You may have heard the saying that those who discover or create new knowledge “stand upon the shoulders of giants.” As a future social worker, you will stand on the shoulders of many individuals who have come before you. These influential people may have fought for women’s suffrage, African American rights, or poverty assistance, among other social causes. You may be familiar with their names through your textbook readings for this course, or they may be entirely unknown to you.
Choose one of the following social work policy makers as the focus of your paper, and identify a signature social policy effected by that person:
Jane Addams
Clara Barton
Dorothy Day
William Edward B. DuBois
Medgar Evers
Mary Richmond
Dorothea Spellman
Harriett Tubman
Booker T. Washington
Submit a 4- to 6-page scholarly paper using the following outline:
- Biography of the Social Work Policy Maker
Provide a brief background of the policy maker, including family and professional history.
- The Social Welfare Policy/Service
Describe the core tenets of the policy developed by the policy maker upon which you focused.
Explain the community needs for this policy.
Describe the population/community served by this policy.
Explain the process of developing and enacting this policy. - Impact of the Policy
describe how this policy addressed the needs of a population/community.
Describe how this policy advocated for a population and served social justice.
Explain how this policy changed the community. - Practice Implications
Discuss how this policy impacts social work practice today.
reference
- Stern, M.J., & Axinn, J. (2018). Social welfare: A history of American response to need (9th ed.). Pearson Education.
Chapter 8, “Conservative Resurgence and Social Change: 1968-1992” (pp. 251-275)
- Almond, D., Hoynes, H. W., & Schanzenbach, D. W. (2011). Inside the war on poverty: The impact of food stamps on birth outcomes Links to an external site.. The Review of Economics and Statistics, 93(2), 387–403.
- U.S. Department of Agriculture. (2016a). Supplemental Nutrition Assistance Program (SNAP): Eligibility Links to an external site.. Retrieved from http://www.fns.usda.gov/snap/eligibility
- U.S. Department of Agriculture. (2016b). Supplemental Nutrition Assistance Program (SNAP): To apply Links to an external site.. Retrieved from http://www.fns.usda.gov/snap/apply
The Review of Economics and Statistics
VOL. XCIII MAY 2011 NUMBER 2
INSIDE THE WAR ON POVERTY: THE IMPACT OF FOOD STAMPS
ON BIRTH OUTCOMES
Douglas Almond, Hilary W. Hoynes, and Diane Whitmore Schanzenbach*
Abstract—This paper evaluates the health impacts of a signature initiative
of the War on Poverty: the introduction of the modern Food Stamp Pro-
gram (FSP). Using variation in the month FSP began operating in each
U.S. county, we find that pregnancies exposed to FSP three months prior
to birth yielded deliveries with increased birth weight, with the largest
gains at the lowest birth weights. We also find small but statistically insig-
nificant improvements in neonatal mortality. We conclude that the sizable
increase in income from FSP improved birth outcomes for both whites
and African Americans, with larger impacts for African American
mothers.
I. Introduction
IN this paper, we evaluate the health consequences of a
sizable improvement in the resources available to Ameri-
ca’s poorest. In particular, we examine the impact of the
Food Stamp Program (FSP), which in 2007 provided $34
billion in payments to about 13 million households, on
infant health. Our paper makes two distinct contributions.
First, although the goal of the FSP is to increase the nutri-
tion of the poor, few papers have examined its impact on
health outcomes. Second, building on work by Hoynes and
Schanzenbach (2009), we argue that the FSP treatment
represents an exogenous increase in income for the poor.
Our analysis therefore represents a causal estimate of the
impact of income on health, an important topic with little
convincing evidence due to concerns about endogeneity
and reverse causality (Currie, 2009).
We use the natural experiment afforded by the nation-
wide rollout of the modern FSP during the 1960s and early
1970s. Our identification strategy uses the sharp timing of
the county-by-county rollout of the FSP, which was initially
constrained by congressional funding authorizations (and
ultimately became available in all counties by 1975). Speci-
fically, we use information on the month the FSP began
operating in each of the roughly 3,100 U.S. counties and
examine the impact of the FSP rollout on mean birth
weight, low birth weight, gestation, and neonatal mortality.
Throughout the history of the FSP, the program para-
meters have been set by the U.S. Department of Agriculture
(USDA) and are uniform across states. In the absence of the
state-level variation often leveraged by economists to eval-
uate transfer programs, previous FSP research has typically
resorted to strong assumptions as to the comparability of
FSP participants and eligible nonparticipants (Currie,
2003). Not surprisingly, the literature is far from settled as
to what casual impact (if any) the FSP has on nutrition and
health.
