Topics in Household Consumptionsrdc.msstate.edu/ridge/grants/thesis_final_report_2014.pdf · Topics...
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NORTHWESTERN UNIVERSITY Topics in Household Consumption A DISSERTATION SUBMITTED TO THE GRADUATE SCHOOL IN PARTIAL FULFILLMENT OF THE REQUIREMENTS for the degree DOCTOR OF PHILOSOPHY Field of Economics By Mary Wasfy Zaki EVANSTON, ILLINOIS September 2014
Transcript of Topics in Household Consumptionsrdc.msstate.edu/ridge/grants/thesis_final_report_2014.pdf · Topics...
NORTHWESTERN UNIVERSITY
Topics in Household Consumption
A DISSERTATION
SUBMITTED TO THE GRADUATE SCHOOL
IN PARTIAL FULFILLMENT OF THE REQUIREMENTS
for the degree
DOCTOR OF PHILOSOPHY
Field of Economics
By
Mary Wasfy Zaki
EVANSTON, ILLINOIS
September 2014
2
.
© Copyright by Mary Zaki 2014
All Rights Reserved
3
ABSTRACT
Topics in Household Consumption
Mary Wasfy Zaki
In the last decade many households have gained access to expensive short-term credit
and free-breakfasts in schools. However, not much is known about their effect on household
consumption and daily behavior. I explore these effects in my dissertation by use of a
natural experiment and a randomized control trial. I analyze the effects of payday loans
in the military setting as military personnel are assigned to locations across the United
States with varying degrees of access to payday loans. In two of the chapters in this
dissertation, I examine how consumption and labor behavior change after the passage
of a federal law that effectively bans military personnel from accessing payday loans in
some states but not others. I use a new military administrative dataset of sales at on-
base grocery and department stores as well the Consumer Expenditure Survey and the
Current Population Survey to conduct the analysis. I find that payday loan access enables
households to smooth consumption but also changes the composition of their consumption.
Diane Schanzenbach and I use experimental data collected by the USDA to measure
the impact of two policy innovations aimed at increasing access to the school breakfast
program. We find both policies increase the take-up rate of school breakfast, though
much of this reflects shifting breakfast consumption from home to school or consumption
of multiple breakfasts and relatively little of the increase is from students gaining access
to breakfast. We find no evidence of improvements in 24-hour nutritional intake, child
health, or student achievement.
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ACKNOWLEDGMENTS
I would like to thank all who have helped me during my graduate school career in
one way or another. Even though this was a long journey with many peaks and valleys,
I cherish it very much, not in a small part, because of those who walked along with me.
First and foremost, I have to thank my superior advisors. Diane Whitmore Schanzenbach
took me under her wings from the first day I met her. Under her tutelage I wrote and
won my first grant and presented at my first conference. She skillfully introduced me to
the world of applied microeconomics and humbly shared with me from her knowledge and
experience. To Diane I am eternally grateful. Seema Jayachandran came to Northwestern
at just the right time for me to take her class and learn applied micro tools. Her advice
and guidance were always wise and thorough. I appreciate the time that she took to
read through all that I produced. I am so grateful and honored to have these two strong
women be my chairs. They are my role models. I am also grateful for Martin Eichenbaum
for being the impetus for me considering applied micro work and supporting me as I
transitioned to that field. Finally, I want to thank Brian Melzer for his great guidance
especially given his expertise in payday loans.
I want to thank Elie Tamer for his advice during my whole time at Northwestern and
especially for introducing me to Diane. I must thank my friends and colleagues Greg
Veramendi, Matthias Kherig, Chris Vickers and Lance Kent who were instrumental in
giving me technical as well as emotional support during the job market process. I want
to thank Michael Mara for his support especially during thesis writing time. You are
cherished friends.
Of course I would also like to thank my friends who made this time wonderful! I had
the best run of roommates I could possibly have. Jingling Guan, thank you for putting
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up with my dirty dishes so that I can concentrate on my work! I’m so glad we had a few
years when we could support each other through academia. I want to specifically thank
my brothers and sisters at Evanston Baptist Church who had prayed tirelessly for me
to get through graduate school. Thank you, and you can now stop! Specifically, I must
thank Sharon Coppenger, Jennifer Lie, Beverly Rah, Rebecca Wheeler, the Dallmanns,
the Addingtons, the Mooneys and the Thompsons. I want to thank Kate Wurtz who sent
me the best stuff in the mail throughout this time.
I want to thank Mom and Dad for being patient and supportive when things were
tough. And I want to thank Brother for the times we talked together and for being my
Survivor buddy. Thank you for your prayers and love. I love you very much.
Finally, I would like to thank God. Thank you for making your way clear and giving
me the tools to traverse it. Jesus, you are my strength and purpose.
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.
For Mom, Dad and Brother.
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Contents
1 Access to Short-term Credit and Consumption Smoothing within the
Paycycle 14
1.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 14
1.2 Institutional Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16
1.2.1 Military . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16
1.2.2 Payday Loans . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 18
1.2.3 Military Lending Act . . . . . . . . . . . . . . . . . . . . . . . . . . . . 19
1.3 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 21
1.3.1 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 21
1.3.2 Identification Framework . . . . . . . . . . . . . . . . . . . . . . . . . . 24
1.4 Payday Loan Impact on Consumption . . . . . . . . . . . . . . . . . . . . . . 26
1.4.1 Timing . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 26
1.4.1.1 Paycycle Consumption Patterns . . . . . . . . . . . . . . . . 26
1.4.1.2 Payday Loan Impact on Timing of Consumption . . . . . . 31
1.4.2 Level . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 34
1.4.3 Composition . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 36
1.5 Robustness Checks . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 38
1.5.1 Transitional Period . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 38
1.5.2 Propensity Score Matching . . . . . . . . . . . . . . . . . . . . . . . . 39
1.5.3 Car-title Loans . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 41
1.6 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 42
1.6.1 Present-biased Preferences . . . . . . . . . . . . . . . . . . . . . . . . . 43
1.6.2 Rational Foresight . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 46
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1.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 48
2 Expanding the School Breakfast Program: Impacts on Children’s Con-
sumption, Nutrition and Health 50
2.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 50
2.2 Literature Review . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 52
2.3 Empirical Approach . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 54
2.3.1 The Need for Re-analysis . . . . . . . . . . . . . . . . . . . . . . . . . 55
2.3.2 Outcomes to be measured . . . . . . . . . . . . . . . . . . . . . . . . . 56
2.3.3 Impact of SBP participation . . . . . . . . . . . . . . . . . . . . . . . 58
2.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 58
2.4.1 Validity of the Experiment . . . . . . . . . . . . . . . . . . . . . . . . 58
2.4.2 Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 59
2.4.3 Difference-in-difference Estimates . . . . . . . . . . . . . . . . . . . . 64
2.4.4 Impact of Eating Breakfast . . . . . . . . . . . . . . . . . . . . . . . . 66
2.5 Discussion and Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . 67
3 Access to Short-term Credit and Household Expenditures and Labor
Force Participation 70
3.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 70
3.2 Institutional Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 72
3.3 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 74
3.3.1 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 74
3.3.2 Identification Framework . . . . . . . . . . . . . . . . . . . . . . . . . . 75
3.4 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 79
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3.4.1 Expenditure Behavior . . . . . . . . . . . . . . . . . . . . . . . . . . . 79
3.4.1.1 Intensive Margin . . . . . . . . . . . . . . . . . . . . . . . . . 79
3.4.1.2 Extensive Margin . . . . . . . . . . . . . . . . . . . . . . . . 81
3.4.1.3 Vehicles and Lodging . . . . . . . . . . . . . . . . . . . . . . 82
3.4.2 Labor Force Behavior . . . . . . . . . . . . . . . . . . . . . . . . . . . . 83
3.5 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 85
4 Figures and Tables 87
Appendices 126
A Figures and Tables 126
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List of Tables
1 Store Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 92
2 Payday Spending Given Previous Paycycle Length . . . . . . . . . . . . . . 93
3 The Impact of Payday Loan Access on the Timing of Consumption . . . . 94
4 The Impact of Payday Loan Access on the Timing of Consumption . . . . 95
5 The Impact of Payday Loan Access on the Level of Consumption . . . . . 96
6 The Impact of Payday Loan Access on the Composition of Consumption . 97
7 Robustness: Impact of Payday Loan Access on the Timing of Consumption,
Omitting 10/2006-9/2008 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 98
8 Robustness: The Impact of Payday Loan Access on the Timing of Con-
sumption Using Propensity Score Matching . . . . . . . . . . . . . . . . . . . 99
9 Robustness: Impact of Payday Loan Access on the Timing of Consumption,
Omitting Car Title Loan Allowing States . . . . . . . . . . . . . . . . . . . . 100
10 Experimental Design Setup . . . . . . . . . . . . . . . . . . . . . . . . . . . . 101
11 Baseline Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . . . . . . 102
12 Effect of School Breakfast Program on First-Year Participation and Nutri-
tion, by Type of Program . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 103
13 Effect of School Breakfast Program on First-Year Academic, Behavior and
Health Outcomes, by Type of Program . . . . . . . . . . . . . . . . . . . . . . 104
14 Effect of School Breakfast Program in Subsequent Years . . . . . . . . . . . 105
15 Effect of Breakfast in the Classroom Program, by Subgroup . . . . . . . . . 106
16 Difference-in-difference Analysis . . . . . . . . . . . . . . . . . . . . . . . . . . 107
17 Instrumental Variables Estimates of the Effect of Breakfast Consumption 108
18 Characteristics of Military Members . . . . . . . . . . . . . . . . . . . . . . . 109
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19 Mean of Household Main Earner Characteristics . . . . . . . . . . . . . . . 110
20 Effect of Payday Loan Access on Total Spending . . . . . . . . . . . . . . . 111
21 Effect of Payday Loan Access on Category Spending . . . . . . . . . . . . . 112
22 Effect of Payday Loan Access on Category Spending . . . . . . . . . . . . . 113
23 Effect of Payday Loan Access on Category Spending . . . . . . . . . . . . . 114
24 Effect of Payday Loan Access on Category Spending . . . . . . . . . . . . . 115
25 Effect of Payday Loan Access on Vehicle Ownership and Housing Choices 116
26 Effect of Payday Loan Access on the Labor Market . . . . . . . . . . . . . . 117
27 Effect of Payday Loan Access on the Labor Market . . . . . . . . . . . . . . 118
A.1 Exchange Product Categories . . . . . . . . . . . . . . . . . . . . . . . . . . . 129
A.2 Impact of Payday Loan Access on the Timing of Consumption with Varying
Previous Paycycle Length . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 130
A.3 The Impact of Payday Loan Access on the Timing of Consumption with
Access Measured by “State Allow” . . . . . . . . . . . . . . . . . . . . . . . . 131
A.4 The Impact of Payday Loan Access on the Timing of Consumption with
Access Measured by “Number of Shops” . . . . . . . . . . . . . . . . . . . . . 132
A.5 The Impact of Payday Loan Access on the Composition of Consumption
with Access Measured by “State Allow” . . . . . . . . . . . . . . . . . . . . . 133
A.6 The Impact of Payday Loan Access on the Composition of Consumption
with Access Measured by “Number of Shops” . . . . . . . . . . . . . . . . . . 134
A.7 The Relationship between MilitaryPayday Loan Access and State Price
Changes . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 135
A.8 Propensity Score Covariates . . . . . . . . . . . . . . . . . . . . . . . . . . . . 136
A.9 Daily Discount Rate . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 137
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A.10 Percent of Civilians are Earners . . . . . . . . . . . . . . . . . . . . . . . . . 138
13
List of Figures
1 Commissary and Exchange Locations . . . . . . . . . . . . . . . . . . . . . . . 87
2 Paycycle Sales Pattern . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 88
3 Difference between Average Log Daily Sales on Paydays and Average Log
Daily Sales on Non-paydays Among Commissaries . . . . . . . . . . . . . . . 89
4 Impact of Payday Loan Access on the Timing of Consumption . . . . . . . 90
5 Difference between Average Log Daily Sales on Paydays and Average Log
Daily Sales on Non-paydays Among Commissaries by Previous Paycycle
Length . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 91
A.1 2013 USAA Military Pay Calendar . . . . . . . . . . . . . . . . . . . . . . . . 126
A.2 Paycycle Sales Pattern (Second Paycycle from Each Month Only) . . . . . 127
A.3 Balance . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 128
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1 Access to Short-term Credit and Consumption
Smoothing within the Paycycle
1.1 Introduction
Access to short-term credit, such as payday loans, may be beneficial to a population
that faces liquidity constraints over the short run. Payday loans can provide a means
for consumers to smooth consumption in the face of income shocks. On the other hand,
consumers may overborrow due to “present-biased” preferences or vulnerabilities to temp-
tation good consumption. Most policy actions on payday loans are concerned with the
latter issue, which leads to various levels of restrictions on payday loans. Past studies
on the effect of payday loan access on household welfare find evidence for both outcomes
(smoothing consumption and overborrowing). Hence, no clear consensus has been reached
among researchers. In this paper, I contribute to the understanding of the effects of pay-
day loans on households by conducting the first study that connects payday loans to
consumption.1 Specifically, I investigate how payday loan access affects the timing, level
and composition of household consumption. Furthermore, this is one of the first papers
that connects credit to high-frequency consumption.2
To uncover the impact of payday loans on food consumption, my research design takes
advantage of a natural experiment that changed the availability of payday loans to mil-
itary personnel across states and time in the United States. As a result of the Military
Lending Act, military personnel and their dependents lost access to payday loans nation-
1Karlan and Zinman (2010) find that access to expensive payday loan type instruments offered in afield experiment increased measures of food security in households 6 months after initial loan take up.
2Agarwal, Bubna and Lipscomb (2012) analyze the daily spending patterns of credit and debit cardholders from a large financial institution in India.
15
wide starting in October 2007. This change did not affect personnel assigned to locations
where payday loans were already inaccessible or illegal,3 but it did end availability for
personnel in payday loan accessible locations. I use this policy change in a difference-in-
difference framework that compares military populations that did and did not lose access
to payday loans as a result of the law change. As the majority of military personnel
cannot choose where to locate, some endogeneity concerns are alleviated.
To get a measure of military consumption, I obtained sales data using several Freedom
of Information Act requests. This data came from on-base grocery stores, Commissaries,
and on-base department stores, Exchanges. These stores are not open to the general
public and provide a convenient and cheap source of daily consumption needs.
Since personnel are all paid on known and regular pay dates, I was able to observe
how they shop between paychecks. I find that expenditures spike on payday and are
significantly lower at the end of a paycycle. Commissary sales on paydays can be 20-25%
higher than sales on non-paydays. This finding cannot be explained by the timing of
price changes. The difference between payday and non-payday spending increases the
longer consumers have been waiting to receive their paychecks. This raises doubts that
consumers use paydays as focal points for shopping. The pattern persists for perishable
goods like produce. I argue that this sales pattern is evidence that the military population
faces liquidity constraints and therefore reveals that food consumption is not smooth, even
over a two-week period.
Using a difference-in-difference framework, I find that payday loan access relieves some
of the liquidity constraints that consumers face by allowing them to smooth consumption
between paychecks. This smoothing effect is stronger when the duration between pay-
checks is longer. Furthermore, this ability to smooth with payday loan access is not
3Payday loans were banned in 9 states in the time period of study.
16
associated with a large drop in the level of food consumption. The smoothing result is
robust according to a re-estimation that uses a propensity score matching technique that
accounts for heterogeneity among bases and states.
I also find that military personnel purchase more alcohol and electronics when given
access to payday loans. The increase in good consumption in some categories may be
explained by cost savings that payday loans provide over alternative credit substitutes.
On the other hand, it may indicate that payday loans lead to temptation purchases at the
cost of other goods and savings. Further evidence suggests that there may be significant
heterogeneity in the population. There are signs of present-biased preferences within the
population. However, a significant portion of the population also display time-consistent,
forward-looking behavior capable of budgeting in atypically long paycycles.
The paper proceeds as follows: Section 2 overviews the military population, payday
loans and the 2007 Military Lending Act; Section 3 describes the main data and the
empirical strategy that will be used in this paper; Section 4 examines how payday loan
access affects the timing, level and composition of consumption; Section 5 contains ro-
bustness checks of the previous section’s results; Section 6 tests for the presence of time
inconsistency and rational foresight in the population; Section 7 concludes.
1.2 Institutional Background
1.2.1 Military
In 2007, the military employed 1.4 million active duty personnel.4 Associated with these
personnel are more than 1.8 million spouses, children and adult dependents. 55.2% are
married and 43.2% have children. 14.4% of active duty personnel are women and 35.9%
42007 Demographics Profile of the Military Community, Department of Defense.
17
identify as minorities. The average age of an active duty member is 28.3 years. 46.3%
of personnel are 25 years old or younger. 17.8% have Bachelor’s degrees or higher while
80.2% have at least a high school diploma and possibly additional education less than a
Bachelor’s degree.5 83.8% of personnel are enlisted while the rest are Officers.
All active duty personnel are paid on the 1st and the 15th of each month, or the closest
business day preceding these dates if they should fall on a federal holiday or a weekend.6
Pay is based on rank and years of service. For example, in 2007 base pay for an enlisted
individual ranked E-4 (the most common rank) with 3 years of service was $24,000 a
year. The military also provides tax-free cash food allowances (e.g. $3,359/year for E-4)
and tax-free cash housing allowances (varies by location but on average it is $10,928/year
for E-4 with no dependents and $13,815/year with dependents). Non-cash compensation
includes comprehensive health care for personnel and dependents and military housing
in place of the housing allowance. In order to compare the military’s cash and non-
cash compensation to civilian pay, the Department of Defense calculates a figure called
Regular Military Compensation (RMC). In 2006, the average enlisted member had an
RMC approximately $5,400 greater than his civilian counterpart.7
Active duty personnel and their families typically move to a new station every 24 to
48 months. Approximately 1/3 of active duty personnel must move each year. Enlisted
personnel have little control as to the location of their placement. Finally, according
to the military, all members are equally likely to be assigned to a particular base after
controlling for rank and occupation (Lleras-Muney, 2010).
5The remainder have unknown educational attainment or have no high school diploma nor GED6http://www.uscg.mil/ppc/mas.asp7The Tenth Quadrennial Review of Military Compensation (2008)
18
1.2.2 Payday Loans
Payday loans are small short term loans with a duration of a week or two. A typical
loan size ranges $250-$300 with fees between $15-$20 per $100 borrowed (Flannery and
Samolyk, 2005). Assuming a 14 day loan, this implies APR rates of 390-520%. A potential
borrower must have a checking account and proof of income in order to take out the loan.
In exchange for the loan a borrower writes a check for the amount of the loan plus the
fee and postdates it to her payday. When payday comes, the borrower can rollover the
account to a subsequent payday for a fee, repay the loan amount plus fee and have the
check returned to her or let the payday loan shop cash the check.
Despite the high cost of this form of credit and its short maturity, the payday loan
industry has exploded since the 1990s. In 2006, there were more than 24,000 payday
loan shops in the U.S., more than the number of McDonald’s and Starbuck’s restaurants
combined.8
Advocacy groups and policy makers have intensely criticized payday loans in the last
decade leading to many regulations. In 2005, at the beginning of the time frame of
interest in this paper, 9 states effectively or fully banned payday loan operations. The
rationale behind these bans is that the targeted borrowers have self-control problems or
they overestimate their abilities to repay. These borrowers then find themselves unable
or unwilling to cover their debt burden, which in turn leads to repeated borrowing and
increased costs. Payday loan lenders claim that they are providing a credit instrument to
the underbanked that is designed to aid borrowers in bridging consumption until paycheck
receipt. Elliehausen and Lawrence (2001) present an example in which it would be cheaper
for an individual to take out a payday loan to repair his vehicle immediately rather
8Carrell & Zinman (2013)
19
than wait till the arrival of his next paycheck and take public transportation. This is
because the present value of the cost of taking public transportation in terms of fare and
time was greater than the payday loan fee minus gas, maintenance and car depreciation.
Furthermore, payday loan lenders claim that payday loans can be a cheaper alternative
to substitutes such as overdraft fees and late credit card payment fees.
Research findings on the effects of payday loans is mixed. Many find that payday loan
access has negative effects on borrowers: Campbell, Martinez-Jerez and Tufano (2012)
find that access to payday loans leads to forced debit and checking account closures due
to excessive overdrafts; Skiba and Tobacman (2011) find that payday loans access leads
to increased Chapter 13 bankruptcy filings; Melzer (2011) finds that payday loan access
increases the difficulty of paying bills and leads households to postpone seeking medical
care. On the other hand, some papers find positive effects from credit access: Morgan,
Strain and Seblani (2012) find that individuals bounce fewer checks; Morse (2011) finds
that payday loans mitigate the effects of income shocks caused by natural disasters as
measured by foreclosures and larceny rates. As mentioned above, this study is the first to
look directly at the impact of payday loans on consumption.
1.2.3 Military Lending Act
In 2006 the Department of Defense presented a report to Congress pushing for restrictions
on high-cost small dollar credit products to military personnel. As a result the Talent-
Nelson amendment was added to the John Warner National Defense Authorization Act
of 2007, setting a national usury cap on loans issued to military personnel and their
dependents. The Department of Defense referenced the high take up of payday loans by
the military population – Tanik (2005) estimates that 19% of military personnel have
20
used payday loans versus 6.75% of the civilian population, which may be related to the
phenomenon of payday loan shops locating near military installments in greater densities
than in comparative locations according to Graves and Peterson (2005). The Department
of Defense argued that high-cost small dollar credit products harm troop morale and
readiness due to resulting financial stress. In fact, Carrell and Zinman (2013) find that
this is the case among young air force personnel. Furthermore, financial distress may
make personnel vulnerable to loss of security clearance.
The 2006 Talent-Nelson amendment led to the Military Lending Act (MLA) coming
into law on October 1, 2007. The MLA put restrictions on several types of loans lent to
active duty personnel or their dependents. Most significantly, the MLA enacts a cap of
36% APR.9 It also prohibited these loans from being secured by checks, electronic access
to bank accounts or vehicle titles. Rollovers and renewals are not allowed unless they are
done at no extra cost. In addition, active duty personnel and their dependents cannot
enter into mandatory arbitration or waive legal rights. These restrictions effectively ban
payday lending to active duty personnel.
Lenders must determine in the loan application process if potential borrowers fall under
the MLA. This can be done in several ways. Lenders can look at the employer names on
pay stubs that are often required in the application process. They also have access to a
Department of Defense database to query a potential borrower’s active duty status. Many
payday loan stores add a statement to their application form that borrowers must check
off in order to receive a loan. For example, Advance America has the following statement:
“I attest that I am not a regular or reserve member of the Army, Navy,
Marine Corps, Air Force, or Coast Guard, serving on active duty under a
9Affected loans are less than $2,000 in size and less than 91 days in term.
21
call or order that does not specify a period of 30 days or less. Nor am I an
Active Guard and/or Reserve member of the military currently serving on
active duty or who has served on active duty within the past 180 days, nor am
I a spouse, child, or other dependent person who derives more than one-half
of my monetary support from a member of the military who is on active duty
or has been on active duty within the past 180 days.”
Fox (2012) found that the MLA was effective in curbing payday loan usage among the
military population because of a sharp decrease in the number of military aid society cases
related to payday loans, an increase in closures of payday loan stores near some military
bases and a scarcity of violations reported by State oversight agencies.
1.3 Empirical Strategy
1.3.1 Data
I will be using sales data from grocery and department stores located on or near mili-
tary bases. The grocery stores, also known as Commissaries, are operated by the Defense
Commissary Agency (DeCA) and carry food and household items excluding alcohol. They
sell mostly brand name goods and do not have a store private label (Wright 2007). The
department stores, or Exchanges, sell more durable items such as appliances, clothing
and housewares. They sell alcohol and private label goods. Exchanges are run by var-
ious branch specific organizations.10 Neither Commissaries nor Exchanges are open to
the general public. Only active duty military, reservists, retirees, family members and
authorized civilians working overseas can access them. Commissary and Exchange usage
10Army and Air Force Exchanges are run by the Army and Air Force Exchange Service. MarineExchanges are run by the Marine Corps Exchange System. The Navy Exchanges are run by the NavyExchange Service Command.
22
is considered part of the benefits package of military service due to their convenience
and cost savings. For example, becaue they receive federal funding, Commissaries are
not-for-profit and can only sell goods at cost plus a 5% surcharge by law.11 There are no
taxes charged at either Commissaries or Exchanges.12 As a result, DeCA reports a price
savings of 30% on goods purchased at Commissaries as compared to those purchased at
other comparable stores (DeCA, 2008).13 Exchanges are for profit but tend to sell certain
goods at or below local prices.14 Thus it is reasonable to expect that Commissary and
Exchange take up is high.
I obtained sales figures from military Commissaries and Exchanges across the United
States via a Freedom of Information Act request from DeCA and the Army and Air
Force Exchange Service (AAFES). Commissary and Exchange data provide a high-quality
measure of consumption since they capture a large fraction of purchases for the military
population. This will be particularly true for food, alcohol and tobacco products. Because
the data are administrative rather than self-reported, there is less scope for measurement
error than similar data collected via a household survey or the home-scanning of purchases.
On the other hand, there are some limitations to this data. The data is aggregated
11The funds from the surcharge are used to cover facility modernizations and new building costs. Costsof regular operations are funded by an appropriation by the Department of Defense (DeCA, 2008). Costsof the actual goods are funded by their resale.
12The only exception to this is gasoline sold at Exchange gas stations. Gasoline is not in my data set.http://www.shopmyexchange.com/exchangestores/faq.htm#13 .
13A DeCA operational goal is to provide a level of “customer savings” compared to other grocerystores. This customer savings measure is reported annually. Prices are collected from major grocerystores, supermarkets and superstores, either through databases or physical audits, and compared to thoseat commissaries. In the calculations, taxes are included in non-commissary good prices while the 5%surcharge is included in commissary good prices.
