are
systematically more likely to have found either negative or positive results, respectively.
[Insert Figure 3 Here]
Figure 3 provides no evidence that our analysis lacks small studies with small effect
sizes. However, there is asymmetry due to a lack of negative effect sizes in studies with “large
N”. In other words, our large N studies tended to have positive effect sizes, showing some
evidence that studies with significant results are more likely to be reported.
While these tests suggest a possible bias where null results are not published, we argue
that the extent of bias is not large for the sample of studies we wish to investigate. First, there is a
high concentration of studies around the zero effect estimate that are precisely measured.
Second, we adopted an exhaustive and relatively inclusive literature search process. Meta-
analyses often exclude non-journal publications such as research reports and program
evaluations. The presence of these types of studies in our analytic sample helps rule out the
possibility of insignificant or unfavorable results being excluded from our analytic sample.
Third, Egger’s test for asymmetry of the funnel plot indicates there is no bias from smaller
studies with small effects.9 Rather, the asymmetry is coming from studies with larger sample
sizes and modestly larger effect estimates.
Moreover, most studies included in this review have relatively large sample sizes with
about 70 percent containing sample sizes larger than 10,000 students. We argue that these types
of large-scale studies are likely to be published even if they had found null effects, because they
have important implications for researchers and policy-makers thinking about merit pay
9 We selected the Egger et al. approach over other strategies given that the Begg method has very low power to
detect biases (Sterne, Gayaghan, & Egger, 2000) and we have a number of imbalances in control and treatment
sample sizes due to the non-experimental nature of many studies included in our review.
programs. Indeed, several large randomized control trials did publish null results (e.g., Fryer,
2013; Springer et al., 2011). Any concern that effect sizes are larger in smaller studies is driven
mostly by one study (Atkinson et al., 2009) with a larger effect (0.690) and relatively small
sample size (181), but this study is given very little weight in our model. Consequently, we do
not believe publication bias is a serious threat to the findings reported.
Risk of bias. Table 5 presents results from our risk of bias analysis using both the critical
evaluation approach and the quality rating approach. Our critical evaluation approach rated each
study from zero to fifteen based on the number of quality criteria met. Studies meeting our
inclusion criteria received a rating of thirteen or above. In total, 36 of 40 studies met the
inclusion criteria and, as displayed in Table 5, our point estimates are very similar to the
estimates for the complete sample (0.043 and 0.052, respectively), suggesting the risk of bias
from study selection criteria is low. Using the quality rating approach, we assigned each study a
rating of one (high risk of bias) to five (low risk of bias) and included only studies with a rating
of four or above. As displayed in Table 5, 18 of 40 studies received a quality rating of four or
five, and the results indicate that our findings do not change substantially when we drop the high
risk of bias studies from our analysis.
[Insert Table 5 Here]
Unit of Analysis. Table 5 also presents summary effects based on the unit of analysis,
either at the school-level or the student-level. There are 9 studies at the school-level, 29 studies at
the student-level, and 3 studies at the teacher/grade-level.10 A concern in pooling these studies
together is that there may be large differences between the summary effects for the different
units of analysis. The results in Table 5 show that the summary effects at the school- and student-
10 When the four reports on the SPBP experiment were averaged together, the aggregated group of studies contained
both student-level and school-level outcomes, resulting in 41 effect estimates for this analysis.
level are both positive and statistically significant. The summary effect at the school level is
larger, at 0.066 compared to 0.051 at the student level, and there is substantial overlap in the 95
percent confidence intervals of the estimates at the school- and student-level. Consequently, we
pool these studies together instead of doing separate analyses where the limited sample size
would lead to imprecise estimates.
Non-independence of effect sizes. Another threat to the validity of meta-analytic results
is the non-independence of effect sizes within studies (recall that our analysis relies on a total of
287 within-study effect estimates). To address this concern, we estimate the overall summary
effect for a range of correlations between multiple within-study outcomes, . Figure 4a shows
the summary effect ranges from 0.069 to 0.046 for  of 0 and 1, respectively, at intervals of 0.1.
Additionally, as displayed in Figure 4b, when robust variance estimation is used, the summary
effect is tightly bounded around 0.051 for a range of ranging from 0 to 0.9 at intervals of 0.1.
Altogether, using an of 0.5 in estimating the summary effect appears reasonable, and results
are robust across different values of .