Hoynes and Schanzenbach (2009) use this county rollout
to examine the impact of the FSP on food consumption
using the PSID. They found that the introduction of the FSP
increased total food spending and decreased out-of-pocket
food spending. Importantly, consistent with the predictions
of canonical microeconomic theory, the magnitude of the
increase in food expenditures was similar to an equivalent-
sized income transfer, implying that most recipient house-
holds were inframarginal (that is, they would spend more
on the subsidized good than the face value of the in-kind
transfer). As one of the largest antipoverty programs in the
United States—comparable in cost to the earned income tax
credit (EITC) and substantially larger than Temporary
Assistance to Needy Families (TANF)—understanding
FSP effects is valuable both in its own right and for what
it reveals about the relationship between income and
health.1
We focus on birth outcomes for several reasons. First,
families represent an important subgroup of the food stamp
caseload. Over 60% of food stamp households include chil-
Received for publication February 4, 2009. Revision accepted for publi-
cation December 9, 2009.
* Almond: Columbia University and NBER; Hoynes: University of
California, Davis and NBER; Schanzenbach: Northwestern University
and NBER.
We thank Justin McCrary for providing the Chay-Greenstone-McCrary
geography crosswalk and Karen Norberg for advice on cause-of-death
codes. This work was supported by a USDA Food Assistance Research
Grant (awarded by the Joint Center for Poverty Research at Northwestern
University and University of Chicago), the Population Research Center at
the University of Chicago, and USDA FANRP Project 235, ‘‘Impact of
Food Stamps and WIC on Health and Long Run Economic Outcomes.’’
We also thank Ken Chay, Janet Currie, Ted Joyce, Bob LaLonde, Doug
Miller, Bob Whitaker, and seminar participants at the Harris School, Dart-
mouth, MIT, LSE, the California Center of Population Research (UCLA),
Duke, Cornell, UC Irvine, IIES (Stockholm University), the NBER Sum-
mer Institute, and the SF Fed Summer Institute for helpful comments.
Alan Barreca, Rachel Henry Currans-Sheehan, Elizabeth Munnich, Ankur
Patel, and Charles Stoecker provided excellent research assistance, and
Usha Patel entered the regionally aggregated vital statistics data for 1960
through 1975.
The online appendix referred to throughout the article is available at
http://www.mitpressjournals.org/doi/suppl/10.1162/REST_a_00089.
1 The cost of the FSP was $33 billion in 2006 (compared to $24 billion
for TANF, $33 billion for the EITC, and $5.4 billion for WIC, the Special
Supplemental Nutrition Program for Women, Infants and Children).
The Review of Economics and Statistics, May 2011, 93(2): 387–403
� 2011 by the President and Fellows of Harvard College and the Massachusetts Institute of Technology
dren, and one-third have at least one preschool-age child.
Second, birth outcomes improved substantially during the
late 1960s and early 1970s. Third, to the extent that the FSP
improved birth outcomes, later-life health outcomes of
these cohorts may have also benefited (Barker, 1992; Black,
Devereux, & Salvanes, 2007). Finally, the vital statistics
data used in this project are ideally suited for analyzing
FSP rollout: the birth (death) microdata contain the county
of birth (death) and the month of birth (death). This, com-
bined with the large sample sizes (for example, more than 1
million birth records per year in the data set), allows us to
use the discrete nature of the FSP rollout with significant
statistical power.
We find that infant outcomes improve with FSP introduc-
tion. Changes in mean birth weight are small, increasing
roughly half a percent for blacks and whites who partici-
pated in the program (effect of the treatment on the treated).
Impacts were larger at the bottom of the birth weight distri-
bution, reducing the incidence of low birth weight among
the treated by 7% for whites and between 5% and 11% for
blacks. Changes in this part of the birth weight distribution
are important because they are closely linked to other new-
born health measures. Although not all treatment effects are
statistically significant, they point consistently to improve-
ments in birth weight following the introduction of the FSP.
We also find that the FSP introduction leads to a reduction
in neonatal mortality, although these results rarely reach
statistical significance. We find very small (but precisely
estimated) impacts of the FSP on fertility, suggesting that
the results are not biased by endogenous sample selection.
All results are robust to various sets of controls, such as
county fixed effects, state-by-year fixed effects, and county-
specific linear trends. Moreover, FSP impact estimates are
robust to and little changed by county-by-year controls for
federal spending on other social programs, suggesting our
basic identification strategy is clean. Finally, we present an
event study analysis that further supports the validity of the
identification strategy.