14A price floor needed to be placed on tobacco, alcohol and gas prices as outlined in DoD Instruction1330.09. These floors put a limit on how much lower prices for these goods could be compared tothose in the local market. For example, liquor prices cannot be priced more than 10 percent less thanthe best local shelf price in Alcohol Beverage Control (ABC) States and 5 percent less than the bestlocal shelf price in non-ABC States. “Local” is not defined and there are indications that these pricingdirections are not always followed. An example of this can be found in the report by Marketplace:http://www.marketplace.org/topics/economy/maps-military-tobacco.
23
at the base level rather than the individual level. This will prove problematic for several
reasons. First, I cannot separate out retiree household purchases (who are not affected
by the MLA) from active duty household purchases. I am able to control for retirees in
some of the specifications I use. Another shortcoming of the data is that it is expenditure
data rather than consumption data. Though it may be appropriate to approximate low
frequency consumption (such as monthly) with low frequency expenditures, this is not
an appropriate procedure for approximating daily consumption. I will argue that daily
consumption information can be gleaned from this daily high-frequency expenditure data.
Finally, this data is not comprehensive of all consumption, spending and lifestyle choices
of the population. Thus, though I will be able to make statements about food and some
durables, further study needs to be made on these other outcome variables.
Commissary sales figures at the store-day-product category level from October 2005 to
September 2010 span 179 Commissaries across 47 States from all branches of the military.15
Exchange data at the store-month-product category level span the same time period for
77 Army and Air Force bases across 35 States. Commissary total sales can be broken up
into three product categories: Produce, Meat and Grocery.16 Exchange categories include
Electronics, Alcohol, Luxury, Tobacco, Commissary-Like, Clothing, Uniforms, Entertain-
ment, Home, and Appliances. Subcategories that make up each Exchange category are
listed in Appendix Table 1.17
15Two other commissaries are dropped (Fort Worth NAS, TX and Richards-Gebaur, MO ) becausethey do not span the length of the study period.
16The Grocery category is a catchall for all products that are not produce or meats.17Only subcategories that are present in all stores are included in Exchange categories. Total Exchange
sales are calculated from the sum of these categories and hence may not match overall total store salesdue to the omitted subcategories.
24
1.3.2 Identification Framework
I will be examining how the level, timing and composition of consumption at stores with
varying levels of accessibility to payday loans changed as a result of the MLA. Such an
analysis will allow me to uncover the effect of payday loan access on military consumption.
Variation of store accessibility to payday loans can be gleaned from the map in Figure
1. The squares and circles on the map represent the locations of the Commissaries and
Exchanges in my dataset. The states that banned payday loans before the passage of the
MLA are signified by grey shading.18 Stores marked by squares have at least one payday
loan shop within their 10 mile radius while those marked by circles do not.19
I will be using a differene-in-difference framework to conduct my analysis. Treatment
will be some measure of payday loan access and it is administered in the pre-ban (pre-
MLA) period on the treatment group. There are 3 different ways to assign store treatment:
1. “State Allow”: Being located in a state that allows payday loans between October
2005 and September 2007. “State Allow” takes on values of 0 and 1.
2. “Near Shop”: Having at least 1 payday loan shop within a 10 mile radius of the
store, regardless of payday loan legal status in the state in which the store is located.
“Access” takes on values of 0 and 1.
18Regarding Maine, I differ from Graves and Peterson (2008) in my assignment of payday loan legality.Through the State of Maine Agency License Management System, I was able to find records of paydayloan stores in Brunswick and Bangor, two cities that contain commissaries. However, there seem to beonly 5 licensed payday loan stores in in the whole state in 2007. There also is no payday loan shoplocation data for Washington, D.C. Thus, the number of payday loan shops within 10 miles of somestores in Washington, D.C., Virginia and Maryland may be underestimated. However, those stores thatare vulnerable to underestimation were checked to be assigned as having at least one payday loan shopin their 10 mile radius.
19Commissary addresses were gathered from the DeCA website. Payday loan store locations wereobtained from supplementary files from Graves and Peterson (2008) and downloaded from Steven Graves’website. Graves and Peterson gathered addresses for 2007 from state government sources if available, andbusiness directories otherwise.
25
3. “Number of Shops”: The number of payday loan shops within a 10 mile radius of
the store. “Number of Shops” is an integer top coded at 10.20
Summary statistics of store treatment assignment can be found in Table 1.
As a result of the Military Lending Act, pay day lending was effectively banned nation-
ally to military personnel starting on October 2007 . This change did not affect personnel
in areas where payday loans were already inaccessible or illegal, but it did end availability
for personnel in payday accessible areas. I will use the difference-in-difference framework
to compare military populations that did and did not lose access to payday loans with
the law change. Opposite of the typical difference-in-difference framework, where neither
group has access to the treatment until it is administered in the post-regulation period
to the treatment group, this setup has treatment administered at the beginning of the
experiment and then taken away in the post-regulation period.
The military setting has features that reduce concerns over endogeneity in this iden-
tification strategy. Store prices on most goods are set nationally to the same price and
changed at the same time in all stores. Thus, no one store can set prices based on whether
on not its patrons have access to payday loans. Second, as stated in the Institutional Back-
ground section, military personnel especially enlisted personnel, do not have much choice
in their geographic placement. Thus, the consumers in our population cannot self-select
into locations based on payday loan availability. This makes the composition of the mili-
tary personnel more similar across ”treated” and ”untreated” groups. There might still be
heterogeneity among the treated and untreated groups even if individuals do not select
into groups. More on this will be discussed in Section 5.2 where I attempt to control for
20Number of shops is top coded at 10 shops to address the concern that results are skewed by outliers.As was seen in Table 1, there are some stores that are surrounded by a very large number of paydayloan shops. All interpretation of results presented in this section are not changed by top coding. In fact,results are more statistically significant if number of shops is not top coded.
26
such differences using a propensity score matching technique.
1.4 Payday Loan Impact on Consumption
1.4.1 Timing
In order to analyze how payday loan access impacts the timing of consumption, I have
to first establish what the timing pattern looks like without the introduction of payday
loans. To do this I will present the pattern of sales between paycheck receipts. I will then
argue that this expenditure pattern is indicative of the underlying consumption pattern.
1.4.1.1 Paycycle Consumption Patterns I define the term “paycycle” as the span
of time between two paydays and inclusive of the first payday. Since all active duty
personnel are paid on the same days, I can track the pattern of their paycycle spending. I
conduct all the analysis in this section on the post-ban period (October 2007-September
2010) data when no active duty personnel can access payday loans. Furthermore, analysis
in this section is done using only Commissary sales data because daily frequency data is
unavailable from Exchanges.
To establish the paycycle expenditure pattern, I use the following specification:
LogSalesit = α + β′DaysSincePaydayt + φt + θi + εit (1)
where LogSales is the natural logarithm of daily sales for store i on date t;
DaysSincePayday is a vector of indicator variables pertaining to the number of days t
is from the closest preceding payday; φ are controls for time (specifically: day of week,
27
federal holidays, Social Security payout days;21 and paycycle22 indicator variables); θ are
store fixed effects and ε is an error term. The DaysSincePayday indicators range from
1 to 18, omitting 0 (payday).
The estimates of β for total store sales are plotted by the solid black line in Figure
2 Panel A. All estimates of the DaysSincePayday coefficients are significantly different
from 0 at the 1% level and are negative. There is a spike in sales on and around payday
as compared to sales on other days in the paycycle. Specifically, there are periods of time
starting from 3 days after payday and ending 14 days after when store daily sales are
20-25% lower than their payday levels.
Some banks and credit unions that cater to military personnel offer special checking
accounts that provide access to military pay earlier than payday. An example of a pay
schedule is presented in Appendix Figure 1 from USAA Bank. As can be seen in the figure
and stated on USAA Bank’s website, funds are provided one business day before payday.
I want to control for these early payout days because they act as paydays. I augment the
previous specification as follows:
LogSalesit = α+β′DaysSincePaydayt+γ′DaysSincePaydayt×EarlyAccesst+φt+θi+εit(2)
where all variables are as before and EarlyAccess is a dummy variable equal to 1 if an
observation is on or after the last business day of a paycycle. Estimates of β are plotted
by the dotted black line in Figure 2 Panel A.23 Indeed there is a noticeable difference in
21Useful to control for retiree shopping behavior.22Paycycle indicator variables are fixed effects for approximately every fortnight.23Since there are no paycycles that are longer than 19 days, there are no observations that are 18 days
since payday but are not one business day before a payday. Hence I do not plot the estimate of the βcoefficient on the 18th day since payday. It will, of course, be almost the same estimate as in the model
28
pattern: namely, sales stay in the 20-25% range below payday spending for the remainder
of the paycycle.
The main takeaway from these figures is that spending on non-paydays is significantly
lower than on paydays or days when people have access to pay. Such a pattern may arise if
consumers are facing liquidity constraints that are alleviated upon receipt of a paycheck.
If consumers are facing binding liquidity constraints, then the expenditure pattern is
somewhat indicative of the consumption pattern (i.e. though consumers would like to
go shopping so that they can consume, they cannot until receipt of their next paycheck).
Thus, I will argue that these patterns are caused in part by liquidity constraints and hence
reveal aspects of the consumption pattern.
It is possible that consumers make their purchases mainly on paydays but consume
smoothly throughout the whole of the paycycle without facing any liquidity constraints.
This can happen because many of the goods purchased from a grocery store are multi-
serving and have some shelf life (e.g. cereal, detergent). But certain goods are more
perishable and would require more frequent store visits to sustain a smooth consumption
pattern. Thus, expenditures on such good categories track consumption better than
looking at store sales as a whole. I examine the sales pattern of produce, the most
perishable category in my data set,24 to see if the purchasing spike on payday persists. If
people are smoothing consumption, then I would expect the paycycle spending pattern to
be much flatter. However, as one can see in Figure 2 Panel B, the pattern of concentrated
spending on paydays persists – expenditures on non-paydays can be 15-20% lower than
on payday. Thus, it is less likely that these consumers are smoothing their consumption
of produce.
without early paycheck controls.24As done in Stephens (2003, 2006)
29
Perhaps people prefer to go shopping on payday because of cost motives, such as price
promotions on that day. According to DeCA, if price changes on a product were to occur
(they do not occur every paycycle for every product), they would happen on 1st or the
16th of each month.25 Thus, Commissaries do not have one day price changes to match
the payday shopping behavior. Rather, prices change on specific days and stay that way
for at least a whole paycycle. It maybe that consumers prefer to go to the store on the
day of a price change. Since military personnel get paid twice a month, on the 1st and the
15th or earlier, there are times in the beginning of the month when payday overlaps with
price changes. However, payday in the second paycycle of the month will never overlap
with a price change. If consumers are shopping on payday because of a price change
motive, then we would expect the payday expenditure spike to not exist if we only look
at second of the month paycycles. β estimates from specifications 1 and 2 are plotted
in Figure 2 in the Appendix. Concentrated spending on payday persists even in these
paycycles, placing doubt on a pricing explanation for the pattern. In fact, rather than a
cost savings, it seems like consumers incur costs by choosing to coordinate Commissary
shopping on payday. There is anecdotal evidence that consumers experience longer check
out lines and slower movement around the store on payday.26 Consumers’ tolerance for
incurring these costs support the argument that they are desperate to go shopping on
payday due to their need to consume.
If consumers use paydays as focal points for shopping but do not face liquidity con-
straints, then we would not expect to see a relationship between length of time between
paychecks and the tendency to shop on payday. However, if consumers do face liquid-
25http://www.commissaries.com/documents/contact deca/faqs/prices commissary.cfm26Anecdotal evidence is from accounts by a commissary employee and military family members that
I have spoken to as well as an article on titled, “How to Navigate the Commissary on Payday” fromhttp://voices.yahoo.com/how-navigate-commissary-payday-6413254.html?cat=46.
30
ity constraints, then an extra day’s wait for a paycheck means that more consumers are
waiting to go to the store the earliest chance that they get and the larger the expenditure
spike is on payday. To test this story, I use the following specification:
LogSalesit = α + φt + θi + βPaydayt + γPaydayt × PreviousPaycycleLengtht + εit (3)
where PreviousPaycycleLength is the number of days in the paycycle previous to the
paycycle of date t; Payday is a dummy variable equal to 1 if t is a payday and the rest of
the variables are defined as above. γ is the percentage increase in payday sales as compared
to non-payday sales for every extra day consumers wait for payday to arrive. Estimates
of γ are found in Table 2. Panel A presents the results for paycycles of all lengths and
Panel B limits the analysis to 14 day paycycles.27 In Panel B, I only analyze paycycles
of fixed length to isolate the effect of wait time for paycheck receipt from the effect of
purchasing behavior by adjustments motivated by the variation in current paycycle length
(e.g. purchasing more/less on payday if the current paycycle is long). All estimates of γ
are positive, large and statistically significant at the 1% level for all product categories.
Every extra wait day for a paycheck leads to an increase of 2.26 percentage points of the
gap between total payday expenditures and total non-payday expenditures in the paycycle
following the wait. Thus more people are going shopping specifically on payday if they
have been waiting longer for a paycheck, a story that aligns with the existence of liquidity
constraints.
27The most common paycycle length is 14 days.
31
1.4.1.2 Payday Loan Impact on Timing of Consumption The pattern of higher
sales on payday as compared to non-paydays reveals a degree of liquidity constraints
affecting the underlying consumption. A decrease in the gap between payday and non-
payday sales would then indicate that consumers are able to smooth consumption more
throughout their paycycle. To see if payday loans impact the timing of consumption, I
test if payday loan access leads to changes in the gap between payday and non-payday
sales. Figure 3 illustrates the difference-in-difference specification used in this subsection.
Each bar in this figure represents the difference between average log daily sales on paydays
and average log daily sales on non-paydays among specified commissaries during certain
periods.28 The two leftmost bars are calculated for commissaries that have at least one
payday loan shop within their 10 mile radius, while the two right-most bars are calculated
for those commissaries that do not. The dark grey shading indicates that calculations are
for the pre-ban period and the light grey shading is for the post-ban period. The gap
between payday spending and non-payday spending decreased by .9 percentage points
from the post-ban to the pre-ban period for commissaries that are not near payday loan
shops. However, the gap between payday spending and non-payday spending decreased
by 2 percentage points from the post-ban to the pre-ban period for commissaries that are
near payday loan shops. The difference-in-difference assumption that I will be making
is that if these latter commissaries were not near payday loans shops, then the the gap
between payday spending and non-payday spending would have decreased only by .9
percentage points from the post-ban to the pre-ban period as it did for the commissaries
that are not near payday loan shops. Thus, I attribute any change in the gap that is
beyond .9 percentage points to payday loan access. In this case, payday loan access
28Log Sales are adjusted for store fixed effects as well as day of week, federal holidays, Social Securitypayout dates, early paycheck days and paycycle fixed effects before being averaged.
32
caused a 1.1 percentage point decrease in the gap between payday spending and non-
payday spending. This is the difference-in-difference estimate of interest. Because payday
loan access decreased the gap, we can infer that payday loans had a smoothing effect
on consumption. A 1.1 percentage point change, in this case, is approximately a 5.8%
decrease in the gap between payday spending and non-payday spending.
The difference-in-difference specification is as follows:
LogSalesit = α + βPaydayt + γPaydayt × PreBant + δPaydayt ×NearShopi+
ρPaydayt ×NearShopi × PreBant + ηUnemploymentRateit + φt + θi + ξit + εit (4)
where NearShop is a dummy equal to 1 if there exists at least 1 payday loan shop within
a 10 mile radius of Commissary i; PreBan is a dummy equal to 1 if an observation occurs
before October 2007 (when there was no federal ban on payday loans to military person-
nel); UnemploymentRate is the monthly unemployment rate in Commissary i’s county; ξ
are all the interaction terms between day of week indicator variables and NearShop and
PreBan and all other variables are defined as before. Note that the PreBan main effect
is absorbed by the time control vector φ and the NearShop main effect is absorbed by
the store fixed effect vector θ. The (triple) difference-in-difference coefficient of interest
is ρ and measures how the difference between payday and non-payday spending differ be-
tween treatment groups before and after federal prohibition of payday loans. A negative
ρ indicates that payday loan access decreased the size of the gap between payday and
non-payday sales. In other words, a negative ρ means access to payday loans increases
paycycle smoothing while a positive ρ means that consumers have become more liquidity
33
constrained.
Estimates of β, γ, δ and ρ for Commissary total sales are presented in Table 3. The first
column presents the estimates for all paycycles in our dataset. The coefficient estimate of
ρ indicates an approximate 1.9 percentage point decrease in the gap between payday and
non-payday spending as a result of payday loan access. In the second column, the analysis
is done on the subset of paycycles that are preceded by 14 day or less paycycles. In this
case, payday loan access does not seem to have any clear effect on consumption smoothing
as coefficient estimates are fairly small. On the other hand, coefficients estimated for the
subset of paycycles that are preceded by paycycles that are greater than 14 days are
large and negative. Payday loan access closes the gap between payday and non-payday
spending by more than 3.8 percentage points. Thus as more consumers face liquidity
constraints waiting through a long paycycle, more use payday loans. Furthermore, the
end result of this payday loan usage is smoother consumption and not increased liquidity
constraints. Formally, I would expect to see a greater payday loan smoothing effect as
time between paychecks increases. Indeed, I find this is true with strong significance by
running a quadruple difference-in-difference specification that examines how the triple
difference-in-difference estimate varies by paycycle length. Results and details are found
in Appendix Table 2. Thus, payday loan access does not bring forth a simple calendar
effect, uniformly shifting when people consume. Rather, consumers utilize payday loans
more when paycheck wait time increases. We see similar results in other Commissary
product categories as presented in Table 3. Furthermore, the results persist with other
specification of “Access” as seen in Appendix Table 3 and 4. Finally, Figure 4 plots
estimates of a specification in which the dummy Payday in Equation 4 is replaced by
the indicator variables DaysSincePayday. The solid line represents what the paycycles
34
expenditure pattern in the treatment group would have looked like in the pre-ban period
if treatment was not administered. The dotted line represents the pattern with payday
loan access. As one can see, the the pattern is flatter, indicating that consumers purchase
more on other days relative to payday and are not as constrained to shop on payday.
1.4.2 Level
The smoothing gains come with a cost. If payday loans are extremely harmful, as in the
case when consumers are very present-biased, we would expect to see a large decrease
in consumption levels when consumers have access to them. This is because consumers
are prone to over borrow and excessively rollover loans leading to situations of elevated
financial distress (Skiba and Tobacman 2008). However, payday loans may be helpful in
situations where consumers do not have such behavioral tendencies yet face unexpected
liquidity constraints. In this case we would expect to see a slight decrease in consumption,
due to the cost of interest on the loans, or an increase if payday loans are a cheaper
substitute to other available smoothing alternatives (e.g. overdraft fees).
I use monthly sales data in this section. Exchange data are already at a monthly
frequency and I aggregate daily Commissary store data into monthly frequency for com-
parison.29 I run the following difference-in-difference specification :
LogSalesit = α + βPreBant ×Accessi + γLogPopulationit +
ηUnemploymentRateit + φt + θi + εit (5)
where LogSales is the log of monthly sales; LogPopulation is the natural logarithm of the
29Results are unchanged with use of daily frequency Commissary Data
35
population of the nearest bases(s) to store i in month-year t; Access is one of the three
definitions of payday loan access listed in Section 3.2; φ are month-year fixed effects;
θ are store fixed effects and ε is an error term. Estimates of the difference-in-difference
coefficient, β, are presented in Table 5.30 β is interpreted as the percentage change in sales
as a result of access to payday loans. Panel A and B in Table 5 presents estimates for
Commissaries. Regardless of treatment specification, I cannot find a clear effect, positive
or negative, of payday loan access on the level of Commissary good consumption.31 None
of the estimates are significant at the 10% level and their magnitudes are small.
It is helpful to investigate whether I have the power to pick up any level effects from
payday loan access. A Department of Defense survey in 200532 estimates that the average
loan taken out by active duty personnel is $360. If personnel pay a $15 fee for every
$100 borrowed, then they would incur a cost of $54 for every paycycle that a loan is
outstanding. The same Department of Defense survey estimates that personnel take out
approximately 4.6 payday loans a year which are held on average for 3 paycycles. Thus,
this means that active duty personnel who use payday loans pay fees for approximately 7
months of the year. Assuming 19% of the military population uses payday loans,33 then
in any month, 11% of the active duty population has a loan outstanding. If the whole cost
of the payday loan is taken out of commissary spending (i.e. $108 per month), then I do
have enough power to pick up an effect. However, if I assume a 0.346 income elasticity for
30There are 5 Commissary stores that have large evident discontinuities in their sales data. Uponfurther inspection, these stores either had structural changes (e.g. an opening of a new store facility)or were severely affected by Hurricane Katrina. Though the timing of consumption within a paycycle(presented in the next subsection) may not be affected as much due to these issues, monthly levels wouldbe. Hence, these stores were dropped from this analysis. 1 Exchange store was dropped because it wasaffected by Hurricane Katrina. 12 Commissary stores and 3 Exchange stores were dropped because theycould not be matched with population data.
31I assume that monthly expenditures on Commissary goods are close estimates of monthly consump-tion.
32Department of Defense (2006).33Tanik (2005).
36
food,34 a $1,844 monthly after-tax paycheck for an E-4 with 3 years of service, and 11%
of after tax income spent on food,35 leading to a $4.11 reduction in food spending per
month, then I do not have enough power to pick up the payday loan access effect. Thus,
conservatively, I can say that I do not find that payday loan access has a very large effect
on the level of food consumption though I do not have power to pick up smaller effects.
Estimates for Exchange sales, presented in Panel C, are approximately 6% higher
when consumers have access to payday loans.These estimates are significant at the 5%
level under all specifications of treatment. I will delve further into the components of these
sales increases in the next section. Thus in neither the Commissary nor Exchange case do
we see that payday loan access has a significant negative cost on the level of consumption.
1.4.3 Composition
Results in Section 4.2 show that the level of Commissary consumption is not affected
by payday loan access. In this section I examine if payday loans affected the content of
what people chose to consume. To do this, I will run the same specification in Section 4.2
on the log of monthly category sales. Again, Commissary data can be broken into three
categories: Grocery, Produce and Meat. I will only look at stores that had data available
for all three categories. Panel A in Table 6 presents the estimates of the difference-
in-difference coefficient. None of the estimates for the product categories seem to be
significantly changed by access to payday loans. Thus, payday loan access does not
significantly change the level or the content of the goods consumed from the Commissary.
Exchange sales levels, on the other hand, did increase as a result of payday loan access.
Panel B in Table 6 presents the estimates of the difference-in-difference coefficients for
34USDA 2005 International Food Consumption Patterns.35Consumer Expenditure Survey, 2005. Table 3: Age of reference person: Average annual expenditures
and characteristics, for ages 25-34.
37
Exchange categories. We see that electronics and alcohol sales increased by more than
7% with access to payday loans. Thus there is a compositional change in the consumption
of Exchange goods when consumers have access to payday loans. These results persist
even with different specifications of “Access” as presented in Appendix Tables 5 and 6.
Running multiple significance tests (such as the 11 presented in Panel B in Table 6)
on the same data may lead to spurious results as the probability of incorrectly rejecting
the null of no effect increases with more tests given a fixed significance level. By adjusting
the significance level for multiple regressions using the Bonferroni correction I find that
electronics and alcohol sales increased as a result of payday loan access at a 3.3% and
12.1% significance level respectively. Thus, the results of the impact of payday loan access
on electronics sales and, to a slightly lesser degree, alcohol sales do not seem to be spurious.
One confounding issue in Exchange data as opposed to that of the Commissary is
that the pricing of tobacco and all forms of alcohol track local or state prices due to
regulations.36 For example, liquor prices cannot be priced more than 10 percent less than
the best local shelf price in Alcohol Beverage Control (ABC) States and 5 percent less than
the best local shelf price in non-ABC States. Though “local” is not explicitly defined and
there are indications that these pricing directives are not always obeyed,37 it is possible
that the results in this section are driven by exogenous price movements. Thus, I examine
state level price changes with the assumption that military demand does not affect state
product prices. I was able to obtain tobacco prices at the state level from the Centers
for Disease Control and the Prevention State Tobacco Tracking and Evaluation System.
I obtained pricing information for beer, wine and general cost of living at an “urban city”
level from the Council for Community and Economic Research. For the latter set of
36DoD Instruction 1330.0937http://www.marketplace.org/topics/economy/maps-military-tobacco
38
data, I created a state price by averaging the prices in urban cities in each state for each
date. Data on tobacco are annual while while others are quarterly. I run the following
specification:
LogPricest = α + βPreRegulationt × StateAllows + φt + θs + εst (6)
where LogPrice is the natural logarithm of average price for state s over time period t;
PreRegulation is a dummy equal to 1 if t is in the pre-regulation before September 2007;
StateAllow is a dummy equal to 1 if s is a state that allows payday loans; φ are time
period fixed effects; θ are state fixed effects and ε is an error term. Estimates of β are
presented in Appendix Table 7. We see in this table that there are no clear indications
that prices moved in states in such a way that would lead military personnel to purchase
more beer and wine.
1.5 Robustness Checks
1.5.1 Transitional Period
In October 2006, news broke that the MLA was going to take effect in October 2007.
It is plausible that payday loan supply and demand adjusted after the announcement
in preparation for the MLA taking effect. Furthermore, the loss of payday loan usage
after the MLA might have come as a surprise to some borrowers who regularly depend on
payday loans. For example, borrowers may have planned to rollover a loan but found out
that they were prohibited from doing so and were obligated to pay back the loan in full.
Such a shock may have led people to consume over the next few cycles in a fashion similar
to those who have liquidity constraints, which would exaggerate the positive effects of
39
payday loans in the difference-in-difference framework. As a robustness check, I reran
the timing specification in Equation 4 over the dataset but omitted observations between
October 2006 and September 2008, treating this length of time as a transitional period.
