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Federal Reserve Bank of Chicago

Causality, Causality, Causality:
The View of Education Inputs and
Outputs from Economics
Lisa Barrow and Cecilia Elena Rouse

WP 2005-15

Causality, Causality, Causality:
The View of Education Inputs and Outputs from Economics

Lisa Barrow
Federal Reserve Bank of Chicago

Cecilia Elena Rouse
Princeton University and NBER

November 1, 2005

Prepared for the Consortium for Policy Research in Education, State of Education Policy
Research Meeting, February 14-15, 2005. We thank Brian Jacob, Jesse Rothstein and Diane
Whitmore Schanzenbach for helpful conversations, Helen Ladd and the editors for insightful
comments and Kyung-Hong Park for research assistance. Any errors in fact or interpretation are
ours. The opinions in this paper do not reflect those of the Federal Reserve Bank of Chicago or
the Federal Reserve System.

Introduction
Frustrated with decades of research on education that seemingly amounts to little

accumulated knowledge on how to improve student academic outcomes, policymakers and
researchers are taking stock of what we do and do not know about the effectiveness of
educational inputs.1 As an example, in 2002 the U.S. Department of Education created the
“What Works Clearinghouse” (WWC)—a data base meant to provide educators and
policymakers with a “trusted source” of information on what “scientifically-based” education
research has to say about what works and does not work in education. The fact that the federal
government was willing to spend $18.5 million (U.S. Department of Education 2002) to fund
such an enterprise reflects the view of many that ultimately we know little about which inputs
matter for student success in education.
Why do we seem to know so little? Many economists would argue it is because research
has not emphasized isolating causal relationships between education inputs and student
outcomes (Angrist 2004). Rather, education research has focused on other aspects of the issue,
such as differences across settings, which usually has not been the major concern for researchers
placing a priority on causality.2 If one believes student outcomes are uniquely tied to the
educational setting, then it is fruitless to try to draw general conclusions about the “average
1

We emphasize that “inputs” can be interpreted either narrowly or broadly. District
organization (e.g., primary, middle, high school vs. K-8 and high school) can be interpreted as an
input as can the structure of teacher contracts. Similarly inputs may be defined as class size, text
books, or computers in the class room. We take the broader interpretation but will only discuss
the evidence regarding a few of the thousands of potential inputs to educational outcomes.
2

Of course all researchers attempt to estimate the causal (or unbiased) effect of an input
on educational outcomes. However, all research necessarily demands sacrifice and some
researchers will sacrifice causality rather than not estimate differences across settings; others
would make the opposite decision. We attempt to draw a distinction between these emphases.

effect” of an education input (which, in this view, does not apply to anyone in reality) (Cook
2001).3 However, the WWC as well as many others in the education research field have started
to highlight research that emphasizes isolating the causal relationships between education inputs
and student outcomes. Some refer to this emphasis as on “identification” (i.e., “identifying” the
impact of a particular input as distinct from other factors) or “internal validity” as termed by
Campbell and Stanley (1963).
In this paper we discuss methodologies for estimating the causal effect of resources on
education outcomes; we also review what we believe to be the best evidence from economics on
a few important inputs: spending, class size, teacher quality, the length of the school year, and
technology. In general we conclude that while the number of papers using credible strategies is
thin4, there is certainly evidence that what schools do matters. But, many unanswered questions
remain.

II.

The Theoretical and Empirical Ideal

Economists’ View of Education Resources5
Economists typically analyze a school’s performance and the effectiveness of its inputs

using an “education production function.” The school produces education using inputs and a

See Cook (2001) for a thoughtful discussion of why education research has by-andlarge rejected randomized experiments.
4

For example, in a recent review of curriculum-based interventions to improve middle
school math achievement, the WWC staff found 77 studies. Of these 77 studies only 10
(studying 5 interventions) were found to have met the WWC standards for evidence which place
an emphasis on causal inference (or internal validity).
5

Parts of this section are drawn from Rouse (2005).

production technology. One can then measure the effect of particular inputs on the output
(education), usually for each student. Specifically, one can think of a production function as:

(1)
where Eist represents the output for student i in school s in year t; NSit represents non-school
inputs into student i’s educational attainment, such as her natural “ability,” the extracurricular
inputs provided by her parents (e.g., music lessons, extra tutoring in subjects), parental inputs
(e.g., reading to their children, doing “educationally-rich” activities at home), and her
educational history (that is, her achievement level in 4 th grade is not only a function of her
current school, but also of her schooling in kindergarten, 1 st, 2nd, and 3rd grade)6; Rist represents
the resources under the control of school s in year t (e.g., class sizes, quality of teaching staff,
and the curriculum); Xist represents the school inputs that are not typically under the control of
public schools (e.g., the quality of a student’s “peers”), and e ist is an error term that represents all
of the other “stuff” that is not otherwise represented (e.g., measurement error).7
6

Why do we categorize a student’s educational history as a “non-school” input? Because
we are attempting to distinguish between contemporaneous inputs under the control of the
current school and inputs over which the current school has no control. Obviously, a school
cannot change what happened to a student in the past.
7

Other researchers in the social sciences often represent this educational production
function using hierarchical linear models (HLM) in which they explicitly account for more of the
organizational structure, i.e., schools are made up of classes which are made up of individual
students (Bryk and Raudenbush 1992). We address issues of identifying causal relationships in
the framework commonly used in economics rather than in HLM; however, the issues of
identification discussed below are also relevant to identification in the HLM framework. While
HLM models allow for more nuanced and structured modeling of the parameters and error term,
whether the coefficient estimates are unbiased continues to rest on whether the covariates
included in the regression fully account for all confounding factors that might affect student
achievement and are correlated with the school input in question. In this regard, HLM is similar
to OLS estimation discussed below.

The function, f, represents the “production function” or the educational practices that
transform the inputs into what a student actually learns. The formulation of the education
production function depicted in equation (1) also highlights some of the issues that complicate
the design of methodologies for estimating the effectiveness of specific school resources—few
of the measures that one would ideally include are observable. Take, for example, educational
output, Eist. We rely on our schools to help children learn academic subjects as well as to help
them become full-functioning, happy adults by teaching democratic values, responsibility,
cooperation, consideration, and other aspects of working well with others.8 As such typical
outcomes (such as test scores or labor market wages) clearly reflect only part of what we expect
from schools. Further, standardized tests do not fully reflect the academic achievement of
students. They typically focus on only a few subjects, and in order to keep the testing affordable
and not-too-intrusive, are relatively short and mostly rely on multiple choice questions (which
are less costly to score). Thus, tests generally provide incomplete and noisy measures of
educational output which make it much harder to detect the effectiveness of inputs.9
Because of non-school factors and other inputs beyond the school’s control, one cannot
easily generate a causal estimate of the effect of school quality on outcomes.10 For example, the
8

That said, in this paper we often refer to the educational output as “student
achievement” for ease of exposition.
9

More formally, a noisy measure of educational output (the dependent variable in a
regression model) will increase the residual variance which will increase the size of the standard
errors. As such, one will be less likely to reject the null hypothesis that an input has no effect on
student outcomes.
10

In this regard, while economists refer to equation (1) as a production function, in many
respects it is not. In order to truly recover the parameters of a production function one would
need to hold everything else constant. Thus, if one were studying the effect of lowering class
size on a student’s achievement, one would require that all other educational inputs, such as

test scores of more disadvantaged students (in School A) will likely be lower than the test scores
of more advantaged students (in School B). If the quality of school resources in each school is
correlated with the socioeconomic status of the students, it will be difficult to disentangle the
role of school inputs from the influences of non-school factors. Suppose School B has more
qualified teachers and more computers in the classroom than does School A. To study the effect
of teacher quality and computers on school outputs, one must develop an analytical strategy that
adequately controls for the non-school factors. In many cases we suspect the school serving
more advantaged students will also have higher quality school inputs. Since (in this example)
more computers and more qualified teachers are positively correlated with student family
background, education production function estimates will overstate the effectiveness of school
resources if one does not adequately control for family background.11
Why is identification so important? From a policy perspective, if one implements a
program based on estimates of school effectiveness that are overstated (understated), then the
benefits to society will be smaller (larger) than anticipated by the research. If the misstatement
(bias) is small, this is not a big problem, however in many cases the bias could be quite large
teaching styles, curriculum, extracurricular activities, and non-school factors remain constant.
Because there are no data that allow the researcher to control for all such inputs, the literature
typically asks a more general question: what is the effect of an exogenous decrease in, say, class
size, on student achievement not requiring that all other inputs remain constant? In this example,
teachers may change their teaching style in response to a smaller class size or parents may ease
up on complementary educational activities such as tutoring (believing their child is receiving a
higher quality education while in school). This more systemic response is what one might
expect from an exogenous change in educational policy. See Todd and Wolpin (2003) for a
more in-depth discussion of this conceptual issue.
11

In some cases the bias may be negative. For example, special needs and English
language learner classes tend to be much smaller than classes for regular or gifted students
(Boozer and Rouse 2001). In this case, one may erroneously conclude that smaller class sizes
lead to worse student outcomes.

leading to no societal benefits, or worse, adverse outcomes. (Or, in the case of understatement, a
potentially beneficial program may not be adopted.)

