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Federal Reserve Bank of Chicago

Paying for Performance:
The Education Impacts of a
Community College Scholarship
Program for Low-income Adults
Lisa Barrow, Lashawn Richburg-Hayes,
Cecilia Elena Rouse, and Thomas Brock

REVISED
February 2012
WP 2009-13

Comments Welcome

Paying for Performance: The Education Impacts of a Community College Scholarship
Program for Low-income Adults

Lisa Barrow
lbarrow@frbchi.org
Federal Reserve Bank of Chicago
Lashawn Richburg-Hayes
Lashawn.Richburg-Hayes2@mdrc.org
MDRC
Cecilia Elena Rouse
rouse@princeton.edu
Princeton University
Thomas Brock
Thomas.Brock@mdrc.org
MDRC

December 2010
REVISED: February 2012
We thank Jonathan Davis, Elizabeth Debraggio, Laurien Gilbert, Shani Schechter, and Zach
Seeskin for expert research assistance and Colleen Sommo and Jed Teres for extensive help in
understanding the data. Joshua Angrist, Jonas Fisher, Luojia Hu, David Lee, Bruce Meyer, Derek
Neal, Chris Taber, and seminar participants at the American Education Finance Association
meetings, Federal Reserve Bank of Chicago, Harris School of Public Policy Studies, and MIT
provided helpful conversations and comments. We also thank Louis Jacobson and Christine
Mokher for graciously providing additional estimates on the value of college courses. The data
used in this paper are derived from data files made available by MDRC. The authors remain
solely responsible for how the data have been used or interpreted. Any views expressed in this
paper do not necessarily reflect those of the Federal Reserve Bank of Chicago or the Federal
Reserve System. Any errors are ours.

Paying for Performance: The Education Impacts of a Community College Scholarship
Program for Low-income Adults
Abstract

We evaluate the effect of performance-based incentive programs on educational outcomes for
community college students from a random assignment experiment at three campuses. Incentive
payments over two semesters were tied to meeting two conditions—enrolling at least half time
and maintaining a “C” or better grade point average. Eligibility increased the likelihood of
enrolling in the second semester after random assignment and total number of credits earned.
Over two years, program group students completed nearly 40 percent more credits. We find little
evidence that program eligibility changed types of courses taken but some evidence of increased
academic performance and effort.

1
I.

Introduction
While the total (monetary and nonmonetary) benefits of attending a two- or four-year

college are seemingly quite high, less than 60 percent of the population 25 to 35 years old reports
having any college experience (Crissey 2009). Even among those who begin college, many have
not completed any degree six years after their initial enrollment. This is particularly true at twoyear colleges which enroll 48 percent of all first-time, first-year college students (Berkner and
Choy 2008).1 Six years after first enrollment, only 14 percent of students beginning at
community colleges have completed an associate’s degree, and only 12 percent have completed a
bachelor’s degree. Nearly one-half have no degree and are no longer enrolled in school.2 As a
result, many researchers and policy-makers have questioned whether there are policies that can
increase enrollment persistence and completion rates at the college level. This paper examines
one such policy—performance-based scholarships—focused on improving academic success and
persistence at community colleges.
Recently, there has been much interest in the ability of incentive awards and scholarships
to improve student outcomes. In this paper, we explore whether a performance-based scholarship
combined with counseling services affected the educational outcomes of low-income community
college students (who were also parents). Students were randomly assigned to treatment and
control groups. The treatment group was eligible to receive scholarship payments over two
semesters for meeting certain benchmarks during the semester and also had access to
supplemental counseling services. These were in addition to the standard financial aid and

1

Relative to the typical four-year institution, community colleges lower the costs of investing in a college education:
their open enrollment policies enable students who lack full preparation to invest in a college education, while their
relatively low tuition and fees make college more affordable to all students.
2
In comparison, 22 percent of students who begin in a public four-year institution and 19 percent of students who
begin in a private (not-for-profit) four-year institution have no degree and are no longer enrolled in school 6 years
after first enrollment (Radford, et al., 2010).

2
counseling services available to control group students. We find that eligibility for the
performance-based scholarship increased persistence by increasing enrollment probability in the
second semester after random assignment.3 After two years, program group students earned 3.7
credit hours more than the control group students, an advantage of 37 percent. We also find some
evidence that the program may have affected academic performance and effort.
Our results are consistent with related studies that have also found positive effects of
performance-based incentives on education outcomes in different settings. At the college level,
Angrist, Lang, and Oreopoulos (2009) provide some evidence that incentive scholarships,
particularly combined with counseling services, may increase academic achievement among
female, first-year students at 4-year colleges and that these effects may persist into their second
year. At the secondary school level, Angrist and Lavy (2009) find in Israel that cash rewards for
high school (Bagrut) certification and intermediate milestones (for example, taking component
tests) increased certification rates among girls by roughly 10 percentage points. They also find
some evidence that the incentive awards increased the likelihood of subsequent post-secondary
school enrollment. Similarly, Jackson (2010a) finds that the Advanced Placement Incentive
Program (APIP) in Texas—which rewards students (and teachers) for AP courses and exam
scores—increased the share of students taking AP or International Baccalaureate (IB) exams. He
also finds some evidence that the APIP increased the shares of students scoring above 1100 on
the SAT Reasoning Test or 24 on the ACT Test, and later evidence (see Jackson 2010b) of
impacts on college matriculation, persistence, and grades. Finally, in a U.S. experiment at the
elementary and 9th grade levels Fryer (2010) finds that financial incentives rewarding students
for education inputs such as reading books, attending school, and turning in homework increased

3

Early results from this study were reported in Brock and Richburg-Hayes (2006).

3
test score achievement. In contrast, he finds that rewarding students for education outcomes such
as grades and test scores led to no improvement in achievement test scores.
This paper is also related to college-level studies looking at merit scholarships and
student aid, more generally. The most compelling evidence on the impact of tuition (and fees)
suggests that students who receive greater grant aid are more likely to enroll in college and to
persist, with larger impacts among two-year college students than four-year college students (see,
e.g., Rouse 1994, Kane 1999, Dynarski 2003, 2000, 2008). Further, Scott-Clayton (2009) finds
that a merit scholarship combined with performance incentives tied to grades and credits earned
(the West Virginia PROMISE program) increases credits earned and the four-year BA
completion rate.
We next discuss a theoretical framework for thinking about educational persistence and
the role of incentive scholarships followed by a description of the intervention studied in section
III. In section IV, we describe the data and present sample characteristics of program participants
in comparison to community college students more generally. The estimation strategy and results
are presented in Section V, and Section VI concludes.

II.

Theoretical framework
A. Persistence and Effort
Following the model outlined by Becker (1967), economists typically hypothesize that

students continue their education until the marginal cost outweighs the marginal benefit. Suppose
that student i’s grade point average (GPA) depends on ability ai, effort ei, and some random
noise εi as follows:
.

(1)

4
Let ε be distributed, F(ε), with density f(ε), and let c(e) reflect the cost of effort. Assume
′

0 and

′′

0. Further assume there is a payoff W for achieving a minimum GPA

with a payoff of zero otherwise.4 Assuming students maximize utility by maximizing the net
expected benefit of effort, the student’s maximization problem is as follows:
max

1

·

. .

0,

Assuming the second order conditions are satisfied, the optimal value of effort,

(2)
, is

characterized by the first-order condition:
′

·

.

(3)

Thus, a student may not enroll or continue in college because the marginal benefit is relatively
low and/or because the costs are relatively high. The research evidence on whether the benefit of
each additional year (or credit) is lower for dropouts than for students who stay in school is
inconclusive (Barrow and Rouse, 2006), but there are many reasons to think that the costs,
broadly construed, may differ across students.

B. Policy intervention and performance-based scholarships
There seems to be agreement that at least some of the dropout is not optimal and many
policy experiments aim to increase educational attainment and persistence. Traditional needbased and merit-based scholarships provide an incentive to enroll in college, such as a reward
payment for registration, effectively lowering the costs of enrolling in college because they are
paid regardless of whether the student passes her classes.

Performance-based scholarships

(PBSs) generally try to improve student outcomes by increasing the immediate financial benefits
from school. For example, payments may be contingent on meeting benchmark performance
4

Alternatively, one could think about there being a payoff to each course completed with a minimum grade level.
We also abstract from the possibility of a higher payoff to achieving grades above the minimum threshold.

5
goals such as minimum GPAs. Thus the incentives can be thought of as increasing the immediate
financial rewards to effort. Because a PBS provides more immediate financial rewards to effort,
we would expect PBS eligible students to allocate more time to educationally productive
activities such as studying which should in turn translate into greater educational attainment. 5
If the density f() in equation (3) is roughly normally distributed with small values in the
tails, then whether and by how much a performance incentive changes an individual student’s
effort will depend on ability and the marginal cost of effort. For a high ability student, increasing
the payoff W will have little effect on her effort because she will essentially be able to meet the
minimum GPA requirement on ability with no effort, i.e. ability alone puts her in the right tail of
the density. Similarly, really low ability will put a student in the left tail of the distribution and an
increase in W will have little effect on her effort because the probability of meeting the minimum
GPA requirement even with high levels of effort is so low and effort is costly. For students in the
middle range of ability, the performance incentive will cause them to increase effort in order to
increase the probability of meeting the minimum GPA requirement. On the cost side (all else
equal) we would expect to see students facing a higher marginal cost of effort to have a smaller
change in effort in response to changes in the payoff W than students facing a lower marginal
cost of effort.6

5

The incentive literature makes clear that to be effective, pay for performance and other incentive-based schemes
must be clear and with tangible consequences or rewards (e.g., Milkovich and Newman, 2002). As a result, the
structure of performance-based scholarships is more likely to generate changes in behavior than are others, such as
Pell Grants, which have less clear benchmarks or have delayed consequences and rewards. For example Pell Grants
require that students make “satisfactory academic progress” for continued eligibility, but it does not affect a
student’s financial aid during the semester in question. Further, both the definition of “satisfactory academic
progress” and the consequences of falling behind academically for Pell eligibility are determined at the institutional
level meaning that the incentives are likely less evident to a student than an incentive structure similar to that in the
program analyzed in this paper.
6
We have attempted to test for such implications of the model empirically by interacting the treatment effect with
prior background variables such as whether or not the individual had already obtained an advanced degree or
certificate, dependency status, and the presence of a child under the age of six. While the signs of some of the
coefficient estimates were consistent with the model, the estimates were generally indistinguishable from zero.
These results are available from the authors on request.