The estimates of the triple difference-in-difference coefficient, ρ, are reported in Table
7. The coefficient estimates have very similar magnitudes, signs and significance as those
found in Table 4 Panel A in which the transitional period is included. Thus, the smoothing
results are not driven by transitional adjustments.
1.5.2 Propensity Score Matching
There might be some concern that the results found in the previous section may be
driven less by access to payday loans and more by characteristic differences between the
locations of treatment and control groups. This concern is most evident when looking at
the geographic location of payday loan banning states in the United States. In Figure
1, we see that these states are concentrated in the Northeast. Thus, it may be the case
that there are intrinsic differences between Northeast and non-Northeast states such that
the non-Northeast states received treatment of payday loans. If this is the case, then
the difference-in-difference analysis done in the previous section would be invalid. In this
section, I will re-estimate the results in the timing section, Section 4.1 using a propensity
score matching technique.
The main assumption in propensity score matching is that potential outcomes are
independent of treatment group conditional on propensity score (Angrist and Pischke,
2008). The propensity score is the probability of being treated conditional on covariate
values. I calculate a propensity score for the treatment measure “Near Shop” using a
logit specification. The covariates I use for the model are a mix of state and base level
40
variables chosen to maximize balance between the matched set of treatment and control
stores. A list of the covariates is located in Appendix Table 8. The covariates are chosen
from a pool of variables that might explain why a state or geographic location received
treatment.
I match control group stores to each of the treatment group stores by nearest neighbor
propensity score matching with replacement. Appendix Figure 3 presents the standardized
percent bias for each covariate for both the full sample of stores and for the matched sub-
sample. This statistic is 100 times the difference of the covariate means of the treatment
and control groups divided by the square root of the average covariate sample variances
of the treated and control groups (Rosenbaum and Rubin, 1985). As seen in the figure,
matching does reduce this bias measure for most of these covariates.
Using the matched subsample, I calculate a triple difference-in-difference estimator in
a similar fashion as the difference-in-difference estimator presented in Todd (1999). In
order to adjust for the triple difference in my setting, I use the difference in the means
of sales on paydays and non-paydays as the outcome variable of interest. Formally, the
estimator is:
△DID
D=1 =1
x1∑{Di=1}
⎡⎢⎢⎢⎢⎣
⎧⎪⎪⎨⎪⎪⎩⎛⎝
1
xtn∑Y1ibb∈Atn
− 1
xtp∑Y1icc∈Atp
⎞⎠ −⎛⎝
1
xtn∑Y0m(i)d
d∈Atn− 1
xtp∑Y0m(i)e
e∈Atp
⎞⎠⎫⎪⎪⎬⎪⎪⎭
−⎧⎪⎪⎪⎨⎪⎪⎪⎩
⎛⎜⎝
1
xt′
n
∑Y0iff∈At′n
− 1
xt′
p
∑Y0igg∈At′p
⎞⎟⎠−⎛⎜⎝
1
xt′
n
∑Y0m(i)hh∈At′n
− 1
xt′
p
∑Y0m(i)jj∈At′p
⎞⎟⎠
⎫⎪⎪⎪⎬⎪⎪⎪⎭
⎤⎥⎥⎥⎥⎥⎦(7)
where D = 1 indicates treatment group; i is indexing commissaries; subscript n indicates
non-paydays; subscript p indicates paydays; superscript t indicates the pre-regulation
period of October 1, 2005 thru September 30, 2007; superscript t′
indicates the post-
41
regulation period of October 1, 2007 thru September 30, 2010; a subscript of 1 indicates
treatment (having access to payday loan stores within a 10 mile radius); a subscript
of 0 indicates no treatment; A is a set of dates; x is the quantity of members in the
indicated set; Y is log total daily sales; and m(i) is the indexing of a commissary that is
the nearest neighbor propensity score match to store i. m(i) is such that Dm(i) = 0, i.e.
from the control group. Given the sampling technique, this estimate is interpreted as the
average treatment effect on the treated. These triple difference-in-difference estimates are
presented in Table 8. We see that all estimates are positive and almost all are significant
at the 10% level. The magnitudes are a bit larger than those found in the Section 4.1,
however the interpretation remains that payday loans enable consumption smoothing.
1.5.3 Car-title Loans
The main types of credit that are affected by the MLA are payday loans, car-title loans
and tax refund anticipation loans. It may be that some of the effects that I find cannot be
fully attributed to payday loan access but to access to one of the other credit instruments
banned by the MLA. In the time period of study, tax refund anticipation loans were legal
in all states. Thus their effect is cancelled out in the difference-in-difference estimation
as both the control and treatment group lose access to these loans. Car-title loans on the
other hand were legal in a subset of the states that allowed payday loans and in one state
(Georgia) that banned payday loans. Thus there is a possibility that the effect of payday
loans is confounded by the simultaneous treatment of car-title loan access. To check for
this, I reran the timing specification in Equation 4 for Commissaries in states that do not
allow car-title loans. The estimates of the triple difference-in-difference coefficient, ρ, are
reported in Table 9. The results remain as before. Thus, there is assurance that payday
42
loans specifically are causing the smoothing results.
1.6 Discussion
The results in Section 4 show that along with the ability to smooth food consumption,
consumers increased their consumption of Exchange goods when they had access to pay-
day loans. One explanation for the increased consumption is that consumers save money
when they have access to payday loans and spend it on Exchange goods. This can be the
case if payday loans are cheaper substitutes for other available credit alternatives, such
as overdraft protection or late fees for utilities and credit cards. For example, a consumer
who needs $100 for two weeks will pay a $15-$20 fee if he takes out a payday loan but
will pay a median fee of $27 for overdraft protection.38 On the other hand, payday loan
access may enable overconsumption. This would happen if consumers have present-biased
preferences or are prone to temptation good consumption. Overconsumption of certain
goods or an increased debt burden comes at the cost of other goods (e.g. lessons for chil-
dren, rent, cable, savings) and lifestyle choices (e.g. second jobs, borrowing in informal
market, spouse entering labor market). Unfortunately, I cannot directly test the validity
of either explanation as my data is limited to Commissary and Exchange expenditures
and not all expenditures, savings and lifestyle choices for this population. Alternatively, I
investigate or discuss reasons why the military population runs into liquidity constraints.
If consumers face liquidity constraints because they have present-biased preferences, con-
sume temptation goods or have an inability to budget, then payday loan access may be
costly to them. On the other hand, if they are liquidity constrained when they are hit
by unexpected income shocks, payday loans can be beneficial. I will conduct one test to
38Data is for 2006. Fee is a flat fee independent of overdraft amount. Source: FDIC (2008)
43
see if consumers may possess present-biased preferences and one to see if consumers have
foresight about the length of their paycycle and can appropriately budget. Analysis in
this section will be done using post-ban period data.
1.6.1 Present-biased Preferences
I will investigate the population’s potential for having present-biased preferences by look-
ing at its daily discount rate. As argued in other studies of high frequency consumption
patterns e.g. Shapiro (2005), Huffman and Barenstein (2005), the existence of high daily
discount rates may be indicative of the presence of consumers with present-biased prefer-
ences. If this is the case, then consumers may suffer negative effects when given access to
payday loans as they are prone to overborrow and enter into worse financial conditions
(Laibson, 2007). To estimate a daily discount rate, I run the following specification using
daily Commissary sales data:
LogSalesit = α + βDaysSincePaydayt + φt + θi + εit (8)
where DaysSincePayday is an integer indicating the number of days t is from payday
in the paycycle and all other variables are as before. β is interpreted as the percentage
change in sales for every day beyond payday. Results of β estimates are presented in
Appendix Table 9. What is of interest is the change in daily consumption rather than
the change in daily expenditures. I assume, like Huffman and Barenstein, that the daily
decline in consumption within a paycycle is 50% of the decline in expenditures. Huffman
and Barenstein view this adjustment as a conservative lower bound of the daily decline
in consumption because the daily decline of expenditures on instant consumption goods
is 70% of the daily decline of total expenditures. In produce, the sales category that
44
most closely tracks consumption, sales go down by 1.5% a day. Applying Huffman and
Barenstein’s adjustment, these expenditure declines imply consumption declines of 0.75%
a day over a paycycle that is on average 15 days long. In comparison, Shapiro (2005) finds
consumption declines close to 0.4% over a 30 day food stamp paycycle.
As in Shapiro (2005), if consumers are time consistent exponential discounters maxi-
mizing:
U =T
∑t=1δt−1u(Ct) (9)
s.t. W =T
∑t=1
PtCtRt
, (10)
where C is units of consumption, u(.) is the special case of isoelastic utility (i.e. u(C) =C1−ρ
1−ρ ), δ is a daily discount factor, t is the day in a paycycle of length T, P is the price
of a unit of consumption good, W the is amount of paycycle salary that is devoted
to commissary good consumption and R is the gross interest rate, then their paycycle
consumption follows:
∆ct+1 = r + γ −∆pt+1ρ
, (11)
where lower case letters are logs of their upper case equivalents, γ = log δ and ∆ denote
changes.39 Note here that I assume that no borrowing can occur as the consumer is
in the post-ban period. I assume that the within paycycle price changes is 0. Interest
paying checking accounts yielded a 1.0008 gross interest rate during the post-ban period,40
which translates into a daily gross interest rate close to 1 and an r close to 0. Assuming
39For more details, see Shapiro (2005).40FRED from the Federal Reserve Bank of St. Louis Federal.
45
log utility (ρ = 1), the 0.75% a day decline in consumption found in my data implies a
daily discount factor of 0.9925 and an annual discount factor of 0.06, much lower than
reasonably expected. Hence, this result calls into question the validity of consumers being
exponential discounters.
If consumers are time inconsistent, on the other hand, and have quasi-hyperbolic
preferences such that:
U = u(C1) +T
∑t=2ξδt−1u(Ct) (12)
then they discount by ξδ from t = 2 to t = 1 but discount only by δ from t = 3 to
t = 2. Here, consuming in the present is much more valuable than consuming at other
points in the future (hence the term “present-biased”). Assuming log utility, δ = 1 and
daily consumption declines of .75% over 15 days, I calibrate ξ = .96.41 This is exactly
the same estimate that Shapiro finds for the food stamp recipient population and asses
to be reasonable compared to estimates from other studies. The similarities between
the consumption patterns of the military population and that of food stamp recipients
indicate that the military population may posses present-biased preferences.
Another alternative explanation for high daily discount rates is presented by Banerjee
and Mullainathan (2010). They construct a model where individuals consume temptation
goods (goods that give immediate benefit but have no benefit for previous or future selves)
with the proportion of marginal dollar that is spent on temptation goods is decreasing
in consumption level. Such consumers produce consumption patterns with observed dis-
count rates that appear much larger than they actually are. This is because individuals
will choose to consume more immediately rather than save money and they end up spend-
41See Shapiro (2005) for details of this calibration.
46
ing the savings on temptation goods. In this model, the existence of loans with no size
limits would tempt consumers to borrow small amounts to consume temptation goods. If
electronics and alcohol fit the definition of a temptation good, then the increase in their
sales when payday loans are accessible would support such a story. Vissing-Jorgensen
(2011) finds that credit shoppers at a Mexican retail chain who have a tendency to pur-
chase electronics and other luxury category items have much higher default losses than
those that do not posses this tendency. She proposes that these individuals have a desire
for indulgence and lower degrees of self control that fit a temptation good purchasing
model. The end result is that these individuals enter into worse financial conditions after
their purchases because of access to credit.
On the other hand, some of the consumption declines throughout the paycycle can be
explained by food perishability and consumers who face shopping costs. If it is optimal for
consumers to conduct infrequent big shopping trips rather than frequent small shopping
trips due to costs to shopping, then they will have less food as time passes due to food
spoilage. Wilde and Ranney (1998, 2000) document and model such a story among food
stamp recipients. They find that perishable foods are consumed the least towards the end
of a food stamp cycle by infrequent shoppers. In this case, consumers are not present-
biased or prone to temptation spending. Thus when these individuals use payday loans
leading to consumption smoothing, it is more likely as a result of them facing unexpected
income shocks.
1.6.2 Rational Foresight
Consumers may face liquidity constraints because they are bad budgeters or have tenden-
cies to under estimate future expenses or over estimate future income. This explanation
47
is supported by recent survey results that found that 69% of storefront payday loan users
took out their first payday loan to cover reoccurring monthly expenses such as utilities,
car payments and rent.42 If consumers are bad budgeters, then they may not understand
the real costs of payday loans or have the capacity to pay them back. I conducted one test
of consumer budgeting ability. As stated before, the longer a paycycle is, the more likely
that individuals are hit by random shocks and become liquidity constrained. All these
liquidity constrained individuals will go shopping at the Commissary on payday because
that is when they receive relief from their liquidity constraints. Thus, holding all other
things equal, the longer a paycycle, the more people are hit by shocks, and the greater
the coordination of shopping on the closest subsequent payday. Greater coordination of
shopping on payday leads to a larger magnitude of my liquidity constraint measure of
the gap between payday and non-payday spending. We would expect a steady increase
between the magnitude of liquidity constraint measure and every extra day of a paycy-
cle. However, some paycycle lengths are a lot rarer than others. Given that paydays are
typically on the 1st or 15th, paycycle are mostly 14 to 17 days long. However, there are
instances when paydays are 18 and 19 days. If consumers are bad budgeters, I would
expect that they would become liquidity constrained in these longer than usual paycycles.
Thus, I test to see if liquidity constraint measures following longer than usual paycycles
are higher than what would be predicted from just income shock effects. To do this, I run
the specification in Equation 3, but I limit my sample to paycycles that are 14 days long43
and that follow paycycles that are 17 days or shorter. The predicted values of liquidity
constraint by previous paycycle length are plotted in Figure 5 by the dashed line. I extend
the line to previous paycycle lengths of 18 and 19 days that are not used in the estimation.
42The Pew Charitable Trusts (2012).43As before, looking at paycycles of equal length enable me to isolate effects of liquidity constraints
from the effects of people purchasing more according to paycycle length.
48
I then plot the average liquidity constraint measure for each paycycle length44 indicated
by the diamonds in Figure 5. As can be seen, the liquidity constraint measures do not
jump dramatically as a result of longer than usual paycycle length. This puts doubt on
an explanation that this population cannot budget or is myopic to paycycle length. If a
population has the capacity to budget, then they may also have the ability to use payday
loans appropriately.
Thus the population displays both time-inconsistency and ability to budget. A likely
explanation of these results is that heterogeneity exists among the population. The ag-
gregate nature of the data limits me from exploring if the consumers who purchase more
alcohol or who shop in the most time-inconsistent fashion are the same ones who budget
and smooth their consumption. In a forthcoming paper, I will be exploring how individual
level military responses in the Continuing Survey of Food Intakes by Individuals, Con-
sumer Expenditure Survey, Current Population Survey and American Time Use Survey
changed as a result of payday loan access.
1.7 Conclusion
Using a novel dataset I find that consumers can use payday loans to smooth consumption
without suffering a large decrease in their level of food consumption. On the other hand,
I find that consumers are consuming more convenience and department store goods when
given access to payday loans. It is unclear whether consumers are paying a high cost
for the smoothing ability or are experiencing savings. There are indications that the
military population may have present-biased preferences or have tendencies to consume
44I control for day of week, federal holidays, Social Security payout days, early paycheck days, paycycleand store fixed effects jointly for all previous paycycle lengths. Again, dates are limited to those that arein 14 day paycycles.
49
temptation goods. However, they also show signs of being able to budget even if a paycycle
is atypically long. If consumers are able to smooth consumption because of payday loans
and avoid high costs, then this sheds some light on why demand for certain kinds of
expensive short-term credit such as borrowing from loan sharks and pawn shops have
existed for so long (Calder, 1999). If payday loans lead some to over consume, then
these findings support survey and experimental evidence that payday loans have varying
welfare effects. In the survey conducted by Elliehausen and Lawrence (2001), many payday
loan borrowers claim that payday loans are helpful and should not be restricted in any
way other than with a cap on fees while others ask for greater restrictions to prevent
themselves from over borrowing. Wilson et al. (2010) find, in an experimental setting,
that payday loan instruments assist many subjects in surviving financial setbacks while
others suffer compared to subjects with no loan access. This paper provides evidence
that payday loans, even with their cost, can function like more mainstream credit and
can provide consumption smoothing benefits. However, it is of value in policy making
to understand further which consumers use payday loans in a way that is harmful (e.g.
those that are highly time-inconsistent or susceptible to temptation good consumption)
and which benefit from smoothing without paying a high cost. With this information,
a more appropriate assessment can be made of the total gains or losses of implementing
payday loan regulations.
50
2 Expanding the School Breakfast Program: Impacts
on Children’s Consumption, Nutrition and Health
2.1 Introduction
School meals programs are front line of defense against childhood hunger, particularly
for the 22.4 percent of children who live in households that experience food insecurity.
While the school lunch program has long been nearly universally offered, availability of
the school breakfast program (SBP) has lagged behind. There have been recent – and
highly successful – attempts to expand access to the SBP. For example, between 1989 and
2000 the total number of breakfasts served doubled (McLaughlin et al. 2002). According
to our calculations from NHANES data, as of 2009-10 almost three-quarters of children
attend a school that offers the SBP, up from approximately half of students in the 1988-94
wave.
A large research literature supports the commonly held notion that breakfast is an
important meal. Children who skip breakfast have lower nutrient and energy intake across
the day – in other words, they do not make up for the skipped meal by consuming more
calories later in the day. Briefel et al. (1999) summarize the research evidence on cognitive
impacts, and conclude“skipping breakfast interferes with cognition and learning, and that
this effect is more pronounced in poorly nourished children.” Despite the importance of
breakfast, only 86 percent of elementary school children aged, and 75 percent of children
aged 12-19, consume any type of breakfast on a typical day (USDA ARS, 2010).
Policy makers have long been troubled by the low take-up rate of the SBP, which was
51
26 percent in 2010 (compared with a 63 percent participation rate in the school lunch
program, see Fox et al. 2013). This is in part troubling because there is evidence that
school breakfast is nutritionally superior to breakfast at home (Bhattacharya et al. 2006;
Devaney and Stuart 1998; Millimet et al. 2010). Two factors appear to drive the low
take-up of breakfast: stigma and timing. Recent policy innovations have attempted to
ameliorate these barriers to participation.
To address (perceived) stigma associated with participation in the school breakfast
program, some districts have offered universal free school breakfast instead of the stan-
dard program that provides free breakfast only to students who are income-eligible for
a subsidy.45 There is some evidence, described below, that this policy change increases
take-up rates. The limitation remains, however, that in order to participate in the break-
fast program a student generally has to arrive at school prior to the start of classes and
this is reported to be an important barrier for some children. To address this, another
recent policy innovation has been to serve breakfast in the classroom (BIC) during the
first few minutes of the school day. BIC eliminates the need for students to arrive to
school early to participate in the school breakfast program, and dramatically increases
participation in the SBP (FRAC 2009; FNS undated). This program has recently gained
momentum, with major expansions in cities such as Washington, D.C., Houston, New
York City, Chicago, San Diego and Memphis.
In this paper we re-analyze experimental data previously collected by the U.S. De-
partment of Agriculture to measure the impact these two popular policy innovations:
universal free breakfast, and breakfast in the classroom. As described below, re-analysis
of the data is necessary because the original evaluation of the experiment was incomplete.
45The USDA has special reimbursement provisions that encourage schools to adopt universal free mealsprograms.
52
In particular, it did not separately estimate the impacts of the two policies even though
the experimental design allowed such estimates to be conducted. In this re-analysis, we
calculate experimental estimates of both the impact of universal free cafeteria breakfast
and the impact of BIC.
We extend the analysis in three additional directions. First, in order to improve
statistical power of the analysis and following the recent program evaluation literature
(Kling et al. 2007; Anderson 2008; Hoynes et al. 2012), we combine similar outcomes into a
summary indexes covering areas such as nutrition at breakfast, nutrition over 24 hours, and
child health outcomes. Second, we address the policy decision facing a school district by
constructing difference-in-difference estimates of the relative effectiveness of BIC compared
with universally free cafeteria breakfast. Third, we implement an instrumental variables
approach to estimate the causal impact of eating breakfast on student outcomes.
2.2 Literature Review
Two recent types of policy innovations have attempted to increase breakfast takeup, and
there has been recent evidence on their impacts using a variety of difference-in-differences
research designs. The first type of policy is the introduction of universal free breakfast,
which allows children to participate in the school breakfast program at no charge regard-
less of whether they are typically eligible for free or reduced-price school meals. Ribar
and Haldeman (2013) study the introduction and discontinuation of universal free school
breakfasts in Guilford County, North Carolina, and find that take-up of school breakfast
increases by 12 to 16 percentage points when the program is universally free of charge.
While most of the increased participation was among students formerly ineligible for sub-
sidized meals, they also find an increase among those who were eligible for free meals all
53
along. When the program was discontinued, there were no changes in attendance rates
or test scores. Leos-Urbel et al. (2013) compare New York City public schools that im-
plement universal free school breakfast to those that retain the traditional program in a
triple-difference framework. They find strong impacts on participation but no impacts on
student test scores, and a small positive impact on attendance for some subgroups.
The second area of recent policy innovation is offering breakfast in the classroom during
the school day. Imberman and Kugler (2014) investigate the very short-term impacts of
the introduction of a BIC program in a large urban school district in the southwestern
United States. The program was introduced on a rolling basis across schools, and the
earliest-adopting schools had the program in place for up to 9 weeks before the state’s
annual standardized test was administered. They find an increase in both reading and
math test scores, but no impact on grades or attendance. Additionally, there was no
difference in impact between those schools that had adopted the program for only one
week vs. those that had the program for a longer time. The pattern in the results led the
authors to conclude that the test score impacts were driven by short-term cognitive gains
on the day of the test due to eating breakfast and not underlying learning gains.46 Dotter
(2012), on the other hand, finds stronger longer-run impacts of the staggered introduction
of a BIC program in elementary schools in San Diego. Using a difference-in-differences
approach, he finds that BIC increases test scores in math and reading by 0.15 and 0.10
standard deviations, respectively. He finds no test score impacts on schools that previously
had universal free breakfast, and no impacts on attendance rates. As shown below, our
results from the randomized experiment are consistent with the earlier literature in that
we find no attendance impacts. On the other hand, we also find no positive impact of
46This interpretation is consistent with earlier research by Figlio and Winicki (2005), which found thatschools with much at stake in a test-based accountability system served higher-calorie lunches duringtesting weeks.
54
BIC on test scores and can rule out effect sizes as large as those found in the earlier,
quasi-experimental literature.
2.3 Empirical Approach
This paper uses data from a randomized experiment implemented in 153 schools across
6 school districts designed to test the impact of universal free school breakfast.47 That
is, at baseline all schools in the experiment at least offered the standard school breakfast
program. Control group schools continued to offer the standard program, which serves
free or reduced-price (maximum price of 30 cents) breakfast to those that are income-
eligible and can be purchased at full price for those ineligible for a meal subsidy (current
average price $1.13, Fox et al. 2013). The breakfast is typically served before school in
the cafeteria. Treatment schools offered school breakfast free of charge to all students
regardless of their usual eligibility for subsidized meals.48 The experimental design first
matched schools into pairs (or occasionally groups of 3 schools), and then treatment status
was randomly assigned within the pair. At that point the treatment schools got to choose
whether to implement their universal school breakfast as a traditional program – that is,
in the cafeteria before school – or as a BIC program. The treatment lasted for 3 years.
The original evaluation found that treatment schools nearly doubled their SBP par-
ticipation, and that students in treatment schools were 4 percentage points more likely to
consume a “nutritionally substantive breakfast.” There were no statistically significant im-
pacts on most other measures of food intake, food security, student health, or achievement
47The experiment was conducted by the USDA in conjunction with Abt Associates from 1999 through2003 and was entitled the School Breakfast Pilot Project. We obtained the public-use data by requestingit from USDA.
48Under normal circumstances, a child is eligible for free meals if his or her family’s income is lessthan or equal to 130 percent of the poverty threshold, and is eligible for reduced-price meals if the familyincome is less than or equal to 185 percent of the poverty threshold.
55
outcomes.
2.3.1 The Need for Re-analysis
In the original evaluations of the experiment (Bernstein et al. 2004), outcomes were
presented separately for the overall treatment and control groups, and then the treatment
group outcomes were presented separately by whether they adopted a cafeteria-based or
classroom program. But it is inappropriate to compare the separate treatment groups to
a pooled control group, and may lead to biased estimates of the policy impacts if different
types of schools selected into cafeteria vs. classroom breakfast programs. In practice, this
is an important concern because there is evidence that the treatment schools differed prior
to program implementation. In the year before the experiment began, schools that would
go on to implement a cafeteria-based program had a 14 percent participation rate in the
SBP, while those that would opt for a BIC program had a 22 percent participation rate. As
shown below, the two types of treatment schools also differed along other characteristics
such as rates of disadvantage. As a result, impact estimates separately comparing them
to a pooled control group may be seriously biased.
Appropriate impact estimates can be constructed, though. As described above, in
the experimental protocol schools were first paired on observable characteristics and then
treatment or control status was randomly assigned within pairs. Subsequently, treatment
schools were allowed to choose the location of their universal school breakfast program.
The design of the experiment is represented in Table 10, below. Since random assignment
was conducted within treatment pairs, it is possible to measure the causal impact of the
universal cafeteria breakfast and the causal impact of BIC by comparing each treatment
group to its matched control group. To graphically demonstrate how to estimate the
56
impact of the program in this experimental design, see that outcomes for groups should
be compared vertically. That is, the impact of a universal cafeteria breakfast could be
estimated as the difference between A and A’. Similarly, the impact of the BIC program
can be estimated as the difference between B and B’. Of course, the overall impact of uni-
versal school breakfast (regardless of location) can be estimated as the difference between
average outcomes in the set A + B compared to those in the control group A’+B’.