The Ideal Way to Measure the Impact of Schooling Inputs
To identify the causal impact of school resources, ideally one would begin with a group

of students and educate them during the year with the first educational input in question (or the
status quo). At the end of the year one would assess the students or administer an appropriate
test, the results of which would perfectly reflect what the students know. 12
Next, one would take the same group of students and revert them back to their initial
conditions at the beginning of the first year. That is, they would be the same age, have the same
living conditions, etc. This second year, one would then educate the students with the second
educational input in question. (For example, in the first year the input might be teachers with
regular teaching credentials and in the second it might teachers who have gone through an
alternative certification program.) At the end of the year, one would again assess what each
student knows.13 The difference between the students’ outcomes using the first input and those
using the second would isolate the value of the second input relative to the first.
Why is this the ideal design for measuring the value of an input? First, because the same

Note that while we describe the ideal outcome as a test, in theory one could use any
other outcome (such as adult wages or voting behavior).
13

In the ideal methodology one need not administer a test at the beginning of each school
year because the students (and all of their characteristics) are identical in both years. If one were
to administer a test at the beginning of the year, the difference between what the students know
at the beginning of the year and the end of the year could (mostly) be attributed to the input used
that year since the students are the same in each testing period. This would constitute the input’s
“value-added” in the each year.

students are educated using each educational input starting from the same initial conditions, one
has guaranteed that all background characteristics of the students are the same, including their
prior exposure to high and low quality schooling, their family situation, and their innate ability.
In other words, one has effectively controlled for Xist and NSit. Second, because the assessments
perfectly reflect what students know, there is no measurement error. The combination of these
two features means that one can isolate the relative influence of the educational inputs. The key
is that by observing how students fare under both regimes one has a “counterfactual” outcome
against which to compare the outcome using the main input of interest. Namely, we observe
how much the students learn using the first input as well as how much they would have learned
had we instead used the second input. As we will discuss, it turns out that establishing a credible
counterfactual outcome is among the most difficult tasks faced by the analyst.
Clearly, the ideal evaluation is impossible to implement. No one can turn back time to
assess the students under the exact same conditions in each year. In addition, there has not been
an assessment devised that perfectly reflects what students know. Rather, existing tests reflect
only a part of what students know, and there are permanent confounding factors (such as
different test-taking abilities) and random confounding factors (such as some students not feeling
well on the day of the test or not getting enough sleep before the test). The analyst’s task is,
nevertheless, to implement a methodology that comes as close to the ideal approach as possible.
One must also consider how generalizable the outcome of any evaluation would be (that
is, whether the evaluation has “external validity” (Campbell and Stanley 1963). If we started
with a “representative” group of students, then the ideal evaluation would uncover the average
relative effectiveness of the input even if the effectiveness of the input varies over the

population. If it is the case that the first or second input is more effective for some students than
others, the students in our study must be representative of the population of students in order to
assess the effectiveness of each input on average. Consider the extreme example in which the
first input is effective for teaching girls but not effective for teaching boys, and the second input
is as effective for teaching boys as the first input is for teaching girls but not at all effective for
teaching girls. Further, assume that 50 percent of the student population is female and 50
percent is male. In this extreme example, the two inputs are equally effective on average.
However, if the students in the study were disproportionately female, we would incorrectly
conclude that, on average, the first input is more effective than the second input. Thus, only by
starting with a group of students who are representative of the population (in general, or the
population of interest for the policy) can one guarantee that the exercise will uncover the true
average treatment effect of the input. Of course, in this extreme but simple example with an
ideal set up in which one knows all of the characteristics of the students, one could estimate the
effectiveness of the inputs for different subgroups of the population and discover, in fact, that the
first input was more effective for girls and the second input was more effective for boys.
This issue of “heterogenous treatment effects” is part of the reason many in education
cast a jaundiced eye toward randomized experiments (and many other quantitative
methodologies). However, the average effect (even if there are different effects for different
subpopulations or in different settings) is important for setting policy, especially if it is difficult
for policymakers to target a policy narrowly or effectively. As such, the first-order question is
whether an intervention works in general or for very broad categories of schools or students.
Among the important subsequent questions is whether it is more effective for some groups or

situations than for others.
In a related manner, one characteristic of many methodologies that emphasize causality is
that the researcher does not delve into the intricacies of why the intervention may have mattered
(or not mattered). For example, in the studies of class size reduction using the randomized
Project STAR data from Tennessee, researchers have not identified why class size reduction
mattered. Was it because there were fewer students in the class per se (i.e., a peer effect story)
or because the teachers changed their teaching styles? It is important to note that this is not an
inherent limitation of the randomization (or other methodologies which emphasize causality).
Rather it follows from the researcher placing a greater emphasis on causality such that he or she
will not attempt to address issues of which subcomponents of an intervention might have
mattered, unless there was randomization along those dimensions as well. That is, unless the
researcher randomly assigned teachers to teaching styles in addition to differing class sizes, he or
she will worry that teachers who adopted certain styles may be different from those who did not
in ways that are not observable. Using survey data (or other observational data) and applying
ordinary least squares regression will not solve this problem (unless, of course, they contain all
of the relevant background variables).
In the next two sections we review methodologies researchers have used in their quest to
study the effectiveness of school inputs.

III.

Methods Using Observational Data
Observational data are gathered from observing existing situations in schools. That is,

they contain the existing input levels in schools (e.g., class sizes and teacher qualifications) as

well as information on students attending the schools. These are “observational” because there
is no attempt on the part of the analyst to manipulate the situation generating the data. Most of
the literature on the effect of educational inputs on student outcomes relies on observational data
typically because they are most readily available. However, the fundamental problem with
observational data is that individuals and schools choose their situations, such that one must
control for all factors that led the individual or school to their choice that might also be
correlated with the outcome of interest. Each of the approaches discussed, below, attempts to
address this fundamental problem in a different way.

Ordinary Least Squares Regression
Traditionally, researchers have used ordinary least squares regression (OLS) to study the

impact of school resources on outcomes (e.g., Coleman et al 1966). In the cross-sectional case,
the analyst relies on a specification such as,
(2)
where the variables are the same as those in equation (1) and ", $, 8, and * are parameters to be
estimated. If all of the other factors (NSit and Xist) are observed in the data set such that one can
include them in the regression (thereby holding them constant), then one can generate an
unbiased (causal) estimate of $. However, we know of no data that contain all of the other
factors for which one must control. Rather, most cross-sectional data contain only limited
information on important non-school and school factors. For example, in school administrative
data one rarely, if ever, has an accurate measure of family income. As a result, researchers
control for whether the student was eligible for the National School Lunch Program, a proxy for

income that is very crude at best.
Today many researchers believe that cross-sectional OLS estimates are likely inaccurate
(i.e., they are statistically biased). As a result, they turn to data that follow a student over
time—longitudinal data. With longitudinal data one can control for observed and unobserved
student characteristics, particularly those that do not change over time. In addition, because
these data have information on students over multiple years, one comes closer to the
comprehensive data required in equation (1). Because of accountability requirements in The No
Child Left Behind Act of 2001, many states are beginning to collect such data on individual
students statewide. This advance in data collection will be an invaluable resource for education
researchers going forward.14
Since these data have not been readily available, one approach that researchers have used
is known as a “value-added” specification (e.g., Summers and Wolfe 1977). These equations
take the form:
(3)
where Eist-1 is the student’s outcome in the previous year. In this case, one estimates the effect of
a (concurrent) resource Rist on the change in a student’s outcome. If Eist-1 fully captures the effect
of all previous schooling and non-schooling inputs on the student’s achievement, then one can
generate an unbiased estimate of $N, the effectiveness of the school input in question. However,
it seems unlikely that a noisy measure of a student’s performance in the prior year (as reflected

Texas, North Carolina, and Florida already have fairly rich databases and have
provided researchers with access to them. That said, we know of no administrative data that
contain all of the information that would be relevant for replicating the ideal research design.

in test scores) will fully control for all relevant factors.15
In general, the basic problem with using OLS regression to estimate the effect of school
resources on student achievement—using either cross-sectional or longitudinal data—is that one
is uncertain whether or not one has controlled for all important factors16 in the regression. As
such, much of the latest and most compelling research on the impact of school resources on
student achievement has moved away from simple OLS regression.