6
While the intention of a performance-based scholarship is to increase student effort in
educationally productive ways, there may be unintended consequences as well. Indeed,
Cornwell, Lee, and Mustard (2005) find that the Georgia HOPE scholarship which had grade
incentives but not credit incentives reduced the likelihood that students registered for a full credit
load and increased the likelihood that students withdrew from courses presumably to increase the
probability that they met the minimum GPA benchmark.

III.

The Opening Doors Scholarship and Counseling Program
The data analyzed were collected as part of the Opening Doors Louisiana (ODLA) study

conducted by MDRC between 2004 and 2005 as part of a larger, multiple site demonstration
project.

The Opening Doors demonstration was a longitudinal study that addressed two

problems facing community colleges: 1) high rates of attrition, especially by low-income
students; and 2) a dearth of reliable evidence on how to help students persist in community
college to achieve long-term academic and labor market success.
The ODLA study was implemented at three community college campuses in the New
Orleans area -- Delgado Community College (DCC) (the City Park and West Bank Campuses)
and Louisiana Technical College (LTC)-West Jefferson campus -- and tested the effectiveness of
an intervention that included a scholarship with both an incentive-based component and one
more similar to traditional merit or need-based scholarships and enhanced counseling services.
The study targeted low-income parents who were primarily first-term students at the college
although some continuing students ready to move from remedial/developmental-level courses to
college-level courses were also accepted into the program. To be eligible for the study, students
had to be: willing to attend school at least half-time; 18 to 34 years old; the parent of at least one

7
dependent child under 19 years old; and have family income below 200 percent of the federal
poverty line. In addition, students had to have earned a high school diploma, a General
Educational Development (GED) certificate, or a passing score on a college entrance
examination, but they could not already have a degree or occupational certificate from an
accredited college or university. These requirements meant that the eligible population was
disproportionately female and poor. See Richburg-Hayes et al. (2009) for more details.

A. Recruitment and random assignment
Students were recruited on campus over four consecutive semesters (including summer)
from spring 2004 to spring 2005 with a sample goal of 1000 students. Once program staff
determined eligibility for the study, students who agreed to participate provided baseline
demographic information, completed a survey on health information, and were randomly
assigned by MDRC to the program or control group. Everyone completing the random
assignment process received a $20 gift card. In Table 1 we present information on the number of
students in each cohort on each campus. In total 1019 students were recruited; 505 were
randomly assigned to the program-eligible group and 514 were assigned to the control group.
Not surprisingly, recruitment was most successful for the fall cohort; the spring 2005 cohort is
unusually small simply because recruitment stopped once recruiters determined that the target
sample would be met. Delgado is the larger of the two institutions, and the City Park campus is
larger than the West Bank campus generating differences in sample sizes across sites.

B. Scholarship and incentives

8
The ODLA offered program-eligible students a $1000 scholarship for each of two
semesters (maximum $2000 total) as a supplement to the Pell Grant and other financial aid
programs. The maximum scholarship payment was generous in that it exceeded full-time tuition
and fees at the two colleges. In 2004-05, tuition and fees were roughly $1500 per year for a fulltime student at Delgado and $900 per year for a full-time student at LTC. That said, these
students typically had a fairly large amount of unmet need that would have to be met by working
and/or taking out student loans. For example, the total cost of attending Delgado (tuition, fees,
books, and room and board) was $12,126 per year in 2004-05. With a full Pell grant of $4050, a
student would have unmet need of more than $8000 (See Richburg-Hayes et al. (2009).).
Scholarship payment was structured such that a student received $250 at the start of the
semester if she enrolled at least half-time (six or more credit hours), she received $250 after
midterms if she stayed enrolled at least half-time and maintained a C-average or better, and she
received $500 after the end of the semester if she stayed enrolled at least half-time and
maintained a C-average or better for the semester. Receiving payment at the end of the semester
was not contingent on receiving the midterm payment so students with less than a C-average
after midterms could raise their grades to qualify for the $500 payment at the end of the
semester. Similarly, failure to qualify for payment in the first semester did not disqualify the
student from payments in the second semester.
In Table 2 we present information on the number and percentage of program and control
group students receiving scholarship payments, the distribution of the size of payments received,
and total dollar value of the payments received in the first and second semester after random
assignment. We also present similar information cumulatively for the first through seventh

9
semester after random assignment. 7 Eighty-four percent of program group students received one
or more scholarship payments in the first semester, 62 percent received one or more scholarship
payments in the second semester, and nearly 90 percent of program students received at least one
scholarship payment over the first through seventh semester after random assignment. Roughly
30 percent received the full $2000 scholarship over the 7 semesters after random assignment, and
nearly 60 percent received $1000 in at least one semester. In each of the first two semesters, the
average scholarship payment among recipients in the program group was around $750. Overall
program group students received total scholarship payments averaging $1133. While we cannot
measure whether program group students were mistakenly told they were not part of the
program, we can check the number of control group students who received scholarship
payments.

Only 3 control group students received any payment so contamination seems

minimal.
When asked how they used the scholarship money, 66% of respondents reported using it
for books and school supplies and about 45% reported using it to help pay bills, buy gas or bus
fare, and pay for child care costs. Asked for the main use of the scholarship money, 46% of
recipients cited to purchase books and school supplies (Richburg-Hayes, et al. 2009). These uses
are consistent with (successful) participants attempting to use the funds to help with educational
expenses or basic household maintenance.

7

With the exception of the spring 2005 cohort, students did not have to enroll in consecutive semesters to take full
advantage of the offer. Because the program ended in August 2005, students from the spring 2005 cohort needed to
attend both the spring and summer 2005 semesters to receive the maximum benefit; whereas, students from the
spring 2004 cohort, for example, had five semesters over which they could take advantage of the program. The
incentive structure was also modified somewhat for the summer semesters at Delgado during which classes met half
as many months but for twice as many hours each session. For the summer semesters at Delgado, program students
were eligible for $500 at the beginning of the semester after registering at least half-time and $500 at the end of the
semester if they stayed enrolled at least half-time and received a C-average or better. Additionally, for the final
semester of the program (summer 2005), Delgado also allowed students a half scholarship of $500 total if they
enrolled in a single, three-hour credit course.

10

C. Enhanced counseling
MDRC had originally hoped that the counseling component would result in counselors
getting to know students on a personal level and taking an active role in non-academic advising.
While this may have been true for some counselors, MDRC’s study of the program
implementation showed that the counselors more typically served as program monitors: checking
up on students’ enrollment status, verifying grade benchmarks were achieved, meeting with
students to explain rules, and handing out scholarship checks (Richburg-Hayes, et al. 2009).

III.

Data sources and sample characteristics
All data used in this study were compiled by MDRC and come from several sources.

From the baseline data collected before random assignment we use basic demographic
characteristics. Scholarship data provide information about the timing and size of the Opening
Doors Scholarship payments. Transcript data for at least 7 semesters following random
assignment were collected from Delgado and LTC and contain data on registration, credits
earned, grades, and withdrawals. Notably, the transcript data only cover semesters in attendance
at DCC and LTC. However, MDRC also matched the ODLA participants to National Student
Clearinghouse (the Clearinghouse) data. The Clearinghouse data provide enrollment, degree, and
certificate data for all students matched to any Clearinghouse reporting institution. That said, the
Clearinghouse coverage is not complete due to non-reporting institutions and students who opt
out of having their data included. Importantly, LTC did not report to the Clearinghouse.
Finally, MDRC attempted to survey all participants with a follow-up survey roughly 12
months after random assignment; however, the follow-up survey was interrupted as a result of

11
Hurricane Katrina on August 29, 2005. Ultimately 79% of the original participants completed a
follow-up survey. Nearly half the sample (492 respondents) was surveyed before Hurricane
Katrina, an average of 13 months after random assignment. The remaining 402 respondents were
surveyed after Hurricane Katrina, an average of 21 months after random assignment. From these
follow-up data we use measures of the participants’ educational experiences, namely reports on
time spent on campus and studying.
Table 3 presents selected mean baseline characteristics for study participants at the time
of random assignment. For comparison, we also present mean characteristics for a nationally
representative sample of first-time, two-year public college students between the ages of 17 and
34 from the U.S. Department of Education’s 2004 Beginning Postsecondary Survey (BPS) and
for the subset of these students from Louisiana.8 Compared with community college students
generally or the subset of students in Louisiana, the eligibility requirements mean that study
participants were nearly 5 years older than typical first-time community college students, more
likely to be female (92 percent versus 57 percent of Louisiana community college students),
more likely to be black (85 percent compared with 43 percent of Louisiana community college
students), more likely to have children (all participants versus 22 percent), and less likely to be
financially dependent on their parents (17 percent of study participants compared with 73 percent
of first-time community college students). Study participants were also less well-prepared
academically: 17 percent of study participants had a GED rather than a high school diploma
compared with only 8 percent of community college students in the nation or Louisiana.
As another way to understand the characteristics of the study participants compared with
community college students more generally, we estimated the likelihood that a community
8

The BPS is a longitudinal study that follows students who are enrolled in a postsecondary institution for the first
time. The most recent BPS cohort consists of approximately 19,000 students who were first interviewed in 2004 as
part of the National Postsecondary Student Aid Study; we use data from 2004.