Surprisingly, the official USDA evaluation failed to provide the experimental impacts
separately for BIC vs. cafeteria-based programs. Below, we first reanalyze the data using
the appropriate control group. This will allow us to make separate conclusions about the
impacts of a universal cafeteria breakfast and universal breakfast in the classroom, which
to date have not been known because of the limitations of the original analysis.
2.3.2 Outcomes to be measured
Many prior analyses of school breakfast programs are limited by the outcome variables
that are available. Among the quasi-experimental literature, studies have looked either at
take-up (Ribar and Haldeman, 2013), or academic achievement (Frisvold 2012; Imberman
and Kugler 2014; Dotter 2012), or detailed nutrition outcomes (Bhattacharya et al. 2006),
or a combination of take-up and achievement (Leos-Urbel et al. 2013). To our knowledge,
no paper in the prior literature has access to all of these outcomes in the same dataset.
Not only do we have detailed information on a range of outcomes, but we also have three
years of outcome data, allowing us to investigate the impacts of the programs as they
mature.
We start by analyzing the impact of each of the programs on take-up, and how the
impacts vary across characteristics such as prior income-eligibility for free breakfast, gen-
57
der, race, and other characteristics that were measured prior to the experiment. Next,
we turn to nutrition and health outcomes. We measure whether a student consumed any
breakfast, or consumed a “nutritionally adequate” breakfast as defined in the prior litera-
ture. We also measure whether a student consumes two breakfasts (typically, one at home
and one at school), and the household’s food security status. We analyze consumption of
total calories, calories by macronutrient (protein, fat, carbohydrates), and nutrient intake
both in milligrams and as percent of RDA, and number of servings of items on the Food
Pyramid, and measure these both for breakfast and over a 24-hour period. For measures
of student health, we have parent-reported health status, height and weight (from which
we calculate BMI and obesity), school attendance, and tardiness. Finally, we analyze
behavioral and cognitive measures such as test scores.
Because we observe many outcome variables and in order to increase statistical pre-
cision, we follow the recent literature (e.g. Kling, Liebman and Katz 2007; Anderson
2008; Hoynes, Schanzenbach and Almond 2012) and estimate summary standardized in-
dices that aggregate information over multiple treatments. The summary index is the
simple average across standardized z-score measures of each component. The z-score is
calculated by subtracting the mean and dividing by the standard deviation of the pooled
control group. In particular, we form five indices. Two nutrition indices cover nutrient
intake at breakfast and over 24-hours, respectively. The health outcomes index includes
parent-reported health status, (reverse coded) number of days absent, and overweight
status.49 The behavior measures include measures of whether a student is inattentive,
defiant, and so on. Finally, the index of academic outcomes combines math and reading
test scores across the three years of the experiment.
49Student is defined as “overweight” if he/she is in the 95th percentile of BMI for his/her age group.
58
2.3.3 Impact of SBP participation
We address whether participation in the SBP improves student outcomes. There are con-
flicting and sometimes perverse-signed impact estimates in the literature (summarized in
Briefel et al. 1999, also Waehrer 2007), though most prior studies have been correla-
tional.50 The prior literature is severely limited because there are few research designs
available to isolate the causal impact of SBP participation on outcomes.
We estimate the impact of participation using the experimental data and an instrumen-
tal variables approach. In particular, we use a school’s random assignment to treatment
status to instrument for a student’s individual-level participation in the SBP. This will
allow us to estimate the impact of participation on the so-called “compliers” in a local
average treatment effect framework – that is, the impact on students who were induced
to participate in the program by the universal school breakfast policy (Angrist and Pis-
chke 2009). The impacts of the program on this group are of particular interest to policy
makers.
2.4 Results
2.4.1 Validity of the Experiment
Table 11 presents means of pre-determined characteristics across the treatment and control
groups. As described above, we present three groups of estimates: first the pooled results
for the impact of universal free breakfast regardless of the type of program adopted,
then separately those for the BIC experiment and cafeteria-based experiment. The first
two columns in each set of results presents means for the control and treatment groups,
50Bhattacharya et al. (2006) is a notable exception, in which the authors use quasi-random variationin SBP availability and find that the program improves nutritional intake among participants.
59
respectively. The third column presents the p-value of a test for whether the means are the
same across groups after conditioning on randomization pool fixed effects. In general, the
treatment and control groups are well-balanced across background characteristics, with
no statistically significant differences for the pooled group or the cafeteria group. Among
the BIC group, however, there is a small difference in student-level eligibility for free
or reduced-price lunch, with the treatment group being slightly less disadvantaged than
the control group. The differences are not statistically significant across other measures
of disadvantage, such as family income less than $20,000 per year, minority status, or
whether the student is from a single parent household. Our subsequent analyses are largely
unchanged if we control for these background characteristics. There are no significant
differences in school-level characteristics (shown in panel B). Note that the schools in
the BIC sample are substantially more disadvantaged than the cafeteria sample. Among
the control groups, 61 percent of the BIC group is eligible for free or reduced-price lunch,
compared with 51 percent of the cafeteria-based group. When restricted to free lunch only,
the rates are 45 and 34 percent, respectively. Furthermore, students in the BIC control
group take up school breakfasts in 22% of school days in the base year as compared to
14% for the cafeteria-based group. These differences underscore the need to compare the
BIC treatment group to the appropriate control group.
2.4.2 Outcomes
Table 12 shows results for participation and nutrition intake during the first year of the
experiment. The table presents coefficients on an indicator for treatment group in a re-
gression that controls for randomization-pool fixed effects and the following covariates:
free and reduced lunch eligibility, household income, race, single parent household, gender
60
and age. Standard errors (adjusted for homoscedasticity at the school level) are shown in
parentheses. Participation is measured as the proportion of days that a student has taken
a school breakfast, whether or not the child took the school breakfast on the day that the
nutrition information was collected. The overall (pooled) impact on SBP participation is
18 percentage points, a near doubling of participation compared with the control group.
There is a substantial difference in treatment effects, however, across program type. The
BIC program increased year 1 participation by 38 percentage points, or a 144 percent
increase in participation. The cafeteria-based program also significantly increases partic-
ipation, but by a more modest 10.5 percentage points, or a 52 percent increase in rate.
Since breakfasts are reimbursed on a per-pupil basis, a child’s participation in SBP de-
termines the total cost of the program. Another way to measure participation is whether
a child “usually” takes a school breakfast. When we define “usually” as participation 75
percent or more days, the impacts on participation are even larger in percentage terms.
The impacts are a 13 percentage-point increase in participation in the pooled sample (an
increase of over 160 percent), and 29 percentage points in the BIC sample (a 242 percent
increase). These increases in program participation could reflect students going from con-
suming no breakfast to a school breakfast, but could also reflect substitution of a home
breakfast for a school breakfast, or consumption of multiple breakfasts. The total impact
on nutritional intake depends on the extent of the substitution.
The impact on breakfast consumption varies depending on the definition of breakfast
chosen.51 At one extreme, we can define any positive caloric intake in the morning to
be breakfast consumption. According to this definition, 96 percent of the pooled control
group eats some breakfast. Overall, universal school breakfast does not change this prob-
51“Breakfast” includes all foods and beverages, excluding water, consumed between 5:00 a.m. and 45minutes after the start of school, and also any foods consumed before 10:30 a.m. that the student/parentreported as being part of breakfast.
61
ability, although the BIC program increases the likelihood that a child eats any breakfast
by 2 percentage points. If we implement a more stringent threshold for what counts as
breakfast – a “nutritionally substantive” breakfast that requires consumption of at least
2 food groups and at least 15 percent of the daily allowance of calories – then the im-
pact is stronger. The pooled impact is an increase of 3 percentage points, compared
to a control group level of 59 percent consuming that quality level of breakfast. This
is driven almost entirely by a 10 percentage-point increase among the BIC group, with
an insignificant 1 percentage-point estimate among the cafeteria-based program group.52
BIC substantially increases both participation and the likelihood that a student actually
eats breakfast, while a universal cafeteria-based program increases participation in the
program but primarily alters where – and not whether – students eat breakfast.
The next row displays the impact on whether a student reports eating two nutritionally
substantive breakfasts, one at school and one at another location . Here again the impact
is primarily driven by the BIC group, which causes a 5-point increase in eating two
breakfasts. This represents more than doubling the likelihood of eating two breakfasts.
The BIC program reduces the likelihood that a student eats breakfast only outside of
school by 45 percentage points, while the universal cafeteria-based program reduces this
likelihood by 13 points.
The final set of rows report impacts on calorie and nutrient intakes, both at breakfast(s)
and over a 24-hour period, as well as on food security. Consistent with the reported meal
intake patterns, BIC participants consume an additional 1.7 percent of the recommended
daily allowance (RDA) of calories (adjusted for child’s age) at breakfast. There is no
measured difference in calorie intake among the cafeteria-based program group. The
program does not appear to be increasing the nutrient intake at breakfast for either
52Impacts are similar if we use alternate definitions of breakfast commonly used in the literature.
62
treatment group.53 The 24-hour dietary impacts suggest that any increase in consumption
at breakfast is offset at other times during the day, and 24-hour calorie and nutrition
intakes are no higher for the treatment groups. Finally, neither program appears to
impact household food security status.
Overall, the universal cafeteria-based program appears to shift where students consume
breakfast, but does not substantially alter whether or how much breakfast is consumed.
On the other hand, the BIC program changes where students eat breakfast as well as how
much they eat. It raises the likelihood that a child eats any breakfast, and also raises the
likelihood that he or she eats two breakfasts. Since the cafeteria-based program does not
change students’ nutritional intake, it would be surprising to find that it impacts other
outcomes. On the other hand, since BIC increases nutritional intake (both in terms of
increasing the likelihood that a child eats any breakfast, and in terms of meal quality)
and also potentially crowds out some classroom instructional time, the expected impacts
are ambiguous.
Table 13 shows impacts on academic, behavioral and health outcomes during the first
year of the experiment. For completeness, we include the impacts from the pooled sample
and the cafeteria-based program, but we concentrate our discussion on the BIC results.54
The BIC treatment has no statistically significant impact on any outcome. The point
estimate for the test score index is -0.05 indicating a statistically insignificant 5 percent of
a standard deviation decline in average math and reading test scores. The standard errors
allow us to reject a positive impact as small as 0.03 standard deviations, which is smaller
53The index consists of consumption of vitamins A, B-6, B-12, C, riboflavin, folate, calcium, iron,magnesium and zinc.
54Further analysis of the relative impact of BIC vs. cafeteria based universal breakfast programs usinga difference-in-difference approach is presented in a later section. Such an analysis may be useful asschools often face the decision to introduce universal school breakfast in the cafeteria or in the classroom.
63
than the results found in the quasi-experimental literature.55 When broken out separately
by subject, the estimated impact (standard error) for math is -0.09 (0.05) and reading
is -0.02 (0.04). The estimated impact of BIC on attendance and tardiness is wrong-
signed. The estimate for attendance is statistically significant at the 5% level but small
in magnitude (i.e. attendance decreases by 0.94 days in a 180-day school year). The BIC
impact on the “bad behavior index” is right-signed, in that the point estimate indicates a
decrease in misbehavior, but not statistically different from zero. There is either negative
or no impact on child health as measured by an index across a variety of outcomes, child’s
BMI or an indicator for being overweight. Note that the control group means across
all of these characteristics indicate that the BIC sample is more disadvantaged than the
cafeteria-based sample.
Table 14 shows impacts for subsequent years. We define the BIC sample consistently
over time based on their status in the first year of the program, even though six BIC
treatment schools switched to a cafeteria-based program at some point during the exper-
iment. The impact on SBP participation is relatively stable over time, with the pooled
impact essentially doubling takeup, BIC increasing takeup by about 150 percent, and the
cafeteria-based program increasing it by approximately 54 percent. There is no evidence
of an impact on test scores, with year two and three impacts being insignificant. Pooling
the test scores across math and reading, and across all 3 years of outcomes, the impacts
are small and statistically insignificant across all groups. Impacts on attendance rates
are sometimes positive and significant, with an estimated 1 percentage point increase in
attendance rate for the BIC group in year 3. The pooled impacts on attendance rates
across all 3 years, however, are wrong-signed and not statistically significantly different
55In order to increase precision of the estimates, we control for baseline test scores in the models. Asexpected, addition of these controls does not change the impact estimates but they do reduce the standarderrors by 20-30 percent.
64
from zero. The BIC appears to increase tardiness significantly in most years, though,
again, the magnitude of the impact is quite small (i.e. less than a day per school year).
Table 15 explores whether the BIC impacts are different across subgroups. Each
triplet of columns represents a different subgroup. The first column in each pair presents
the control group mean, the second column presents the impact of BIC treatment after
conditioning on randomization pool fixed effects and previously mentioned demographic
controls and the last column presents the number of observations. There is some varia-
tion in the impact on participation and breakfast eating. Free-lunch ineligible students
increase their participation rates by more in response to BIC than do free-lunch eligible
students, but the impact on breakfast consumption is slightly stronger among the more
disadvantaged group. Similarly, BIC increases the likelihood that boys participate in the
program more than girls, but has a stronger increase on the likelihood that a girl eats
a nutritionally substantial breakfast. Among high-poverty, urban schools, BIC increases
participation by 138 percent, and increases breakfast eating by over 27 percent. Despite
differences in treatment intensity, there is no significant positive impact on test scores,
attendance or the child health index.56 Results are generally stable across the behavior
index measure (indicating an improvement in behavior), and reach statistical significance
among minority students.
2.4.3 Difference-in-difference Estimates
The more relevant policy question for a school or district considering implementing a uni-
versal school breakfast program is the relative effectiveness of a traditional cafeteria-based
school breakfast relative to breakfast in the classroom. To experimentally address this
56We constructed the urban, high-poverty sample to be similar to the sample used in Dotter (2012).We find a negative point estimate for test score impacts, but our standard errors are sufficiently largethat we cannot rule out impacts as large as he finds.
65
policy question, schools would need to have been randomly assigned across these groups.
Referring back to Table 10, this would mean that schools should have been randomly
assigned to columns in addition to rows (i.e. randomly assigned to group A or group
B). Under a design like this, a simple difference-in-difference estimate (i.e. comparing
outcomes across cells [A – A’] – [B – B’] = δ) would yield an unbiased estimate of the
relative impact of universal breakfast in the cafeteria vs. the classroom.
Unfortunately, schools were not randomly assigned but instead self-selected into treat-
ment type. Under the arguably palatable assumption that schools choose the program
that will improve their outcomes the most, we can estimate an upper bound on the rel-
ative effectiveness of the two types of universal breakfast programs by comparing effect
sizes across the groups. The relative effect of a classroom vs. cafeteria universal program
is an important policy-relevant question, with little evidence to date on it. Therefore we
calculate the difference-in-difference estimates, attempting to estimate the relative effec-
tiveness of BIC compared to a cafeteria-based program, even though this parameter is
not experimentally identified.
We calculate the difference-in-difference estimates, comparing each treatment type
to its randomly assigned control group, then test for differences in impact across the two
treatment types. Results are shown in Table 16. Most notably, BIC increases participation
relative to universal cafeteria breakfast by an average of 28 percentage points. Similarly,
BIC increases the likelihood of actually eating breakfast (not merely participating in the
program) by between 2 and 8 percentage points depending on the definition of breakfast.
It also raises the likelihood that a child eats two breakfasts by 5 points relative to the
cafeteria-based program. On the other hand, there are signs that the cafeteria-based
program, relative to the BIC program, increases the likelihood that a child is not tardy
66
(by around 1.2 days over a 180-day school year according to the pooled-year results). This
makes sense as participation in the cafeteria-based program requires a child be present at
school before school starts. Since there are few statistically significant impacts of universal
breakfast, the difference-in-differences estimates also show no impact of BIC relative to a
cafeteria breakfast on other nutrition, health, attendance, behavior or test score outcomes.
2.4.4 Impact of Eating Breakfast
An elusive question in the literature has been what is the impact of eating breakfast –
whether at home or school – on a child’s outcomes. As shown in Table 12 above, being
randomly assigned to the BIC treatment increases the likelihood that a student consumes
breakfast. We can thus use the school’s random assignment to BIC as an instrument
for breakfast consumption, and estimate the causal impact of breakfast consumption.
It is important to emphasize that this is a local average treatment effect, and provides
an estimate of the causal impact of breakfast consumption for those students who were
induced to start eating breakfast because of the treatment. Results are presented in Table
17, and are limited only to the BIC sample (i.e. the randomization pools in which the
treatment group participated in BIC).
The first triplet of columns shows results for a nutritionally substantial breakfast (i.e.,
as before this includes consumption of food from 2 food groups and at least 15 percent of
daily RDA of calories). The first column shows the OLS relationship between breakfast
eating and a variety of outcomes, after controlling for other background characteristics.
Consistent with the prior literature, eating breakfast is correlated with better dietary
outcomes. Eating breakfast is associated with a 0.46 standard deviation increase in nu-
tritional intake as measured by the 24-hour micronutrient index, and a 16 percentage
67
point increase in daily calories. There is no systematic relationship in these data between
breakfast eating and child’s BMI, whether the child is overweight, or the index of health
outcomes. There is also no significantly significant association between breakfast eating
and child outcomes such as behavior, attendance or test scores.
Moving to column 2, we can estimate the causal impact of being induced to eat a
substantive breakfast by the BIC program. The instrument predicts a 10-point increase
in breakfast eating, and is a strong predictor with an F-statistic of over 16. Instrumenting
for breakfast consumption flips the signs of most of the estimates, suggesting that the
correlations in the OLS results are largely driven by selection. The standard errors are
quite large and most of the IV estimates is statistically significantly different from zero.
Nonetheless, the point estimates from the IV results for behavior suggest that eating
breakfast may improve these outcomes. On the other hand, the estimates on attendance,
child health and test scores become more negative when instrumented.
Instead of defining breakfast as a binary variable equal to one if consumption is at or
above a floor, an alternative measure of breakfast, displayed in columns (4) and (5), is
the total calorie consumption in the morning. Results are generally similar as those in
the first two columns, with the point estimates in the IV results suggesting declines in
overweight and bad behavior but wrong-signed, though small, estimates on child health,
attendance and test scores. The standard errors are large and none of the estimates are
statistically significantly different from zero.
2.5 Discussion and Conclusions
The USDA implemented an extremely important experiment on the impacts of making
school breakfast uniformly available at no cost, both in the cafeteria before school and in
68
the classroom. Our reanalysis isolated the impact of each of these programs on nutrition,
health, attendance and achievement. We find that expanding the school breakfast program
substantially increases program takeup, especially under the BIC treatment. Furthermore,
universal free school breakfast and BIC also increase the likelihood that a child eats a
nutritionally substantive breakfast. BIC also increases the likelihood that a child eats two
breakfasts. The additional consumption appears to be offset across the rest of the day, so
there is no measurable impact on 24-hour nutrition as measured by calories or nutritional
intake.
Despite the increase in breakfast consumption under BIC, we find no positive impact
on most other outcomes. In contrast to the earlier, quasi-experimental literature, we find
no positive impact on test scores and some evidence of negative impacts. Similarly, there
appears to be no positive impact on attendance rates or child health. There is suggestive
evidence that BIC may improve behavior, though.
Of course, the results should be viewed with the important caveat that our results
do not indicate that the school breakfast program is not effective. There is already a
reasonably high program participation rate among the control group, and a higher break-
fast consumption rate among the control group, indicating that some children who do
not participate in the school program eat breakfast at home. In other words, our results
do not shed light on what would happen if the school breakfast program were reduced or
eliminated, nor do they suggest that reducing or eliminating the school breakfast program
is warranted. The results speak only to attempts to further expand the program, through
universal access or BIC programs. These results indicate that much of the increase in
program participation induced by program expansions represents substitution from con-
sumption of breakfast at home to school. A substantial share of children is induced to
69
start consuming breakfast by the program, and a slightly smaller share is induced to con-
sume two breakfasts. The relatively modest measured benefits suggest that policy-makers
should carefully consider how to trade these off against the increased program costs.
70
3 Access to Short-term Credit and Household Ex-
penditures and Labor Force Participation
3.1 Introduction
Zaki (2014) took advantage of exogenous variation in payday loan access across time
and geography in the military setting to examine the effect of payday loan access on
daily food consumption and monthly durable consumption. She found that payday loan
access allowed military households to smooth food consumption over the short run, had
no measurable effect on their level of food consumption but encouraged their purchase
of electronics and alcohol. There are some shortcomings to this study however. The
consumption data, which are from military grocery stores, are at the store rather than
individual level. This fact introduces noisiness to the measured impact of payday loan
access as some individuals, military retirees, can shop at these grocery stores but do not
experience a change in payday loan access. Also, the lack of individual or household level
data prevents analysis of heterogeneous effects of payday loan access based on demographic
characteristics. Finally, since the data set is from grocery and department stores only, she
is unable to analyze effects of payday loan access on the rest of the household consumption
set.
To complement this study, I turn to other data sets that have the potential to overcome
some of the mentioned shortcomings. The Consumer Expenditure Survey collects monthly
expenditure data for a wide variety of spending categories at the household level. It
also collects many demographic characteristics of surveyed household members as well
as some labor force information. The Current Population Survey collects monthly labor
information from surveyed households. Both surveys interview military households but
71
vary in their methodology as to which ones. I use these surveys to get a fuller picture of
the effects of payday loans on daily household life.
The core of the identification strategy used in this papers follows that of Zaki (2014).
Military households are assigned to bases across states, some of which allow payday loan
shops to operate within their borders and some that do not. This assignment provides
an exogenous variation in payday loan access for military households across states. The
enactment of the Military Lending Act (MLA) prohibited active duty personnel and their
households from accessing payday loans and other forms of short-term credit after Oc-
tober 2007. The law provides an exogenous variation in payday loan access for military
households across time. Thus, the military setting is ideal to test the effects of payday
loan access in a difference-in-difference framework as a group of military households, those
living in payday loan allowing states, are affected by the MLA and another group, those
living in payday loan banning states, are not. For greater robustness, I include a set
of civilian households with similar characteristics as military households in the analysis
as another control group. The main identification strategy in this paper will be a triple
difference-in-difference comparing the behavior of those military households that experi-
enced payday loan access changes to that of those military military households that did
not and to civilian households that did not.
The outcome variables analyzed are overall and category specific household spending
and various measures of household labor force participation. I find mixed results on the
effect of payday loan access on overall spending, but there are some indications that it was
negative. Households reduced spending on vehicle operation, vehicle financing, alimony
and child support when they had access to payday loans. Young households also reduced
spending on fees related to banking and conventional credit. There is also some evidence
72
that young households reduced their participation in the labor force by working less hours
and having fewer members earn money. On the other hand, spending on utilities and
home goods increased as a result of payday loan access. Young households spent more on
basic utilities and home repair when they had access to payday loans. They also spent
more on food eaten away from home and electronics. Finally, households tended to live
in rental housing over owned housing when they had access to payday loans.
At first look, payday loan access seems to lead households to consume and behave
differently. However, there are two large caveats that go along with these results. First,
interpretation of significance of results is convoluted due to the number of hypotheses
tested throughout the paper (more than one for each spending and behavior outcome
variable). If I correct for this issue using the conservative Bonferroni correction, then
almost none of the results are significant at an acceptable level. Second, putting aside
the first caveat, the magnitudes of all results with significance at the 10% level seem
implausibly large. Thus, interpretation of these results should be approached with great
caution.
This paper proceeds as follows: Section 2 summarizes the Military Lending Act and
the corresponding types of short-term credit covered under that law; Section 3 describes
the data sets that are used and the identification framework utilized to analyze them;
Section 4 presents the results of the analysis and Section 5 discusses the results.
3.2 Institutional Background
The Military Lending Act is a federal law that became effective on October of 2007 as
a result of the Talent-Nelson amendment to the John Warner National Defense Autho-
rization Act of 2007. It effectively prohibited active duty personnel and their dependents
73
from obtaining various forms of short-term credit by placing a 36% APR cap on these
instruments when loaned to covered individuals. This cap is very binding as the APR
rates for the covered loan instruments are easily over 300% APR. There is evidence that
the law was effective in prohibiting use of these instruments among the targeted popu-
lation (Fox, 2012). The Department of Defense lobbied for this law claiming that there
is prevalence in small-dollar “predatory” credit usage among the military (Tanik, 2005),
that lenders target military populations (Graves and Peterson, 2005) and that such credit
reduces military readiness and performance (Carrell and Zinman, 2013; Department of
Defense, 2006).
The three main forms of credit covered under this law are payday loans, car title loans
and tax refund anticipation loans. Payday loans and tax refund anticipation loans are
pay advances for a future income (i.e. a paycheck or a tax refund respectively). A car
title loan is a short-term loan that uses an owned car as collateral. All these loans charge
fees that compute to over 300% APR. In the time period of study, tax refund anticipation
loans were legal in all states, preventing identification of their effects in this paper. Payday
loans were legal in 41 states while car-title loans were legal in a much smaller number of
states. Thus, I will mainly refer to the effect of payday loans in this paper.57
Much debate exists over the effects of payday loan use. There is concern that borrowers
have self-control problems or overestimate their ability to repay leading to high costs to
borrowing. Research findings on the welfare effects of payday loans are mixed. Some find
that payday loan access leads to negative outcomes (e.g. increased debit and checking
account closures in Campbell, Martinez-Jerez and Tufano (2012), increased Chapter 13
bankruptcy filings in Skiba and Tobacman (2011), increased difficulty in paying bills in
Melzer (2011)) and some find it leads to positive outcomes (e.g. increased ability to
57Results in this paper remain the same even when controlling for the existence of car title loans.