[Insert Figure 4 Here]
Summary of Literature on the Effect of Merit Pay on Teacher Retention
Theories of personnel economics suggest that merit pay can improve the composition of
the workforce through the attraction and retention of high performing teachers. While this is a
primary mechanism through which merit pay programs may realize their intended purpose of
improving student outcomes and learning opportunities, the vast majority of primary studies
included in our analysis did not focus on teacher attrition. This is problematic because teacher
attrition is an important outcome for districts and policy makers; and if teacher attrition is high,
the effect of merit pay on student test scores may be driven by the effectiveness of the teachers
who remain relative to the effectiveness of new teachers or substitute teachers replacing the
teachers who left. High teacher attrition due to merit pay programs could then have adverse
unintended consequences for schools and districts because there is high cost associated with
recruiting and training new teachers.
The limited number of primary studies on how merit pay teacher is associated with
teacher turnover precludes a full meta-analysis, but we gathered fifteen studies investigating
teacher labor market outcomes. Table 6 shows that six of these studies found mostly significant
positive effects on teacher retention or recruitment (Booker & Glazerman, 2009; Clotfelter,
Glennie, Ladd, & Vigdor, 2008; Cowan & Goldhaber, 2015; Fulbeck, 2014; Glazerman et al.,
2013; Springer et al., 2010). Seven of these studies show some positive results but the findings
were inconsistent (Choi, 2015; Glazerman & Seifullah, 2012; Hough, 2012; Springer, Lewis, et
al., 2009; Springer, Podgursky, et al., 2009; Springer et al., 2015; Steele et al., 2010). Finally,
two studies found mostly insignificant effects (Dee & Wyckoff, 2015; Fryer, 2013).
[Insert Table 6 Here]
While we are wary of relying on these vote-counting methods to summarize significant
study effects, these studies offer preliminary signs that merit pay programs have the potential to
decrease overall teacher turnover and increase recruitment to high poverty schools. Many of
these studies found positive effects at least while the merit pay program was in operation and
suggest that positive results are most consistent among teachers who are actually eligible to
receive the award. For example, Cowan and Goldhaber (2015) found that the Challenging
Schools Bonus increased the proportion of targeted National Board Certified teachers in high
poverty schools, but overall turnover rates remain unchanged. It is unclear whether the effects of
merit pay in these studies persist over time with some researchers finding significant effects only
in the first few years of program implementation (Glazerman & Seifullah, 2012; Springer, Lewis,
et al., 2009) and others finding effects only when schools have implemented merit pay for
several years (Choi, 2015). Many questions remain, such as whether merit pay can attract and
retain relatively more effective teachers, and we urge investigators to further explore how merit
pay affects teacher recruitment and retention.
Our meta-analysis investigates primary studies that report on the effect of merit pay on
student test scores. Overall, we find a modest, statistically significant positive association (0.052
standard deviations) between teacher merit pay programs and student test scores. In substantive
terms, the effect is roughly equivalent to 4 additional weeks of learning.
Theoretically, merit pay has the potential to improve student test scores by either
motivating teachers to improve their performance or by attracting and retaining more effective
teachers. However, several previous large-scale empirical studies, especially randomized
controlled experiments, which examined the effects of merit pay have resulted in null effects on
student test scores (e.g., Fryer, 2013; Springer et al., 2011; Springer et al., 2012). Our review
broadens this perspective by including studies conducted outside the United States, reports
evaluating programs where merit pay is part of a larger intervention that may include teacher
training, and unpublished dissertations and theses. We acknowledge that our inclusive approach
may have resulted in the inclusion of less methodologically rigorous studies, but our results are
robust to the exclusion of lower quality studies. Indeed, we find that aggregating results from
multiple studies across different cultural, economic, and political contexts suggests that incentive
pay, as argued by merit pay advocates, offers a promising strategy to improve student test scores.