Regression Discontinuity
Imagine that an educational input is assigned to students based on the value of some

measure. For example, suppose that a state imposes a maximum class size of 25 students per
teacher. If the number of students exceeds 25 students, then the students are to have a teacher
plus a teacher’s aide. If there are more than 40 students then the school must create two classes
(each with one teacher). Because of the cutoffs imposed by the law, students in schools with 39
students in, say, the 3rd grade will experience a much larger class size (39 students) than students
in schools with 41 students in the 3rd grade who will be educated in class sizes of 20 and 21. The
key is that the variation in whether a school has 39 students in the 3rd grade or 41 students likely
occurs by chance. More specifically, it is unlikely there are other factors that determine whether
there are 39 or 41 students in the 3rd grade that also affect student outcomes. As such, one can
compare the outcomes of students in schools with 39 students to those of students in schools

See Todd and Wolpin (2003) for a more comprehensive discussion of what different
empirical models using longitudinal data identify and under what assumptions.
16

Statistically “important factors” are those that influence the student’s performance on
the outcome measure and that are correlated with the resource in question.

with 41 students and attribute any difference to the effect of class size.
This basic methodology is known as a “regression discontinuity” design (Cook and
Campbell 1979), and it has grown in popularity in research on education quality. More generally
this design will work when the input in question (in this example, class size) is at least partly
determined by a known discontinuous function17 of an observed characteristic (in this example,
3rd grade enrollment). Because of the discontinuous relationship between the input in question
and the observed characteristic, the researcher can control directly for the observed characteristic
while still identifying the effect of the input in question on student outcomes making the strategy
much more compelling than typical OLS.18
An important disadvantage of regression discontinuity designs is that the range of values
over which one gets identifying variation tends to be rather small. (For example, the most
compelling comparison in the class size example is between schools with enrollments of 39 vs.
41; one can imagine that schools with 15 rather than 35 3rd-grade students also vary along other
dimensions that may or may not be observable.) In addition, if the effect of class size on student

That is, class sizes and enrollment do not simply increase one-for-one forever, but there
is a change in the relationship at some point. In this example, class sizes increase one-for-one
until there are 40 students in the class and then class sizes abruptly (and discontinuously)
decrease to 20 and 21 students.
18

In order for regression discontinuity design methods to provide credible estimates of
the effect of educational inputs on student outcomes, the key individuals involved (e.g., parents,
principals, teachers, students) must not have control over the exact value of the measure on
which eligibility for the input will be based. Thus, these key individuals must not have control
over the exact size of the 3rd grade class in our example. If the underlying measure can be
manipulated, then one could manipulate the school enrollment to engineer the desired class size.
If the desired class size is correlated with other unobserved determinants of student outcomes,
such as commitment to education, then the estimate of the effectiveness of class size will be
biased. In this example, the methodology seems more credible when applied to public
schools—that do not have complete control over their enrollment—than to private schools.

achievement in the range for which one can generate unbiased estimates is different from that in
other ranges, then the estimated parameters may not generalize.19 However, because regression
discontinuity provides a credible way to estimate a parameter with internal validity, it provides
an invaluable tool for education research. Further, while it may not appear to be very practical,
regression discontinuity is a candidate analytical design whenever there are cutoffs for program
participation. In Section V, below, we discuss papers that use this design to study the
effectiveness of professional development, smaller class sizes, and summer school and grade
retention.

Natural Experiments (Instrumental Variables)
“Natural experiments” provide another approach for analyzing observational data in a

way that comes closer to the ideal experiment than OLS. In this approach, researchers attempt to
locate determinants of schooling inputs that would not be expected to independently alter their
educational outcomes.
Here’s the basic idea used in this methodology. Suppose we were interested in studying
the effect of financial resources on student outcomes. And, we knew of a determinant of
financial resources, say, a change in the state education financing formula, that would increase
the amount of money allocated to one group of schools. Suppose further we were certain that
this change in the financing formula did not have any direct effect on the students’ outcomes,

For example, when class sizes vary by only 1 or 2 students—which may be the viable
range for policy changes—teachers may not change their teaching styles significantly. However,
when class sizes change a lot (e.g., 39 students vs. 20 students) then many other educational
practices may change making it difficult to isolate the effect of class size, per se. Or, the effect
of class size reduction may matter for, say, classes with over 30 students but not for classes with
20-25 students.

except through the impact on the schools’ revenues.20 We would then estimate the effect of state
aid on outcomes in two steps: In the first step we would estimate the effect of the state aid on
school revenue. In the next step we would measure the effect of the change in state aid on
students’ outcomes. If we found that the outcomes of the students improved, then we could be
sure that increased revenues were the cause of the outcome improvement since we were certain
that the change in state aid had no direct effect on outcomes. The ratio of the outcome
improvement caused by the change in state aid to the change in the educational input caused by
the state aid is a straightforward estimate of the causal effect of financial resources on student
achievement. This instrumental variables (IV) estimator uses the “exogenous” event (a change
in the state financing formula) as the instrumental variable.21 This is, indeed, the approach taken
in the recent paper by Jonathan Guryan (2003) to study the impact of “money” on student
outcomes (see section V, below).
As another example of how this estimation strategy works, consider the recent paper by

Thus, for example, one would need to be careful with state aid formulas that were
designed to be redistributive. In this case, schools in poor areas would likely receive more state
aid and yet their students would likely perform worse on tests than students in wealthier areas.
As such, one would not want to simply use the level of state aid as the outside determinant of
resources. However, some changes in the formula may have been driven by factors that are
uncorrelated with the characteristics of the districts such that these changes would be valid
outside determinants of state aid.
21

Some investigators refer to the fact that schools use varying levels of a particular input
as a “natural experiment.” (For example, we have heard researchers propose studying the effect
of a whole school reform model by “exploiting the natural variation” arising from the fact that
some schools have adopted the model and others have not.) This is not what most economists
would refer to as a “natural experiment” particularly since the method of analysis that follows is
simply OLS (in which one relates whether or not a school uses the whole school reform model in
question to student outcomes). One is still left with the question as to why some schools adopted
the model and others did not, and whether this same (unobserved) factor that led them to adopt it
is correlated with student outcomes.

Angrist and Lavy (2002) that studies the effect of technology on student achievement. Angrist
and Lavy note that schools in Israel that received a technology grant were more likely to use
computer-assisted instruction (CAI) (again, see section V, below). The grant program is a
suitable instrumental variable so long as one can assume that any difference between schools that
received funding through the program and those that did not is only the use of computers in the
schools and not other observable characteristics of the schools (e.g., schools with more
motivated principals were more likely to apply for the grant program and have better performing
schools). Angrist and Lavy study the correlation of participation in the program with other
school environment characteristics (e.g., class size, hours of instruction, non-computer
technology) and conclude that the program increased CAI instruction without changing other
characteristics of the schools. That said, this highlights the main empirical challenge in IV
strategies: the researcher must make the claim that the instrumental variable only affects the
outcome through its effect on the educational input (the endogenous variable) in question. As
such, the researcher must make assumptions about unobservable factors—which are inherently
difficult to prove or disprove.22
Another disadvantage of IV strategies is that like regression discontinuity designs, if
there is heterogeneity in the effect of an input on student outcomes, the estimated effect may not
generalize to other segments of the population. The reason is that IV identifies the effect of an
input on student achievement among those students (or schools) that are induced to change their
behavior because of the instrumental variable (Imbens and Angrist 1994). Thus, in the case of

In this regard, IV shares much in common with OLS. Both strategies rely on assuming
that the error term is not correlated with either the input in question (in the case of OLS) or the
instrumental variable (in the case of IV), conditional on the (other) observed covariates.

the technology grant program in Israel, IV identifies an effect of CAI only for those schools that
increased their intensity of CAI because of the grant program (there are others that may have
received money from the program that would have increased their CAI intensity even without
the program). If student achievement is particularly responsive to increases in CAI intensity in
these schools, then the IV estimate of the effectiveness of technology will overstate the average
effect across all schools. While quite popular, especially among economists, it is extremely
difficult to find credible instrumental variables such that this methodology is unlikely to become
a mainstay of education research.