74
smooth daily food consumption in Zaki (2014), decreased number of bounced checks in
Morgan, Strain and Seblani (2012), and a decrease in the instances of foreclosures in areas
hit by natural disasters in Morse (2011)). This paper adds to this strand of literature by
documenting the effects of payday loans on a fuller range of expenditure categories as well
as labor force participation measures.
3.3 Empirical Strategy
3.3.1 Data
All data used come from one of two surveys: the Consumer Expenditure Survey and the
Basic Current Population Survey. For both surveys, data are collected for the period of
October 2005 thru September 2010. The Consumer Expenditure Survey contains data on
household spending. Households are surveyed quarterly for up to a year and spending is
reported on a monthly frequency for a variety of categories. The Basic Current Population
Survey contains data on household labor force behavior (e.g. whether a member is in the
labor force and number of hours worked per week). Here households are surveyed for
four consecutive months and resurveyed for four more consecutive months after an eight
month break. Though the Current Population Survey interviews households with military
members, they only record labor information of the civilians within that household.
Military personnel will enter the two surveys differently. In the Consumer Expenditure
Survey, military personnel will only be surveyed if they live off base. In the Current
Population Survey, military personnel both on and off base can be surveyed, but only
if they live in households with other civilians. Hence, given the survey methodology,
surveyed military members constitute a different demographic makeup than the average
active duty member. A comparison of some demographic characteristics is presented in
75
Table 18. The average age of a surveyed military member in both surveys is greater
than the average age of an active duty military member. This may be due in part to
the fact that the military incentivizes(financially) or mandates that enlisted personnel of
lower ranks (especially enlisted singles) to live on base, hence keeping them out of the
Consumer Expenditure Survey. Furthermore, it is reasonable to believe that the pool
of military personnel with (civilian) dependents are on average older than their single
counterpart. As is expected, the average number of children and average household size
are larger for military members contained in the Current Population Survey than those in
the Consumer Expenditure Survey or in the full military population. Similarly, a greater
number of military members in the Current Population Survey belong to a household type
with both a husband and wife compared to those in the Consumer Expenditure Survey and
the full military population. The greater percentage of surveyed military personnel tend
to hold bachelors degrees compared to the full military population, indicating perhaps a
greater presence of officers in the surveyed population. Both surveys contain a smaller
proportion of minorities as compared to that in the full military population. Finally, the
proportion of males in the military sample of the Current Population Survey is higher
than that in both the Current Expenditure Survey and the full military population.
3.3.2 Identification Framework
As in Zaki (2014), I use a difference-in-difference framework to analyze the effects of
access to specific forms of short-term credit on household expenditure and labor force
behavior. The treatment and control groups are determined by military household state
of residence and the treatment, payday loan access, is administered in the pre-MLA time
period (October 2005 thru September 2007). The MLA prohibited active duty personnel
76
and their dependents from accessing payday loans and several other forms of short-term
credit after it became effective on October 2007. However, this only affected military
personnel assigned to bases in states that allowed payday loans at the time of the law.58
Military personnel assigned to bases in states that banned payday loans59 experienced no
change in short-term credit access as a result of the law. The latter group thus can be used
as a control for the former group in a difference-in-difference framework. A specification
corresponding to the one implemented in Zaki (2014) is:
Yit = φt + θs + ξi + βAccessi × PreBant + εit (13)
where Y is an outcome variable of interest for household i on date t; φ are date fixed
effects; θ are state fixed effects; ξ are household level covariates (specifically indicator
variables for number of adults, children, seniors, members and controls for husband/wife
units, the presence of at least one household member with a high school degree and the
age of the main household income earner); PreBan is a dummy variable equal to 1 if t is
before October 2007; Access is a dummy variable equal to 1 if household i lives in a state
that allows payday loans in the Pre-ban period and ε is the error term. The difference-in-
difference coefficient of interest is β and is interpreted as the impact of short-term credit
access on the outcome variable.
One concern with this difference-in-difference specification is that it does not take into
account other (non-MLA) factors that might affect the control and treatment groups dif-
ferentially over the study period (e.g. state level factors). Fortunately, surveyed civilians
58More details on these states can be found in Zaki (2014)59States only need to have banned payday loans in the period of study before the Military Lending Act
becomes effective (i.e. October 2005 thru September 2007).
77
living in the same states as control and treatment group members can be affected by the
non-MLA factors while not being affected by the MLA.60 The difference-in-difference mea-
sure of civilians in payday loan allowing states and in payday loan banning states estimates
the relative impact of non-MLA related factors on outcome variables across treatment
groups and across time. This difference-in-difference can be differenced from the original
difference-in-difference estimate to construct a more robust measure of the impact of pay-
day loan access on outcome variables of interest. This difference-in-difference-in-difference
is measured by the δ coefficient in the following specification:
Yit = φt + θs + ξi + δMilitaryi + βAccessi × PreBant + ρAccessi ×Militaryi +
ηPreBant ×Militaryi + γAccessi × PreBant ×Militaryi + εit (14)
where all variables are the same as above and Military is a dummy variable that is equal
to 1 if household i is a “military” household.
I define “military” households as households who have a main earner who is also a
member of the armed forces. These are households that have a high probability of being
covered under the MLA. All military household respondents are kept in the sample. In
order to select civilian households that resemble military households, I create a propensity
score for each household that measures the likelihood of being a military household based
on age, education level, race and sex of main earner, family size, number of children, family
type, state of residence, population of primary sampling unit and whether residence is in
an urban or rural setting. I selected civilian households who had propensity scores in the
60Some payday loan allowing states ban payday loans after the MLA becomes effective but before ourstudy period ends. I do not presently account for this in my calculations.
78
98th percentile. A comparison of the characteristics of the selected civilian households and
the military households from the Consumer Expenditure Survey are presented in Table
19. We see that despite using this method, there are some differences between civilian
and military populations. The main earners of selected civilian households tend to be
younger, less educated, have a higher probability of being male, a minority and living in
a less populous location than those of military households in the sample.
Finally, to see if young households are impacted differently than older households
by access to payday loans, I will also present estimates of the difference-in-difference-in-
difference coefficient interacted with a dummy variable, Y oung, that is equal to 1 if the
main household earner is younger than 28 years old.61 This measure is estimated by the
following specification:
Yit = φt + θs + ξi + δMilitaryi + βAccessi × PreBant +
ρAccessi ×Militaryi + ηPreBant ×Militaryi + νAccessi × Y oungi +
ϑPreBant × Y oungi + %Militaryi × Y oungi +
γAccessi × PreBant ×Militaryi + ςAccessi × PreBant × Y oungi +
τAccessi ×Militaryi × Y oungi + υPreBant ×Militaryi × Y oungi +
ϕAccessi × PreBant ×Militaryi × Y oungi + εit (15)
where all variables are previously defined.
61The mean age of active duty personnel according to the 2007 Department of Defense Demographicsreport.
79
3.4 Results
3.4.1 Expenditure Behavior
Household respondents in the Consumer Expenditure Survey are interviewed quarterly
about their monthly spending in the three months preceding the interview month. I
average the reported monthly spending per interview quarter per household as to minimize
serial correlation between monthly responses within one interview.62 Standard errors in
the following analysis are clustered at the state level, the level of the policy change.
3.4.1.1 Intensive Margin I first look at total spending per household. Column 1 in
Table 20 presents the estimate of the difference-in-difference-in-difference estimate from
Equation 14 where the outcome variable is the natural logarithm of average monthly
spending of a household in an interview quarter. The estimate indicates that payday
loan access led households to cut their average spending by 20%. Given the number of
household respondents,63 results may be driven by outliers. Thus, I trim the top 5% and
the bottom 5% of average monthly spending observations and re-estimate the difference-
in-difference-in-difference coefficient. The estimate from the trimmed sample, presented in
Column 2 of Table 20, is indeed smaller in magnitude (9.8% monthly spending reduction)
and less significant than that found in the full sample. Columns 3 and 4 in Table 17
present the triple and quadruple difference-in-difference terms of interest from Equation
15 run on the full and trimmed samples respectively. Again we see a large difference in
results between the two samples. The trimmed sample estimates in Column 4 indicate
that payday loan access had little impact on the total spending of older households, but
had a large negative, though not significant at the 10% level, impact on total spending of
62Results do not change dramatically when non-averaged monthly spending is used.63714 military households and 794 civilian households.
80
younger households.
Table 21 presents the estimates of the impact of payday loan access on specific spend-
ing categories. Again, the outcome variable is the natural logarithm of average monthly
spending in a category by a household in an interview quarter. Thus, observations will
be dropped if there is no spending in the category in an interview quarter. Since outliers
do seem to have an impact, as shown in Table 20, observations in the top 5% or bottom
5% of average household monthly spending in each category are dropped. Three spending
categories have coefficient estimates with significance at the 10% level or less.64 House-
holds who spent money operating their vehicles by purchasing items such as gas reduced
this spending by 18.7% when they had access to payday loans. On the other hand house-
holds increased spending on utilities, both basic and luxury (e.g. cable and internet) by
18.7% and 25% respectively. To examine if these effects were concentrated in younger or
older households, I run specification 15 on the same data set and spending categories and
present the estimates of the coefficients of interest in Table 22. Younger households did
not significantly reduce spending on vehicle operation more so than older households as a
result of payday loan access. They also did not increase spending on luxury utilities more
so than older households. However I do find that young households significantly increased
their spending on basic utilities as compared to older households when they had access to
payday loans. These young households seem to drive the basic utilities spending results
found in Table 21.65 I also find signs that younger households spent more on eating out
and doing home repairs than did older households when they had access to payday loans.
64The significance level is actually higher due to the testing of multiple categories. However, given thelow sample size, finding results with a lot of power is difficult with this data set.
65Evidence of payday loans being used for regular expenses, such as utilities, can be found in a surveyconducted by the Pew Charitable Trusts (2013).
81
3.4.1.2 Extensive Margin I now turn to analyzing whether payday loan access
caused households to start or stop spending in a given spending category. Table 23 & 24
present equivalent analysis to Tables 21 & 22 but with a binary variable corresponding
to any spending in a given category in the interview quarter as the outcome variable.
Results are presented for the trimmed sample where observations in the top and bottom
5% of average total monthly household spending are dropped. In Panel A of Table 23 we
see that payday loan access again had an impact on spending on vehicles. The probability
of spending on vehicle access (e.g. car payments and interest on car financing) drops by
32.5 percentage points. Potentially households are choosing not to make car purchases.
Furthermore, payday loan access leads to a 3.9 percentage point drop in the probability
of spending on vehicle operation. Thus some households stopped using vehicles when
they had access to short-term credit. Correspondingly, we do see, in Panel D, that the
probability of using public transportation increased with payday loan access, though not
significantly. Payday loan access also decreases the probability of paying alimony and
child support by 14 percentage points. On the other hand payday loan access increased
the probability of purchasing electronics by 19.7 percentage points. This is in line with
the findings in Zaki (2014). Households were also more likely to purchase goods for their
home (e.g. appliances, dinnerware, furniture, etc.) when they had access to payday loans.
As far as lodging, payday loan access led to a large decrease in the probability of spending
related to owning a home and an increase in the probability of spending on renting a home.
The probability of home maintenance spending and mortgage spending decreased by 28.3
and 21.2 percentage points respectively. The probability of spending on rent increased
by 29 percentage points. The probability of spending on any lodging did not change as
a result of payday loan access. Thus, there are signs that payday loan access increases
82
the probability of living in a rented unit rather than owning a home. This complements
the result in the Pew Charitable Trusts 2012 study that found that renters are 57% more
likely to use payday loans than home owners. I will present further evidence of this lodging
story in the next section.
We see in Table 24 older and younger households were not significantly impacted
differently by access to payday loans except in electronics and banking and credit spending.
Payday loan access increased the probability of young households purchasing electronics by
26 percentage points more than it did for older households. Payday loan access decreased
the likelihood of young households paying bank and credit fees by 42 percentage points
more than it did for older households. In fact, it seems that payday loans increased
the likelihood of older households paying bank and credit fees by 18 percentage points.
Potentially payday loans are substituting for other forms of credit for young households.
3.4.1.3 Vehicles and Lodging In Tables 21 through 24 we saw indications that
payday loan access led to a decrease in spending on vehicles and owned lodging and an
increase in spending on rented lodging. To further examine these findings, I analyze the
effect of payday loan access on the number of owned vehicles by households and the type
of lodging that households reside in. Respondents of the Consumer Expenditure Survey
report these two variables at each interview. Vehicles include cars, trucks and vans. Types
of lodging are owned homes, rented lodging, student housing and housing with no pay.
The outcome variables I use for this section are the number of owned vehicles by household
and a dummy variable that is equal to 1 if the household rents their lodging. Estimates
of relevant coefficients in Specification 14 and 15 are presented in Table 25. We see in
Column 1 that the magnitude of the estimate of the difference-in-difference-in-difference
is negative, indicating that short-term credit access led to the presence of fewer owned
83
cars per household. However, the result is not statistically significant at the 10% level.
Column 2 indicates that younger households were more prone to reducing their number
of owned vehicles than older households were when they had access to payday loans.
Again, this result is not statistically significant. On the other hand Columns 3 and 4
indicate that there was a significant substitution of other types of housing with rented
housing when people have access to payday loans. The probability of living in a rented
home increased by 26 percentage points with access to payday loans and this effect was
of similar magnitude for older and younger households.
3.4.2 Labor Force Behavior
The Current Population Survey only reports labor statistics of civilians within a house-
hold. Thus, labor outcomes between civilians in military households and civilians in
civilian households interviewed in the Current Population Survey are not comparable and
the triple difference-in-difference specification is inappropriate to use. In Panel A of Table
26 I estimate the effect of payday loan access on labor outcomes using the following two
specifications only on military household observations:
Laborit = φt + θs + ξi +UnemploymentRatest + βAccessi × PreBant + εit (16)
and
84
Laborit = φt + θs + ξi +UnemploymentRatest + βAccessi × PreBant +
δPreBant × Y oungi + πAccessi × Y oungi +
γAccessi × PreBant × Y oungi + εit (17)
where Labor is a labor force characteristic of household i on date t, UnemploymentRate
is the the unemployment rate of state s on date t and the rest of the variables are defined
previously. Panel A of Table 26 presents the estimates of β and γ coefficients in these
two specifications above where the outcome variables are number of civilian earners in a
household and total number of hours worked by civilians in a household per week. None
of the estimates are significantly different from zero.
I then redo the exercise above for military households in the Consumer Expenditure
Survey. Results are found in Panel B of Table 26. Again, I do not find any estimates
that are significant at the 10% level. However, I do find that the magnitudes of the
difference-in-difference estimates for young households are much larger and negative, with
the interpretation that payday loan access led young households to reduce their activity
in the labor force.
Finally, since the Consumer Expenditure Survey collects labor information from all
household members including those in the military, I am able to estimate the triple
difference-in-difference measure66 (Equations 14 and 15) for the total number of house-
hold earners and total number of hours worked in the household per week. Estimates of
this coefficient are found in Table 27. We see in Column 2 that the number of earners
in young households decreased by .47 people as compared to that of older households
66I also include the state unemployment rate in these estimates.
85
when households had access to payday loans. We also see that older households worked
11.8 hours more per week when they had access to payday loans and younger households
decreased the number of hours they worked per week by 15 hours.
It is unclear why there is such a discrepancy between the results of the two surveys.
To examine this further, I calculate the percent of civilian members in military households
that are earners to see if there is generally a large difference in labor activity between the
households from each survey. Results are found in Appendix Table 10 and are not too
revealing. The percentage of civilian earners in military households is the same in both
surveys. That statistic also trends in the same direction from the pre-ban period to the
post-ban period.
3.5 Discussion
Household and individual level data from the Consumer Expenditure Survey and the
Current Population survey allow me to isolate military households during the period before
and after the enactment of the Military Lending Act to examine the effects of payday
loan access. The biggest shortcoming of these data sources, especially the Consumer
Expenditure Survey, is small sample size that leads to low power in making inference and
greater susceptibility of outliers driving results. To combat the latter problem, I trim
the extreme observations. It is difficult to combat the former issue. However, to increase
accuracy in the measure of the impact of payday loan access, I include a sample of civilians
as a control group along with the control group of military households not affected by the
Military Lending Act.
Though, there are some indications from the results that payday loan access leads
households to change their consumption and labor force behavior, the results need to be
86
approached with caution. Firstly, though some coefficients are presented as being signif-
icant at the 10% level, this is somewhat misleading as I re-run the same tests numerous
times for each outcome variable. In 10% of the multiple comparisons, our coefficient of
interest will appear to be significant by chance. One way to adjust for this problem is to
apply the conservative Bonferroni correction. Taking this adjustment into account and
given the low sample size of the Consumer Expenditure Survey, almost no coefficient esti-
mate is found to be significant at the 10% level. Secondly, the magnitudes of the estimates
of interest that were found to be significant seem impossibly large. Not every household
interviewed actually uses payday loans or is using payday loans in the time period they are
being interviewed. Thus, the estimated effects of payday loan usage, rather than access,
would be amplified to an even bigger magnitude. Finally, there is a large discrepancy
between the labor force results derived from the Current Population Survey (which has
a larger military household sample) and from the Consumer Expenditure Survey. These
issues lead me to be skeptical of the validity of the identification strategy when combined
with the Consumer Expenditure Survey.
87
4 Figures and Tables
Figure 1: Commissary and Exchange Locations
88
Figure 2: Paycycle Sales Pattern
Panel A: Total
Panel B: Produce
Note: Data from post-ban period that spans October 1, 2007 thru September 30, 2010.
89
Figure 3: Difference between Average Log Daily Sales on Paydays and Average Log DailySales on Non-paydays Among Commissaries
Note: Log Sales are adjusted for store fixed effects as well as day of week, federal holidays, 3rd of MonthSocial Security days fixed effects before being averaged. The log of daily sales is for total store sales.A Commissary is designated to be “Near Payday Loan Shop” if there is at least one payday loan shopwithin a 10 miles of the store. The pre-ban period spans October 1 2005 thru September 30, 2005. Thepost-ban period spans October 1, 2007 thru September 30, 2010.
90
Figure 4: Impact of Payday Loan Access on the Timing of Consumption
Dependent Variable: Log Daily Total Sales
91
Figure 5: Difference between Average Log Daily Sales on Paydays and Average Log DailySales on Non-paydays Among Commissaries by Previous Paycycle Length
Dependent Variable: Log Daily Total Sales
Note: Analysis done only for 14 day long paycycles. The predicted estimation is based on observationsonly from 14 day long paycycles that are preceded by 14 through 17 day paycycles. All observations(whether predicted or actual) control for store and paycycle fixed effects as well as day of week, federalholidays, Social Security payout days and early paycheck days fixed effects. The log of daily sales is fortotal store sales. Data is from post-ban period that spans October 1, 2007 thru September 30, 2010.
92
Tab
le1:
Sto
reSta
tist
ics
Panel
A:
Com
mis
sari
es
Sta
teA
llow
sSta
teD
oes
Not
Allow
Nea
rShop
Not
Nea
rShop
All
Num
ber
ofC
omm
issa
ries
140
39
130
49
179
Num
ber
ofSta
tes
38
939
17
47
Mea
n#
ofP
LSh
ops
wit
hin
10M
iles
33
0.5
35.7
025
Ave
rage
Dai
lyS
ales
(Pos
t-ban
)$89,7
18
$75,3
60
$96,8
93
$57,0
71
$86,7
58
Panel
A:
Exch
anges
Sta
teA
llow
sSta
teD
oes
Not
Allow
Nea
rShop
Not
Nea
rShop
All
Num
ber
ofC
omm
issa
ries
60
14
59
15
74
Num
ber
ofSta
tes
29
730
936
Mea
n#
ofP
LSh
ops
wit
hin
10M
iles
39.1
1.4
40.1
032.7
Ave
rage
Mon
thly
Sal
es(P
ost-
ban
)$3,3
69,3
97
$3,9
38,3
58
$3,5
39,1
36
$3,2
32,7
90
$3,4
77,0
39
Not
e:“S
tate
Allow
s”in
dic
ates
that
itis
lega
lfo
ra
pay
day
loan
shop
toop
erate
inth
est
ate
.H
avin
g“N
ear
Shop”
isd
efined
as
aC
omm
issa
ryb
ein
gw
ithin
10m
iles
ofat
leas
ton
ep
ayday
loan
shop
.E
xch
ange
data
on
lyav
ailable
from
Arm
yand
Air
Forc
em
ilit
ary
inst
allm
ents
.
93
Table 2: Payday Spending Given Previous Paycycle Length
Dependent Variable: Log Daily Sales
Panel A: All Paycycles
Product Category
Total Produce MeatPayday x PreviousPaycycleLength 0.0259∗∗∗ 0.0219∗∗∗ 0.0398∗∗∗
(0.0015) (0.0014) (0.0022)N 170325 167182 162732
Panel B: 14 Day Paycycles
Product Category
Total Produce MeatPayday x PreviousPaycycleLength 0.0395∗∗∗ 0.0349∗∗∗ 0.0548∗∗∗
(0.0018) (0.0014) (0.0025)N 74382 73002 71061
Note: Table presents the estimates of the γ coefficients in the following regression:
LogSalesit = α + φt + θi + βPaydayt + γPaydayt × PreviousPaycycleLengtht + εitwhere LogSales is the natural logarithm of daily sales of a product category for Commissary store i ondate t; φ are controls for time (specifically: day of week, federal holidays, Social Security payout days;early paycheck days and paycycle indicator variables); θ are store fixed effects; Payday is a dummyvariable equal to 1 if t is a payday and PreviousPaycycleLength is the number of days in the paycycleprevious to the paycycle of date t. Errors are clustered at the state level and are in parentheses. Salesare from the post-ban period of October 1, 2007 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
94
Table 3: The Impact of Payday Loan Access on the Timing of Consumption
Dependent Variable: Log Total Daily Sales
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday 0.2070∗∗∗ 0.1890∗∗∗ 0.2210∗∗∗
(0.0249) (0.0226) (0.0285)
Payday x PreBan 0.0062 0.0003 0.0317∗∗
(0.0100) (0.0080) (0.0153)
Payday x NearShop 0.0074 -0.0083 0.0247(0.0245) (0.0226) (0.0277)
Payday x NearShop x PreBan -0.0187∗ -0.0019 -0.0382∗∗
(0.0111) (0.0095) (0.0170)N 283731 160550 123181
Note: Table presents the estimates of the β, γ, δ and ρ coefficients in the following triple difference-in-difference specification:
LogSalesit = α+βPaydayt+γPaydayt×PreBant+δPaydayt×NearShopi+ρPaydayt×NearShopi×PreBant + ηUnemploytmentRateit + φt + θi + ξit + εitwhere LogSales is the natural logarithm of daily total sales for Commissary store i on date t; Payday isa dummy variable equal to 1 if t is on payday; PreBan is a dummy equal to 1 if t is in the pre-regulationperiod of October 1, 2005 thru September 30, 2007; NearShop is a dummy equal to 1 if there exists atleast 1 payday loan shop within a 10 mile radius of the Commissary; UnemploymentRate is the monthlyunemployment rate in Commissary i’s county; φ are controls for time (specifically: day of week, federalholidays, Social Security payout days, early paycheck days and paycycle indicator variables); θ are storefixed effects; ξ are all the interaction terms between day of week indicator variables and NearShop andPreBan and ε is an error term. Errors are clustered at the state level and are in parentheses. Sales arefrom the period of October 1, 2005 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
95
Table 4: The Impact of Payday Loan Access on the Timing of Consumption
Dependent Variable: Log Daily Sales
Panel A: Produce
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x NearShop x PreBan -0.0172 -0.0003 -0.0377∗∗
(0.0109) (0.0100) (0.0144)N 278503 157596 120907
Panel B: Meat
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x NearShop x PreBan -0.0162 -0.0022 -0.0303∗∗
(0.0116) (0.0115) (0.0147)N 271160 153453 117707
Note: Table presents the estimates of the ρ coefficients in the following triple difference-in-differencespecification:
LogSalesit = α+βPaydayt+γPaydayt×PreBant+δPaydayt×NearShopi+ρPaydayt×NearShopi×PreBant + ηUnemploytmentRateit + φt + θi + ξit + εitwhere LogSales is the natural logarithm of daily product category sales for Commissary store i on date t;Payday is a dummy variable equal to 1 if t is on payday; PreBan is a dummy equal to 1 if t is in the pre-regulation period of October 1, 2005 thru September 30, 2007; NearShop is a dummy equal to 1 if thereexists at least 1 payday loan shop within a 10 mile radius of the Commissary; UnemploymentRate is themonthly unemployment rate in Commissary i’s county; φ are controls for time (specifically: day of week,federal holidays, Social Security payout days, early paycheck days and paycycle indicator variables); θ arestore fixed effects; ξ are all the interaction terms between day of week indicator variables and NearShopand PreBan and ε is an error term. Errors are clustered at the state level and are in parentheses. Salesare from the period of October 1, 2005 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
96
Table 5: The Impact of Payday Loan Access on the Level of Consumption
Dependent Variable: Log Total Monthly Sales
Panel A: All Commissaries
AccessState Allow Near Shop Number of Shops
PreBan x Access 0.0005 0.0042 -0.0003(0.0156) (0.0172) (0.0013)
N 9720 9720 9720
Panel B: Commissaries at Same Bases as Available Exchanges
AccessState Allow Near Shop Number of Shops
PreBan x Access -0.0081 -0.0035 -0.0009(0.0118) (0.0129) (0.0012)
N 4140 4140 4140
Panel C: Exchanges
AccessState Allow Near Shop Number of Shops
PreBan x Access 0.0609∗∗ 0.0613∗∗ 0.0065∗∗
(0.0246) (0.0247) (0.0026)N 4200 4200 4200
Note: Table presents the estimates of the β coefficients in the following regression:
LogSalesit = α + βPreBant ×Accessi + γLogPopulationit + ηUnemploytmentRateit + φt + θi + εitwhere LogSales is the natural logarithm of total monthly sales for store i in month-year t; LogPopulationis the natural logarithm of the population of the nearest bases(s) to store i in month-year t;UnemploymentRate is the monthly unemployment rate in Commissary i’s county; PreBan is a dummyequal to 1 if t is in the pre-regulation period of October 2005 thru September 2007; φ are month-yearfixed effects; θ are store fixed effects and ε is an error term. Access is one of three measures indicatingaccess to payday loans. Specifically, “State Allow” is a dummy equal to 1 if Commissary is located in astate that allows payday loans, “Near Shop” is a dummy equal to 1 if there exists at least 1 payday loanshop within its 10 mile radius and “Number of Shops” is the number of payday loan shops within a 10 mileradius of the Commissary top coded at 10 shops. Stores that could not be matched to base populationdata were dropped. Furthermore, stores with structural changes (e.g. an opening of a new store facility)or that were affected by Hurricane Katrina were dropped. Total sales in Exchanges used here are thesum of sales in the product categories that are present in all stores (See Table 1 in Appendix). Errorsare clustered at the state level and are in parentheses. Sales are for the period of October 2005 thruSeptember 2010.*p<0.1, **p<0.05, ***p<0.01
97
Tab
le6:
The
Impac
tof
Pay
day
Loa
nA
cces
son
the
Com
pos
itio
nof
Con
sum
pti
on
Dep
enden
tV
aria
ble
:L
ogT
otal
Mon
thly
Sal
es
Pan
elA
:A
llC
omm
issa
ries
Gro
cery
Pro
duce
Mea
tN
earS
hop
xP
reB
an0.