We find that the effects of merit pay programs are sensitive to how the program has been
designed and implemented. Therefore, the more pertinent question may be how merit pay
programs should be designed if positive effects are detected in some contexts while null or even
negative effects are detected in others. Our evidence, for example, suggests that group incentives
result in larger positive effects on average than incentives given to individuals. Numerous other
design questions deserve further exploration. Incentives accompanied by school-wide public
announcements (Glewwe et al., 2010), incentives making use of loss aversion (Fryer, Levitt,
List, & Sadoff, 2012), and incentives awarded based on sophisticated composite evaluative
criteria (Dee & Wyckoff, 2015) have been explored by different researchers and shown to have
positive effects. We advise continued study into whether the effects of these various program
features vary across different contexts as incentive pay program design can take on a number of
different forms with differing tradeoffs (Barlevy & Neal, 2011; Neal, 2010; Springer & Balch,
2010; Springer, 2012; Ritter & Barnett, 2013).
Other relevant program features which we lacked the information to investigate more
deeply include the amount of pay, how long the program has been implemented, and whether
school staff are well informed about the program’s guidelines. The latter proved salient in the
recent national impact evaluation of the Teacher Incentive Fund where approximately 40 percent
of treatment teachers were unaware they were eligible for a bonus (Wellington et al., 2016). We
suggest more explicit attention to these types of program features in future research in order to
further elucidate how different program features could result in different outcomes.
Finally, this meta-analysis contributes another step toward understanding the different
motivational aspects of compensation as grounded in the general personnel economics literature.
Primary studies in our sample often suggest that merit pay encourages teachers to increase their
effort, a pathway well supported by principal-agent theory. Indeed, when aggregating these
studies together, our evidence supports the notion that opportunities to earn pay incentives can
lead to improved test scores, perhaps through some increased teacher effort (or, nefariously,
gaming of the performance measure system). We note that our study is specifically focused on
incentivized outcomes: student test scores. While a sensible goal of any incentive program
should be to bring about direct improvements to the targeted outcome, increased teacher effort
could feasibly improve other student outcomes (e.g., alternative tests, attendance, students' self-
confidence). Future evaluations of merit pay programs should pay closer attention to these
alternative outcomes.
Teacher recruitment and retention, however, is another theoretically supported pathway
through which merit pay can affect student test scores. Our qualitative review of the emerging
literature on this pathway suggests that the positive effect reported in our primary studies may
partly be the result of lower levels of teacher turnover. Certainly, some studies find that pay
incentives have the potential to increase teacher recruitment to high-need schools, and decrease
attrition. We highly suggest continued investigation into teacher labor market outcomes,
especially into the effects of pay incentives on the mobility patterns of highly effective teachers
and the exit decisions of traditionally low-performing teachers. Regardless of the outcome, our
study exposes the sensitivity of effect sizes to program design and study context, and we urge
researchers and policy-makers to pay careful attention to these features when evaluating the
effectiveness of incentive pay programs.
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* denotes primary studies used in meta-analysis
Table 1
Quality Criteria for Assessing Risk of Bias
Critical Evaluation Criteria Quality Rating Considerations
Was the intervention clearly defined? Was the study a randomized control trial?
Were the research question(s) for this study
clearly stated, and did the subsequent
investigation answer the question(s)?
Was implementation fidelity measured and
adequately described, and what are the
implications of implementation fidelity on
Did the study provide a clear review of prior
research? What are the relative strengths of the study
Were the inclusion and exclusion criteria for
being in the study specified and applied
uniformly to all participants?
Was the analytic approach adequately
described, and what are the relative merits of the
approach used?
Was a sample size justification or power
description provided? Was the comparison condition adequately
described, and does the comparison group
provide a reasonable counterfactual?
Did the study clearly define a control or
comparison condition? Were threats to internal and external validity
considered and addressed?
Did the analytic strategy adjust statistically for
confounding variables? Were findings robust to different analytical
decisions and model specifications?
Was the analytic strategy clearly defined and
appropriate for answering the stated research
Was baseline equivalence established
between treatment and comparison groups?
(This is unnecessary for some approaches such
as the difference-in-difference design.)
Did the study include additional analyses
(robustness/sensitivity checks) and subgroup
analyses or adjust analyses?
What sampling decisions were made by the
authors and did the analytic sample present any
concerns to internal or external validity?
Were the outcome measures clearly defined,
valid, reliable, and implemented consistently
across study participants?
Was the timeframe sufficient so that one could
reasonably expect to see an association between
exposure and outcome if it existed?
Did the study contain specific objectives or
Was the study population clearly specified
and defined?
Did the authors address study limitations,
sources of bias, impressions and, if relevant,
other limitation such as multiplicity of analysis?