IV.

Methods Using Experimental Data
Finally we come to what many describe as the “gold standard” in evaluation

methodology: randomized designs. In this case, one group of students is randomly assigned to
be educated with the input in question (the treatment group) and a second group of students is
(randomly) assigned to be educated with the status quo or another input (the control group). One
then tests the students at the end of the evaluation. The difference in student outcomes between
those in the treatment group and those in the control group represents the effect of the input in
question relative to an alternative. Why is this the ideal design for measuring the impact of
school inputs on student outcomes? First, the random assignment of students to an educational
input initially controls for all background characteristics of students, including their prior
exposure to high and low quality schooling. That is, on average, both groups would have the
same distribution of students along observable and unobservable dimensions such that one need

not control for Xist and NSit.23 Further, because a random event determined to which group
(treatment or control) a student was assigned, one need not be concerned that students who
expected to benefit more from an input were those likely to be educated using it (a concern under
OLS), and the error term is uncorrelated with the input in question. Randomization makes the
identification of causality in experiments more transparent than many other methodologies; thus,
experiments are quite compelling.
That said, experiments are not well-suited to answering all questions. First, the more
aggregated the unit observation, the more “cumbersome” a randomized evaluation becomes. For
example, to study the effect of district-wide open enrollment on student outcomes using an
experimental design one must randomly assign districts to treatment and control groups. While
there are more than 14,000 districts in the U.S. from which to choose, the logistics of getting a
sufficient number of districts to cooperate, such that one would have a large enough sample with
which to draw conclusions, would be quite daunting.
In addition, in an “ideal” experiment the random assignment process completely
determines the status of individuals in the treatment and control groups. In many experimental
settings involving human subjects, however, there is slippage between the random assignment
status of experimental subjects and whether or not they actually receive the treatment.24 For

While researchers will often also attempt to administer a pre-test at the beginning of a
randomized evaluation it is not necessary to do so to generate an unbiased estimate of the effect
of the input in question on student outcomes, if the randomization is conducted correctly. The
reason is that the characteristics (both observed and unobserved) of the students in treatment and
control groups are the same, on average, at the beginning of the evaluation. Hence, controlling
for the student’s pre-test will not change the estimate of the effectiveness of the input in
question. Controlling for the pre-test can, at times, improve statistical precision (i.e., lower the
standard errors).
24

This problem is exacerbated in multi-year studies.

example, in the Tennessee Project STAR experiment some students randomly assigned to small
classes ended up in larger classes and vice versa. In a randomized experiment, if one simply
compares the outcomes of students originally assigned to the treatment group to those originally
assigned to the control group (regardless of which treatment the student actually received), one
estimates the “intention-to-treat” effect (Rubin 1974; Efron and Feldman 1991). While of
interest, the intent-to-treat effect may be unsatisfying for those educators and policymakers who
desire an estimate of the effects of a particular input for students who are educated actually using
the input—the effect of “treatment on the treated.” The estimated intent-to-treat effect does not
establish whether the input in question—properly implemented—is better than an alternative.
Note that the difference between the intent to treat and the treatment on the treated is “take up”
(or implementation). Students randomly assigned to the treatment group may actually choose to
use another input (that is not the input in question), and students randomly assigned to the
control group may actually use the input in the question (i.e., get “treated”).
While the effect of treatment on the treated is important, we believe there are at least two
reasons why we should also be interested in intention-to-treat. First, it is the only policy
instrument available to policy makers. If the state of Tennessee decides to lower class sizes for
all students, all policymakers in Tennessee can do is mandate lower class sizes. If all schools
comply with the new law, then one might expect results that follow from the treatment on the
treated parameter. In reality, some schools may not be able to meet the new lower class size
requirements. If so, any anticipated gains in student achievement will be diluted. Take the
extreme case in which no schools are able to reduce class sizes (say, for example, because of
lack of building capacity). In this case, even if student achievement is much higher with smaller
class sizes, there will be no achievement gains from the program because the program was not

implemented. When considering a policy change, policymakers must consider both halves of the
issue: both how the treatment affects the treated and whether the program can and will be
implemented as desired.25 Because it combines both halves of the issue, the intention-to-treat
estimates reflect the overall potential gains from an educational policy change. Second, as in
many experimental settings, the randomization only occurred in the intention-to-treat, and, as
such, this estimate is the only unambiguously unbiased estimate that one can obtain from an OLS
regression, assuming the initial selection was truly random. That said, one can estimate the
effect of treatment on the treated by using an IV strategy in which one uses the random
assignment as an instrumental variable for whether or not the student received the treatment (the
input in question). This is a case in which, if the initial selection was truly random, the
instrumental variable will not be correlated with the error term in the outcome equation and
therefore will be valid.
Although experimental approaches probably come closest to the ideal evaluation design,
they do have some analytical shortcomings which are worth highlighting. For example, they
tend to be rather “blunt” instruments. One implements an experimental design out of concerns
for obtaining an unbiased estimate of the effect of the input on student achievement. However,
one can only truly get such an unbiased estimate from the point of random assignment, and
unless the experimental design is sufficiently complicated, one can really only answer one
question (whether those assigned to the treatment group fared differently from those assigned to
the control group). Cost concerns (and complicated implementation) often preclude comparing

This discussion is analogous to the distinction between “efficacy” (i.e., how well a
drug might work in theory) and “effectiveness” (i.e., how well a drug works in practice given the
fact that patients may not follow the protocol exactly).

the effectiveness of more than two or three different inputs in one study. Note, however, that
one can ask whether the effect differs for subgroups identified based on characteristics measured
before random assignment takes place, provided sample sizes are large enough. Similarly, it is
rare that researchers using experimental designs attempt to determine (at least causally) which
dimensions of an intervention may have worked or not worked. Again, the reason is that unless
random assignment also occurred along the “subdimensions” any such analysis will not
necessarily yield causal estimates of the effectiveness of the subdimensions.
Keeping in mind these many empirical challenges, we now turn to a brief summary of
what these methodologies suggest about the importance of schooling inputs on student outcomes.

Does School Quality Matter?

Coleman, Hanushek, and Card and Krueger
The Coleman Report (Coleman et al. 1966) is credited with launching an explosion of

studies estimating the relationships between educational outcomes and school inputs. Many
papers were written criticizing the methodology used in the Coleman Report including
arguments that longitudinal studies or well-designed experiments were needed to make causal
inferences (e.g., Sewell 1967). Further, even the Report’s authors note that their cross-sectional
analysis does not provide a strong basis for causal interpretation. However, the Report was
broadly interpreted to find that schools do not matter; instead, family background and peers
explained most of the variation in education outcomes.
By the mid-1980s, Hanushek (1986) includes 147 studies in a survey of the literature
relating educational outcomes to school inputs. Ten years later, Hanushek (1996) finds more
than double the number of studies to survey. The reviews and conclusions of Hanushek’s

analyses reinforced the findings of the Coleman Report, and by the early 1990s, many people
were firmly convinced that “money does not matter,” namely, that once family inputs into
schooling were taken into account, school resources did not matter. As Hanushek (1997) writes,
“Simple resource policies hold little hope for improving student outcomes.” He further
concludes, “Three decades of intensive research leave a clear picture that school resource
variations are not closely related to variations in student outcomes and, by implication, that
aggressive spending programs are unlikely to be good investment programs unless coupled with
other fundamental reforms.” (Hanushek 1996)
Although Hanushek’s meta-analyses have been extremely influential, researchers have
criticized them along a number of dimensions. Hedges, Lain, and Greenwald (1994) note that
many of the studies Hanushek surveys can be faulted for methodological reasons similar to those
discussed above. For example, many of the surveyed studies are based on cross-sectional,
observational data and do not have longitudinal data on student outcomes or natural experiment
features. Further, Hanushek relies on simple “vote counting” in his analysis. Using more
sophisticated meta-analytical techniques, Hedges, Lain, and Greenwald conclude that among the
studies surveyed in Hanushek (1989), per pupil expenditures, teacher experience, and teacherpupil ratios are positively related to student outcomes. They also find that the effect sizes for per
pupil expenditures are large and educationally important.
Krueger (2003) makes a more basic point in criticizing Hanushek for weighting all
estimates equally and thus giving more weight to studies that publish more estimates. Focusing
on the class size results included in Hanushek (1996), Krueger uses alternative weighting
strategies, including giving equal weight to each study rather than equal weight to each estimate,
and finds support for a positive relationship between smaller class sizes and better student