12
college student in the BPS would complete an associate’s degree or higher and their number of
years of schooling within six years. We then used the coefficient estimates to predict educational
attainment for each sample. Not surprisingly, when evaluated at the mean of the individual
characteristics, we estimate that the students in the Opening Doors sample are about 3.5
percentage points less likely than students in the BPS to complete at least an associate’s degree,
and they are predicted to complete 0.18 fewer years of schooling within six years of initial
enrollment. In sum, the study participants were generally more likely to possess characteristics
that are associated with an increased risk of failing to complete a college degree than the typical
community college student in Louisiana or the nation.
We present mean characteristics by random assignment status in the first two columns of
Table 4. In each case the means are adjusted for randomization pool fixed effects reflecting the
campus and cohort of study recruitment. In the third column we present the p-value for the test
that the adjusted mean for students assigned to the program group is equal to the adjusted mean
for the students assigned to the control group.

Two characteristics—sex and race—are

statistically different between the treatment and control groups at the 10 percent level of
significance. At the 5 percent level of statistical significance, the control group is more likely to
report race as “other” and more likely to report living in section 8 or public housing. However,
jointly the baseline characteristics do not predict treatment status (p-value on the F-test = 0.19).9

IV.

9

Estimation and Results

Similarly combining baseline characteristics into an “outcome” index we find no statistically significant
differences by treatment status (p-value = 0.532). Results for all estimates including baseline controls are similar and
available from the authors on request. Notably, the precision of our estimates is not improved by including baseline
controls.

13
Below we present estimates of the effect of program eligibility on a variety of outcomes.
We model each outcome Y for individual i as follows:
Θ

,

(4)

where Ti is a treatment status indicator for individual i being eligible for the program scholarship
and enhanced counseling, Xi is a vector of baseline characteristics (which may or may not be
included), pi is a vector of indicators for the student’s cohort and campus of random assignment,
νi is the error term, and α, β, Θ, and γ are parameters to be estimated with β representing the
average effect on outcome Y of being randomly assigned to be eligible for the scholarship and
enhanced counseling services.
A. Program effects at the participating colleges
In Table 5 we present estimates of the effect of program eligibility on various short-run
outcomes measured by transcript data provided by DCC and LTC. In column (1) we provide
outcome means for the control group participants. The program effect estimates with standard
errors in column (2) are estimated including controls for randomization pool fixed effects but no
other baseline characteristics. Because we provide estimates for a number of related outcomes, in
column (3) we present p-values adjusted for multiple testing.10
The top panel of Table 5 includes transcript outcome measures for the first semester after
random assignment. We find that program-eligible students were 5 percentage points more likely
to be enrolled in any course at the intervention institution after the end of the drop/add period;
however, the impact does not remain statistically significant at the 5 percent level after adjusting

10

We calculate adjusted p-values using bootstrap resampling of vectors in a stepdown fashion following Westfall
and Young (1993). In Table 5 we adjust the p-values considering the group of outcomes within semester.

14
for multiple testing.11 We find that program-eligible students attempted and earned more credits
as well. In fact, program group students earned roughly 1.2 credits more than control group
students in the first semester (a difference that is significant at the 5% level once adjusting for
multiple testing). Notably, this impact is mostly explained by gains in regular credits attempted
and earned (rather than remedial credits). In order to receive any scholarship payment, students
were required to register for at least 6 credits. In results not reported (here but available on
request), while program eligible students were less likely to be enrolled less than half time (1 to 5
credits) and more likely to be enrolled either part-time (6 to 11 credits) or full-time (a minimum
of 12 credits), the differences are not statistically significant. Overall, if we create an index of the
first semester outcomes as in Anderson (2008) we find a statistically significant difference
between treatment and control students (p-value = 0.022).12
We present program effect estimates for outcomes in the second semester after random
assignment in the bottom panel of Table 5. Here we find that program eligibility increased
persistence: program-eligible students were 15 percentage points more likely to have enrolled in
any course after the second semester drop/add period with an adjusted p-value<0.0001. This
strong effect on enrollment generates several other statistically significant differences because,
for example, one cannot earn credits without enrolling. Program group students attempted 1.2
credits more than control group students and by the end of the second semester had earned 1.1
more credit hours, 40 percent more than the control group students.
Such increases in credit accumulation can be decomposed into two impacts: an impact of
the program on enrollment and an impact of the program on credits attempted/earned conditional
11

The “drop/add” period is the period at the beginning of the semester during which students may elect to add or
drop a course for which they had initially registered. It typically ended 5 days after the start of the semester.
12
The index includes all semester 1 outcomes presented in Table 5 as well as the indicators for full-time and parttime status discussed in the text. In creating these indices, we weighted by the inverse of the covariance matrix.

15
on enrollment. Following Lavy (2009), one can write the average number of credits earned or
attempted by students in group i as:
1

(5)

where Pi is the share of students registering that semester, Yi1 is the number of credits earned or
attempted by students registering and Yi0 is the number of credits earned or attempted by students
not registering. By assumption, credits attempted and credits earned equal zero among students
who do not register so the average expected number of credits earned/attempted for group i is
PiYi1. The average treatment effect is P1Y11- P0Y01 where group 1 is the program group and group
0 is the control group. The average treatment effect can be rewritten as (P1 – P0) Y11+ P0 (Y11 Y01). The first term represents the portion of the unconditional increase that is due to the impact
of the program on the likelihood of enrollment while the second represents the increase in credits
attempted or earned conditional on enrollment.13 We estimate that all of the unconditional
increase in credits attempted in the second semester is due to an increase in the likelihood of
enrollment while for credits earned in the second semester, 27 percent of the increase is due to
the increase in credits earned conditional on enrollment.14
Once again, program group students do not seem to be shifting credits disproportionately
toward remedial courses. We also find (in results not reported here) that program group students
were 12.2 percentage points more likely to enroll part-time, but there is no statistical difference
13

To do this calculation, we estimate the ATE components separately by randomization pool. Specifically, we
calculate the weighted average of each component for the 11 pools where the weights are the share of the students in
each pool. To estimate the share of the impact resulting from enrollment, we divide the weighted average of this
component by the weighted average of the ATE.
14
In the first semester when the program effect on registration is smaller, we estimate that 86 percent of the increase
in credits attempted is due to the increased enrollment while for credits earned 71 percent of the increase is due to
the increase in credits earned conditional on enrollment.

16
in the percentage enrolled full-time or less than half time. Once again, an index of second
semester outcomes is statistically different between treatment and control group students with a
p-value < 0.001.15
B. Longer-run outcomes and effects on enrollment at “all” institutions
In order to consider longer-run outcomes for program and control group students, we
focus on the first two cohorts of students for whom we observe the greatest number of semesters
of potential study both before and after Hurricane Katrina.16 Limiting the sample to these first
two cohorts, in the first column of Table 6 we present estimates for longer run outcomes based
on transcript data. Outcomes related to enrollment are presented in the top panel while outcomes
related to credits earned are presented in the bottom panel. During the first year after random
assignment, a student could have enrolled for up to 3 semesters and earned at least 36 credits if
she had enrolled full-time (12 or more credits) in each semester. While program group students
were (statistically) no more likely to be enrolled in any course in the first semester after random
assignment, they were 18 percentage points more likely to be enrolled in the second semester and
nearly 12 percentage points more likely to be enrolled in the third semester. Cumulatively the
program students were enrolled for 0.35 more semesters than the control group at the
intervention campus in the first year. In the second year after random assignment, we find that
program students had enrolled for 0.13 more semesters than the control group students and that
cumulatively after two years the program group had enrolled for nearly 0.5 more semesters.

15

The index includes all semester 2 outcomes reported in Table 5 as well as indictors for full-time and part-time
enrollment.
16
Program impact estimates for outcomes presented in Table 5 are quite similar if we limit the sample to the first
two cohorts of students. These results are available from the authors on request.

17
In the bottom panel, we present results on total credits earned. After the first year,
students in the program group had earned 3.3 more credits (or roughly one-quarter of one fulltime semester’s worth of credits) and nearly 45 percent greater than the number of credits earned
by the control group. In the second year after random assignment (semesters 4, 5, and 6), we find
no statistically significant difference in the total number of credits earned; however, the positive
point estimate indicates that control group students were not catching up to program group
students over a longer time horizon.17 Two years after random assignment, program group
students had enrolled nearly one-half of one semester more than control group students and
earned an additional 3.7 credits.
While program eligibility increased persistence and the number of credits earned as
shown above, these reflect outcomes at the intervention campus. Clearly control group students
had less incentive to stay at the intervention campus if they decided that a different campus
would be a better match. As a result, one might expect that our estimates of the program’s impact
are biased upward. In order to examine this possibility, we supplement our transcript data with
those available from the National Student Clearinghouse in order to include education outcomes
at other institutions. As mentioned in the data discussion, these Clearinghouse data are not ideal
because not all institutions report to the Clearinghouse, and students may decline to have their
information included. In particular, LTC does not report to the Clearinghouse.18 Therefore, we
report results for all study participants as well as the sub-sample of participants who were

17

In results not shown here, we estimate the impacts on the likelihood of enrollment in the 4th, 5th, and 6th semesters
after random assignment separately. While the point estimates are positive (reinforcing the likelihood that the
control group students were not catching up to the program group students), the magnitudes were not statistically
significant at conventional levels. These results are available on request.
18
MDRC was able to match nearly 80 percent of participants with a record in the Clearinghouse data. Of the
participants not matched with a Clearinghouse record, 71 percent were from a cohort recruited at LTC.