Was the interpretation of results consistent
with estimates, and did the author consider other
relevant evidence?
Note: In the critical evaluation approach, studies meeting 13 out of 15 criteria were considered low risk of bias. In
the quality rating approaching, studies with a rating of four or five out of five were considered low risk of bias.
Table 2
Descriptive Information on Primary Studies by Study and Program Characteristics
Full Sample Randomized
Control Trial U.S. Only
Study Characteristics
Publication year 1997-2016 2004–2015 1997-2016
Peer reviewed 45% (18 studies) 50% (5 studies) 36% (10 studies)
Randomized control trial
design 25% (10 studies) 100% (10 studies) 25% (7 studies)
Average Sample Size
594,751 students
9,254 schools
14,024 students
6,406 schools 737,474 students
5,641 schools
Range of Sample Size 323-8,561,194
92-43,251 schools
297-8442 schools
92–40,393 schools
Program Characteristics
Range of treatment
duration 1–12 years 1–4 years 1–12 years
Range of award receipt $26 – $20,000 $169 – $15,000 $200 – $20,000
Rank-order tournament 25% (10 studies) 20% (2 studies) 13% (5 studies)
Group incentive structure 33% (13 studies) 60% (6 studies) 29% (8 studies)
Merit pay + other 43% (17 studies) 10% (1 studies) 57% (16 studies)
Merit pay + training 18% (7 studies) 10% (1 study) 21% (6 studies)
Public announcement of
results 3% (1 study) 0% (0 studies) 0% (0 studies)
Award type Gifts, one time
bonuses, and salary
One time bonuses
and salary increases One time bonuses
and salary increases
Number of Studies 40 10 28
Note: Merit pay + other refers to whether merit pay was implemented in conjunction with other reforms such as
additional training. Merit pay + training refers to merit pay program that was implemented in conjunction with a
training/professional development component. The full sample of 40 “studies” includes one that is an average of
four reports or articles on the School-wide Performance Bonus Program and another that is an average of two
reports on the Teacher Advancement Program. The percentages shown represent the percent of studies within each
Table 3
Meta-Analytic Results of the Effect of Merit Pay on Student Test Scores
Model Panel A: Main effect estimates Panel B: Heterogeneity of study
N Effect
Estimate Standard
Error Lower
Bound Upper
Bound I2 T
2 Cochrane
Overall Effect
subjects 40 0.052 0.008 0.037 0.068
89.564 0.001 373.696 <.001
only 28 0.035 0.007 0.021 0.050
88.554 0.001 235.890 <.001
By Subject
Math 33 0.066 0.009 0.048 0.084
92.830 0.002 446.304 <.001
ELA 27 0.037 0.007 0.022 0.051
88.782 0.001 231.779 <.001
Note: Assumed correlations between multiple, within-study outcomes is 0.5. Not all studies presented results
separated by subject.
Table 4
Meta-Analytic Results of Moderators of the Effect of Merit Pay on Student Test Scores
Panel A: Main effect estimates Panel B: Heterogeneity of study effects
N Effect
Error Lower
Bound Upper
Bound I2 T
2 Cochrane
Overall Effect
All subjects 40 0.052 0.008 0.037 0.068 89.564 0.001 373.696 <.001
By Study Characteristics
Peer-reviewed 18 0.106 0.017 0.072 0.140 87.412 0.004 135.045 <.001
Randomized 12 0.074 0.019 0.036 0.112 76.131 0.003 46.084 <.001
By Program Characteristics
Group incentive 13 0.111 0.027 0.058 0.164 94.776 0.007 229.704 <.001
tournament 10 0.063 0.027 0.010 0.115 91.438 0.005 105.118 .019
Merit pay+other 17 0.044 0.009 0.026 0.061 77.416 0.001 70.847 <.001
Merit pay+training 7 0.041 0.023 -.004 0.086 73.968 0.002 23.048 .076
Note: Assumed correlations between multiple, within-study outcomes is 0.5. Merit pay + other refers to whether merit pay
was implemented in conjunction with other reforms such as additional training. Merit pay + training refers to merit pay
program that was implemented in conjunction with training/professional development component.