outcomes.
Today, while researchers recognize the importance of family background and other nonschool inputs in determining educational outcomes, many have come to question the findings of
the Hanushek meta-analyses as well as the validity of many of the individual studies estimating
education production functions. Card and Krueger (1992) perhaps marks the turning of the tide
on the view that schools do not matter. Instead of focusing on direct education outcomes, Card
and Krueger focus on how school quality affects the returns to schooling (i.e., the increase in
earnings associated with an additional year of schooling). Assuming that school quality for men
working in a given labor market varies exogenously by their state of birth and cohort, Card and
Krueger find that men who were educated in states and years with higher quality
schools—schools with lower pupil-teacher ratios, longer school years, and higher relative
teacher pay—earn more for an additional year of education than men educated in states and
years with lower quality schools. These results are consistent with earlier work finding positive
relationships between school quality and earnings (e.g., Johnson and Stafford 1973; Rizzuto and
Wachtel 1980) and work that attributes much of the closing of the black-white wage gap to
improvements in school quality for African American students (e.g., Smith and Welch 1989).
While some researchers challenged the assumptions used in Card and Krueger (1992), others
began to consider that school resources may affect students’ earnings after leaving school
without having measurable effects on academic achievement while in school (Burtless 1996).

Recent Studies
Since Card and Krueger (1992), there have been many new papers examining the effects

of school inputs on student achievement, several of which use estimation strategies aimed at

identifying the causal relationships between school inputs and student outcomes. In this section
we review a few of the best studies in economics assessing school spending, class size, teacher
quality, time in school, and technology.

Spending

Because some students may be more expensive to educate than others and schools and
districts differ in the types of students they serve, simply looking at the relationship between
average student test scores and per pupil spending may indicate that greater school spending is
associated with lower student achievement. As a result, researchers rely on alternative strategies
for identifying the causal relationship between spending and student outcomes. Barrow and
Rouse (2004) and Guryan (2003) use changes in state school financing aid formulas as
instrumental variables to isolate plausibly exogenous changes in school spending. Barrow and
Rouse (2004) examine the general question of whether spending on schools is valued by the
“market” by looking at the effects of increased school spending on local property values. Indeed,
the authors find that school spending is valued, on average, since they estimate that property
values increased by the expected amount in school districts that received an extra $1 per pupil in
state school financing. If potential residents did not value the additional spending because school
districts were viewed as spending excessively or wastefully, additional state aid should not have
resulted in such large increases in property values.
Guryan (2003) looks more specifically at the relationship between school spending and
student achievement in Massachusetts. He finds that additional state aid resulting from a change
in the financing formulas led to a significant increase in math, reading, and science test scores
for both 4th and 8th grade students. Specifically, he estimates that a $1000 increase in per-pupil

spending leads to a one-third to one-half of a standard deviation increase in average test scores.
In sum, Barrow and Rouse (2004) and Guryan (2003) both suggest that money matters when it
comes to public schools. Below we look at studies that examine more specifically whether
different inputs matter.

2. Class size
Although the effect of class size on student achievement has most often been studied
using observational data, Boozer and Rouse (2001) provide a clear demonstration of how
estimates of class size effects can be misleading due to the relationship between class size and
student ability as well as how school-level measures of pupil-teacher ratios can mask significant
within-school variation in actual class size. Thus, one should be suspect of estimates that do not
make use of more sophisticated estimation techniques to uncover the causal relationship between
class size and student achievement. Fortunately, class size is one of the education topics that has
been studied using a variety of estimation techniques, including regression discontinuity,
instrumental variables, and randomized evaluation.
Angrist and Lavy (1999) use a regression-discontinuity estimator to look at the effect of
class size on student test scores in Israel. Public schools in Israel have a maximum class size of
40 pupils which generates a non-linear, non-monotonic relationship between grade enrollment
and class size. As discussed above, this will generate large differences in class size between
grades with enrollment of 39 students and grades with enrollment of 41 students. For fourth and
fifth grade students, Angrist and Lavy (1999) find that reductions in class size increase test
scores by statistically significant and educationally important amounts. They do not find similar
effects for third grade students.

Two other papers have used regression discontinuity and/or instrumental variables as
well. Hoxby (2000) uses class size minimums and maximums in Connecticut to look at the effect
on student test scores of changes in class size driven by movements in enrollment populations
that push schools over and under the class size thresholds. She finds mixed results on the
relationship between class size and student performance. Boozer and Rouse (2001) use state
class size maximums as an instrumental variable for student-level class size in the NELS88 and
find that smaller classes improve student achievement.
Perhaps the best known and most convincing evidence on the impact of class size comes
from the Tennessee Student/Teacher Achievement Ratio experiment (Project STAR) in which
Tennessee kindergarten students were randomly assigned to small classes (13 to 17 students per
teacher), regularly-sized classes (22 to 25 students per teacher), or regularly-sized classes with a
teacher’s aid (22 to 25 students per teacher). The experiment continued through the third grade
and then students were returned to regularly sized classes. Finn and Achilles (1990) and Krueger
(1999) find that students in the smaller classes outperformed students in the larger classes on
standardized tests. Additionally in a longer-term follow-up of Project STAR, Krueger and
Whitmore (2001) find that students who were randomly assigned to smaller classes were
significantly more likely to take a college entrance exam and that this effect was greater for
African American students.
At this point, many education researchers and policymakers have been convinced that
smaller class sizes can improve student outcomes on average. However, many unanswered
questions remain. For example, we need to know more about the cost of class size reduction
relative to other interventions and whether it is cost effective. In addition, California’s
experience with class size reduction in the 1990s highlighted that implementation—especially on

a large scale—can go awry (Bohrnstedt and Stecher 1999). Importantly, even the evidence from
Project STAR suggests that the impact of class size reduction differs across schools and
subpopulations of students (for example, Krueger (1999) found the largest effects for African
American and low-income students). Clearly we need to know more about the conditions under
which reducing class sizes will be most fruitful.

3. Teacher quality
The preponderance of evidence suggests that teachers matter for student outcomes.
Hanushek, Rivkin, and Kain (2005) use Texas data on elementary students linked to teachers at
the school-grade level in order to estimate the effect of teachers on student learning while
Aaronson, Barrow, and Sander (2003) use Chicago Public Schools data on high school students
linked to teachers at the classroom level to examine teacher quality. Both studies find large
variation in teacher quality as measured by the effect of teachers on student test score gains.
Hanushek, Rivkin, and Kain (2005) estimate that a one standard deviation increase in teacher
quality at the grade level will increase student test scores by roughly 10 percent of a standard
deviation while Aaronson, Barrow, and Sander (2003) find that a one standard deviation
improvement in 9th grade math teacher quality for one semester is associated with a gain equal to
10 to 20 percent of the average math test score gain experienced in a typical school year.
When it comes to determining what makes a good teacher, the research is much less
clear. Research by Clotfelter, Ladd, and Vigdor (2004) in North Carolina illustrates the great
tendency for the most qualified teachers to teach in schools with the most advantaged students as
well as for parents of more advantaged children to get their children into classes with more
qualified teachers. This sorting of teachers and students makes it difficult to disentangle the

causal effects of various measures of teacher quality. In addition, the characteristics of teachers
available in the large administrative data sets are typically limited to those that determine
compensation, such as whether or not a teacher has a master’s degree and how many years she
has been teaching in the school district.
Researchers have found some evidence that teacher quality improves sharply after one or
two years of experience (e.g., Clotfelter, Ladd, and Vigdor 2004; Hanushek, Rivkin, and Kain
2005). However, new teachers exit teaching at fairly high rates, and Aaronson, Barrow, and
Sander (2003) find that teachers in the lowest quality decile in one year are 26 percent less likely
to be teaching in the next year than teachers in the highest quality decile suggesting that some of
the experience results may be driven by selection if only the higher quality teachers stay beyond
one or two years. Aaronson, Barrow, and Sander (2003) also find some evidence that
undergraduate major may be related to teacher quality, while Clotfelter, Ladd, and Vigdor (2004)
find evidence that teachers who score best on licensing tests are indeed higher quality teachers.
Using a regression discontinuity design, Jacob and Lefgren (2004a) take advantage of the
nonlinear relationship between school-level student achievement in Chicago Public Schools and
the assignment of schools to probationary status in order to examine the relationship between
professional development and student achievement. In 1996, elementary schools in which fewer
than 15 percent of students met national norms on a standardized test of reading were placed on
probation and given resources (up to $90,000 in the first year) to purchase staff development
services. Schools with more than 15 percent of students meeting national norms were not placed
on probation and not given the additional resources. Jacob and Lefgren thus assume that whether
a school has just fewer than 15 percent of students that met the reading norm or slightly more
than 15 percent of students that met the norm is by chance.