18
recruited on either of the DCC campuses. These results are presented in the remaining columns
of Table 6.
In column (2) of Table 6 we supplement the transcript data provided by the institutions
with data from the Clearinghouse. The results are roughly similar to those presented in column
(1) with the largest impacts in the percentage of students enrolled in any course in the second and
third semesters after random assignment. Program-eligible students also enrolled for roughly
one-third more semesters in the first year following random assignment.
Columns (3) and (4) limit the sample to students recruited at the Delgado campuses since
Delgado reports to the Clearinghouse. Using Delgado transcript data, the estimated program
effects are somewhat larger than the transcript data estimates presented in column (1) which
include LTC recruits. Using Clearinghouse data for the Delgado campuses only, we find that
program-eligible students were 18.8 percentage points more likely to enroll in the second
semester and 15.2 percentage points more likely to enroll in the third semesters after random
assignment. Over the first year, program-eligible students enrolled in 0.40 more semesters than
control group students; over two years, program-eligible students enrolled in 0.52 more
semesters than control group students.
Overall the Table 6 results suggest that the program increases enrollment persistence and
educational attainment rather than simply encouraging program students to maintain enrollment
and earn credits at a particular institution in the short run. If the scholarship served only to
encourage program group students to stay at the intervention campus while control group
students enrolled at other campuses, then we would have expected to see no difference between
treatment and control students in second and third semester enrollments once we accounted for

19
enrollment at all campuses reporting to the Clearinghouse. Indeed, including data on enrollment
from the Clearinghouse data reduces the point estimate of the program effect on second semester
enrollment by a small amount; however, the estimated program impact remains large and
statistically significant.19

C. Does program eligibility affect the types of courses taken?
One unintended consequence of the incentive-based scholarship may have been to affect
the types of courses for which students registered. We have shown in Table 5 that program
group students did not reduce the number of total credits attempted and program and control
group students did not differ in the number of remedial credits attempted. However, program
group students may have attempted to register for “easier” courses in order to increase the
probability that they would be able to meet the minimum semester GPA of 2.0 to qualify for the
mid-semester and end-of-semester scholarship payments. While we do not have direct
information about the difficulty of different courses offered, we do have information about the
“fields” of the courses taken and can assess whether program and control group students took
different numbers of credits in different fields.
Jacobson, LaLonde, and Sullivan (2005) find that among displaced workers, earnings
gains per credit are larger for quantitative or technically-oriented courses than for non-technical
courses. Similarly, Jacobson and Mohker (2009) find that additional courses in health-related

19

Ideally, we would also like to use these data to examine long run outcomes such as certificate and degree receipt.
Unfortunately, because these students are not typically enrolled full-time and because we have Clearinghouse data
only up through two years after random assignment, we observe very few students completing degree or certification
requirements. Only 12 of the original Delgado students show up as having received a certificate or degree: 6 have
received a certificate, 5 received an Associates’ degree, and 1 received a Masters’ degree.

20
fields are the most valuable followed by vocational/technical courses, professional courses, and
courses in the science, technology, engineering, and mathematics (STEM) cluster. They find no
statistically significant value of additional courses in social sciences or humanities. If we assume
monetary returns to courses are higher for more difficult courses, we can infer whether the
program induced students to take easier courses by looking at the estimated program effects on
credits attempted by field. Shifts in course-taking away from health-related, vocational/technical,
STEM, and professional courses toward courses in the social sciences and humanities would
provide evidence the program may have induced students to take easier courses.20
We follow Jacobson and Mohker (2009) in assigning each course to one of eight
categories—Health

Related;

Humanities;

Professional;

STEM;

Social

Sciences;

Vocational/Technical; Remedial; or Other. See Appendix A for more detail. In column (1) of
Table 7, we present the cumulative average number of credits attempted by field for the control
group students in the first two semesters after random assignment. This ranges from 0.22 credits
in the Vocational/Technical field to 4.17 credits in STEM courses (column (1)). We then use the
(cumulative) number of credits attempted in each field as an outcome variable and present the
program effect estimates for each field in column (2). If scholarship eligibility does not affect
the fields of courses taken and those induced by the program to register take a similar
distribution of classes to those who would have registered anyway, then we would expect to find
increases in the number of credits attempted between treatment and control group students for all
fields. As can be seen in column (2), all program effect estimates are positive, but only the
program impact of 0.41 credits attempted in social sciences can be rejected at the 5 percent level

20

We note, however, that this prediction is not entirely clean because changes in the pattern of course-taking may
occur instead because those students induced by the program to enroll take courses in different fields than those who
would have enrolled anyway.

21
after adjusting for multiple testing, providing some evidence that the performance-based
scholarship induced eligible students to register for easier courses, on average. 21
The results are less clear, however, when we focus on the types of credits earned, the
results of which are presented in columns (3) and (4). Average credits earned by field for the
control group students are presented in column (3) and range from 0.16 credits in the
vocational/technical field to 2.38 credits earned in STEM. In column (4) we present the
associated program effect estimates. Once again we find that the program impact on credits
earned is positive for each field. Further, program group students earn an additional 0.654 STEM
credits (adjusted p-value = 0.018) and 0.412 social science credits (adjusted p-value = 0.002)
than control group students; no other differences in credits earned by field are statistically
different from zero at conventional levels after adjusting for multiple testing. While Social
Sciences are likely to be “easier” classes as measured by the average earnings effect per course
taken, by this same measure STEM classes are likely to be “harder” classes. Thus, we conclude
that there is little evidence that the program resulted in students earning relatively more credits in
“easier” courses as measured by their value in terms of future earnings.22

D. Does program eligibility increase academic performance and effort?
Clearly enrolling in school requires more educational effort than not enrolling. However,
the fact that program eligibility increased the number of credits earned in the first semester after
random assignment and that 27 percent of the increase in second semester credits earned is due
21

If we simply categorize courses as “hard”—Health Related, Professional, STEM, and Vocational/Technical—or
“easy”—Humanities, Social Sciences, Remedial, and Other—we find that the program effect on credits attempted is
0.81 credits for hard courses (adjusted p-value = 0.229) and 0.93 credits for easy courses (adjusted p-value=0.051).
Adjusted p-values are calculated taking into consideration all credits attempted and credits earned outcomes tested in
Table 7 in addition to the aggregate easy and hard categories.
22
Again if we simply categorize courses as hard or easy (see footnote 21) we find program effect estimates of 1.183
more hard credits and 1.124 more easy credits in the first two semesters after random assignment. Both are
statistically different from zero after adjusting for multiple testing.

22
to an increase in credits earned conditional on enrollment suggest that program eligibility may
have had an impact on student effort for a student who would have enrolled regardless of
scholarship eligibility. To look for evidence of a program effect on academic performance and
effort more directly, we turn to estimates of the effect of program eligibility on course grades,
term GPA, hours spent on campus, and hours spent studying.
Because not all courses result in a letter grade, we begin by simply looking at the
distribution of course grades by treatment status. These are presented in Figures 1a and 1b,
respectively, for the first and second semesters after random assignment. For each group the bars
represent the percent of courses earning that grade. Looking at the letter grades for the first
semester on the left hand side of figure 1a, we can see that students in the program group earn
somewhat higher shares of grades “A,” “B,” and “C.” Specifically, 53 percent of courses taken
by control group students resulted in a grade of A, B, or C compared with 62 percent of courses
taken by students in the program group. In contrast, 14 percent of courses taken by students in
the control group resulted in a grade of “F” compared with 9.5 percent of courses taken by
students in the program group. Looking at the “ungraded” course outcomes, nearly 21 percent of
courses taken by control group students resulted in a withdrawal compared with 15 percent of
courses taken by program group students. Indeed, a simple chi-squared test for independence of
treatment status and course grade category has a p-value of 0.000.
In the second semester of the program, the grade distributions look more similar although
the distributions are still statistically different with the p-value on the chi-squared test for
independence of treatment status and course grade category equal to 0.021. Grades of A, B, and
C are more common among courses taken by program group students (57 percent of course
grades for program group students versus 51 percent of course grades for control group

23
students). Courses taken by program group students are somewhat less likely to end up with a
grade of F and less likely to end up as a withdrawal.23
The grade distributions in Figure 1, particularly for the first semester in which there is a
smaller program effect on registration, suggest that indeed program eligibility improved
students’ academic outcomes for both graded and ungraded course outcomes. MDRC calculated
term GPAs from the transcript data for students who enrolled. Using indicators for “GPA greater
than or equal to 2.0” and “no GPA,” we find that 58 percent of program group students earn a
GPA of 2.0 or higher in the first semester compared to 47 percent of control group students, a
difference that is statistically significant at the 1 percent level after adjusting for multiple testing.
Program group students are 7.7 percentage points less likely to have no GPA with an adjusted pvalue of 0.11. These differences are even larger in the second semester after random assignment
because program eligibility has such a large effect on enrollment. Thus, we look at upper and
lower bound estimates of the effect of program eligibility on term GPAs and other measures of
effort based on survey responses using assumptions about selection.
In addition, the MDRC follow-up survey includes two questions that may be used to
assess whether the program affected hours spent on campus and hours spent studying in the first
and second semester. For the survey questions on hours spent on campus, the potential response
categories are: none, 1 to 3, 4 to 6, 7 to 9, 10 to 12, and more than 12. For the survey questions
on hours spent studying, the potential response categories are: none, 1 to 3, 4 to 6, 7 to 9, 10 to
12, 13 to 15, 16 to 18, and more than 18 hours. We convert the responses to continuous
measures using the midpoint of the range and assigning 15 hours to respondents who report more
than 12 hours per week on campus and 20 hours to respondents reporting more than 18 hours per
23

Eleven percent of program group courses receive a grade of F and 22 percent ended up with a withdrawal. In
comparison, 13 percent of control group courses ended up with a grade of F and 28 percent ended up with a
withdrawal.