Table 5
Risk of Bias and Unit of Analysis
Model Panel A: Main effect estimates Panel B: Heterogeneity of study effects
N Effect
Estimate Standard
Error Lower
Bound Upper
Bound I2 T
2 Cochrane
Main Effect
All 40 0.052 0.008 0.037 0.068 89.564 0.001 373.696
Risk of Bias
Critical evaluation
approach 36 0.043 0.007 0.029 0.058 89.121 0.001 321.716 <.001
Quality rating
approach 18 0.057 0.015 0.027 0.086 86.584 0.003 126.717 <.001
Unit of Analysis
School level 9 0.066 0.024 0.019 0.114 86.630 0.004 59.835 <.001
Student level 29 0.051 0.010 0.031 0.072 90.067 0.002 281.899 <.001
Note: Assumed correlations between multiple, within-study outcomes is 0.5. Not all studies presented results separated by
Figure 1. Flow diagram depicting the literature screening process resulting in the final sample of
primary studies included in the quantitative analysis. Adapted from Moher et al. (2009).
Full-text articles excluded,
with reasons
(n=10 , no incentive
(n=12, missing information)
(n=10, poor methodology, no
valid comparison group)
(n=27, no student
achievement data)
(n=12, early draft of final
(n=22, teacher retention and
miscellaneous reasons)
Studies included in
quantitative synthesis
(n = 44)
Full-text articles
assessed for eligibility
n = 137
Records excluded
(n = 19,771)
Records screened
(n = 19,908)
Additional records identified
through other sources
(n = 37)
Records identified through
database searching
(n = 19,871)
Figure 2. Forest plot for overall effect estimates of merit pay programs on student test scores
from primary studies.
Figure 3. Contour enhanced funnel plot with one effect estimate per primary study
Figure 4. Sensitivity of overall effect estimate to (A) Different correlations between multiple
within-study outcomes (
and (B) Different correlations ( using robust variance estimation
Supplemental Tables
Table S1
Results by Database
Database Results
Directory of Open Access Journal (DOAJ) 5761
WorldCat (incudes dissertation and theses) 3869
Taylor and Francis Online 1463
ProQuest 1378
Wiley Online Library 1102
Google Scholar 1000
JSTOR 1000
SpringerLink 987
ERIC 758
SciVerse Science Direct 681
NBER 357
Web of Science 327
Project MUSE 309
EconLit 208
ProQuest Dissertations and Theses 206
Education Full Text 145
OneFile (GALE) 120
PsycINFO 94
Sociological abstracts 34
Total 19871
Table S2
Coding Guide
Study Characteristics
Variable Description Operationalization
id ID Number assigned to study Continuous
leadauth Name of lead author Nominal
title Title of paper Nominal
yearpub Year paper was published Continuous
pubtype Type of publication (academic journal, policy report,
conference paper, etc.) Nominal
rct Randomized control trial indicator 0, 1
randomized Did this study intend to randomize whether
students/teachers/schools were placed into control vs.
experiment groups?
evaluate Is this study an evaluation of an existing intervention? 0,1
peer review Is the study a peer-reviewed publication? 0,1
working paper Is it a working paper? 0,1
use Is the study based in the U.S.? 0,1
otherctry Name of the country where the study was conducted if
not the U.S. Nominal
state Name of state (if U.S.=1) Nominal
depvar The dependent variable(s) of the study: test score,
teacher value-added scores, teacher attendance, etc. Nominal
design Type of design: pre-post randomized control group,
pre-post nonrandomized, post-test only matched
samples, etc.