Food stamps are the fundamental safety net in the
United States. Unlike other means-tested programs, there is
no additional targeting to specific subpopulations. Current
benefits average about $200 per recipient household per
month. Our analysis constitutes the first evidence that
despite the fact that if did not target pregnant mothers (or
even women), introduction of the FSP improved newborn
health.
II. Introduction of the Food Stamp Program
The modern FSP began with President Kennedy’s 1961
announcement of a pilot food stamp program that was to be
established in 8 impoverished counties. The pilot programs
were expanded to 43 counties in 1962 and 1963. The suc-
cess with these pilot programs led to the Food Stamp Act of
1964 (FSA), which gave local areas the authority to start up
the FSP in their county. As with the current FSP, the pro-
gram was federally funded, and benefits were redeemable at
approved retail food stores. In the period following the pas-
sage of the FSA, a steady stream of counties initiated such
programs, and federal spending on the FSP more than
doubled between 1967 and 1969 (from $115 million to
$250 million). Support for requiring counties to participate
in FSP grew due to a national spotlight on hunger (Berry,
1984). This interest culminated in passage of 1973 amend-
ments to the Food Stamp Act, which mandated that all
counties offer FSP by 1975.
Figure 1 plots the percentage of counties with an FSP
from 1960 to 1975.2 During the pilot phase (1961–1964),
FSP coverage increased slowly. Beginning in 1964, pro-
gram growth accelerated, and coverage expanded at a
steady pace until all counties were covered in 1974.
Furthermore, there was substantial heterogeneity in the tim-
ing of adoption of the FSP, both within and across states.
The map in figure 2 shades counties according to the date
of FSP adoption (darker shading denotes a later start-up
date). Our basic identification strategy considers the month
of FSP adoption for each county the FSP ‘‘treatment.’’3
For our identification strategy to yield causal estimates of
the program, it is key to establish that the timing of FSP
adoption appears to be exogenous. Prior to the FSP, some
counties provided food aid through the Commodity Distri-
bution Program (CDP), which took surplus food purchased
by the federal government as part of an agricultural price
support policy and distributed those goods to the poor. The
1964 Food Stamp Act allowed counties to voluntarily set
up an FSP, but the act also stated that no county could run
both the FSP and the CDP. Thus, for counties that pre-
viously ran a CDP, adoption of the FSP implies termination
of the CDP.4 The political accounts of the time suggest that
debates about adopting the FSP pitted powerful agricultural
interests (which favored the CDP) against advocates for the
poor (who favored the FSP; see MacDonald, 1977; Berry,
1984).5 In particular, counties with strong support for farm-
2 Counties are weighted by their 1970 population. Note this is not the
food stamp caseload, but represents the percentage of the U.S. population
that lived in a county with an FSP.
3 This timing lines up exceptionally well with county-level FSP spend-
ing as measured in the Regional Economic Information System data. See
online appendix table 3.
4 This transition in nutritional assistance would tend to bias FSP impact
estimates downward, but we do not think this bias is substantial because
of the limited scope of the CDP. The CDP was not available in all coun-
ties, and recipients often had to travel long distances to pick up the items.
Further, the commodities were distributed infrequently and inconsistently,
and provided a narrow set of commodities. The most frequently available
were flour, cornmeal, rice, dried milk, peanut butter, and rolled wheat
(Citizens’ Board of Inquiry 1968). In contrast, food stamp benefits can be
used to purchase all food items (except hot foods for immediate consump-
tion, alcoholic beverages, and vitamins).
5 In fact, as Berry (1984) and Ripley (1969) noted, passage of the 1964
Food Stamp Act was achieved through classic legislative logrolling. The
farm interest coalition (southern Democrats, Republicans) wanted to pass
an important cotton-wheat subsidy bill while advocates for the poor
(northern Democrats) wanted to pass the FSA. Neither had majorities, yet
they made an arrangement, supported each others’ bills, and both bills
passed.
388 THE REVIEW OF ECONOMICS AND STATISTICS
ing interests (such as southern or rural counties) may be late
adopters of the FSP. Counties with strong support for the
low-income population (such as northern, urban counties
with large populations of poor) may adopt FSP earlier in
the period. This systematic variation in food stamp adoption
could lead to spurious estimates of the program impact if
FIGURE 2.—FOOD STAMP PROGRAM START DATE BY COUNTY (1961–1975)
Authors’ tabulations of food stamp administrative data (U.S. Department of Agriculture, various years). The shading corresponds to the county FSP start date, where darker shading indicates later county imple-
mentation.