0082
0.00
39-0
.018
3(0
.018
2)(0
.020
1)(0
.024
5)N
9420
9420
9420
Pan
elB
:E
xch
ange
s
Ele
ctro
nic
sA
lcoh
olL
uxury
Tob
acco
Com
mis
sary
-Lik
eN
earS
hop
xP
reB
an0.
0793
∗∗∗
0.07
76∗∗
0.03
65∗
0.05
070.
0364
(0.0
250)
(0.0
288)
(0.0
200)
(0.0
312)
(0.0
291)
N42
0042
0042
0042
0042
00
Clo
thin
gU
nif
orm
sE
nte
rtai
nm
ent
Hom
eA
pplian
ces
Oth
erN
earS
hop
xP
reB
an0.
0177
-0.0
253
0.00
080.
0492
0.04
460.
0435
(0.0
386)
(0.0
331)
(0.0
426)
(0.0
373)
(0.0
524)
(0.0
316)
N42
0042
0042
0042
0042
0042
00
Not
e:T
able
pre
sents
the
esti
mat
esof
theβ
coeffi
cien
tsin
the
follow
ing
regre
ssio
n:
LogSales i
t=α+βNearShop
i×PreBant+γLogPopulation
it+ηUnem
ploytmentRate
it+φt+θ i+ε it
wher
eLogSales
isth
enat
ura
llo
gari
thm
ofm
onth
lysa
les
ina
giv
enp
rodu
ctca
tegory
for
storei
inm
onth
-yea
rt;LogPopulation
isth
enat
ura
llo
gari
thm
ofth
ep
opula
tion
of
the
nea
rest
base
s(s)
tost
orei
inm
onth
-yea
rt;Unem
ploymentRate
isth
em
onth
lyun
emplo
ym
ent
rate
inC
omm
issa
ryi’
sco
unty
;PreBan
isa
du
mm
yeq
ual
to1
ift
isin
the
pre
-reg
ula
tion
per
iod
of
Oct
ob
er2005
thru
Sep
tem
ber
2007
;φ
are
mon
th-y
ear
fixed
effec
ts;θ
are
store
fixed
effec
tsandε
isan
erro
rte
rm.NearShop
isa
dum
my
equal
to1
ifth
ere
exis
tsat
leas
t1
pay
day
loan
shop
wit
hin
a10
mile
rad
ius
of
storei.
Sto
res
that
could
not
be
matc
hed
tobase
pop
ula
tion
data
wer
edro
pp
ed.
Furt
her
mor
e,st
ores
that
wer
eaff
ecte
dby
Hurr
ican
eK
atr
ina
wer
edro
pp
ed.
Err
ors
are
clu
ster
edat
the
state
leve
land
are
inp
aren
thes
es.
Sal
esar
efo
rth
ep
erio
dof
Oct
ob
er2005
thru
Sep
tem
ber
2010.
*p<
0.1,
**p<
0.05
,**
*p<
0.01
98
Table 7: Robustness: Impact of Payday Loan Access on the Timing of Consumption,Omitting 10/2006-9/2008
Dependent Variable: Log Daily Sales
All 14 Days or Less >14 DaysPayday x NearShop x PreBan -0.0184 -0.0061 -0.0311∗
(0.0129) (0.0120) (0.0170)N 169882 91206 78676
Note: Table presents the estimates of the ρ coefficients in the following triple difference-in-differencespecification:
LogSalesit = α+βPaydayt+γPaydayt×PreBant+δPaydayt×NearShopi+ρPaydayt×NearShopi×PreBant + ηUnemploytmentRateit + φt + θi + ξit + εitwhere LogSales is the natural logarithm of daily total sales for Commissary store i on date t; Payday isa dummy variable equal to 1 if t is on payday; PreBan is a dummy equal to 1 if t is in the pre-regulationperiod of October 1, 2005 thru September 30, 2007; NearShop is a dummy equal to 1 if there exists atleast 1 payday loan shop within a 10 mile radius of the Commissary; UnemploymentRate is the monthlyunemployment rate in Commissary i’s county; φ are controls for time (specifically: day of week, federalholidays, Social Security payout days, early paycheck days and paycycle indicator variables); θ are storefixed effects; ξ are all the interaction terms between day of week indicator variables and NearShop andPreBan and ε is an error term. Errors are clustered at the state level and are in parentheses. Sales arefrom the period of October 1, 2005 thru September 28, 2006 and October 1, 2008 September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
99
Table 8: Robustness: The Impact of Payday Loan Access on the Timing of ConsumptionUsing Propensity Score Matching
Dependent Variable: Log Daily Sales
All 14 Days or Less >14 DaysTriple Difference-in-Difference -0.0286∗ -0.0131 -0.0434∗∗
(0.0158) (0.0167) (0.0186)
Note: Table presents the triple difference-in-difference matching estimator. All Commissaries that haveat least 1 payday loan shop within their 10 mile radius are in the sample and are considered the treatedgroup (D = 1). Each of these Commissaries is matched to a Commissary that does not have any paydayloan shops within its 10 mile radius using nearest neighbor propensity score matching with replacementand considered the untreated group (D = 0). The estimates are calculated as follows:
△DID
D=1 =1
x1∑
{Di=1}
⎡⎢⎢⎢⎢⎢⎣
⎧⎪⎪⎪⎨⎪⎪⎪⎩
⎛⎝
1
xtn∑Y1ibb∈At
n
− 1
xtp∑Y1icc∈At
p
⎞⎠−⎛⎜⎝
1
xtn∑Y0m(i)d
d∈Atn
− 1
xtp∑Y0m(i)e
e∈Atp
⎞⎟⎠
⎫⎪⎪⎪⎬⎪⎪⎪⎭
−⎧⎪⎪⎪⎨⎪⎪⎪⎩
⎛⎜⎝
1
xt′
n
∑Y0iff∈At
′
n
− 1
xt′
p
∑Y0igg∈At
′
p
⎞⎟⎠−⎛⎜⎝
1
xt′
n
∑Y0m(i)hh∈At
′
n
− 1
xt′
p
∑Y0m(i)jj∈At
′
p
⎞⎟⎠
⎫⎪⎪⎪⎬⎪⎪⎪⎭
⎤⎥⎥⎥⎥⎥⎦
where i is indexing Commissaries; subscript n indicates non-paydays; subscript p indicates paydays;superscript t indicates the pre-regulation period of October 1, 2005 thru September 30, 2007; superscriptt′
indicates the post-regulation period of October 1, 2007-September 30, 2010; a subscript of 1 indicatestreatment (being in a state that allows payday loans); a subscript of 0 indicates no treatment; A is a setof dates; x is the quantity of members in the indicated set; Y is log total daily sales; and m(i) is theindexing of a Commissary that is the nearest neighbor propensity score match to store i. m(i) is suchthat Dm(i) = 0. The interpretation of the presented estimates are treatment effect on the treated. Errorsare bootstrapped. Sales are from the period of October 1, 2005 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
100
Table 9: Robustness: Impact of Payday Loan Access on the Timing of Consumption,Omitting Car Title Loan Allowing States
Dependent Variable: Log Daily Sales
All 14 Days or Less >14 DaysPayday x NearShop x PreBan -0.0340∗∗∗ -0.0240∗ -0.0462∗∗∗
(0.0121) (0.0132) (0.0158)N 121884 68991 52893
Note: Table presents the estimates of the ρ coefficients in the following triple difference-in-differencespecification:
LogSalesit = α+βPaydayt+γPaydayt×PreBant+δPaydayt×NearShopi+ρPaydayt×NearShopi×PreBant + ηUnemploytmentRateit + φt + θi + ξit + εitwhere LogSales is the natural logarithm of daily total sales for Commissary store i on date t; Payday isa dummy variable equal to 1 if t is on payday; PreBan is a dummy equal to 1 if t is in the pre-regulationperiod of October 1, 2005 thru September 30, 2007; NearShop is a dummy equal to 1 if there exists atleast 1 payday loan shop within a 10 mile radius of the Commissary; UnemploymentRate is the monthlyunemployment rate in Commissary i’s county; φ are controls for time (specifically: day of week, federalholidays, Social Security payout days, early paycheck days and paycycle indicator variables); θ are storefixed effects; ξ are all the interaction terms between day of week indicator variables and NearShop andPreBan and ε is an error term. Errors are clustered at the state level and are in parentheses. Sales arefrom the period of October 1, 2005 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
101
Table 10: Experimental Design Setup
LocationCafeteria Classroom
Treatment A BControl A’ B’
102
Tab
le11
:B
asel
ine
Sum
mar
ySta
tist
ics
Any
Univ
ers
al
Sch
ool
Bre
akfa
stB
ICO
nly
Cafe
teri
aO
nly
Contr
ol
Tre
atm
ent
p-v
alu
eN
Contr
ol
Tre
atm
ent
p-v
alu
eN
Contr
ol
Tre
atm
ent
p-v
alu
eN
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
(9)
(10)
(11)
(12)
Stu
dent-level
chara
cteristics
Eligi
ble
for
Fre
eor
Red
uce
dL
un
ch0.
540.
54
0.3
943
58
0.61
0.58
0.0
210
540.
510.5
20.
9733
39
Eligi
ble
for
Fre
eL
unch
0.37
0.37
0.20
435
80.4
50.3
90.
00105
40.
340.
360.
80
3339
Inco
me<
$20K
0.19
0.1
80.1
83278
0.2
00.
18
0.1
078
30.1
80.
180.
6025
21B
lack
0.10
0.09
0.2
14169
0.1
00.1
00.
73103
50.
10
0.08
0.1
631
67N
on-w
hit
e0.
390.3
90.
62
4169
0.37
0.35
0.1
410
35
0.40
0.41
0.96
3167
Fem
ale
0.51
0.52
0.3
14358
0.5
30.
52
0.6
0105
40.
510.
530.
1633
39Sin
gle
Par
ent
Hou
seh
old
0.24
0.25
0.7
0342
30.
220.
230.
64
809
0.25
0.26
0.8
426
40A
ge(y
ears
)9.
89.
80.
29
4358
9.9
9.9
0.62
1054
9.8
9.8
0.2
933
39
SB
PP
arti
cip
atio
n(%
ofd
ays)
-B
ase
Yea
r16
.26
16.
36
0.4
833
80
21.5
522
.80
0.54
939
14.4
213
.83
0.17
2475
School-level
chara
cteristics
%E
ligi
ble
for
Fre
eor
Red
uce
dL
un
ch-
Bas
eY
ear
45.6
45.6
0.8
1151
54.4
54.7
0.73
3742
.242
.90.
9611
7
%E
ligi
ble
for
Fre
eor
Red
uce
dL
un
ch-
Yea
r1
46.2
45.2
0.2
0153
55.1
52.9
0.19
3842
.442
.90.
6311
9
%M
inor
ity
Stu
den
ts-
Bas
eY
ear
32.6
33.8
0.9
0153
33.4
29.1
0.11
3831
.735
.20.
4611
9
Sch
ool
size
-B
ase
Yea
r50
747
10.
15
151
646
550
0.20
37481
447
0.30
117
Not
es:
P-v
alu
esre
pre
sent
ate
stfo
rw
het
her
the
row
vari
ab
leis
diff
eren
tin
the
trea
tmen
tgro
up
than
the
contr
olgro
up
,aft
erco
ndit
ionin
gon
random
izat
ion
pool
fixed
effec
ts.
103
Tab
le12
:E
ffec
tof
Sch
ool
Bre
akfa
stP
rogr
amon
Fir
st-Y
ear
Par
tici
pat
ion
and
Nutr
itio
n,
by
Typ
eof
Pro
gram
Any
Univ
ers
al
Sch
ool
Bre
akfa
stB
ICO
nly
Cafe
teri
aO
nly
Contr
ol
gro
up
mean
Impact
NC
ontr
ol
gro
up
mean
Impact
NC
ontr
ol
gro
up
mean
Impact
N
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
(9)
SB
PP
arti
cipat
ion
(%of
day
s)21
.69
18.4
4***
3380
26.2
937.
86***
939
20.0
110.5
0***
2475
(1.
58)
(2.1
8)(
1.1
5)
Usu
ally
par
tici
pat
e(>
=75
%of
day
s)0.
08
0.13*
**
3380
0.1
20.2
9***
939
0.07
0.06**
*247
5(
0.02
)(
0.0
4)(
0.0
1)
Ate
Any
Bre
akfa
st0.
96
0.0
04278
0.96
0.0
2*104
80.9
6-0
.00
326
5(
0.00
)(
0.0
1)(
0.0
1)
Ate
Nutr
itio
nal
lySubst
anti
ve
Bre
akfa
st0.5
90.
03**
4278
0.6
00.
10***
1048
0.59
0.0
1326
5(
0.01
)(
0.0
2)(
0.0
1)
Ate
2Subst
anti
veB
reakfa
sts
0.02
0.0
1**
*427
80.
02
0.0
5**
*104
80.0
2-0
.00
3265
(0.
00)
(0.0
1)(
0.0
0)
Eats
Bre
akfa
stO
uts
ide
ofSch
ool
Only
0.69
-0.2
1***
427
80.6
4-0
.45***
1048
0.7
0-0
.13***
3265
(0.
02)
(0.0
3)(
0.0
1)
Bre
akfa
st:
Tot
alE
ner
gy(%
RD
A)
20.
58
0.3
742
78
20.
671.
70**
1048
20.5
7-0
.10
3265
(0.
32)
(0.7
8)(
0.3
2)
Bre
akfa
st:
Mic
ronutr
ient
Index
0.00
0.0
24278
-0.0
90.0
310
48
0.0
30.0
13265
(0.
02)
(0.0
5)(
0.0
2)
24
Hour:
Tota
lE
ner
gy(%
RD
A)
101.9
4-1
.15
3347
103.
32
-2.0
080
310
1.6
5-1
.16
257
0(
0.81
)(
1.8
6)(
0.9
0)
24
Hour:
Mic
ronutr
ient
Index
-0.0
00.0
033
47
-0.0
7-0
.04
803
0.0
20.0
12570
(0.
02)
(0.0
4)(
0.0
2)
Food
Inse
cure
0.2
3-0
.01
337
50.
26
-0.0
2809
0.2
2-0
.00
2592
(0.
01)
(0.0
2)(
0.0
1)
Not
es:
Sta
ndar
der
rors
(clu
ster
edat
the
sch
ool
level
)are
inpare
nth
eses
.A
llre
gre
ssio
ns
contr
ol
for
random
izati
on
-pool
fixed
effec
tsan
dth
efo
llow
ing
cova
riat
es:
free
and
red
uce
dlu
nch
elig
ibilit
y,house
hold
inco
me,
race
,si
ngle
pare
nt
house
hold
,gen
der
an
dage.
Defi
nit
ions
ofb
reak
fast
are
asfo
llow
s:an
ybre
akfa
stis
defi
ned
as
consu
mpti
on
of
any
calo
ries
bet
wee
n5:0
0a.m
.and
45
min
ute
saft
erth
est
art
ofsc
hool
,an
dal
soan
yfo
ods
con
sum
edb
efore
10:3
0a.m
.th
at
the
stu
den
t/pare
nt
rep
ort
edas
bei
ng
part
of
bre
akfa
ston
the
surv
eyd
ate.
Ach
ild
ate
anutr
itio
nal
lysu
bst
anti
vebre
akfa
stif
he
or
she
consu
med
food
from
at
least
2m
ain
food
gro
up
sand
>15
%of
calo
rie
RD
Adu
rin
gth
esa
me
bre
akfa
stti
me
per
iod.
Ach
ild
ate
2su
bst
anti
ve
bre
akfa
sts
ifhe
or
she
consu
med
anutr
itio
nally
subst
anti
veb
reak
fast
atsc
hool
asw
ell
asan
oth
ernutr
itio
nally
subst
anti
veb
reakfa
stat
anoth
erlo
cati
on
duri
ng
the
bre
akfa
stti
me
per
iod
.M
icro
nu
trie
nt
index
com
bin
esth
ein
take
as
ap
erce
nta
ge
of
RD
Afo
rth
efo
llow
ing:
Vit
am
ins
A,
B-6
,B
-12,
C,
rib
oflav
in,
fola
te,
calc
ium
,ir
on,
mag
nes
ium
,an
dzi
nc.
104
Tab
le13
:E
ffec
tof
Sch
ool
Bre
akfa
stP
rogr
amon
Fir
st-Y
ear
Aca
dem
ic,
Beh
avio
ran
dH
ealt
hO
utc
omes
,by
Typ
eof
Pro
gram
Any
Univ
ers
al
Sch
ool
Bre
akfa
stB
ICO
nly
Cafe
teri
aO
nly
Contr
ol
gro
up
mean
Impact
NC
ontr
ol
gro
up
mean
Impact
NC
ontr
ol
gro
up
mean
Impact
N
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
(9)
Tes
tSco
reIn
dex
-0.0
1-0
.03*
257
2-0
.03
-0.0
555
4-0
.00
-0.0
220
24
(0.
02)
(0.
04)
(0.
02)
Att
endan
ce(%
ofday
s)95
.71
-0.2
2*367
895.
64-0
.52*
*88
995
.76
-0.1
828
13
(0.
11)
(0.
26)
(0.
12)
Tar
din
ess
(%of
day
s)2.
47-0
.34*
205
12.
370.
1144
52.5
1-0
.40*
1630
(0.
20)
(0.
42)
(0.
23)
Bad
Beh
avio
rIn
dex
-0.0
00.
00408
90.0
3-0
.04
998
-0.0
10.
0231
19
(0.
02)
(0.
04)
(0.
02)
Hea
lth
Index
-0.0
0-0
.02*
435
20.
03-0
.06*
1053
-0.0
1-0
.02
3334
(0.
01)
(0.
03)
(0.
01)
BM
Ip
erce
nti
lefo
rA
ge63
.35
1.18
*430
066.
130.7
610
4362
.67
1.12*
3292
(0.
63)
(1.
42)
(0.
68)
Ove
rwei
ght
0.18
-0.0
1430
00.
23-0
.04
1043
0.1
6-0
.00
3292
(0.
01)
(0.
02)
(0.
01)
Not
es:
Sta
ndar
der
rors
(clu
ster
edat
the
sch
oolle
vel)
are
inpare
nth
eses
.A
llre
gre
ssio
ns
contr
olfo
rra
ndom
izati
on-p
oolfi
xed
effec
tsand
the
follow
ing
cova
riat
es:
free
and
reduce
dlu
nch
elig
ibilit
y,hou
sehold
inco
me,
race
,si
ngle
pare
nt
house
hold
,gen
der
and
age.
Tes
tsc
ore
index
isth
eav
erag
eof
mat
han
dre
adin
gz-
score
s,st
andard
ized
by
sub
ject
an
dgra
de
base
don
the
poole
dco
ntr
ol
gro
up
.A
tten
dan
cean
dta
rdin
ess
ism
easu
red
asth
ep
erce
nt
ofto
talsc
hoold
ays.
Bad
beh
avio
rin
dex
conta
ins
15
teach
er-r
eport
edm
easu
res
of
the
stu
den
t’s
inab
ilit
yto
contr
olb
ehav
ior
and
focu
s.H
ealt
hin
dex
com
bin
esatt
endan
ce,
pare
nt-
rep
ort
edhea
lth
statu
s,and
ind
icato
rva
riable
sfo
rw
het
her
the
child
isov
erw
eigh
tor
has
any
par
ent-
rep
ort
edhea
lth
pro
ble
ms.
105
Tab
le14
:E
ffec
tof
Sch
ool
Bre
akfa
stP
rogr
amin
Subse
quen
tY
ears
Any
Univ
ers
al
Sch
ool
Bre
akfa
stB
ICO
nly
Cafe
teri
aO
nly
Contr
ol
gro
up
mean
Impact
NC
ontr
ol
gro
up
mean
Impact
NC
ontr
ol
gro
up
mean
Impact
N
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
(9)
Yea
r2
SB
PP
arti
cipat
ion
(%of
day
s)20.
9721
.38*
**
2459
26.0
041
.59*
**70
918
.97
12.
89**
*177
9(
1.79
)(
2.95)
(1.
39)
Tes
tSco
reIn
dex
-0.0
1-0
.05
1546
-0.0
90.
01341
0.01
-0.0
6*120
8(
0.03
)(
0.06)
(0.
03)
Att
endan
ce(%
ofday
s)95
.55
0.19
2696
95.
480.
0166
395
.61
0.17
2053
(0.
13)
(0.
34)
(0.
14)
Tar
din
ess
(%of
day
s)1.
75-0
.11
1511
0.98
0.37
*33
71.9
1-0
.20
1194
(0.
18)
(0.
21)
(0.
21)
Yea
r3
SB
PP
arti
cipat
ion
(%of
day
s)19.
4018
.08*
**
1679
22.6
736
.07*
**45
718
.16
11.
00**
*124
0(
1.85
)(
3.43)
(1.
48)
Tes
tSco
reIn
dex
-0.0
1-0
.00
1285
-0.0
1-0
.02
255
-0.0
10.
01
1030
(0.
04)
(0.
05)
(0.
04)
Att
endan
ce(%
ofday
s)95
.52
0.19
1827
94.
731.
00***
426
95.7
7-0
.04
1414
(0.
15)
(0.
34)
(0.
16)
Tar
din
ess
(%of
day
s)2.
12-0
.18
988
1.51
1.14
206
2.29
-0.4
279
5(
0.26
)(
0.87)
(0.
26)
Pooled
Outcomes:
Yea
rs1,2
and
3SB
PP
arti
cipat
ion
(%of
day
s)21.
3518
.68*
**
3380
25.5
038
.52*
**93
919
.82
10.
72**
*247
5(
1.53
)(
2.16)
(1.
04)
Tes
tSco
reIn
dex
-0.0
2-0
.02
2619
-0.0
7-0
.01
571
-0.0
0-0
.02
2054
(0.
02)
(0.
04)
(0.
02)
Att
endan
ce(%
ofday
s)95
.59
-0.0
837
1795
.49
-0.3
389
695
.65
-0.0
628
45
(0.
10)
(0.
25)
(0.
11)
Tar
din
ess
(%of
day
s)2.
23-0
.23
2064
1.76
0.42
*44
62.3
3-0
.33**
1642
(0.
14)
(0.
24)
(0.
16)
Not
es:
Sta
ndar
der
rors
(clu
ster
edat
the
sch
ool
level
)are
inpare
nth
eses
.A
llre
gre
ssio
ns
contr
ol
for
random
izati
on
-pool
fixed
effec
tsan
dth
efo
llow
ing
cova
riat
es:
free
and
red
uce
dlu
nch
elig
ibilit
y,h
ouse
hold
inco
me,
race
,si
ngle
pare
nt
house
hold
,gen
der
and
age.
106
Table 15: Effect of Breakfast in the Classroom Program, by Subgroup
A: Free-lunch eligible B: Free-lunch ineligibleControl group mean Impact N Control group mean Impact N
SBP Participation (% of days) 41.48 24.00*** 382 14.76 46.30*** 557( 2.60) ( 2.62)
Ate Nutritionally Substantive Breakfast 0.62 0.10*** 436 0.58 0.09*** 612( 0.04) ( 0.03)
Attendance (% of days) 95.17 -1.32*** 370 96.03 -0.14 519( 0.32) ( 0.32)
Health Index -0.03 -0.10** 438 0.08 -0.05 615( 0.04) ( 0.04)
Bad Behavior Index 0.16 -0.04 418 -0.08 -0.04 580( 0.06) ( 0.05)
Test Score Index -0.26 -0.04 214 0.14 -0.06 340( 0.07) ( 0.05)
C: Male D: FemaleControl group mean Impact N Control group mean Impact N
SBP Participation (% of days) 24.03 41.70*** 442 28.34 34.38*** 497( 2.19) ( 2.69)
Ate Nutritionally Substantive Breakfast 0.66 0.07** 498 0.55 0.11** 550( 0.03) ( 0.04)
Attendance (% of days) 95.80 -0.37 419 95.51 -0.58* 470( 0.30) ( 0.35)
Health Index 0.07 -0.03 502 0.00 -0.09* 551( 0.05) ( 0.05)
Bad Behavior Index 0.23 -0.02 475 -0.16 -0.05 523( 0.05) ( 0.05)
Test Score Index 0.03 -0.07 255 -0.08 -0.02 299( 0.06) ( 0.06)
E: Urban, High-Poverty School F: MinorityControl group mean Impact N Control group mean Impact N
SBP Participation (% of days) 27.30 37.74*** 206 34.80 31.21*** 314( 5.07) ( 3.33)
Ate Nutritionally Substantive Breakfast 0.63 0.17*** 225 0.66 0.08 374( 0.03) ( 0.05)
Attendance (% of days) 95.50 -0.90*** 203 95.83 -0.56* 314( 0.20) ( 0.32)
Health Index 0.02 -0.28*** 226 0.06 -0.18*** 374( 0.04) ( 0.04)
Bad Behavior Index 0.10 0.07 220 0.19 -0.18*** 354( 0.18) ( 0.07)
Test Score Index -0.19 -0.29*** 126 -0.17 -0.15** 197( 0.07) ( 0.07)
Notes: Outcomes reported for first year only.