24
week spent studying.24 Students who report not being enrolled in the intervention school that
semester are assigned missing hours for both activities.
In Table 8, column (2) we present estimates of how program eligibility affected term
GPA and effort ignoring the selection effect. Because program eligibility affects the probability
that a student is enrolled in school, it also affects whether we observe GPA as well as our
measures of effort—hours spent on campus and hours spent studying. Furthermore, observations
on hours spent on campus and studying are limited to follow-up survey respondents. As a result,
we follow the trimming strategy of Lee (2009) in estimating upper and lower bounds of
treatment effects in the presence of sample selection.25,26 Namely, we trim the top or bottom
“excess” share of observations from the treatment group (assuming treatment increased
registration) and compare this trimmed mean to the control group mean in order to generate the
lower and upper bound estimates of the effect of program eligibility on the outcome of interest.
These lower and upper bound estimates are presented in columns (3) and (4). Once again
the mean of the outcome variable for the control group is presented in column (1).27 Ignoring
selection, program eligibility raised first semester GPA by 0.18 points. The lower bound estimate
24

We have also tried converting to continuous measures using the minimum or maximum of the range. The results
for hours spent studying are quite similar to those using the midpoint assumption. For hours spent on campus, the
lower bound estimates are also insensitive to the interpolation assumption. The upper bound estimates for the effect
of the program on hours on campus are somewhat more sensitive to the assumption ranging from 0.31 to 0.70 hours
in the first semester and ranging from 1.2 to 2.1 hours in the second semester.
25
In our particular application, we trim the sample within randomization pool and then calculate the weighted mean
of the separate estimates to get the overall estimates of the bounds.
26
An alternative strategy is to assume that the students not enrolling would have had GPAs or hours of effort at the
bottom of the distribution and then artificially censor the data and estimate Tobit regressions as in Angrist,
Bettinger, and Kremer (2006). One could also make similar assumptions and estimate quantile regressions looking
for treatment effects in the upper quantiles of the distributions. If we do the latter for GPA effects, we estimate a
0.13 grade point effect on GPA at the median in the first semester (median control group GPA=2.0) and no effect at
the 75th percentile (control group GPA=3.0). In the second semester we find no effect at the median (control group
GPA of 0.0) and a 0.5 grade point effect on GPA at the 75th percentile (control group GPA=2.29). Using the strategy
of Angrist, Bettinger, and Kremer (2006) we generally get somewhat larger estimates although the estimates are
sensitive to the choice of the artificial censoring points.
27
If we control for student baseline characteristics for the outcomes presented in table 8, the treatment impacts are
generally somewhat larger. For example, the estimated impact on first semester GPA rises to 0.24 with a standard
error of 0.084. With the exception of hours spent on campus during the second semester, all other point estimates
rise as well, but none are large enough to become statistically different from zero at conventional levels.

25
is 0.04 points and the upper bound estimate is 0.38 points. The estimated impact on second
semester GPA is smaller. Ignoring selection, program-eligible students had second semester
GPAs that were 0.07 points higher than control group students. The lower bound estimated
impact is -0.23 points, and the upper bound estimate is 0.36 points.28
We assume that students’ decisions about whether to enroll are driven by expectations
about their own ability and that their expectations are correct on average (following the literature
on dropout decisions and students’ learning about their own ability to acquire human capital (See
Stinebrickner and Stinebrickner (2009) and Trachter (2009).). As a result, we expect those
induced by the program to enroll in college will, on average, be drawn from the bottom of the
potential GPA distribution. This seems most compelling for the second semester after random
assignment when most students have experienced a semester’s worth of information about their
own ability. Indeed conditional on registering for the first semester, first semester GPA is a
significant predictor of registering second semester. This argument is somewhat less compelling
for the first semester in which students presumably have received no new information about their
ability to acquire human capital between being inducted into the study and enrolling in classes.
As a result, 0.18 GPA points is our preferred estimate of the effect of program eligibility on
student GPA in the first semester after random assignment.29
In the second semester after random assignment we believe the selection mechanism is
operating such that those induced by the program to persist are coming from the bottom of the
potential GPA distribution. As a result, our preferred estimate of the effect of program eligibility
28

If the students induced by the program to earn a GPA earned the lowest GPAs among the program group students
(in other words those induced to earn a GPA are the students who are trimmed from the program group) then the
upper bound estimate of the effect of the program on GPA is the correct estimate of the effect of the program on
GPA among students who would have earned a GPA in the absence of the program. Likewise, the lower bound
estimate is the correct estimate if the students induced by the program to earn a GPA earned the highest GPAs
among the program group students.
29
If we instead assume all students with missing GPAs earned a 4.0, for example, the point estimate of the treatment
effect is still positive.

26
on term GPA in the second semester is between 0.07 and the upper bound estimate of 0.36. In
fact, if we impute second semester GPAs equal to first semester GPAs for students without a
second semester GPA our estimate of the effect of program eligibility on second semester GPA
equals 0.148 grade points with a standard error of (0.092).30 Thus, we conclude that program
eligibility induced or enabled students to put more effort toward their courses resulting in
somewhat higher semester GPAs.
When we examine the first semester survey outcomes—hours spent on campus and hours
spent studying—we find at most small effects of program eligibility on student effort on these
margins, and the point estimates are not statistically different from zero. On average in the first
semester, program-eligible students report having spent 0.07 more hours on campus and 0.12
more hours studying than students in the control group. The lower and upper bounds for the
effect estimates are -0.15 and 0.44 for hours on campus and -0.6 and 0.6 for hours studying.
Even if we think the upper bound estimates are the more realistic point estimates, program
eligibility only increased studying and time on campus by about 30 minutes per week, roughly a
5 percent increase at the control group mean.
The estimated program impacts are larger for the second semester (as are the standard
errors). On average, program eligible students report having spent 0.48 more hours on campus
during the second semester and 0.68 more hours studying. Bounds on estimates for hours spent
on campus and studying in the second semester are also larger and include negative values. That
said, if we believe the upper bound estimates are more realistic, the estimated effects on hours
spent on campus and studying are closer to 90 additional minutes per week for each, a 25 percent
increase in time on campus at the control group mean and a 40 percent increase in time spent
studying at the control group mean. While the likely direction of selection is difficult to assert,
30

The point estimate is driven to zero if we impute a second semester GPA of 2.6 for all students missing GPAs.

27
we believe the (positive) upper bound estimate is closer to the “truth” than the (negative) lower
bound estimate. We draw this conclusion because empirically we find that first semester hours
spent studying and on campus for control group students who enroll in both the first and second
semester are higher than first semester hours spent on campus and studying for control group
students who enroll in the first but not the second semester. As in theory the control group
represents the counterfactual for the program group, this finding suggests that the program group
students who were induced to enroll in the second semester as a result of the program come from
the bottom of the distributions of hours studied and on campus as assumed in the calculation of
the upper bound. As a result, we believe the results provide suggestive evidence that program
eligibility had positive effects on hours spent on campus and studying during the second
semester after random assignment and that the correct estimates are somewhere between the
average and upper bound estimates.

V.

Conclusion
We evaluate the effect of eligibility for a performance-based scholarship combined with

counseling on education outcomes for low-income community college students who are also
parents. We find evidence that the program increased student enrollment persistence and may
have increased student effort. In particular, program eligibility increased enrollment by 15 to 18
percentage points relative to control group enrollment in the second semester after random
assignment.
The program also may have affected academic performance and effort. First semester
GPAs for program group students were 0.18 points higher than first semester GPAs for control

28
group students. Assuming those induced to register in the second semester have lower GPAs on
average, the program effect on GPA ranges between 0.07 and 0.36 GPA points. We find little
evidence of a program effect on effort in the first semester as measured by time on campus or
time spent studying. In the second semester, the upper bound estimates of the effect on time
spent on campus and time spent studying are increases of 25 and 40 percent, respectively.
Over two years following random assignment, program group students earned 3.69
credits more than control group students. This translates into an additional 1.23 courses. Based
on data from Florida, Jacobson and Mokher (2009) estimate that for a student beginning at a
two-year college, each course completed is worth an additional $121 per year in annual earnings,
similar to estimates for displaced workers from Jacobson, LaLonde, and Sullivan (2005).31
Assuming this value stays constant in real terms, over 20 years 1.23 additional courses is worth
$2977. The cost of this gain in terms of scholarship payments was roughly $1100 per pupil. As
long as the administrative and other costs were less than $1877 per pupil, which seems quite
likely, the benefits of this program in terms of increased future income would seem to outweigh
the cost of providing the scholarship.
That said, we have no longer-term information on wages in order to say that inducing
these particular students to persist and earn more credits resulted in higher future earnings. The
scholarship itself was fairly valuable in terms of hourly wages. At baseline, MDRC collected
information on whether students were currently employed and if so, their current wage. Just over

31

This estimate corresponds to the last two columns of the Results for Regression Models table in Appendix 4 of
Jacobson and Mohker (2009) and is based on a regression of quarterly earnings on highest credential received
(certificate, AA, BA, or graduate degree); total number of courses taken; and controls for educational preparation
and performance, student demographics, experience, location, and school characteristics. For our purposes, the
authors provided estimates that limited the sample to students beginning their post-secondary education at a twoyear college and do not include concentration indicators. If the sample is limited to students beginning at a four-year
college, each course is worth $216 per year. Estimates from Jacobson, LaLonde, and Sullivan (2005) (Table 3,
column (6)) imply that women’s earnings increased $101 per year (1995$) per course (3 credits) completed which
translates into a 13.1 percent return for one academic year’s worth of credits (9 courses).