FIGURE 1.—WEIGHTED PERCENTAGE OF COUNTIES WITH A FOOD STAMP PROGRAM, 1960–1975
Authors’ tabulations of food stamp administrative data (U.S. Department of Agriculture, various years). Counties are weighted by their 1960 population.
389INSIDE THE WAR ON POVERTY
those same county characteristics are associated with differ-
ential trends in the outcome variables.
In earlier work (Hoynes & Schanzenbach, 2009), we
documented that larger counties with a greater fraction of
the population that was urban, black, or low income indeed
implemented the FSP earlier, consistent with the historical
accounts. We sought to predict FSP adoption date with 1960
county characteristics—those recorded immediately prior to
the pilot FSP phase. That analysis showed that larger coun-
ties and those with a higher share of black, elderly, young,
or low income implemented earlier and those where more of
the land was used in farming implement later.6 Neverthe-
less, the county characteristics explain very little of the var-
iation in adoption dates (see online appendix figure 1). This
is consistent with the characterization of funding limits con-
trolling the movement of counties off the waiting list to start
up their FSP: ‘‘The program was quite in demand, as con-
gressmen wanted to reap the good will and publicity that
accompanied the opening of a new project. At this time there
was always a long waiting list of counties that wanted to join
the program. Only funding controlled the growth of the pro-
gram as it expanded’’ (Berry, 1984, pp. 36–37).
We view the weakness of this model fit as a strength
when it comes to our identification approachin that much of
the variation in the implementation of FSP appears to be
idiosyncratic. Nonetheless, in order to control for possible
differences in trends across counties that are spuriously cor-
related with the county treatment effect, all of our regres-
sions include interactions of these 1960 pretreatment county
characteristics with time trends as in Acemoglu, Autor, and
Lyle (2004) and Hoynes and Schanzenbach (2009).
FSP introduction took place during a period of tremen-
dous expansion in cash and noncash transfer programs as
the War on Poverty and Great Society programs were
expanding. To disentangle the FSP from these other pro-
grams, the county-by-month variation in FSP rollout is key.
Further, given that virtually all means-tested programs are
administered at the state level, our controls for state-by-year
fixed effects should absorb these program impacts. To be
sure, however, our models include controls for per capita
real county government (non–food stamp) transfers.7
III. Background Literature
The goal of the FSP is to improve nutrition among the
low-income population. As such, many studies have exam-
ined the impact of the FSP on nutritional availability and
intake, food consumption, food expenditures, and food inse-
curity (see Currie, 2003, and Fraker, 1990, for reviews of
the literature).
Almost all existing studies of the impact of the FSP use
research designs that rely on comparisons of program parti-
cipants to nonparticipants at the individual level. This
approach is subject to the usual criticisms regarding selec-
tion into the program. For example, a number of researchers
(Currie, 2003; Currie & Moretti, 2008; Fraker, 1990) have
pointed out that if food stamp recipients are healthier, are
more motivated, or have better access to health care than
other eligible women, then comparisons between partici-
pants and nonparticipants could produce positive program
estimates even if the true effect is 0. Conversely, if food
stamp participants are more disadvantaged than other
families, such comparisons may understate the program’s
impact. In fact, as Currie (2003) reported, several studies,
including Basiotis, Cramer-LeBlanc, and Kennedy (1998)
and Butler and Raymond (1996), find that food stamp parti-
cipation leads to a reduction in nutritional intake. These
unexpected results are almost certainly driven by negative
selection in participation.
Many researchers who evaluate the impact of other gov-
ernment programs avoid these selection problems by com-
paring outcomes across individuals living in states with
different levels of benefit generosity or other program
parameters. A long literature on the effects of cash assis-
tance programs is based on this type of identification strat-
egy (Moffitt, 1992; Blank, 2002). Unfortunately, the FSP
is a federal program for which there is very little geo-
graphic variation (aside from the variation we use in
this paper) or variation in eligibility criteria or benefit
levels, so prior researchers have had to employ alternative
approaches.