The authors find that schools on probation primarily spent the additional resources on
professional and staff development purchased from a wide variety of external sources including
universities, nonprofit organizations, and independent consultants. The authors find that teachers
report a 25 percent increase in the frequency of attending professional development programs,
and others (e.g., Smylie et al. 2001) have reported a more substantial increase in the quality of
the professional development teachers received. Unfortunately, however, the authors find no
evidence that the increase in the quantity and quality of professional development induced by
schools’ probationary status translated into improved student achievement.
In sum, the best evidence suggests that teachers matter; however, we still have much to
learn about how to identify quality teachers when making hiring decisions or how to increase
teacher productivity with training or professional development.

4. Time in school
The length of the school year in the U.S. is a frequent target of criticism in discussions of
why students in the U.S. score badly on standardized tests relative to other developed countries.
Several studies document erosion of students’ skills over the summer vacation (e.g., Cooper et
al. 2000), and there is some evidence that summer school can improve student achievement (
e.g., Jacob and Lefgren 2004b).
Jacob and Lefgren (2004b) utilize regression discontinuity to look at the effect of summer
school and grade retention on student achievement in Chicago. In 1996, Chicago Public Schools
instituted a policy of requiring 3rd and 6th grade students to attend summer school if they did not
meet minimum test score thresholds. Students were then retained in grade if they did not achieve
the minimum test score following summer school. The authors are able to use the discontinuity

of the treatment rule in order to assess the benefits of the summer school and grade retention
policy on student achievement. Namely, students scoring just below the minimum “passing” test
score and students scoring just above the minimum passing test score are assumed to be quite
similar except that those scoring just below the threshold are assigned to summer school. Jacob
and Lefgren (2004b) find that the net effect of summer school and grade retention was to
increase student achievement among 3rd grade students. However, the authors find no similar
achievement gains for 6th grade students.26
Pischke (2003) specifically looks at the effect of school-year length by taking advantage
of a natural experiment occurring in West Germany in the late 1960s. Adoption of a common
fall-start to the school year led students in most states to experience two short school years,
equivalent to roughly two-thirds of the standard length school year. In contrast, students in WestBerlin and Hamburg attended one long school year. Pischke (2003) finds that the shorter school
year increased grade repetition among elementary school students, but that the shorter school
year had no effect on the number of students attending the highest secondary school track or
subsequent earnings as adults. Thus, there is little evidence of long-lasting negative effects of a
shorter school year.
The Pischke (2003) results point to an important difficulty in estimating educational
policy effects with observational data even in the presence of a natural experiment. Although we
may believe that the natural experiment is valid in that it generated exogenous variation in the
length of a school year and that it should only affect student outcomes through the experiment’s

The authors also use regression discontinuity to look at the effect of grade retention
alone using the post summer school test scores. Once again, they find that grade retention is
beneficial to 3rd grade student achievement, but has no effect on 6th grade student achievement.

effect on the length of a school year, it is quite likely that teachers changed their behavior to
compensate for the temporarily shortened school year. Since the behavioral response to a shortterm change in the school year may be different from the responses generated by a permanent
change in the length of the school year, the results may lack external validity.

5. Technology
Research on the success of computer-aided instruction (CAI) has yielded mixed evidence
at best. Some research using observational data has shown computers can offer highly
individualized instruction, allow students to learn at their own paces, enhance assessment, and
increase student motivation (e.g., Sandholz et al. 1997; Means and Olson 1995; Lepper 1985).
In contrast, other research reports that computers are frequently poorly embraced by teachers,
can disrupt classrooms, and fail to increase student achievement in any measurable way (e.g.,
Cuban 2001; Becker 2000; Angrist and Lavy 2002; Rouse and Krueger 2004).
A common critique of the literature is that both student outcomes and what constitutes
“computer use” are poorly defined (Cuban, 2001). For example, while Angrist and Lavy (2002)
are able to use an instrumental variables estimator to look at the effect of CAI on student test
scores, the intensity of computer use is defined by the teacher’s response to a rather vague
question about how often they used “computer software or instructional computer programmes”
(Angrist and Lavy 2002). The authors find no evidence that greater use of CAI improved
student test scores in math or Hebrew.
Borman and Rachuba (2001) and Rouse and Krueger (2004) have the advantages of
being able to evaluate the effect of much more specific computer use—the use of a particular
instructional software—and to implement random assignment of students to treatment and

control groups. Both studies evaluate the popular Fast ForWord (FFW) computerized reading
instruction program using random assignment within schools in large urban school districts. The
studies’ findings are remarkably similar: both rule out large impacts of computerized instruction
with estimated effects that are not statistically different from zero.
While these studies suggest that CAI does not significantly improve student educational
outcomes, one might find that different computerized reading programs were successful or that
the use of CAI in other subjects significantly raised students’ learning in those subjects. Further,
one might find that FFW was effective when used in other settings. Both randomized
evaluations of FFW were conducted in schools, but it may be that schools are not the best
environment in which to implement the program (FFW is also often used by psychologists and
reading specialists in private practice). While the schools and teachers in the studies did their
best to engage students and keep them on task, the many disruptions that occur during the
semester may have compromised students’ ability to benefit from the program; the same students
may have benefitted from the program in a different setting. Currently, however, there is very
little evidence that CAI is effective in schools.

VI.

Conclusion
Educators and policy makers are increasingly intent on using scientifically-based

evidence when making decisions about education policy. Thus, education research today must
necessarily be focused on identifying the causal relationships between education inputs and
student outcomes. The good news is that the body of credible research on causal relationships is
growing, and we have started to gather evidence that some school inputs matter while others do
not.

As this body of knowledge grows, we can also get inside the “black box” of the inputs
that work. Once we understand that an input improves student outcomes, on average, we can
look at the next set of questions: Do all students benefit from a particular input? Who benefits
most from a particular input? Which aspects of multidimensional programs are most beneficial?
(A challenge will be to develop studies that also generate causal estimates of this next generation
of questions!) As we develop a knowledge base regarding what works in education, we will also
need a better understanding about how to implement appropriate policies using that knowledge.
In addition, policymakers need information with which to assess the tradeoffs between
different inputs to make sensible decisions. For example, Jacob and Lefgren (2004b) find a
small, but statistically significant, positive effect of summer school and grade retention on
student reading skills at a cost of about $750 per student.27 This cost per student may be
compared to other interventions, such as class size reduction, that have larger effects (more than
three times as large) on student reading skills but also cost more than $2000 per student (Krueger
1999). As a result, implementing the summer school and grade retention may be more costeffective for some school districts than reducing class sizes. This conclusion could not be based
on estimates of the effectiveness of grade retention and summer school alone. Clearly, more
information on such tradeoffs in educational practice is critical.
Policymakers must also understand that it is much more difficult to credibly evaluate the
effectiveness of school policies after the fact. Rather, if research and evaluation are part of a

Authors’ calculations based on the following assumptions. The current annual cost per
pupil in the Chicago Public Schools is about $9000. If the current school year is about 180 days,
then the cost per pupil per day is $50. The summer school program for 3rd graders was for 6
weeks for one-half day, or for 15 days. Thus, the cost per pupil for the summer school was about
$750.