29
50 percent of the study participants were currently employed at baseline (52 percent of the
control group and 51 percent of the treatment group), and of those 86 percent were paid on an
hourly basis. The average wage among those employed hourly was $7.32 with a median wage of
$7.00. At $7.32 per hour, a student would have to work 102.5 hours over the semester to earn
$750 or roughly 7 hours per week over a 15 week semester. Assuming students were planning to
devote some hours to school without the PBS, for many an additional 4 or 5 hours of studying to
meet the GPA benchmarks may have been a better paying job than their alternative.
This study leaves open several questions about how this program or any other
performance-based scholarship may affect educational outcomes. Angrist, Lang, and Oreopoulos
(2009) find some effects of a performance-based scholarship on academic achievement in a more
traditional college setting, but these impacts are driven by female students. Given that the
Opening Doors Louisiana participants are predominantly women, the question remains whether
performance-based scholarships can improve academic outcomes for men. Furthermore, one
would hope that performance-based scholarships would have an effect because they enable or
encourage students to spend more time in educationally productive activities such as studying.
Stinebrickner and Stinebrickner (2003) provide evidence that hours working while in school
have a negative effect on academic performance. Therefore, scholarships for nontraditional
students such as those in the Opening Doors study may enable students to decrease hours worked
and increase time on educational activities and subsequently increase academic achievement. At
the same time, such scholarships may have less desirable consequences. While we did not find
much evidence that scholarship eligibility changed students’ course-taking behavior, it is
possible that performance-based scholarships may increase effort in ways that are not
educationally productive such as cheating or harassing professors for better grades.

30
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33

Appendix A
We follow Jacobson and Mokher (2009) and classify courses into eight broad
categories—Health Related; Humanities; Professional; Science, Technology, Engineering, and
Mathematics (STEM); Social Sciences; Vocational/Technical; Remedial; and Other. All courses
are categorized based on their “discipline” code which loosely corresponds to an academic
department rather than categorizing classes based on the course title itself.
In Table A we list each course prefix and the associated department, academic area, or
program description by the field in which we categorized them. In a few cases we had to use
information about individual course descriptions, course catalogs, syllabi, and/or online college
brochures in order to make a decision on field categorization. As described more fully below,
DSPE courses are placed in the Health Related field; HNRS courses are placed in the Humanities
field; CISX and ENSC courses were placed in the STEM field; ELAP, ETRN, IDEL, and PWEL
courses were placed in the Vocational/Technical field, and SPWF courses were placed in the
“Other” field category.
Courses at DCC in the “Direct Support Professional” program, prefix DSPE, are placed
in the Health Related field because they are in the Allied Health Division at the City Park
Campus. The “Honors” courses at Delgado Community College—those with the prefix HNRS—
were placed in the “Humanities” field based on course titles and descriptions in the 2005-06
catalog. Two of the course titles were Literature and Medicine and Activism and Change.
Modernism in the Arts (HUMA 220) is listed under the honors section of the 2005-06 catalog so
we assume that this is the same course as HNRS 220.

34
An online brochure from LTC describes CISX 1000 as an introduction to information
systems so the CISX courses were placed in the STEM field. At other colleges ENSC courses are
in environmental science so we assume that this is true at LTC as well, and these courses are also
placed in STEM. An online syllabus from LTC describes ELAP 1400 as “basic electricity marine
application” so we place the ELAP courses in the Vocational/Technical field. Online brochures
from LTC describe ETRN courses as having to do with alternating and direct current circuits and
IDEL courses as electronics electives so courses with both prefixes are placed in the
Vocational/Technical field. Finally, an online LTC syllabus describes PWEL 1130 as Training
and Testing Pipe GTAW (Cu.Ni) so courses with the PWEL prefix are also placed in the
Vocational/Technical field.
We were unable to decipher what program is described by the SPWF prefix so these few
courses at DCC were placed in the Other category.

35
Appendix Table A: Course Field Categorization

Course Prefix by Field
Health Related
DIET
DMTP
DSPE
EMTE
HEIT
HESC
HMDT
HNUR
MLTS
MSTH
NURS
OPHT
PHAR
PRNU
RCPS
RSPT
SURG
WELL
Humanities
ASLS
ENGL
ENRE
ESLN
FNAR
FREN
HIST
HNRS
HUMA
MUSB
MUSC
PHIL
SPAH
SPAN
THEA
VISC
Other

Department, Academic Area, or Program Description
Dietetic Technician
Dietary Manager
Direct Support Professional1
Emergency Medical Technician‐Paramedic
Health Information Technology
Health Sciences
Medical Terminology
Nursing Fundamentals
Medical Laboratory Technician
Massage Therapy
Nursing
Ophthalmic Assistant
Pharmacy Technician
Practical Nursing
Respiratory Therapist
Respiratory Care Technology
Surgical Technology
Wellness
American Sign Language Studies
English
English/Reading
English as a Second Language
Fine Arts
French
History
Honors2
Humanities
Music Business
Music
Philosophy
Special Topics in Arts and Humanities
Spanish
Theatre Arts
Visual Communications (Commercial Art)

36
ADOT
Administrative Office Technology
CCSS
College Success Skills
CULA
Culinary Arts
HORT
Horticulture
INTD
Interior Design
JOBS
Job Seeking Skills
KYBD
Keyboarding
MSCM
Mass Communication
ORNT
Freshman Orientation
PHYE
Physical Education
SFTY
Safety
SPCA
Special Topics in Communication
SPCH
Speech/Oral Communication
SPWF
Unknown3
Professional
ACCT
Accounting
ARCH
Architectural/Design Construction Technology
BUSG
Business Studies/General
BUSL
Business Law
CADD
Computer Aided Design and Drafting
CRJU
Criminal Justice
HOST
Hospitality
MANG
Management
MARK
Marketing
OSYS
Office Systems
RLST
Real Estate
Remedial
DVEN
Developmental English
DVMA
Developmental Math
DVRE
Developmental Reading
READ
Reading
WKEY
Skills Improvement
Social Sciences
ANTH
Anthropology and Geography
ECED
Early Childhood Education
ECON
Economics
EDUC
Education
POLI
Political Science
PSYC
Psychology
SOCI
Sociology
Science, Technology, Engineering and Mathematics (STEM)

37
BIOL
CHEM
CISX
CMIN
CNET
CPTR
ENSC
GEOL
HBIO
MATH
PHYS
SCIE
Vocational/Technical
BLDG
CARP
COOP
ELAP
ELCT
ELEC
ELET
ELST
ETRN
IDEL
MOVH
PWEL
TECH
TEVP
WELD

Biology
Chemistry
Computer Information Systems4
Computer Information Technology
Computer Network Technology
Computers
Environmental Sciences5
Geology
Microbiology
Mathematics
Physics
Science
Building Technology Specialist
Carpentry
Cooperative Education
Electricity6
Electrical Technology
Electrician
Electrical‐Electronics Engineering Technology
Electronics Servicing Technology
Electrical Circuits7
Electronics 8
Motor Vehicle Technology
Plumbing9
Technology‐General
Television Production
Welding

Notes: 1 Courses are in the Allied Health Division at the City Park Campus.2 All course
titles under HNRS seem to be Humanities courses. See Appendix text for more detail. 3
We were unable to decipher the field for SPWF and so include it in the “Other”
category. 4 An online brochure from LTC describes CISX 1000 as introduction to
information systems. 5 At other colleges ENSC courses are in environmental science. 6
An online syllabus from LTC describes ELAP 1400 as basic electricity marine application.
7
An online brochure from LTC describes ETRN courses as having to do with alternating
and direct current circuits. 8 An online brochure from LTC describes IDEL 2995 as
Special Projects III. Other IDEL courses are Electronics Electives. 9 An online LTC syllabus
describes PWEL 1130 as Training and Testing Pipe GTAW (Cu.Ni).

38

Figure 1a: First Semester Course Grade Distribution
by Treatment Status
30
25
20
15
10
5
0

Control Group

Program Group

Figure 1b: Second Semester Course Grade Distribution
by Treatment Status
30
25
20
15
10
5
0

Control Group

Program Group

39
Table 1: Total Sample Size by Campus and Cohort

Cohort
Spring 2004
Summer 2004
Fall 2004
Spring 2005
All cohorts

Delgado CC
‐‐ City Park
172
133
246
58
609

Delgado CC
‐‐ West
Bank
45
72
91
0
208

Louisiana
Technical
College
72
43
48
39
202

Total
289
248
385
97
1019

40
Table 2: Scholarship Payment by Random Assignment
Random Assignment
Program Group

Control Group

First semester
Number of students receiving 1 or more payment
Percent of students receiving 1 or more payment
Percent received $250 (among recipients)
Percent received $500 (among recipients)
Percent received $1000 (among recipients)
Total dollars received (among recipients)

424

2

84.0
22.4
15.1
60.6
751.8

0.4
50.0
0.0
50.0
625.0

Second semester
Number of students receiving 1 or more payment
Percent of students receiving 1 or more payment
Percent received $250 (among recipients)
Percent received $500 (among recipients)
Percent received $1000 (among recipients)
Total dollars received (among recipients)

314

1

62.2
23.9
14.6
58.3
736.1

0.2
100.0
0.0
0.0
250.0

Cumulative, 1‐7 semesters after random assignment
Percent of students receiving 1 or more payment
Percent ever receiving $1000 scholarship
Percent receiving full $2000 scholarship
Total dollar value of payments received

89.7
59.4
30.5
1132.9

0.4
0.2
0.0
2.9

Notes: Distribution of payments among recipients may not sum to 100 because a few received
payments of other sizes.