confdsgn Coder’s confidence in validity of the design Uncertain,
somewhat certain,
certain (0, 1, 2)
program Name of program/experiment Nominal
lngthrt Length of merit pay program in years Continuous
lvlrandm Level of randomization (district, school, teacher, etc.) Nominal
eqvscores Pre-test score equivalence between treatment and
control 0,1
eqvgrade Grade equivalence between treatment and control 0,1
eqvfrpl Free and reduced price lunch (FRPL) equivalence
between treatment and control 0,1
eqvsubject Academic subject equivalence 0,1
eqvrace Race equivalence between treatment and control 0,1
noneqv List any characteristics that were statistically
significantly different between treatment and control Nominal
confidenceeqv Coder’s confidence in equivalence of the treatment and
control groups Uncertain,
somewhat certain,
certain (0, 1, 2)
component Indicator of whether merit pay was a component of
some larger program, such as a district wide initiative
that also included teacher mentors
district Name of district Nominal
comparison Comparison group (business as usual, BAU, or other
intervention) 1-BAU, 0-Other
gradelvl Grade level of the intervention Categorical
minamnt Minimum amount of merit pay received Continuous
maxamnt Maximum amount of merit pay received Continuous
avgamnt Average amount paid per teacher Continuous
paytype Pay type: bonus, change in salary bracket, gift Nominal
recurring Can a teacher receive the bonus more than once? 0,1
competition Was merit pay a competition such that some teachers
receiving a bonus meant others could not? 0,1
recipient Did the teachers directly receive the pay? 0,1
paycriteria Criteria teachers to receive merit pay: test scores,
observation ratings, multiple evaluative measures, etc. Nominal
publiconly Public school only indicator (1-public only, 0-private
only or both public/private) 0,1
training_received Indicator for whether teachers received any training as
part of the merit pay program 0,1
public_announce When teachers received a merit pay incentive was
there a public announcement for the bonus winners? 0,1
groupincentive Did the teachers receive incentives as part of a group? 0,1
Study Outcomes
Variable Description Operationalization
year Year(s) in which study was conducted Continuous
outcometype Test score or pass rate Nominal
math Outcome is math test scores 0,1
reading Outcome is reading/ELA test scores 0,1
schlevel School level: elem, ms, hs, k-8 Categorical
lvlmeasure Level of measure: student, school, or teacher Nominal
instrument Name of test administered to students (e.g., Iowa Test
of Basic Skills) Nominal
sig10 Outcome is significant at 10% level 0,1
sig5 Outcome is significant at 5% level 0,1
sig1 Outcome is significant at 1% level 0,1
method Analytical design (e.g., OLS, RD, Diff in Diff, IV) Nominal
standardized Were the coefficients standardized? 0,1
sd Standard deviation of the dependent variable Continuous
beta Regression coefficient from regressing outcome on
merit pay Continuous
stdbeta Standardized beta coefficient Continuous
avgbeta Average if multiple standardized beta coefficients are
reported from in one study
se Standard error of beta coefficient Continuous
stdse Standard error of standardized beta coefficient Continuous
stdvar Standardized variance (stdse squared) Continuous
tstat t statistic if reported Continuous
r_sq if reported Continuous
samplesize Sample size Continuous
avgsamplesize Average sample size if multiple outcomes are reported Continuous
prevscores Lagged dependent score if included in regression 0,1
frpl Binary indicator if FRPL was included as covariate 0,1
sped Binary indicator if SPED was included as covariate 0,1
lep Binary indicator if LEP was included as covariate 0,1
pct_frpl Binary indicator if % FRPL was included as covariate 0,1
pct_sped Binary indicator if % SPED was included as covariate 0,1
pct_lep Binary indicator if % LEP was included as covariate 0,1
notes Additional notes about the study Qualitative notes
ResearchGate has not been able to resolve any citations for this publication.
This paper examines the role of worker performance feedback and measurement precision in the design of incentive pay systems, specifically in the context of an individual teacher value-added merit pay tournament. We first build a model in which workers use proximity to an award threshold to update their beliefs about their own ability, which informs their expected marginal return to effort. The model predicts that effort will be maximized at some point proximal to but above the award threshold in order to maximize the likelihood of winning an award when effort translates into value-added with noise. As the noise in the value-added measure increases, teacher effort becomes less responsive to prior value-added because the value-added score becomes a less reliable measure of ability. Using administrative teacher-student linked data from Houston, we test the central prediction of the model that there should be excess achievement gains near award thresholds. The data strongly reject the existence of such excess gains. We argue that a likely reason for this lack of responsiveness is that the value-added measures used to determine awards were too noisy to provide informative feedback about one's ability.
Pay-for-performance is a popular public education reform, but there is little evidence about the characteristics of a well-designed incentive pay plan for teachers. Some of the literature suggests that effective incentive plans must offer relatively large awards to induce behavioral changes. On the other hand, the experimental economics literature suggests that plans with only a handful of awardees can be less effective at changing behavior than plans that offer an array of possible awards. Still other research suggests that group-based incentives are the most effective strategy when teamwork and cooperation are integral to the production process—as is arguably the case in education. This study takes advantage of a pilot pay-for-performance program in Texas to explore incentive design not only from the perspective of the employer—by examining changes in teacher productivity and retention—but also from the perspective of the employee—by examining the preferences revealed by the incentives teachers design for themselves. We find that when given the opportunity, teachers design relatively weak, group-oriented incentive pay plans. In turn, those relatively weak incentives do not appear to be associated with any significant changes in teacher productivity, although they are correlated with teacher turnover, which, in the long run, could theoretically improve student outcomes.