new policy from the beginning, then researchers can collect the necessary data (which are often
difficult—if not impossible—to collect after the policy has been implemented). Further, if a
policy change is only to be implemented in a small number of locations, researchers can help
policymakers design the selection of locations in a way that meets both political and research
needs. Indeed, some of our best opportunities for learning more about the impact of education
resources on student outcomes will come from just such partnerships between policymakers and
researchers.
Finally we note that good policy is not based on the results of a single study, but rather
from a pattern of results extending over time and across a number of settings. Let’s take the
evidence on small class sizes, as an example. The evidence from the Tennessee class size
reduction experiment is important because it has been analyzed by multiple researchers, and the
basic results have been found to be robust to alternative ways of analyzing the data. That said,
without other credible evidence that smaller class sizes make a difference for students, one
would not want to draw such conclusions. Another recent example of the caution with which
one must approach a single study comes from the evidence on the Fast ForWord computerized
language program. Results from Miller et al. (1999) suggest the program has a large and
statistically significant effect on student outcomes. However, as discussed earlier, this finding
was not found to be robust in alternative settings. Indeed, the purpose of the federally-funded
WWC is to provide policymakers with summaries (or meta-analyses) of the best research on any
particular topic. This effort reflects the fact that it is only by piecing together results from a
variety of high-quality studies that we can begin to develop a picture of what does, and does not,
work in education.

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Working Paper Series
A series of research studies on regional economic issues relating to the Seventh Federal
Reserve District, and on financial and economic topics.
Outsourcing Business Services and the Role of Central Administrative Offices
Yukako Ono

WP-02-01

Strategic Responses to Regulatory Threat in the Credit Card Market*
Victor Stango

WP-02-02

The Optimal Mix of Taxes on Money, Consumption and Income
Fiorella De Fiore and Pedro Teles

WP-02-03

Expectation Traps and Monetary Policy
Stefania Albanesi, V. V. Chari and Lawrence J. Christiano

WP-02-04

Monetary Policy in a Financial Crisis
Lawrence J. Christiano, Christopher Gust and Jorge Roldos

WP-02-05

Regulatory Incentives and Consolidation: The Case of Commercial Bank Mergers
and the Community Reinvestment Act
Raphael Bostic, Hamid Mehran, Anna Paulson and Marc Saidenberg

WP-02-06

Technological Progress and the Geographic Expansion of the Banking Industry
Allen N. Berger and Robert DeYoung

WP-02-07

Choosing the Right Parents: Changes in the Intergenerational Transmission
of Inequality  Between 1980 and the Early 1990s
David I. Levine and Bhashkar Mazumder

WP-02-08

The Immediacy Implications of Exchange Organization
James T. Moser

WP-02-09

Maternal Employment and Overweight Children
Patricia M. Anderson, Kristin F. Butcher and Phillip B. Levine

WP-02-10

The Costs and Benefits of Moral Suasion: Evidence from the Rescue of
Long-Term Capital Management
Craig Furfine

WP-02-11

On the Cyclical Behavior of Employment, Unemployment and Labor Force Participation
Marcelo Veracierto

WP-02-12

Do Safeguard Tariffs and Antidumping Duties Open or Close Technology Gaps?
Meredith A. Crowley

WP-02-13

Technology Shocks Matter
Jonas D. M. Fisher

WP-02-14

Money as a Mechanism in a Bewley Economy
Edward J. Green and Ruilin Zhou

WP-02-15

Working Paper Series (continued)
Optimal Fiscal and Monetary Policy: Equivalence Results
Isabel Correia, Juan Pablo Nicolini and Pedro Teles

WP-02-16

Real Exchange Rate Fluctuations and the Dynamics of Retail Trade Industries
on the U.S.-Canada Border
Jeffrey R. Campbell and Beverly Lapham

WP-02-17

Bank Procyclicality, Credit Crunches, and Asymmetric Monetary Policy Effects:
A Unifying Model
Robert R. Bliss and George G. Kaufman

WP-02-18

Location of Headquarter Growth During the 90s
Thomas H. Klier

WP-02-19

The Value of Banking Relationships During a Financial Crisis:
Evidence from Failures of Japanese Banks
Elijah Brewer III, Hesna Genay, William Curt Hunter and George G. Kaufman

WP-02-20

On the Distribution and Dynamics of Health Costs
Eric French and John Bailey Jones

WP-02-21

The Effects of Progressive Taxation on Labor Supply when Hours and Wages are
Jointly Determined
Daniel Aaronson and Eric French

WP-02-22

Inter-industry Contagion and the Competitive Effects of Financial Distress Announcements:
Evidence from Commercial Banks and Life Insurance Companies
Elijah Brewer III and William E. Jackson III

WP-02-23

State-Contingent Bank Regulation With Unobserved Action and
Unobserved Characteristics
David A. Marshall and Edward Simpson Prescott

WP-02-24

Local Market Consolidation and Bank Productive Efficiency
Douglas D. Evanoff and Evren Örs

WP-02-25

Life-Cycle Dynamics in Industrial Sectors. The Role of Banking Market Structure
Nicola Cetorelli

WP-02-26

Private School Location and Neighborhood Characteristics
Lisa Barrow

WP-02-27

Teachers and Student Achievement in the Chicago Public High Schools
Daniel Aaronson, Lisa Barrow and William Sander

WP-02-28

The Crime of 1873: Back to the Scene
François R. Velde

WP-02-29

Trade Structure, Industrial Structure, and International Business Cycles
Marianne Baxter and Michael A. Kouparitsas

WP-02-30

Estimating the Returns to Community College Schooling for Displaced Workers
Louis Jacobson, Robert LaLonde and Daniel G. Sullivan

WP-02-31

Working Paper Series (continued)
A Proposal for Efficiently Resolving Out-of-the-Money Swap Positions
at Large Insolvent Banks
George G. Kaufman

WP-03-01

Depositor Liquidity and Loss-Sharing in Bank Failure Resolutions
George G. Kaufman

WP-03-02

Subordinated Debt and Prompt Corrective Regulatory Action
Douglas D. Evanoff and Larry D. Wall

WP-03-03

When is Inter-Transaction Time Informative?
Craig Furfine

WP-03-04

Tenure Choice with Location Selection: The Case of Hispanic Neighborhoods
in Chicago
Maude Toussaint-Comeau and Sherrie L.W. Rhine

WP-03-05

Distinguishing Limited Commitment from Moral Hazard in Models of
Growth with Inequality*
Anna L. Paulson and Robert Townsend

WP-03-06

Resolving Large Complex Financial Organizations
Robert R. Bliss

WP-03-07

The Case of the Missing Productivity Growth:
Or, Does information technology explain why productivity accelerated in the United States
but not the United Kingdom?
Susanto Basu, John G. Fernald, Nicholas Oulton and Sylaja Srinivasan

WP-03-08

Inside-Outside Money Competition
Ramon Marimon, Juan Pablo Nicolini and Pedro Teles

WP-03-09

The Importance of Check-Cashing Businesses to the Unbanked: Racial/Ethnic Differences
William H. Greene, Sherrie L.W. Rhine and Maude Toussaint-Comeau

WP-03-10

A Firm’s First Year
Jaap H. Abbring and Jeffrey R. Campbell

WP-03-11

Market Size Matters
Jeffrey R. Campbell and Hugo A. Hopenhayn

WP-03-12

The Cost of Business Cycles under Endogenous Growth
Gadi Barlevy

WP-03-13

The Past, Present, and Probable Future for Community Banks
Robert DeYoung, William C. Hunter and Gregory F. Udell

WP-03-14

Measuring Productivity Growth in Asia: Do Market Imperfections Matter?
John Fernald and Brent Neiman

WP-03-15

Revised Estimates of Intergenerational Income Mobility in the United States
Bhashkar Mazumder

WP-03-16

Working Paper Series (continued)
Product Market Evidence on the Employment Effects of the Minimum Wage
Daniel Aaronson and Eric French

WP-03-17

Estimating Models of On-the-Job Search using Record Statistics
Gadi Barlevy

WP-03-18

Banking Market Conditions and Deposit Interest Rates
Richard J. Rosen

WP-03-19

Creating a National State Rainy Day Fund: A Modest Proposal to Improve Future
State Fiscal Performance
Richard Mattoon