Identification issues aside, it is noteworthy that few FSP
studies examine the impact on health outcomes. We are
aware of two studies. Currie and Cole (1991) examine the
impact of the FSP on birth weight using sibling comparisons
and instrumental variable methods and find no significant
impacts of the FSP. Our work is closer to that of Currie and
Moretti (2008), who use the county rollout of FSP in Califor-
nia to analyze birth outcomes. They find that FSP introduc-
tion was associated with a reduction in birth weight, which
was driven particularly by first births among teens and by
changes for Los Angeles County. As discussed below, this
negative effect is possible if the FSP led to fertility changes
or increases in the survival of low-birth-weight fetuses. The
timing of FSP assignment in Currie and Moretti (2008) differs
from ours in that they consider FSP availability at the begin-
ning of pregnancy and its impact on birth weight, whereas we
focus on availability toward the end of pregnancy.8
The literature (see the review in Currie, 2009) provides
few estimates of the causal impact of income on birth
6 For more detail, see table 1 in Hoynes and Schanzenbach (2009).
7 The Special Supplemental Food Program for Women, Infants and
Children (WIC), available to low-income pregnant women and children
up to age 5 in families, was introduced in 1974. Given the timing of WIC
implementation relative to FSP, there is little concern that the introduc-
tion of WIC biases our estimates of the introduction of FSP, and results
limited to pre-1974 are qualitatively similar.
8 Table 3 shows the sensitivity of our impact estimates to the timing of
FSP assignment.
390 THE REVIEW OF ECONOMICS AND STATISTICS
weight. Cramer (1995) finds that mothers with more income
have higher-birth-weight babies, although income is identi-
fied cross-sectionally. Kehrer and Wolin (1979) find evi-
dence that the Gary Income Maintenance Experiment may
have improved birth weight. However sample sizes are
small (N ¼ 404 births), and although positive effects were
found for woman as being and high risk for low birth
weight (young, smokers, short birth interval), perverse
effects were found for woman classified as being of low risk
low birth weight. Currie and Cole (1993), using IV and
mother-fixed effects estimators, find that AFDC income
leads to improvements in birth weight. Baker (2008) uses
the 1993 expansion in the EITC, which disproportionately
benefited families with two or more children, finding a 7
gram increase in the birth weight of subsequent children. In
general, the literature has been plagued by imprecise esti-
mates due to small sample sizes as well as a lack of well-
identified sources of variation in income. As a result, we
argue that our paper provides some of the best evidence to
date on the impact of income on birth outcomes.
IV. Food Stamps and Infant Health
The FSP introduction represents an exogenous and siz-
able increase in income for the poor. Canonical microeco-
nomic theory predicts that in-kind transfers like food
stamps will have the same impact on spending as an equiva-
lent cash transfer for consumers who are inframarginal.
Hoynes and Schanzenbach (2009) use the same FSP rollout
identification approach and data from the PSID to examine
the impacts of food stamps on food expenditures; they find
that recipients of food stamps behave as if the benefits were
paid in cash. Therefore, not only can we think of the FSP
introduction as a large income transfer, we can think of it as
for the most part the equivalent of a cash income transfer.
With this framing, an increase in income could lead to
changes in infant health through many channels. We would
expect that spending on all normal goods would increase,
therefore leading to increases in food consumption regard-
less of whether the benefits are paid in cash or in kind. We
have little information on how particular subcategories of
food demand change with FSP availability: Hoynes and
Schanzenbach (2009) are able to measure impacts on total
food expenditures, but cannot provide information on the
quantity or quality of food consumed (or other goods).
The medical literature on the determinants of birth
weight provides a useful structure for thinking about the
possible channels for the health effects of the FSP. As Kra-
mer (1987a, 1987b) suggested, birth weight is usefully
decomposed into that related to the gestation length (prema-
turity, or GL) and growth conditional on gestation length
(intrauterine growth, or IUG). Of the two, GL is thought to
be more difficult to manipulate, though empirically more
important than IUG in affecting birth weight in developed
countries (Kramer, 1987a, 1987b). Maternal nutrition and
cigarette smoking are the two most important determinants
of IUG that are potentially modifiable (Kramer, 1987a,
1987b). Finally, there is evidence that birth weight is gener-
ally most responsive to nutritional changes affecting the
third trimester of pregnancy.9 Kramer (1987a) writes, ‘‘It is
important to analyze additional health measures in addition
to birth weight: A final reminder concerns the need for
future research to keep sight of the truly important out-
comes of infant and child mortality, morbidity, and func-
tional performance. After all, birth weight and gestational
age are important only insofar as they affect these out-
comes’’ (p. 510).