41
Table 3: Characteristics of Opening Doors Louisiana Participants and Beginning Postsecondary
Survey (BPS) Students
BPS

Characteristics
Age (years)
Share age 17‐18
Share age 19‐20
Share age 21‐35
Female
Race/ethnicity shares
Hispanic
Black
Asian
American Indian
Other (non white)
Children
Has any children
Has child under 6 (conditional on any)
Number of children (conditional on any)
Average household size
Financially dependent on parents
Education
Highest grade completed (years)
Years since high school
Completed any college courses
Enrolled to complete certificate program
Enrolled to transfer to 4 year college
Highest degree completed
GED
High school diploma
Technical certificate, associate's degree
or higher
First member of family to attend college
US citizen
Number of Observations

Opening Doors
Louisiana Study
(1)
25.293
0.041
0.138
0.819
0.924

2‐Year Public
College
Students
(2)
20.591
0.391
0.334
0.276
0.542

Louisiana sub‐
sample
(3)
20.947
0.183
0.499
0.318
0.568

0.026
0.849
0.004
0.005
0.004

0.157
0.137
0.047
0.007
0.045

0.097
0.432
0.067
0.000
0.044

1
0.806
1.813
3.655
0.172

0.155
0.714
1.919
3.690
0.727

0.222
0.623
1.607
3.927
0.732

11.714
6.598
0.337
0.135
0.155

2.065
0.149
0.134
0.420

2.181
0.069
0.215
0.245

0.169
0.697

0.082
0.867

0.083
0.903

0.103
0.426
0.990
1019

0.006
0.322
0.925
5680

0.023
0.277
0.986
70

42

Notes: Based on authors' calculations from MDRC data and data from the U.S. Department of
Education's 2004 Beginning Postsecondary Survey (BPS). We limit the BPS data to first‐time students
between the ages of 17 and 34 at two‐year public colleges in column (2) and to the subset of first‐
time, two‐year public college students in Louisiana in column (3). BPS means are weighted by the
2004 study weight. Sample sizes for the BPS have been rounded to the nearest 10.

43
Table 4: Randomization of Program and Control Groups
Random assignment
Baseline characteristic
Female %
Age (years)
Marital status %
Married, living w/ spouse
Married, not living w/ spouse
Unmarried, living w/ partner
Unmarried, not living w/ partner

Program
Group
91.0
25.2

Control
p‐value of
Group
difference
93.8
0.09
25.3
0.69

N
1019
1019

8.8
11.0
5.2
75.0

7.6
10.5
7.5
74.4

0.47
0.81
0.14
0.83

1003
1003
1003
1003

Race/ethnicitya %
Hispanic
Black
White
Asian
Multi‐racial
Other
Number of children
Age of youngest child (years)
Receiving any government benefit %
Unemployment insurance
Household receiving SSI
Household receiving TANF
Household receiving food stamps
Public housing or section 8 housing
Financially dependent on parents %
Ever employed %
Currently employed %
Earned HS diploma %
Earned GED %
Earned tech certificate %

3.0
86.9
8.6
0.2
0.8
0.0
1.8
3.1
72.4
5.1
14.2
10.5
61.7
15.3
17.6
98.0
51.0
70.7
15.2
10.7

2.2
82.8
12.3
0.6
0.6
0.8
1.9
3.2
69.5
3.8
12.2
10.1
62.0
20.6
16.8
97.5
52.2
68.7
18.6
10.0

0.44
0.07
0.06
0.31
0.70
0.05
0.21
0.66
0.31
0.32
0.35
0.84
0.94
0.04
0.71
0.56
0.70
0.49
0.15
0.69

985
985
985
985
985
985
1014
1000
1015
996
996
996
996
901
1006
1014
1017
1016
1016
1016

Main reason for enrolling in collegeb %
Complete certificate program
Obtain AA
Transfer to 4‐yr college
Obtain job skills
Other reason
Completed any college courses before RA %
First family member to attend college %

12.7
57.5
15.9
12.3
6.1
32.8
42.8

14.4
55.1
15.2
14.3
6.1
34.6
42.5

0.43
0.43
0.76
0.34
1.00
0.54
0.93

1005
1005
1005
1005
1005
993
976

44
Notes: All means are adjusted for campus interacted with cohort. aHispanic and race categories
are mutually exclusive. bCategories are not mutually exclusive.

45
Table 5: Educational Outcomes Based on Transcript Data: All Cohorts

First semester after random assignment
Enrolled in any course (%)

Control Group
Mean
(1)

Program
Effects
(2)

76.654

5.346
(2.294)
0.557
(0.279)
0.497
(0.254)
1.222
(0.285)
0.934
(0.242)

Total credits attempted

7.99

Regular credits attempted

5.101

Total credits earned

4.609

Regular credits earned

3.113

Second semester after random assignment
Enrolled in any course (%)

49.611

Total credits attempted

4.93

Regular credits attempted

3.547

Total credits earned

2.77

Regular credits earned

2.111

14.956
(2.849)
1.234
(0.300)
0.913
(0.258)
1.126
(0.265)
0.854
(0.232)

P‐values
adjusted for
multiple testing
(3)
0.070
0.129
0.129
<0.0001
0.001

<0.0001
0.0001
0.001
<0.0001
0.001

Notes: Each estimate comes from a separate regression. Standard errors are in parentheses. Sample
size is 1019. All outcome characteristics are based on transcript data from the intervention campuses.
Each regression also includes controls for the randomization pool. P‐values are adjusted using
bootstrap resampling with the stepdown approach. We consider the full set of outcomes in this table
within semester in making the adjustments as well as the part‐time and full‐time enrollment indicators
discussed in the text.

46
Table 6: Longer Run Outcomes and Effects on Enrollment at "All" Institutions: First Two Cohorts

Semesters enrolled in school
Registered for any course in 1st
semester
Registered for any course in
2nd semester
Registered for any course in
3rd semester
Number of semesters enrolled
in any course in 1st year
Number of semesters enrolled
in any course in second year
Number of semesters enrolled
in any course over first 2 years
Total credits earned
Total credits earned in first
year

Total credits earned in second
year

Total credits earned over first 2
years

Number of observations

Transcript Data
All Students
(1)

Transcript +
Clearinghouse
Data All
Students
(2)

Transcript
Data Delgado
only
(3)

Clearinghouse
Data Delgado
Only
(4)

4.681
(3.470)
[0.172]
18.142
(3.997)
[<0.0001]
11.789
(4.041)
[0.008]
0.346
(0.088)
[0.001]
0.125
(0.065)
[0.234]
0.471
(0.129)
[0.003]

5.062
(3.459)
[0.149]
17.553
(4.000)
[<0.0001]
12.420
(4.140)
[0.007]
0.350
(0.088)
[0.001]
0.120
(0.075)
[0.400]
0.471
(0.137)
[0.005]

5.662
(3.755)
[0.154]
19.229
(4.636)
[0.0004]
14.685
(4.815)
[0.005]
0.396
(0.102)
[0.0006]
0.151
(0.076)
[0.223]
0.547
(0.149)
[0.005]

5.662
(3.755)
[0.154]
18.798
(4.593)
[0.0004]
15.213
(4.793)
[0.004]
0.397
(0.101)
[0.0006]
0.120
(0.080)
[0.459]
0.517
(0.150)
[0.005]

3.345
(0.849)
[0.001]

4.016
(0.977)
[0.0004]

0.343
(0.456)
[0.676]

0.402
(0.485)
[0.747]

3.688
(1.180)
[0.013]

4.417
(1.313)
[0.006]

537

537

422

422

47

Notes: Each estimate comes from a separate regression. Standard errors are in parentheses; p‐values
adjusted for multiple testing are shown in brackets. Estimates shown in columns (1) and (2) limit the
sample to the first two study cohorts. Estimates show in columns (3) and (4) limit the sample to the first
two cohorts of students at Delgado only. Cumulative outcomes for the first and second years reflect
three semesters of potential enrollment. Cumulative outcomes over the first two years reflect six
semesters of potential enrollment. We adjust p‐values considering outcomes shown in this table,
registration in semester 4, registration in semester 5, and registration in semester 6, within year and
sample. For purposed of adjusting p‐values, we include outcomes reflecting cumulative measures over
the first two years with second year outcomes.

48
Table 7. Credits Attempted and Earned by Course Subject Field: All Cohorts
Credits Attempted
Control
Group Mean
(1)

Program
Effect
Estimates
(2)

Credits Earned
Control
Group Mean
(3)

Program
Effect
Estimates
(4)

First and second semesters after
random assignment
Health Related

1.587

Humanities

3.101

Professional

0.507

Science, Technology, Engineering,
& Mathematics (STEM)

4.173

Social Sciences

0.760

Vocational/Technical

0.218

Remedial

1.156

Other

1.400

0.063
(0.262)
[0.809]
0.159
(0.179)
[0.768]
0.133
(0.124)
[0.768]
0.354
(0.225)
[0.553]
0.411
(0.118)
[0.008]
0.255
(0.140)
[0.456]
0.156
(0.153)
[0.768]
0.204
(0.129)
[0.553]

1.012

1.673

0.314

2.384

0.503

0.164

0.425

0.897

0.146
(0.231)
[0.768]
0.372
(0.167)
[0.246]
0.143
(0.103)
[0.586]
0.654
(0.204)
[0.019]
0.412
(0.107)
[0.002]
0.240
(0.129)
[0.441]
0.143
(0.079)
[0.456]
0.196
(0.106)
[0.456]

Notes: Each cell represents an estimate from a separate regression and comes from a regression that
includes indicators for randomization pool but no other baseline characteristics. See text and Appendix A
for course subject field descriptions. Standard errors are in parentheses; p‐values adjusted for multiple
testing are shown in brackets. There are 1010 observations used in each regression. All outcomes shown
plus the aggregate "easy" and "hard" course credit variables discussed in the text are taken into account
when adjusting the p‐values for multiple testing.