WP-03-20

Managerial Incentive and Financial Contagion
Sujit Chakravorti, Anna Llyina and Subir Lall

WP-03-21

Women and the Phillips Curve: Do Women’s and Men’s Labor Market Outcomes
Differentially Affect Real Wage Growth and Inflation?
Katharine Anderson, Lisa Barrow and Kristin F. Butcher

WP-03-22

Evaluating the Calvo Model of Sticky Prices
Martin Eichenbaum and Jonas D.M. Fisher

WP-03-23

The Growing Importance of Family and Community: An Analysis of Changes in the
Sibling Correlation in Earnings
Bhashkar Mazumder and David I. Levine

WP-03-24

Should We Teach Old Dogs New Tricks? The Impact of Community College Retraining
on Older Displaced Workers
Louis Jacobson, Robert J. LaLonde and Daniel Sullivan

WP-03-25

Trade Deflection and Trade Depression
Chad P. Brown and Meredith A. Crowley

WP-03-26

China and Emerging Asia: Comrades or Competitors?
Alan G. Ahearne, John G. Fernald, Prakash Loungani and John W. Schindler

WP-03-27

International Business Cycles Under Fixed and Flexible Exchange Rate Regimes
Michael A. Kouparitsas

WP-03-28

Firing Costs and Business Cycle Fluctuations
Marcelo Veracierto

WP-03-29

Spatial Organization of Firms
Yukako Ono

WP-03-30

Government Equity and Money: John Law’s System in 1720 France
François R. Velde

WP-03-31

Deregulation and the Relationship Between Bank CEO
Compensation and Risk-Taking
Elijah Brewer III, William Curt Hunter and William E. Jackson III

WP-03-32

Working Paper Series (continued)
Compatibility and Pricing with Indirect Network Effects: Evidence from ATMs
Christopher R. Knittel and Victor Stango

WP-03-33

Self-Employment as an Alternative to Unemployment
Ellen R. Rissman

WP-03-34

Where the Headquarters are – Evidence from Large Public Companies 1990-2000
Tyler Diacon and Thomas H. Klier

WP-03-35

Standing Facilities and Interbank Borrowing: Evidence from the Federal Reserve’s
New Discount Window
Craig Furfine

WP-04-01

Netting, Financial Contracts, and Banks: The Economic Implications
William J. Bergman, Robert R. Bliss, Christian A. Johnson and George G. Kaufman

WP-04-02

Real Effects of Bank Competition
Nicola Cetorelli

WP-04-03

Finance as a Barrier To Entry: Bank Competition and Industry Structure in
Local U.S. Markets?
Nicola Cetorelli and Philip E. Strahan

WP-04-04

The Dynamics of Work and Debt
Jeffrey R. Campbell and Zvi Hercowitz

WP-04-05

Fiscal Policy in the Aftermath of 9/11
Jonas Fisher and Martin Eichenbaum

WP-04-06

Merger Momentum and Investor Sentiment: The Stock Market Reaction
To Merger Announcements
Richard J. Rosen

WP-04-07

Earnings Inequality and the Business Cycle
Gadi Barlevy and Daniel Tsiddon

WP-04-08

Platform Competition in Two-Sided Markets: The Case of Payment Networks
Sujit Chakravorti and Roberto Roson

WP-04-09

Nominal Debt as a Burden on Monetary Policy
Javier Díaz-Giménez, Giorgia Giovannetti, Ramon Marimon, and Pedro Teles

WP-04-10

On the Timing of Innovation in Stochastic Schumpeterian Growth Models
Gadi Barlevy

WP-04-11

Policy Externalities: How US Antidumping Affects Japanese Exports to the EU
Chad P. Bown and Meredith A. Crowley

WP-04-12

Sibling Similarities, Differences and Economic Inequality
Bhashkar Mazumder

WP-04-13

Determinants of Business Cycle Comovement: A Robust Analysis
Marianne Baxter and Michael A. Kouparitsas

WP-04-14

Working Paper Series (continued)
The Occupational Assimilation of Hispanics in the U.S.: Evidence from Panel Data
Maude Toussaint-Comeau

WP-04-15

Reading, Writing, and Raisinets1: Are School Finances Contributing to Children’s Obesity?
Patricia M. Anderson and Kristin F. Butcher

WP-04-16

Learning by Observing: Information Spillovers in the Execution and Valuation
of Commercial Bank M&As
Gayle DeLong and Robert DeYoung

WP-04-17

Prospects for Immigrant-Native Wealth Assimilation:
Evidence from Financial Market Participation
Una Okonkwo Osili and Anna Paulson

WP-04-18

Individuals and Institutions: Evidence from International Migrants in the U.S.
Una Okonkwo Osili and Anna Paulson

WP-04-19

Are Technology Improvements Contractionary?
Susanto Basu, John Fernald and Miles Kimball

WP-04-20

The Minimum Wage, Restaurant Prices and Labor Market Structure
Daniel Aaronson, Eric French and James MacDonald

WP-04-21

Betcha can’t acquire just one: merger programs and compensation
Richard J. Rosen

WP-04-22

Not Working: Demographic Changes, Policy Changes,
and the Distribution of Weeks (Not) Worked
Lisa Barrow and Kristin F. Butcher

WP-04-23

The Role of Collateralized Household Debt in Macroeconomic Stabilization
Jeffrey R. Campbell and Zvi Hercowitz

WP-04-24

Advertising and Pricing at Multiple-Output Firms: Evidence from U.S. Thrift Institutions
Robert DeYoung and Evren Örs

WP-04-25

Monetary Policy with State Contingent Interest Rates
Bernardino Adão, Isabel Correia and Pedro Teles

WP-04-26

Comparing location decisions of domestic and foreign auto supplier plants
Thomas Klier, Paul Ma and Daniel P. McMillen

WP-04-27

China’s export growth and US trade policy
Chad P. Bown and Meredith A. Crowley

WP-04-28

Where do manufacturing firms locate their Headquarters?
J. Vernon Henderson and Yukako Ono

WP-04-29

Monetary Policy with Single Instrument Feedback Rules
Bernardino Adão, Isabel Correia and Pedro Teles

WP-04-30

Working Paper Series (continued)
Firm-Specific Capital, Nominal Rigidities and the Business Cycle
David Altig, Lawrence J. Christiano, Martin Eichenbaum and Jesper Linde

WP-05-01

Do Returns to Schooling Differ by Race and Ethnicity?
Lisa Barrow and Cecilia Elena Rouse

WP-05-02

Derivatives and Systemic Risk: Netting, Collateral, and Closeout
Robert R. Bliss and George G. Kaufman

WP-05-03

Risk Overhang and Loan Portfolio Decisions
Robert DeYoung, Anne Gron and Andrew Winton

WP-05-04

Characterizations in a random record model with a non-identically distributed initial record
Gadi Barlevy and H. N. Nagaraja

WP-05-05

Price discovery in a market under stress: the U.S. Treasury market in fall 1998
Craig H. Furfine and Eli M. Remolona

WP-05-06

Politics and Efficiency of Separating Capital and Ordinary Government Budgets
Marco Bassetto with Thomas J. Sargent

WP-05-07

Rigid Prices: Evidence from U.S. Scanner Data
Jeffrey R. Campbell and Benjamin Eden

WP-05-08

Entrepreneurship, Frictions, and Wealth
Marco Cagetti and Mariacristina De Nardi

WP-05-09

Wealth inequality: data and models
Marco Cagetti and Mariacristina De Nardi

WP-05-10

What Determines Bilateral Trade Flows?
Marianne Baxter and Michael A. Kouparitsas

WP-05-11

Intergenerational Economic Mobility in the U.S., 1940 to 2000
Daniel Aaronson and Bhashkar Mazumder

WP-05-12

Differential Mortality, Uncertain Medical Expenses, and the Saving of Elderly Singles
Mariacristina De Nardi, Eric French, and John Bailey Jones

WP-05-13

Fixed Term Employment Contracts in an Equilibrium Search Model
Fernando Alvarez and Marcelo Veracierto

WP-05-14

Causality, Causality, Causality: The View of Education Inputs and Outputs from Economics
Lisa Barrow and Cecilia Elena Rouse

WP-05-15

Full text of Working Papers (Federal Reserve Bank of Chicago) : Causality, Causality, Causality : The View of Education Inputs and Outputs From Economics, Working Paper 2005-15

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