We examine impacts on neonatal mortality because it is
commonly linked to the health environment during preg-
nancy; it is therefore plausible that FSP transfers may have
been a factor. Estimates from Almond, Chay, and Lee
(2005) indicate that a 1 pound increase in birth weight
causes neonatal mortality to fall by 7 deaths per 1,000
births, or 24%. Postneonatal mortality, by contrast, is
viewed as being more determined by postbirth factors.10
This discussion suggests that we would expect FSP to
affect birth weight and neonatal mortality but not necessarily
gestational length. One obvious channel for food stamp
impacts is through improvements in nutrition. The introduc-
tion of the FSP transfer increases total family resources and is
predicted to increase the quality and quantity of food con-
sumed, thereby leading to improvements in infant health. The
increased transfer income could also encourage behaviors that
could harm infant health, such as smoking or drinking.11
Health improvements may work through other channels as
well, for instance, reducing stress (such as financial stress)
experienced by the mother, which itself may have a direct
impact on birth weight. We explore these issues by separately
testing for FSP impacts on length of gestation and birth weight
and by exploring the sensitivity of our impact estimates to the
timing of FSP assignment by pregnancy trimester.
Overall, we expect that access to the FSP should improve
infant health. The same forces that improve infant health,
however, could also lead to a change in the composition of
births. In particular, if improvements in fetal health lead to
fewer fetal deaths, there could be a negative compositional
effect on birth weight from the improved survivability of
marginal fetuses. This could bias downward the estimated
9 See the literature review of Rush et al. (1980). For example, the cohort
exposed to the Dutch famine in the third trimester had lower average birth
weight than cohorts exposed earlier in pregnancy (Painter, Rosebooma, &
Bleker, 2005).
10 The initial health at birth is generally much better among infants who
die in the postneonatal period than among infants dying in the first month
of life. For example, while 72% of all neonatal deaths had a low birth
weight (below 2,500 grams), only 20% of all postneonatal deaths were
low-birth-weight infants (Starfield, 1985). Postneonatal deaths tend to be
caused by negative events after birth, most often by infectious diseases
and accidents (Grossman & Jacobowitz, 1981). Further, postneonatal
deaths may be more responsive to hospital access than neonatal deaths
(see Almond, Chay, & Greenstone, 2007).
11 Although recipients cannot purchase cigarettes directly with FSP
benefits, the increase in resources to the household may increase cigarette
consumption, which would work to reduce birth weight.
391INSIDE THE WAR ON POVERTY
effects of the FSP on birth weight and infant mortality.12 In
addition, if FSP introduction leads to increases in fertility
for disadvantaged women, this could also lead to negative
compositional effect and a subsequent downward bias on
the estimates.13 To evaluate such channels, we test for
impacts of the FSP on total births (finding no effect).
V. Data
The data for our analysis are combined from several
sources. The key treatment or policy variable is the month
and year that each county implemented a food stamp pro-
gram, which comes from USDA annual reports on county
food stamp caseloads (USDA, various years). These adminis-
trative FSP data are combined with two microdata sets on
births and deaths from the National Center for Health Statis-
tics. In some cases, we augment the core microdata with digi-
tized print vital statistics documents to extend analysis to the
years preceding the beginning of the microdata. These data
are merged with other county-level data from several sources.
A. Vital Statistics Natality Data
These data are coded from birth certificates and are avail-
able beginning in 1968. Depending on the state-year, these
data are either a 100% or 50% sample of births, and there
are about 2 million observations per year. Reported birth
outcomes include birth weight, gender, plurality, and (in
some state-years) gestational length. Data on the month and
county of birth permit linkage of natality outcomes to the
month the FSP was introduced in a given county. There are
also (limited) demographic variables, including age and race
of the mother and (in some states and years) mother’s educa-
tion and marital status. Online appendix table 1 provides
information on the availability of these variables over time.
We use the natality data and collapse the data to county-
race-quarter cells covering the years 1968 to 1977. We use
quarters (rather than months) to keep the sample size man-
ageable. The results are unchanged if we instead use county-
race-month cells. We end the sample in 1977, two years after
all counties have implemented the FSP and before the pro-
gram changes enacted in 1978 led to increases in take-up.
Unfortunately, natality microdata are available only
beginning in 1968. By 1968, half of the population lived in
counties with on FSP in place. In the interest of examining
the full FSP rollout, we obtained annual print vital statistics
documents and digitized the available data. With these print
documents, we augment the microdata with counts of the
total number of births by county and year (not available by
race) for 1959 to 1967 and counts of births by birth weight
ranges by state, race and year (not available by county) for
1959 to 1967.14
B. Vital Statistics Death Data
These data are coded from death certificates and are
available beginning in 1959. The data encompass the uni-
verse of death certificates (except in 1972, when they are a
50% sample) and report the age and race of the decedent,
the cause of death, and the month and county of death. We
collapse the data to county-race-quarter cells covering the
years 1959 to 1977.