107
Table 16: Difference-in-difference Analysis
Difference-in-difference Coefficient Estimate N(1) (2)
Year 1SBP Participation (% of days) 27.98*** 3380
( 2.47)Usually participate (>=75% of days) 0.24*** 3380
( 0.04)Ate Any Breakfast 0.02* 4278
( 0.01)Ate Nutritionally Substantive Breakfast 0.08*** 4278
( 0.03)Ate 2 Substantive Breakfasts 0.05*** 4278
( 0.01)Eats Breakfast Outside of School Only -0.30*** 4278
( 0.03)Breakfast: Total Energy (% RDA) 1.56* 4278
( 0.89)Breakfast: Micronutrient Index 0.00 4278
( 0.06)24 Hour: Total Energy (% RDA) -0.12 3347
( 1.91)24 Hour: Micronutrient Index -0.04 3347
( 0.04)Food Insecure -0.01 3375
( 0.02)Test Score Index -0.03 2477
( 0.04)Attendance (% of days) -0.29 3678
( 0.29)Tardiness (% of days) 0.47 2051
( 0.47)Bad Behavior Index -0.06 4089
( 0.04)Health Index -0.04 4352
( 0.03)BMI percentile for Age -0.01 4300
( 1.51)Overweight -0.03 4300
( 0.03)Year 2SBP Participation (% of days) 28.17*** 2459
( 3.21)Test Score Index 0.07 1504
( 0.07)Attendance (% of days) 0.02 2696
( 0.36)Tardiness (% of days) 0.49* 1511
( 0.27)Year 3SBP Participation (% of days) 24.83*** 1679
( 3.77)Test Score Index -0.08 1248
( 0.07)Attendance (% of days) 0.99*** 1827
( 0.37)Tardiness (% of days) 1.42* 988
( 0.74)Pooled Outcomes: Years 1, 2 and 3SBP Participation (% of days) 27.94*** 3380
( 2.28)Test Score Index 0.02 2516
( 0.04)Attendance (% of days) -0.17 3717
( 0.28)Tardiness (% of days) 0.69** 2064
( 0.29)
108
Table 17: Instrumental Variables Estimates of the Effect of Breakfast Consumption
Endogenous Variable:Ate Nutritionally
Substantive Breakfast
Endogenous Variable:Total Energy (%RDA)
Intake at BreakfastOLS IV N OLS IV N(1) (2) (3) (4) (5) (6)
FIRST STAGE 0.10*** 1.70**Instrument ( 0.02) ( 0.78)
F-statistic 16.53 4.79
SECOND STAGE24 Hour: Micronutrient Index 0.46*** -0.35 802 0.02*** -0.02 802
( 0.05) ( 0.39) ( 0.00) ( 0.03)24 Hour: Total Energy (% RDA) 15.58*** -17.11 802 0.99*** -1.19 802
( 2.09) (18.64) ( 0.09) ( 1.62)BMI percentile for Age 2.05 8.34 1039 -0.03 0.49 1039
( 2.00) (13.75) ( 0.09) ( 0.77)Overweight 0.04 -0.36 1039 -0.00 -0.02 1039
( 0.03) ( 0.25) ( 0.00) ( 0.02)Health Index 0.03 -0.65* 1047 -0.00 -0.04 1047
( 0.04) ( 0.34) ( 0.00) ( 0.03)Bad Behavior Index 0.02 -0.34 993 0.00 -0.02 993
( 0.05) ( 0.38) ( 0.00) ( 0.02)Attendance (% of days) 0.29 -6.64** 884 0.00 -0.40 884
( 0.30) ( 3.20) ( 0.01) ( 0.28)Test Score Index -0.03 -0.39 531 -0.00 -0.02 531
( 0.04) ( 0.47) ( 0.00) ( 0.02)
Notes: Instrumental variable is BIC treatment. Outcomes for first year only.
109
Tab
le18
:C
har
acte
rist
ics
ofM
ilit
ary
Mem
ber
s
CE
XC
PS
Fu
llM
ilit
ary
Forc
eA
llE
nlist
edO
ffice
rA
ge33.5
33.2
28.3
27.1
34.6
No.
ofC
hild
ren
0.8
1.1
0.9
..
Fam
ily
Siz
e2.7
3.4
2.4
..
Mal
e84.7
%91.8
%85.6
%85.8
%84.8
%H
usb
and/w
ife
H.H
.62.2
%90.2
%55.2
%52.3
%70.5
%M
inor
ity
23.9
%18.4
%35.9
%38.3
%23.6
%B
ach
elor
’sD
egre
eor
ab
ove
27.8
%30.7
%17.8
%4.4
%87.3
%
Sou
rce:
“CE
X”:
Con
sum
erE
xp
end
iture
Su
rvey
“CP
S”:
Curr
ent
Pop
ula
tion
Su
rvey
“Fu
llM
ilit
ary
For
ce”:
2007
Dem
ogra
ph
ics
Pro
file
of
the
Milit
ary
Com
mu
nit
y,D
epart
men
tof
Def
ense
Not
e:O
bse
rvat
ions
inth
efi
rst
two
colu
mns
are
collec
ted
for
the
per
iod
of
Oct
ob
er2005
thru
Sep
tem
ber
2010.
The
firs
tth
ree
row
spre
sent
mea
ns
ofth
egi
ven
char
acte
rist
ics
and
the
rem
ain
ing
row
sp
rese
nt
the
per
centa
ge
of
mem
ber
sw
ith
the
state
dch
ara
cter
isti
cs.
110
Tab
le19
:M
ean
ofH
ouse
hol
dM
ain
Ear
ner
Char
acte
rist
ics
AL
LP
reB
an
Post
Ban
Civ
ilia
nM
ilit
ary
p-v
alue
NC
ivilia
nM
ilit
ary
p-v
alue
NC
ivilia
nM
ilit
ary
p-v
alue
NA
ge29
.67
33.5
40.0
015
5329
.55
34.4
70.
0066
329
.76
32.9
10.
00890
No.
ofC
hild
ren
0.77
0.84
0.20
155
30.7
80.
860.
38
663
0.76
0.83
0.35
890
Fam
ily
Siz
e2.
602.
720.1
015
532.6
22.
740.
28
663
2.59
2.71
0.21
890
Mal
e0.
960.
850.
0015
530.9
70.
860.
00
663
0.96
0.84
0.00
890
Husb
./w
ife
H.H
.0.
650.
620.
3115
530.6
60.
630.
44
663
0.63
0.61
0.53
890
Wh
ite
0.71
0.76
0.04
155
30.7
10.
750.
24
663
0.72
0.77
0.08
890
>H
.S.
Deg
ree
0.34
0.40
0.0
3155
30.3
30.
400.
06
663
0.36
0.40
0.24
890
Loca
tion
:U
rban
1.00
0.99
0.4
515
530.9
90.
990.
39
663
1.00
1.00
.890
Loca
tion
:P
op.<
1.2
mil.
0.62
0.48
0.00
155
30.6
50.
530.
00
663
0.60
0.45
0.00
890
Sou
rce:
Con
sum
erE
xp
end
iture
Su
rvey
Not
e:F
ourt
hth
rough
nin
thro
ws
are
mea
ns
ofbin
ary
vari
able
s.C
ivilia
nco
unte
rpart
sto
surv
eym
ilit
ary
resp
ond
ents
are
chose
nac
cord
ing
toth
eir
pro
pen
sity
scor
eas
outl
ined
inth
epap
er.
111T
able
20:
Eff
ect
ofP
ayday
Loa
nA
cces
son
Tot
alSp
endin
g
Dep
enden
tV
aria
ble
:L
ogT
otal
Sp
endin
g
(1)
(2)
(3)
(4)
Pre
Ban
xA
cces
sx
Milit
ary
-0.1
99*
-0.0
98
-0.2
72*
0.0
34
(0.1
05)
(0.0
83)
(0.1
59)
(0.1
41)
Pre
Ban
xA
cces
sx
Milit
ary
xY
ou
ng
0.1
02
-0.3
09
(0.1
89)
(0.2
07)
Tri
mto
pan
db
otto
m5%
No
Yes
No
Yes
N3728
3356
3728
3356
Not
e:C
olum
n1
and
2p
rese
nt
the
esti
mat
eof
theγ
coeffi
cien
tin
the
follow
ing
regre
ssio
n:
LogSpending i
t=
φt+θ s+ξ i+δM
ilitary
i+βAccess i×PreBant+ρAccess i×Military
i+ηPreBant×Military
i+
γAccess i×PreBant×Military
i+ε it
and
Col
um
ns
3an
d4
pre
sent
the
esti
mat
esof
theγ
andϕ
coeffi
cien
tsin
the
follow
ing
regre
ssio
n:
LogSpending i
t=
φt+θ s+ξ i+δM
ilitary
i+βAccess i×PreBant+ρAccess i×Military
i+ηPreBant×Military
i+
νAccess i×Young i+ϑPreBant×Young i+%Military
i×Young i+γAccess i×PreBant×Military
i+
ςAccess i×PreBant×Young i+τAccess i×Military
i×Young i+υPreBant×Military
i×Young i+
ϕAccess i×PreBant×Military
i×Young i+ε it
wher
eLogSpending
isth
enat
ura
llo
gari
thm
of
tota
lav
erage
month
lysp
endin
gof
hou
seholdi
inin
terv
iew
qu
art
ert;φ
are
date
fixed
effec
ts;θ
are
stat
efi
xed
effec
ts;ξ
are
hou
sehol
dle
vel
cova
riate
s(s
pec
ifica
lly
indic
ato
rva
riable
sfo
rnum
ber
of
ad
ult
s,ch
ild
ren,
sen
iors
,m
emb
ers
and
contr
ols
for
husb
and
/wif
eunit
s,th
ep
rese
nce
of
at
least
one
house
hold
mem
ber
wit
ha
hig
hsc
hool
deg
ree
an
dth
eage
of
the
mai
nhou
sehol
din
com
eea
rner
);PreBan
isa
dum
my
vari
able
equ
al
to1
ift
isb
efore
Oct
ob
er2007;Access
isa
dum
my
vari
able
equal
to1
ifh
ouse
hol
di
lives
ina
stat
eth
at
allow
spay
day
loans
inth
eP
re-b
an
per
iod
;Young
isa
du
mm
yva
riable
equ
al
to1
ifth
em
ain
inco
me
earn
eris
28ye
ars
old
oryo
unge
randMilitary
isa
dum
my
vari
ab
leth
at
iseq
ual
to1
ifth
ehou
sehold
has
am
ain
earn
erw
ho
isin
the
arm
edfo
rces
.E
rror
sar
ecl
ust
ered
at
the
state
leve
land
are
inp
are
nth
eses
.D
ata
from
the
Consu
mer
Exp
endit
ure
Su
rvey
.D
ata
cove
rth
ep
erio
dof
Oct
ober
2005
thru
Sep
tem
ber
2010.
*p<
0.1,
**p<
0.05
,**
*p<
0.01
112T
able
21:
Eff
ect
ofP
ayday
Loa
nA
cces
son
Cat
egor
ySp
endin
g
Dep
enden
tV
aria
ble
:L
ogof
Cat
egor
ySp
endin
g
Panel
AV
ehic
le(A
cces
s)V
ehic
le(O
per
ati
ng)
Veh
icle
(All)
Food
(Aw
ay)
Food
(Hom
e)F
ood
(All)
Pre
Ban
xA
cces
sx
Milit
ary
0.07
0-0
.187*
-0.2
350.
194
-0.0
57
0.004
(0.1
96)
(0.1
02)
(0.1
83)
(0.2
13)
(0.1
09)
(0.1
24)
N19
33326
132
59299
333
3733
55
Panel
BH
ome
Goods
Hom
eM
ainte
nance
Uti
liti
es(B
asi
c)U
tiliti
es(L
uxury
)R
ent
Lodgi
ng
(All)
Pre
Ban
xA
cces
sx
Milit
ary
0.16
80.
344
0.1
87*
0.250
**
0.1
340.
043
(0.4
86)
(0.3
44)
(0.1
09)
(0.1
03)
(0.1
15)
(0.1
02)
N22
08174
833
10298
816
6333
49
Panel
CE
lect
ronic
sA
lcoh
olR
ecre
ati
onC
loth
ing
Giv
ing
Pre
Ban
xA
cces
sx
Milit
ary
-0.3
29-0
.308
0.0
050.
158
-0.0
54(0
.476
)(0
.316
)(0
.275
)(0
.341
)(0
.372
)
N18
22156
025
13279
015
04
Not
e:T
able
pre
sents
the
esti
mat
eof
theγ
coeffi
cien
tin
the
follow
ing
regre
ssio
n:
LogSpending i
t=
φt+θ s+ξ i+δM
ilitary
i+βAccess i×PreBant+ρAccess i×Military
i+ηPreBant×Military
i+
γAccess i×PreBant×Military
i+ε it
wher
eLogSpending
isth
en
atura
llo
gari
thm
of
aver
age
month
lysp
endin
gof
house
holdi
inin
terv
iew
quart
ert
ina
giv
enca
tegory
;φ
are
dat
efi
xed
effec
ts;θ
are
stat
efixed
effec
ts;ξ
are
house
hold
leve
lco
vari
ate
s(s
pec
ifica
lly
ind
icato
rva
riab
les
for
nu
mb
erof
adult
s,ch
ild
ren,
sen
iors
,m
emb
ers
and
contr
ols
for
hu
sband
/w
ife
un
its,
the
pre
sence
of
at
least
one
house
hold
mem
ber
wit
ha
hig
hsc
hool
deg
ree
and
the
age
ofth
em
ain
hou
sehol
din
com
eea
rner
);PreBan
isa
du
mm
yva
riable
equ
al
to1
ift
isb
efore
Oct
ob
er2007;Access
isa
du
mm
yva
riab
leeq
ual
to1
ifhou
sehol
di
lives
ina
state
that
allow
spay
day
loan
sin
the
Pre
-ban
per
iod
an
dMilitary
isa
du
mm
yva
riab
leth
atis
equal
to1
ifth
eh
ouse
hol
dh
as
am
ain
earn
erw
ho
isin
the
arm
edfo
rces
.E
rrors
are
clust
ered
at
the
state
leve
lan
dar
ein
par
enth
eses
.Sam
ple
istr
imm
edfo
rea
chca
tegory
by
dro
pp
ing
obse
rvati
ons
that
hav
eth
eto
p5%
an
dth
eb
ott
om
5%
of
valu
esof
aver
age
mon
thly
cate
gory
spen
din
g.C
ateg
orie
sw
ith
more
than
1,5
00
obse
rvati
on
saft
ertr
imm
ing
are
pre
sente
d.
Data
from
the
Con
sum
erE
xp
endit
ure
Su
rvey
.D
ata
cove
rth
ep
erio
dof
Oct
ob
er2005
thru
Sep
tem
ber
2010.
*p<
0.1,
**p<
0.05
,**
*p<
0.01
113
Table 22: Effect of Payday Loan Access on Category Spending
Dependent Variable: Log of Category Spending
Panel A Vehicle (Access) Vehicle (Operating) Vehicle (All) Food (Away) Food (Home) Food (All)PreBan x Access x Military 0.226 -0.156 -0.150 -0.048 0.049 0.023
(0.151) (0.230) (0.373) (0.184) (0.116) (0.103)
PreBan x Access x Military x Young -0.468 -0.070 -0.304 0.538* -0.145 0.016(0.320) (0.367) (0.473) (0.318) (0.109) (0.136)
N 1933 3261 3259 2993 3337 3355
Panel B Home Goods Home Maintenance Utilities (Basic) Utilities (Luxury) Rent Lodging (All)PreBan x Access x Military -0.049 -0.118 -0.047 0.207 0.050 0.048
(0.596) (0.331) (0.136) (0.140) (0.149) (0.190)
PreBan x Access x Military x Young 0.492 1.065* 0.582*** 0.018 0.102 0.010(0.642) (0.556) (0.160) (0.222) (0.240) (0.219)
N 2208 1748 3310 2988 1663 3349
Panel C Electronics Alcohol Recreation Clothing GivingPreBan x Access x Military -0.404 -0.405 0.088 0.305 -0.015
(0.676) (0.570) (0.544) (0.275) (0.582)
PreBan x Access x Military x Young -0.387 0.125 -0.573 -0.474 -0.197(0.879) (0.832) (0.624) (0.396) (0.932)
N 1822 1560 2513 2790 1504
Note: Table presents the estimates of the γ and ϕ coefficients in the following regression:
LogSpendingit = φt + θs + ξi + δMilitaryi + βAccessi × PreBant + ρAccessi ×Militaryi + ηPreBant×Militaryi + νAccessi × Y oungi + ϑPreBant × Y oungi + %Militaryi × Y oungi +γAccessi × PreBant ×Militaryi + ςAccessi × PreBant × Y oungi +τAccessi ×Militaryi × Y oungi + υPreBant ×Militaryi × Y oungi +ϕAccessi × PreBant ×Militaryi × Y oungi + εit
where LogSpending is the natural logarithm of average monthly spending of household i in interviewquarter t in a given category; φ are date fixed effects; θ are state fixed effects; ξ are household levelcovariates (specifically indicator variables for number of adults, children, seniors, members and controlsfor husband/wife units, the presence of at least one household member with a high school degree and theage of the main household income earner); PreBan is a dummy variable equal to 1 if t is before October2007; Access is a dummy variable equal to 1 if household i lives in a state that allows payday loans inthe Pre-ban period; Y oung is a dummy variable equal to 1 if the main income earner is 28 years old oryounger and Military is a dummy variable that is equal to 1 if the household has a main earner who isin the armed forces. Errors are clustered at the state level and are in parentheses. Sample is trimmedfor each category by dropping observations that have the top 5% and the bottom 5% of values of averagemonthly category spending. Categories with more than 1,500 observations after trimming are presented.Data from the Consumer Expenditure Survey. Data cover the period of October 2005 thru September2010.*p<0.1, **p<0.05, ***p<0.01
114
Tab
le23
:E
ffec
tof
Pay
day
Loa
nA
cces
son
Cat
egor
ySp
endin
g
Dep
enden
tV
aria
ble
:O
ccurr
ence
ofSp
endin
g
Panel
AV
ehic
le(A
cces
s)V
ehic
le(O
per
ati
ng)
Veh
icle
(All)
Food
(Aw
ay)
Food
(Hom
e)F
ood
(All)
Pre
Ban
xA
cces
sx
Milit
ary
-0.3
25**
*-0
.039**
-0.0
43**
-0.0
47
0.0
09
0.0
01
(0.1
10)
(0.0
17)
(0.0
18)
(0.0
78)
(0.0
34)
(0.0
01)
Panel
BC
hild
Car
eJew
eler
y/W
atc
hes
Clo
thin
gE
du
cati
on
Ele
ctro
nic
sL
ife
Insu
rance
Ch
ild
Sup
port
/A
lim
ony
Pre
Ban
xA
cces
sx
Milit
ary
0.02
00.0
50
0.0
04
0.0
540.1
97*
-0.0
52
-0.1
40***
(0.0
72)
(0.0
41)
(0.0
61)
(0.1
24)
(0.1
02)
(0.0
43)
(0.0
44)
Panel
CH
ome
Goods
Hom
eM
ain
ten
ance
Uti
liti
es(B
asi
c)U
tiliti
es(L
uxury
)M
ort
gage
Ren
tL
od
ging
(All)
Pre
Ban
xA
cces
sx
Milit
ary
0.21
6*-0
.283***
-0.0
00
-0.0
14
-0.2
12*
0.2
90*
**
-0.0
02
(0.1
09)
(0.1
01)
(0.0
45)
(0.0
56)
(0.1
19)
(0.0
97)
(0.0
02)
Panel
DB
ankin
g/C
redit
Rec
reati
on
Pu
blic
Tra
nsp
ort
ati
on
Tri
ps
Tob
acc
oA
lcohol
Giv
ing
Pre
Ban
xA
cces
sx
Milit
ary
-0.0
01-0
.071
0.0
44
-0.0
58
-0.1
41
0.0
10
0.0
43(0
.108
)(0
.109)
(0.0
78)
(0.0
77)
(0.0
90)
(0.1
23)
(0.0
88)
Not
e:T
able
pre
sents
the
esti
mat
eof
theγ
coeffi
cien
tin
the
follow
ing
regre
ssio
n:
Spending i
t=
φt+θ s+ξ i+δM
ilitary
i+βAccess i×PreBant+ρAccess i×Military
i+ηPreBant×Military
i+
γAccess i×PreBant×Military
i+ε it
wher
eSpending
isa
du
mm
yva
riab
leeq
ual
to1
ifth
ere
isany
spen
din
gin
asp
ecifi
edca
tegory
by
house
holdi
inin
terv
iew
qu
art
ert;
φar
edat
efi
xed
effec
ts;θ
are
stat
efixed
effec
ts;ξ
are
house
hold
leve
lco
vari
ate
s(s
pec
ifica
lly
ind
icato
rva
riab
les
for
nu
mb
erof
adult
s,ch
ild
ren,
sen
iors
,m
emb
ers
and
contr
ols
for
hu
sband
/w
ife
un
its,
the
pre
sence
of
at
least
one
house
hold
mem
ber
wit
ha
hig
hsc
hool
deg
ree
and
the
age
ofth
em
ain
house
hol
din
com
eea
rner
);PreBan
isa
du
mm
yva
riable
equ
al
to1
ift
isb
efore
Oct
ob
er2007;Access
isa
du
mm
yva
riab
leeq
ual
to1
ifhou
sehol
di
lives
ina
state
that
allow
spay
day
loan
sin
the
Pre
-ban
per
iod
an
dMilitary
isa
du
mm
yva
riab
leth
atis
equal
to1
ifth
eh
ouse
hol
dh
as
am
ain
earn
erw
ho
isin
the
arm
edfo
rces
.E
rrors
are
clust
ered
at
the
state
leve
lan
dar
ein
par
enth
eses
.Sam
ple
istr
imm
edby
dro
ppin
gobse
rvati
on
sth
at
hav
eth
eto
p5%
and
the
bott
om
5%
of
valu
esof
aver
age
tota
lm
onth
lyhou
sehol
dsp
endin
g(N=
3,3
56).