49

Table 8: Effects on Achievement and Effort with Lee Bounds

Term GPA 1st semester after RA

Control
Mean
(1)
2.203

Term GPA 2nd semester after RA

2.171

Hours per week spent:
On campus 1st semester

11.980

Studying 1st semester

8.847

On campus 2nd semester

6.129

Studying 2nd semester

4.470

Treatment
Impact
(2)
0.182
(0.085)
0.068
(0.104)

Lower
Bound
(3)
0.040
(0.107)
‐0.225
(0.147)

Upper
Bound
(4)
0.381
(0.109)
0.361
(0.152)

0.066
(0.321)
0.119
(0.457)
0.476
(0.390)
0.684
(0.519)

‐0.148
(0.387)
‐0.578
(0.677)
‐0.042
(0.541)
‐0.458
(0.808)

0.437
(0.478)
0.639
(0.576)
1.472
(0.588)
1.758
(0.713)

Notes: Each row represents an estimate from a separate regression. Standard errors are in
parentheses. Outcome measures are based on transcript data and survey responses to the
MDRC follow‐up survey. Categorical responses on hours per week are converted to a
continuous measure by assigning the midpoint of the category. Upper and lower bound
estimates and standard errors are calculated following Lee (2009). Data are trimmed at the
randomization pool level. Estimates shown represent the average of these estimates
weighted by observation shares. Overall there are 739 GPA observations for semester 1
and 517 GPA observations for semester 2. Hours per week spent on campus is available for
635 observations in the 1st semester and 460 observations in the 2nd semester. Hours
spent studying is available for 637 observations in the 1st semester and 214 observations in
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WP-07-04

The Age of Reason: Financial Decisions Over the Lifecycle
Sumit Agarwal, John C. Driscoll, Xavier Gabaix, and David Laibson

WP-07-05

Information Acquisition in Financial Markets: a Correction
Gadi Barlevy and Pietro Veronesi

WP-07-06

Monetary Policy, Output Composition and the Great Moderation
Benoît Mojon

WP-07-07

Estate Taxation, Entrepreneurship, and Wealth
Marco Cagetti and Mariacristina De Nardi

WP-07-08

Conflict of Interest and Certification in the U.S. IPO Market
Luca Benzoni and Carola Schenone

WP-07-09

The Reaction of Consumer Spending and Debt to Tax Rebates –
Evidence from Consumer Credit Data
Sumit Agarwal, Chunlin Liu, and Nicholas S. Souleles

WP-07-10

Portfolio Choice over the Life-Cycle when the Stock and Labor Markets are Cointegrated
Luca Benzoni, Pierre Collin-Dufresne, and Robert S. Goldstein

WP-07-11

Nonparametric Analysis of Intergenerational Income Mobility
with Application to the United States
Debopam Bhattacharya and Bhashkar Mazumder

WP-07-12

How the Credit Channel Works: Differentiating the Bank Lending Channel
and the Balance Sheet Channel
Lamont K. Black and Richard J. Rosen

WP-07-13

Labor Market Transitions and Self-Employment
Ellen R. Rissman

WP-07-14

First-Time Home Buyers and Residential Investment Volatility
Jonas D.M. Fisher and Martin Gervais

WP-07-15

Establishments Dynamics and Matching Frictions in Classical Competitive Equilibrium
Marcelo Veracierto

WP-07-16

Technology’s Edge: The Educational Benefits of Computer-Aided Instruction
Lisa Barrow, Lisa Markman, and Cecilia Elena Rouse

WP-07-17

3

Working Paper Series (continued)
The Widow’s Offering: Inheritance, Family Structure, and the Charitable Gifts of Women
Leslie McGranahan
Demand Volatility and the Lag between the Growth of Temporary
and Permanent Employment
Sainan Jin, Yukako Ono, and Qinghua Zhang

WP-07-18

WP-07-19

A Conversation with 590 Nascent Entrepreneurs
Jeffrey R. Campbell and Mariacristina De Nardi

WP-07-20

Cyclical Dumping and US Antidumping Protection: 1980-2001
Meredith A. Crowley

WP-07-21

Health Capital and the Prenatal Environment:
The Effect of Maternal Fasting During Pregnancy
Douglas Almond and Bhashkar Mazumder

WP-07-22

The Spending and Debt Response to Minimum Wage Hikes
Daniel Aaronson, Sumit Agarwal, and Eric French

WP-07-23

The Impact of Mexican Immigrants on U.S. Wage Structure
Maude Toussaint-Comeau

WP-07-24

A Leverage-based Model of Speculative Bubbles
Gadi Barlevy

WP-08-01

Displacement, Asymmetric Information and Heterogeneous Human Capital
Luojia Hu and Christopher Taber

WP-08-02

BankCaR (Bank Capital-at-Risk): A credit risk model for US commercial bank charge-offs
Jon Frye and Eduard Pelz

WP-08-03

Bank Lending, Financing Constraints and SME Investment
Santiago Carbó-Valverde, Francisco Rodríguez-Fernández, and Gregory F. Udell

WP-08-04

Global Inflation
Matteo Ciccarelli and Benoît Mojon

WP-08-05

Scale and the Origins of Structural Change
Francisco J. Buera and Joseph P. Kaboski

WP-08-06

Inventories, Lumpy Trade, and Large Devaluations
George Alessandria, Joseph P. Kaboski, and Virgiliu Midrigan

WP-08-07

School Vouchers and Student Achievement: Recent Evidence, Remaining Questions
Cecilia Elena Rouse and Lisa Barrow

WP-08-08

4

Working Paper Series (continued)
Does It Pay to Read Your Junk Mail? Evidence of the Effect of Advertising on
Home Equity Credit Choices
Sumit Agarwal and Brent W. Ambrose

WP-08-09

The Choice between Arm’s-Length and Relationship Debt: Evidence from eLoans
Sumit Agarwal and Robert Hauswald

WP-08-10

Consumer Choice and Merchant Acceptance of Payment Media
Wilko Bolt and Sujit Chakravorti

WP-08-11

Investment Shocks and Business Cycles
Alejandro Justiniano, Giorgio E. Primiceri, and Andrea Tambalotti

WP-08-12

New Vehicle Characteristics and the Cost of the
Corporate Average Fuel Economy Standard
Thomas Klier and Joshua Linn

WP-08-13

Realized Volatility
Torben G. Andersen and Luca Benzoni

WP-08-14

Revenue Bubbles and Structural Deficits: What’s a state to do?
Richard Mattoon and Leslie McGranahan

WP-08-15

The role of lenders in the home price boom
Richard J. Rosen

WP-08-16

Bank Crises and Investor Confidence
Una Okonkwo Osili and Anna Paulson

WP-08-17

Life Expectancy and Old Age Savings
Mariacristina De Nardi, Eric French, and John Bailey Jones

WP-08-18

Remittance Behavior among New U.S. Immigrants
Katherine Meckel

WP-08-19

Birth Cohort and the Black-White Achievement Gap:
The Roles of Access and Health Soon After Birth
Kenneth Y. Chay, Jonathan Guryan, and Bhashkar Mazumder

WP-08-20

Public Investment and Budget Rules for State vs. Local Governments
Marco Bassetto

WP-08-21

Why Has Home Ownership Fallen Among the Young?
Jonas D.M. Fisher and Martin Gervais

WP-09-01

Why do the Elderly Save? The Role of Medical Expenses
Mariacristina De Nardi, Eric French, and John Bailey Jones

WP-09-02

Using Stock Returns to Identify Government Spending Shocks
Jonas D.M. Fisher and Ryan Peters

WP-09-03

5

Working Paper Series (continued)
Stochastic Volatility
Torben G. Andersen and Luca Benzoni

WP-09-04

The Effect of Disability Insurance Receipt on Labor Supply
Eric French and Jae Song

WP-09-05

CEO Overconfidence and Dividend Policy
Sanjay Deshmukh, Anand M. Goel, and Keith M. Howe

WP-09-06

Do Financial Counseling Mandates Improve Mortgage Choice and Performance?
Evidence from a Legislative Experiment
Sumit Agarwal,Gene Amromin, Itzhak Ben-David, Souphala Chomsisengphet,
and Douglas D. Evanoff

WP-09-07

Perverse Incentives at the Banks? Evidence from a Natural Experiment
Sumit Agarwal and Faye H. Wang

WP-09-08

Pay for Percentile
Gadi Barlevy and Derek Neal

WP-09-09

The Life and Times of Nicolas Dutot
François R. Velde

WP-09-10

Regulating Two-Sided Markets: An Empirical Investigation
Santiago Carbó Valverde, Sujit Chakravorti, and Francisco Rodriguez Fernandez

WP-09-11

The Case of the Undying Debt
François R. Velde

WP-09-12

Paying for Performance: The Education Impacts of a Community College Scholarship
Program for Low-income Adults
Lisa Barrow, Lashawn Richburg-Hayes, Cecilia Elena Rouse, and Thomas Brock

WP-09-13

6