Our mortality measure is the neonatal mortality rate,
defined as deaths in the first 28 days of life per 1,000 live
births. We focus on deaths from all causes, as this gives us
the most power (further cutting of the county-quarter-race
cells by detailed cause of death leads to many very thin
cells) and is unaffected by changes in the coding of cause
of death (conversion from ICD-7 to ICD-8) in 1968. We
have attempted to identify causes of death that could be
affected by nutritional deficiencies and also present results
for these and other deaths.15 We consider nutritional causes
both because the FSP was targeted at those in nutritional
risk and widespread concerns about nutritional status
among the poor during this period. Online appendix table 2
lists the broad categories for cause of death.
Our main neonatal results use the natality microdata to
form the denominator (live births in the same county-race-
quarter). This limits the sample to the years 1968 to 1977.
In an extension, we use the digitized vital statistics docu-
ments and county-year counts of births to construct the
denominator for live births and therefore neonatal death
rates (for all races) for 1959 to 1977.16
C. County Population Data
The SEER population data are used to construct esti-
mates of the population of women ages 15 to 44 by county-
race-year.17 These are used with the natality data to con-
12 The estimates described in table 5 imply an imprecise 1% to 2%
increase in the number of births among the treated. If we assume this
increase is accounted for by reductions in early prenatal (embryonic) mor-
tality, only to appear as deaths after birth during infancy, this would imply
nearly a doubling of the infant mortality rate, which stood close to 2%
nationally in 1970. Such an increase is not observed and would obviously
overwhelm any reductions in infant mortality among those who would
have survived until birth absent the FSP. That said, our data clearly do
not allow us to distinguish between births that reflect a prevented embryo-
nic or fetal death versus induced conceptions. But the magnitudes
involved suggest that postponement of intrauterine mortality to the first
year of life could not have been the norm or the infant mortality rate
would have risen substantially. Thus, if we take the table 5 point estimates
at face value (despite the large standard errors), either mortality was post-
poned beyond infancy or the number of conceptions increased.
13 The existing literature suggests that the elasticity of fertility with
respect to additional transfers from income support programs is very
small (Moffitt, 1998).
14 For historical vital statistics documents, see http://www.cdc.gov/
nchs/products/pubs/pubd/vsus/1963/1963.htm.
15 We thank Karen Norberg for helping us identify the cause of death
classifications. We are responsible for any classification errors.
16 We need quarterly births by race-county to match the quarterly
deaths in the numerator. We use the distribution of births by quarter for
each county in 1968 and assume that quarterly pattern holds for all years
1959–1967. In practice the ‘‘seasonality’’ of births across quarters is mini-
mal.
17 See National Cancer Institute, http://seer.cancer.gov/popdata/
download.html.
392 THE REVIEW OF ECONOMICS AND STATISTICS
struct fertility rates, defined as births per 1,000 women ages
15 to 44. Our main results use fertility rates by county-race-
quarter for 1968 to 1977. We also use the digitized annual
counts of births by county to construct fertility rates by
county-year (not race, not quarter) for the full period 1959
to 1977.
D. County Control Variables
The 1960 City and County Data Book, which compiles
data from the 1960 Census of Population and Census of
Agriculture, is used to measure economic, demographic,
and agricultural variables for the counties’ pretreatment
(before FSP is rolled out) period. In particular, we use the
percentage of the 1960 population that lives in an urban
area, is black, is less than 5 years old, is 65 years or over,
has income less than $3,000 (in 1959 dollars), the percen-
tage of land in the county that is farmland, and log of the
county population. We use the Bureau of Economic Analy-
sis, Regional Economic Information System (REIS) data to
construct annual, county real per capita income, and gov-
ernment transfers to individuals, including cash public
assistance benefits (Aid to Families with Dependent Chil-
dren AFDC; Supplemental Security Income, SSI; and Gen-
eral Assistance), medical spending (Medicare and military
health care), and cash retirement and disability payments.18
These data are available electronically beginning in 1968.
We extended the REIS data to 1959 by hand-entering data
from microfiche for 1959, 1962, and 1965 to 1968.19
VI. Methodology
We estimate the impact of the introduction of the FSP on
county-level birth outcomes, infant mortality, and fertility,
separately by race. Specifically, we estimate the following
model:
Yct ¼ aþ dFSPct þ bCB60c � tþ cXct
þ gc þ dt þ lst þ ect: ð1Þ
Yct (race suppressed) is a measure of infant health or fer-
tility defined in county c at time t. In all specifications, we
include unrestricted fixed effects for county gc and time dt.