Dat
afr
om
the
Con
sum
erE
xp
endit
ure
Su
rvey
.D
ata
cove
rth
ep
erio
dof
Oct
ob
er2005
thru
Sep
tem
ber
2010
.*p<
0.1,
**p<
0.05
,**
*p<
0.01
115
Table 24: Effect of Payday Loan Access on Category Spending
Dependent Variable: Occurrence of Spending
Panel A Vehicle (Access) Vehicle (Operating) Vehicle (All) Food (Away) Food (Home) Food (All)PreBan x Access x Military -0.172 -0.021 -0.023 -0.028 0.024 0.002
(0.216) (0.035) (0.035) (0.112) (0.017) (0.002)
PreBan x Access x Military x Young -0.239 -0.031 -0.034 -0.080 -0.051 -0.003(0.251) (0.104) (0.103) (0.123) (0.054) (0.003)
Panel B Child Care Jewelery/Watches Clothing Education Electronics Life InsurancePreBan x Access x Military 0.004 0.072 0.016 0.198 0.119 -0.139
(0.135) (0.104) (0.078) (0.235) (0.145) (0.090)
PreBan x Access x Military x Young 0.034 -0.088 -0.147 -0.364 0.260* 0.198(0.172) (0.162) (0.165) (0.231) (0.143) (0.186)
Panel C Home Goods Home Maintenance Utilities (Basic) Utilities (Luxury) Mortgage RentPreBan x Access x Military 0.223** -0.290*** -0.034 -0.025 -0.221 0.364**
(0.091) (0.091) (0.031) (0.134) (0.174) (0.145)
PreBan x Access x Military x Young -0.047 0.041 0.094 0.000 0.045 -0.208(0.192) (0.224) (0.058) (0.200) (0.255) (0.274)
Panel D Lodging (All) Banking/Credit Recreation Public Transportation Trips TobaccoPreBan x Access x Military 0.001 0.182* -0.062 -0.005 -0.037 0.028
(0.001) (0.095) (0.156) (0.117) (0.176) (0.144)
PreBan x Access x Military x Young -0.008 -0.418*** -0.072 0.022 -0.077 -0.294(0.009) (0.073) (0.195) (0.164) (0.280) (0.194)
Panel E Child Support/Alimony AlcoholPreBan x Access x Military -0.104* -0.070
(0.060) (0.181)
PreBan x Access x Military x Young -0.084 0.106(0.091) (0.154)
Note: Table presents the estimates of the γ and ϕ coefficients in the following regression:
Spendingit = φt + θs + ξi + δMilitaryi + βAccessi × PreBant + ρAccessi ×Militaryi +ηPreBant ×Militaryi + νAccessi × Y oungi + ϑPreBant × Y oungi +%Militaryi × Y oungi + γAccessi × PreBant ×Militaryi +ςAccessi × PreBant × Y oungi + τAccessi ×Militaryi × Y oungi +υPreBant ×Militaryi × Y oungi + ϕAccessi × PreBant ×Militaryi × Y oungi + εit
where Spending is a dummy variable equal to 1 if there is any spending in a specified category byhousehold i in interview quarter t; φ are date fixed effects; θ are state fixed effects; ξ are household levelcovariates (specifically indicator variables for number of adults, children, seniors, members and controlsfor husband/wife units, the presence of at least one household member with a high school degree and theage of the main household income earner); PreBan is a dummy variable equal to 1 if t is before October2007; Access is a dummy variable equal to 1 if household i lives in a state that allows payday loans inthe Pre-ban period; Y oung is a dummy variable equal to 1 if the main income earner is 28 years old oryounger and Military is a dummy variable that is equal to 1 if the household has a main earner who isin the armed forces. Errors are clustered at the state level and are in parentheses. Sample is trimmedby dropping observations that have the top 5% and the bottom 5% of values of average total monthlyhousehold spending (N = 3,356). Data from the Consumer Expenditure Survey. Data cover the periodof October 2005 thru September 2010.*p<0.1, **p<0.05, ***p<0.01
116
Tab
le25
:E
ffec
tof
Pay
day
Loa
nA
cces
son
Veh
icle
Ow
ner
ship
and
Hou
sing
Choi
ces
No.
of
Ow
ned
Veh
icle
sR
enti
ng
(1)
(2)
(3)
(4)
Pre
Ban
xA
cces
sx
Milit
ary
-0.1
35
0.1
18
0.2
67***
0.2
66**
(0.4
68)
(0.4
08)
(0.0
98)
(0.1
31)
Pre
Ban
xA
cces
sx
Milit
ary
xY
ou
ng
-0.3
98
-0.0
45
(0.4
80)
(0.2
37)
N3356
3356
3356
3356
Not
e:C
olum
n1
and
3pre
sent
the
esti
mat
eof
theγ
coeffi
cien
tin
the
follow
ing
regre
ssio
n:
Yit=
φt+θ s+ξ i+δM
ilitary
i+βAccess i×PreBant+ρAccess i×Military
i+ηPreBant×Military
i+
γAccess i×PreBant×Military
i+ε it
and
Col
um
ns
2an
d4
pre
sent
the
esti
mat
esof
theγ
andϕ
coeffi
cien
tsin
the
follow
ing
regre
ssio
n:
Yit=
φt+θ s+ξ i+δM
ilitary
i+βAccess i×PreBant+ρAccess i×Military
i+ηPreBant×Military
i+
νAccess i×Young i+ϑPreBant×Young i+%Military
i×Young i+γAccess i×PreBant×Military
i+
ςAccess i×PreBant×Young i+τAccess i×Military
i×Young i+υPreBant×Military
i×Young i+
ϕAccess i×PreBant×Military
i×Young i+ε it
wher
eY
isth
enum
ber
ofve
hic
les
owned
by
house
holdi
inin
terv
iew
quart
ert
or
adu
mm
yva
riable
that
iseq
ual
to1
ifhouse
hold
live
din
are
nte
du
nit
inth
ein
terv
iew
qu
arte
r;φ
are
date
fixed
effec
ts;θ
are
state
fixed
effec
ts;ξ
are
house
hold
leve
lco
vari
ate
s(s
pec
ifica
lly
indic
ator
vari
able
sfo
rnu
mb
erof
adult
s,ch
ild
ren,
sen
iors
,m
emb
ers
and
contr
ols
for
husb
an
d/w
ife
unit
s,th
epre
sen
ceof
at
least
one
hou
sehol
dm
emb
erw
ith
ah
igh
school
deg
ree
and
the
age
of
the
main
house
hold
inco
me
earn
er);PreBan
isa
du
mm
yva
riable
equ
al
to1
ift
isb
efor
eO
ctob
er20
07;Access
isa
du
mm
yva
riable
equal
to1
ifhouse
holdi
lives
ina
state
that
allow
sp
ayday
loans
inth
eP
re-b
anp
erio
d;Young
isa
du
mm
yva
riab
leeq
ual
to1
ifth
em
ain
inco
me
earn
eris
28
years
old
or
youn
ger
andMilitary
isa
du
mm
yva
riab
leth
atis
equal
to1
ifth
ehou
sehol
dhas
am
ain
earn
erw
ho
isin
the
arm
edfo
rces
.Sam
ple
istr
imm
edob
serv
ati
ons
that
hav
eth
eto
p5%
and
the
bot
tom
5%of
valu
esof
aver
age
month
lyca
tegory
spen
din
g.
Err
ors
are
clust
ered
at
the
state
leve
land
are
inpar
enth
eses
.D
ata
from
the
Con
sum
erE
xp
end
iture
Su
rvey
.D
ata
cove
rth
ep
erio
dof
Oct
ob
er2005
thru
Sep
tem
ber
2010.
*p<
0.1,
**p<
0.05
,**
*p<
0.01
117
Table 26: Effect of Payday Loan Access on the Labor Market
(1) (2) (3) (4)Panel A: Current Population Survey No. of Civilian Earners Civilian Hours Worked/WeekPreBan x Access -0.009 -0.018 0.117 -1.001
(0.043) (0.039) (1.582) (1.658)
PreBan x Access x Young 0.035 3.748(0.068) (2.960)
N 20059 20059 20059 20059
Panel B: Consumer Expenditure Survey No. of Civilian Earners Civilian Hours Worked/WeekPreBan x Access -0.020 0.150 -4.439 0.067
(0.129) (0.152) (4.959) (6.229)
PreBan x Access x Young -0.622 -17.101(0.434) (14.601)
N 1049 1049 1049 1049
Note: Columns 1 and 3 in Panels A & B present the estimate of the β coefficient in the followingregression:
Laborit = φt + θs + ξi +UnemploymentRatest + βAccessi × PreBant + εit
and Columns 2 and 4 in Panels A & B present the estimates of the β and γ coefficients in the followingregression:
Laborit = φt + θs + ξi +UnemploymentRatest + βAccessi × PreBant + δPreBant × Y oungi +πAccessi × Y oungi + γAccessi × PreBant × Y oungi + εit
where Labor is a labor category characteristic of household i on date t; φ are date fixed effects; θ arestate fixed effects; ξ are household level covariates (specifically indicator variables for number of adults,children, seniors, members and controls for husband/wife units, the presence of at least one householdmember with a high school degree and the age of the main household income earner); UnemploymentRateis the state unemployment rate on date t; PreBan is a dummy variable equal to 1 if t is before October2007; Access is a dummy variable equal to 1 if household i lives in a state that allows payday loans inthe Pre-ban period and Y oung is a dummy variable equal to 1 if the main income earner is 28 years oldor younger. Only military households with 2 adults or more are included in the estimates. Errors areclustered at the state level and are in parentheses. Data cover the period of October 2005 thru September2010.*p<0.1, **p<0.05, ***p<0.01
118
Table 27: Effect of Payday Loan Access on the Labor Market
(1) (2) (3) (4)No. of Earners All Hours Worked/Week
PreBan x Access x Military 0.054 0.237 1.174 11.781**(0.111) (0.158) (3.106) (4.850)
PreBan x Access x Military x Young -0.470*** -26.683***(0.128) (7.486)
N 3356 3356 3356 3356
Note: Column 1 and 3 present the estimate of the γ coefficient in the following regression:
Yit = φt + θs + ξi + δMilitaryi + βAccessi × PreBant + ρAccessi ×Militaryi +ηPreBant ×Militaryi + γAccessi × PreBant ×Militaryi + εit
and Columns 2 and 4 in Panel C present the estimates of the γ and ϕ coefficients in the followingregression:
Yit = φt + θs + ξi + δMilitaryi + βAccessi × PreBant + ρAccessi ×Militaryi +ηPreBant ×Militaryi + νAccessi × Y oungi + ϑPreBant × Y oungi +%Militaryi × Y oungi + γAccessi × PreBant ×Militaryi +ςAccessi × PreBant × Y oungi + τAccessi ×Militaryi × Y oungi +υPreBant ×Militaryi × Y oungi +ϕAccessi × PreBant ×Militaryi × Y oungi + εit
where Labor is a labor category characteristic of household i on date t; φ are date fixed effects; θ arestate fixed effects; ξ are household level covariates (specifically indicator variables for number of adults,children, seniors, members and controls for husband/wife units, the presence of at least one householdmember with a high school degree and the age of the main household income earner); UnemploymentRateis the state unemployment rate on date t; PreBan is a dummy variable equal to 1 if t is before October2007; Access is a dummy variable equal to 1 if household i lives in a state that allows payday loans inthe Pre-ban period; Y oung is a dummy variable equal to 1 if the main income earner is 28 years old oryounger and Military is a dummy variable that is equal to 1 if the household has a main earner who isin the armed forces. Military and matched civilian households from the Consumer Expenditure Survey,are included in the estimates, save for those who at the time of their interview reported a total amountof spending that was in the top 5% or bottom 5% of all observations. Errors are clustered at the statelevel and are in parentheses. Data cover the period of October 2005 thru September 2010.*p<0.1, **p<0.05, ***p<0.01
119
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126
Appendices
A Figures and Tables
Figure A.1: 2013 USAA Military Pay Calendar
Source: www.usaa.com
127
Figure A.2: Paycycle Sales Pattern (Second Paycycle from Each Month Only)
Note: Data from post-ban period.
128
Figure A.3: Balance
129
Table A.1: Exchange Product CategoriesCATEGORY SUBCATEGORY
Electronics Photo EquipmentComputersTV/Stereo
Tobacco TobaccoAlcohol Wine
Beer/AleLiquor
Commissary-Like FoodSoda
ToiletriesHousehold Cleaning Supplies
StationaryLuxury Cosmetics/Perfumes
WatchesClothing Men’s Clothing
Men’s FurnishingsWomen’s OuterwearWomen’s Lingerie
FootwearEntertainment Books/Magazines
CDs/DVDsToys
Sports GoodsUniforms Military Clothing
Home LinensKitchen
Home AccentsOutdoor Living
Appliances AppliancesOther Luggage
Pet SuppliesHardware
130
Table A.2: Impact of Payday Loan Access on the Timing of Consumption with VaryingPrevious Paycycle Length
Dependent Variable: Log Daily SalesAccess
State Allow Near Shop Number of ShopsPreBan x Payday x Access x PreviousPaycycleLength -0.0140∗∗ -0.0114∗∗ -0.0011∗∗
(0.0069) (0.0053) (0.0005)N 283731 283731 283731
Note: The table presents the coefficient estimate on the quadruple interaction term of variables Payday,Access, PreBan and PreviousPaycycleLength in a quadruple difference-in-difference specification. Allthe double, triple and quadruple interactions of these variables are included in the specification as well asPayday, θi, φt and ξit. The dependent variable is the natural logarithm of daily total Commissary salesfor store i on date t; Payday is a dummy variable equal to 1 if t is a payday; PreBan is a dummy equal to 1if t is in the pre-regulation period of October 1, 2005 thru September 30, 2007; PreviousPaycycleLengthis a variable that contains the number of days in the paycycle preceding the paycycle containing date t;φ are controls for time (specifically: day of week, federal holidays, Social Security payout dates, earlypaycheck dates and paycycle indicator variables); θ are store fixed effects; ξ are all the interaction termsbetween day of week indicator variables and NearShop; PreBan and PreviousPaycycleLength and εis an error term. Access is one of three measures indicating access to payday loans. Specifically, “StateAllow” is a dummy equal to 1 if a Commissary is located in a state that allows payday loans, “Near Shop”is a dummy equal to 1 if there exists at least 1 payday loan shop within its 10 mile radius and “Numberof Shops” is the number of payday loan shops within a 10 mile radius of the commissary top coded at 10shops. Errors are clustered at the state level and are in parentheses. Sales are from the period of October1, 2005 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
131
Table A.3: The Impact of Payday Loan Access on the Timing of Consumption with AccessMeasured by “State Allow”
Dependent Variable: Log Daily Sales
Panel A: Total
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x State Allow x PreBan -0.0125 0.0088 -0.0333∗
(0.0108) (0.0090) (0.0180)N 283731 160550 123181
Panel B: Produce
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x State Allow x PreBan -0.0140 0.0036 -0.0309∗
(0.0125) (0.0101) (0.0174)N 278503 157596 120907
Panel C: Meat
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x State Allow x PreBan -0.0136 0.0093 -0.0339∗
(0.0140) (0.0115) (0.0184)N 271160 153453 117707
Note: Table presents the estimates of the ρ coefficients in the following triple difference-in-differencespecification:
LogSalesit = α+βPaydayt+γPaydayt×PreBant+δPaydayt×StateAllowi+ρPaydayt×StateAllowi×PreBant + ηUnemploytmentRateit + φt + θi + ξit + εitwhere LogSales is the natural logarithm of daily product category sales for Commissary store i on datet; Payday is a dummy variable equal to 1 if t is on payday; PreBan is a dummy equal to 1 if t is inthe pre-regulation period of October 1, 2005 thru September 30, 2007; StateAllow is a dummy equal to1 if Commissary i is located in a State that allows payday loans; UnemploymentRate is the monthlyunemployment rate in Commissary i’s county; φ are controls for time (specifically: day of week, federalholidays, Social Security payout days, early paycheck days and paycycle indicator variables); θ are storefixed effects; ξ are all the interaction terms between day of week indicator variables and NearShop andPreBan and ε is an error term. Errors are clustered at the state level and are in parentheses. Sales arefrom the period of October 1, 2005 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
132
Table A.4: The Impact of Payday Loan Access on the Timing of Consumption with AccessMeasured by “Number of Shops”
Dependent Variable: Log Daily Sales
Panel A: Total
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x Number of Shops x PreBan -0.0013 0.0002 -0.0028∗∗
(0.0009) (0.0009) (0.0014)N 283731 160550 123181
Panel B: Produce
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x Number of Shops x PreBan -0.0010 0.0006 -0.0026∗
(0.0010) (0.0010) (0.0013)N 278503 157596 120907
Panel C: Meat
Previous Paycycle Length
All 14 Days or Less >14 DaysPayday x Number of Shops x PreBan -0.0017 -0.0003 -0.0026∗
(0.0011) (0.0011) (0.0015)N 271160 153453 117707
Note: Table presents the estimates of the ρ coefficients in the following triple difference-in-differencespecification:
LogSalesit = α + βPaydayt + γPaydayt × PreBant + δPaydayt × NumberofShopsi + ρPaydayt ×NumberofShopsi × PreBant + ηUnemploytmentRateit + φt + θi + ξit + εitwhere LogSales is the natural logarithm of daily product category sales for Commissary store i on datet; Payday is a dummy variable equal to 1 if t is on payday; PreBan is a dummy equal to 1 if t isin the pre-regulation period of October 1, 2005 thru September 30, 2007; NumberofShops is equal tothe number of payday loan shop within a 10 mile radius of the Commissary top coded at 10 shops;UnemploymentRate is the monthly unemployment rate in Commissary i’s county; φ are controls fortime (specifically: day of week, federal holidays, Social Security payout days, early paycheck days andpaycycle indicator variables); θ are store fixed effects; ξ are all the interaction terms between day of weekindicator variables and NearShop and PreBan and ε is an error term. Errors are clustered at the statelevel and are in parentheses. Sales are from the period of October 1, 2005 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
133
Tab
leA
.5:
The
Impac
tof
Pay
day
Loa
nA
cces
son
the
Com
pos
itio
nof
Con
sum
pti
onw
ith
Acc
ess
Mea
sure
dby
“Sta
teA
llow
”
Dep
enden
tV
aria
ble
:L
ogT
otal
Mon
thly
Sal
es
Pan
elA
:A
llC
omm
issa
ries
Gro
cery
Pro
duce
Mea
tSta
teA
llow
xP
reB
an0.
0044
-0.0
045
-0.0
149
(0.0
152)
(0.0
171)
(0.0
243)
N94
2094
2094
20
Pan
elB
:E
xch
ange
s
Ele
ctro
nic
sA
lcoh
olL
uxury
Tob
acco
Com
mis
sary
-Lik
eSta
teA
llow
xP
reB
an0.
0684
∗∗0.
0833
∗∗0.
0323
0.03
770.
0455
(0.0
262)
(0.0
313)
(0.0
198)
(0.0
293)
(0.0
308)
N42
0042
0042
0042
0042
00
Clo
thin
gU
nif
orm
sE
nte
rtai
nm
ent
Hom
eA
pplian
ces
Oth
erSta
teA
llow
xP
reB
an0.
0079
-0.0
135
-0.0
135
0.05
15∗
0.03
730.
0534
∗
(0.0
230)
(0.0
278)
(0.0
307)
(0.0
270)
(0.0
335)
(0.0
286)
N42
0042
0042
0042
0042
0042
00
Not
e:T
able
pre
sents
the
esti
mat
esof
theβ
coeffi
cien
tsin
the
follow
ing
regre
ssio
n:
LogSales i
t=α+βStateAllow
i×PreBant+γLogPopulation
it+ηUnem
ploytmentRate
it+φt+θ i+ε it
wher
eLogSales
isth
enat
ura
llo
gari
thm
ofm
onth
lysa
les
ina
giv
enp
rodu
ctca
tegory
for
storei
inm
onth
-yea
rt;LogPopulation
isth
enat
ura
llo
gari
thm
ofth
ep
opula
tion
of
the
nea
rest
base
s(s)
tost
orei
inm
onth
-yea
rt;Unem
ploymentRate
isth
em
onth
lyun
emplo
ym
ent
rate
inC
omm
issa
ryi’
sco
unty
;PreBan
isa
du
mm
yeq
ual
to1
ift
isin
the
pre
-reg
ula
tion
per
iod
of
Oct
ob
er2005
thru
Sep
tem
ber
2007
;φ
are
mon
th-y
ear
fixed
effec
ts;θ
are
store
fixed
effec
tsandε
isan
erro
rte
rm.StateAllow
isa
du
mm
yeq
ual
to1
ifC
omm
issa
ryi
islo
cate
din
Sta
teth
atal
low
sp
ayday
loans.
Fu
rther
more
,st
ore
sth
at
wer
eaff
ecte
dby
Hurr
icane
Katr
ina
wer
ed
ropp
ed.
Err
ors
are
clu
ster
edat
the
stat
ele
vel
and
are
inpare
nth
eses
.Sale
sare
for
the
per
iod
of
Oct
ob
er2005
thru
Sep
tem
ber
2010.
*p<
0.1,
**p<
0.05
,**
*p<
0.01
134T
able
A.6
:T
he
Impac
tof
Pay
day
Loa
nA
cces
son
the
Com
pos
itio
nof
Con
sum
pti
onw
ith
Acc
ess
Mea
sure
dby
“Num
ber
ofShop
s”
Dep
enden
tV
aria
ble
:L
ogT
otal
Mon
thly
Sal
es
Pan
elA
:A
llC
omm
issa
ries
Gro
cery
Pro
duce
Mea
tN
um
ber
ofShop
sx
Pre
Ban
0.00
000.
0001
-0.0
029
(0.0
014)
(0.0
017)
(0.0
027)
N94
2094
2094
20
Pan
elB
:E
xch
ange
s
Ele
ctro
nic
sA
lcoh
olL
uxury
Tob
acco
Com
mis
sary
-Lik
eN
um
ber
ofShop
sx
Pre
Ban
0.00
91∗∗∗
0.00
73∗∗
0.00
330.
0057
0.00
52(0
.002
8)(0
.002
8)(0
.002
0)(0
.003
8)(0
.003
2)N
4200
4200
4200
4200
4200
Clo
thin
gU
nif
orm
sE
nte
rtai
nm
ent
Hom
eA
pplian
ces
Oth
erN
um
ber
ofShop
sx
Pre
Ban
0.00
080.
0021
0.00
040.
0044
0.00
470.
0044
(0.0
036)
(0.0
033)
(0.0
042)
(0.0
035)
(0.0
050)
(0.0
034)
N42
0042
0042
0042
0042
0042
00
Not
e:T
able
pre
sents
the
esti
mat
esof
theβ
coeffi
cien
tsin
the
follow
ing
regre
ssio
n:
LogSales i
t=α+βNumberofShops i×PreBant+γLogPopulation
it+ηUnem
ploytmentRate
it+φt+θ i+ε it
wher
eLogSales
isth
enat
ura
llo
gari
thm
ofm
onth
lysa
les
ina
giv
enp
rodu
ctca
tegory
for
storei
inm
onth
-yea
rt;LogPopulation
isth
enat
ura
llo
gari
thm
ofth
ep
opula
tion
of
the
nea
rest
base
s(s)
tost
orei
inm
onth
-yea
rt;Unem
ploymentRate
isth
em
onth
lyun
emplo
ym
ent
rate
inC
omm
issa
ryi’
sco
unty
;PreBan
isa
du
mm
yeq
ual
to1
ift
isin
the
pre
-reg
ula
tion
per
iod
of
Oct
ob
er2005
thru
Sep
tem
ber
2007
;φ
are
mon
th-y
ear
fixed
effec
ts;θ
are
store
fixed
effec
tsandε
isan
erro
rte
rm.NumberofShops
isth
enu
mb
erof
pay
day
loan
shop
wit
hin
a10
mile
radiu
sof
stor
ei
top
coded
at
10
shop
s.F
urt
her
more
,st
ore
sth
at
wer
eaff
ecte
dby
Hurr
icane
Katr
ina
wer
edro
pp
ed.
Err
ors
are
clust
ered
atth
est
ate
level
an
dare
inp
are
nth
eses
.S
ale
sare
for
the
per
iod
of
Oct
ob
er2005
thru
Sep
tem
ber
2010
.*p<
0.1,
**p<
0.05
,**
*p<
0.01
135
Tab
leA
.7:
The
Rel
atio
nsh
ipb
etw
een
Milit
aryP
ayday
Loa
nA
cces
san
dSta
teP
rice
Chan
ges
Dep
enden
tV
aria
ble
:L
ogP
rice
s
Log
Tob
acco
Pri
ceL
og
Bee
rP
rice
Log
Win
eP
rice
Log
of
Cost
of
Liv
ing
Index
Pre
Ban
xSta
teA
llow
0.02
490.0
133
-0.0
056
-0.0
011
(0.0
360
)(0
.0228)
(0.0
370)
(0.0
077)
N230
697
697
697
Not
e:T
able
pre
sents
the
esti
mat
esof
theβ
coeffi
cien
tsin
the
follow
ing
regre
ssio
n:
LogPrice
st=α+βPreBant×StateAllow
s+φt+θ s+ε s
t
wher
eLogPrice
isth
en
atura
llo
gari
thm
ofav
erage
pri
cefo
rst
ates
over
tim
ep
erio
dt;PreBan
isa
dum
my
equ
al
to1
ift
isb
efore
Sep
tem
ber
2007
;StateAllow
isa
dum
my
equal
to1
ifs
isa
state
that
allow
sp
ayday
loans;φ
are
tim
ep
erio
dfi
xed
effec
ts;θ
are
state
fixed
effec
tsan
dε
isan
erro
rte
rm.
For
Tob
acc
o,t
isannual,
data
spans
2005-2
010
and
2007
isdro
pp
ed.
For
Bee
ran
dW
ine,t
isqu
arte
rly
and
the
dat
asp
ans
the
fou
rth
quar
ter
of
2005
thru
the
thir
dqu
art
erof
2010
wit
hth
e4th
quart
erm
issi
ng
in2007,
2008
an
d20
09as
they
are
not
avai
lab
lein
the
dat
a.E
rrors
are
clu
ster
edat
the
state
leve
lan
dare
inpare
nth
eses
.*p<
0.1
,**p<
0.0
5,
***p<
0.0
1
Sou
rces
:T
obac
copri
ces
from
the
Cen
ters
for
Dis
ease
Contr
ol
an
dP
reve
nti
on
Sta
teT
ob
acc
oT
rack
ing
an
dE
valu
ati
on
Syst
em.
All
oth
erp
rodu
ctpri
ces
and
cost
oflivin
gin
dex
from
the
Coun
cil
for
Com
munit
yand
Eco
nom
icR
esea
rch.
136
Tab
leA
.8:
Pro
pen
sity
Sco
reC
ovar
iate
s
Cov
aria
teL
evel
Abbre
via
tion
Sou
rce
Unem
plo
ym
ent
rate
,July
200
7C
ounty
unem
plo
ym
ent
rate
BL
S
%In
div
idual
sb
elow
pov
erty
,20
05-2
007
Sta
tein
dp
ovp
erce
nt
SM
AD
B
%In
div
idual
snot
cove
red
by
hea
lth
insu
rance
,2006
Sta
teno
hea
lth
insu
rance
06SM
AD
B
Med
ian
House
hol
dIn
com
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137
Table A.9: Daily Discount Rate
Dependent Variable: Log Daily Sales
Product Category
TOTAL PRODUCE MEATDaysSincePayday -0.0188∗∗∗ -0.0150∗∗∗ -0.0223∗∗∗
(0.0006) (0.0005) (0.0007)N 170325 167182 162732
Note: Table presents the estimates of the β coefficients in the following regression:
LogSalesit = α + βDaysSincePaydayt + φt + θi + εitwhere LogSales is the natural logarithm of daily sales in a given product category for Commissary storei on date t; DaysSincePayday is a continuous variable pertaining to the number of days t is from theclosest preceding payday; EarlyAccess is a dummy variable equal to 1 if t is on or after the last businessday in a paycycle; φ are controls for time (specifically: day of week, federal holidays, Social Securitypayout dates, early paycheck dates and paycycle indicator variables); θ are store fixed effects and ε is anerror term. Errors are clustered at the state level and are in parentheses. Sales are from the post-banperiod of October 1, 2007 thru September 30, 2010.*p<0.1, **p<0.05, ***p<0.01
138
Table A.10: Percent of Civilians are Earners
All Pre-ban Period Post-ban PeriodCurrent Population Survey 64.24% 66.02% 63.06%Consumer Expenditure Survey 64.14% 68.09% 61.44%
Note: Members in military households in corresponding surveys over the period of October 2005 thruSeptember 2010.