Full-text available
Systematic reviews should build on a protocol that describes the rationale, hypothesis, and planned methods of the review; few reviews report whether a protocol exists. Detailed, well-described protocols can facilitate the understanding and appraisal of the review methods, as well as the detection of modifications to methods and selective reporting in completed reviews. We describe the development of a reporting guideline, the Preferred Reporting Items for Systematic reviews and Meta-Analyses for Protocols 2015 (PRISMA-P 2015). PRISMA-P consists of a 17-item checklist intended to facilitate the preparation and reporting of a robust protocol for the systematic review. Funders and those commissioning reviews might consider mandating the use of the checklist to facilitate the submission of relevant protocol information in funding applications. Similarly, peer reviewers and editors can use the guidance to gauge the completeness and transparency of a systematic review protocol submitted for publication in a journal or other medium.
Full-text available
We report findings from a quasi-experimental evaluation of the recently implemented US$5,000 retention bonus program for effective teachers in Tennessee’s Priority Schools. We estimate the impact of the program on teacher retention using a fuzzy regression discontinuity design by exploiting a discontinuity in the probability of treatment conditional on the composite teacher effectiveness rating that assigns bonus eligibility. Point estimates for the main effect of the bonus are not different from zero. However, for teachers of tested subjects and grades, the program has a consistently positive effect that is both statistically and substantively significant. We hypothesize that the null finding for the main effect is driven by teachers of untested subjects and grades given the amount of weight Tennessee’s teacher evaluation system attributes to school-level performance. This creates a strong incentive to exit the Priority Schools that are by definition low performing. Implementation concerns, including the timing of application process and observed noncompliance in bonus distribution, present obstacles for both the program’s effectiveness and its evaluation.
Full-text available
This article presents findings from the first independent, third-party appraisal of the impact of the Teacher Advancement Program (TAP) on student test score gains in mathematics. TAP is a comprehensive school reform model designed to attract highly effective teachers, improve instructional effectiveness, and elevate student achievement. We use a panel data set to estimate a TAP treatment effect by comparing student test score gains in mathematics in schools that participated in TAP with student test score gains in non-TAP schools. Ordinary least squares estimation reveals a positive TAP treatment effect on student test score gains in the elementary grades, with weaker but still positive point estimates in the secondary grades. When estimation methods control for selection bias, the positive effect remains at the elementary level, but most estimates for grades 6 through 10 turn negative. Our findings are qualified by the lack of information on the fidelity of implementation across TAP schools and on variation in features of TAP programs at the school level.
This paper studies the impacts of teacher pay-for-performance (P4P) reforms adopted with complementary human resource management (HRM) practices on student achievement and workforce flows. Since 2005, dozens of Minnesota school districts in cooperation with teachers’ unions implemented P4P as part of the state’s Quality Compensation program. Exploiting district variation in participation status and timing, we find evidence that P4P-centered HRM reform raises students’ achievement by 0.03 standard deviations. Falsification tests suggest that gains are causal. They appear to be driven especially by productivity increases among less-experienced teachers.
Extensive teacher mobility can undermine policy efforts to develop a high-quality workforce. In response, policymakers have increasingly championed financial incentives to retain teachers. In 2006, the Denver Public Schools adopted an alternative teacher compensation reform, the Professional Compensation System for Teachers ("ProComp"). Using longitudinal teacher-level data from 2001-2002 to 2010-2011, I estimate hazard models that identify the relationship between ProComp and teacher mobility. Specifically, I compare mobility patterns of teachers who received a ProComp incentive with those who did not, with special attention to teacher mobility in high-poverty schools. Results suggest receiving a ProComp incentive is associated with a significant decrease in the odds of departure. This appears to be driven by a decrease in a teacher's odds of leaving the district rather than moving to a new school within the district, by voluntary ProComp participants and by teachers who receive incentives that total more than $5,000.
IntroductionIndividual studiesThe summary effectHeterogeneity of effect sizesSummary points