We examine the sensitivity to including state-by-year fixed
effects lst or county-specific linear time trends, which are
not shown in equation (1).
FSPct is the food stamp treatment variable equal to 1 if
the county has a food stamp program in place. The timing
of the treatment dummy depends on the particular outcome
variable used. For the analysis of births, we assign FSP ¼ 1
if there is an FSP in place at the beginning of the quarter
prior to birth to proxy for beginning of the third trimester.20
We assign the treatment at the beginning of the third trime-
ster following the evidence that this period is the most
important for determining birth weight. However, we
explore the sensitivity to changing the timing of the FSP
treatment. Neonatal deaths are thought to be tied primarily
to prenatal conditions, and we therefore use the same FSP
timing (we use the age at death and measure the FSP as of
three months prior to birth, to proxy for the beginning of
the third trimester). We have less guidance for the correct
timing for FSP treatment for fertility; we explore FSP avail-
ability between three quarters prior to birth (to proxy for
conception) and seven quarters prior to birth.
The vector Xct contains the annual county-level controls
from the REIS, including real per capita transfers and the
log of real annual county per capita income. CB60c are the
1960 county characteristics, which we interact with a linear
time trend to control for differential trends in health out-
comes that might be correlated with the timing of FSP
adoption.
We consider several outcome variables in our main spe-
cifications. First, using the natality data, we measure infant
health at birth as continuous mean birth weight in grams
and fraction low birth weight (less than 2,500 grams, or
about 5.5 pounds). These measures are means within
county-race-quarter. Second, using the mortality data, we
examine impacts on neonatal mortality rates (per 1,000 live
births) for all causes and for those likely to be affected by
nutritional deficiencies.
All estimates are weighted using the number of births in
the county-race-quarter, and the standard errors are clus-
tered by county. Further, to protect against estimation pro-
blems associated with thinness in the data, for the natality
(mortality) analysis, we drop all county-race-quarter cells
where there are fewer than 25 (50) births.21 The results are
not sensitive to this sample selection. We also drop Alaska
because of difficulties in matching FSP service areas with
counties.
18 Beginning in 1969, the REIS data permit more detailed categories for
tabulating government transfers (including the ability to capture Medicaid
spending). However, because the natality data begin in 1968 and the mor-
tality data begin in 1959, we have adopted these three categories. In ana-
lyses of the data limited to 1969 and after, the results are robust to adding
more detailed categories. The REIS data also measure food stamp transfer
payments, but for obvious reasons, we do not use this as a control in our
model. We have, however, used the REIS data as a check on our USDA-
measured county food stamp start dates. REIS-measured per capita spend-
ing on FSP sharply increases precisely at the USDA-measured implemen-
tation date. In the year prior to FSP introduction, 99% of counties report
no spending on FSP; in the year of introduction, this falls to 1.3% and is
less than 0.3% in subsequent years (online appendix table 3).
19 We used linear interpolation to fill in the missing years. We thank
Gary Kennedy of the Bureau of Economic Analysis for providing the
REIS data microfiche.
20 To be precise, because we collapse the data to the county-quarter, the
FSP variable can sometimes equal something other than a 0 or 1. The
natality data are available at the monthly level, and we use that to assign
FSP status as of three months prior to birth (proxy for beginning of the
third trimester). When the data are collapsed to the county-quarter, this
policy variable is averaged among the three months of observations in
that cell. Therefore, the policy variable ranges from 0 to 1, with most
values at 0 or 1.
21 Neonatal mortality rates average 12 (19) per 1,000 births for whites
(blacks) during our sample period. We use a higher threshold for the mor-
tality analysis because of the low incidence of infant mortality.
393INSIDE THE WAR ON POVERTY
VII. Results for Natality
Table 1 presents the main results for mean birth weight
and the fraction of births that are low birth weight (LBW)
for 1968 to 1977. Results are presented separately for whites
and blacks. For each outcome, we report estimates from four
specifications with different controls. Column 1 includes
county and time (year � quarter) fixed effects, county per
capita income, REIS county-level per capita transfers, and
1960 county characteristics interacted with linear time. The
remaining columns control for trends in three ways: column
2 with state-specific linear time trends, column 3 with
unrestricted state-by-year fixed effects, and (4) with county-
specific linear time trends. In this and all subsequent tables,
the number of observations refers to county-quarter cells.22
The first four columns in panel A report the impact of hav-
ing FSP in place in the third trimester of pregnancy on mean
birth weight for births to white women. These columns indi-
cate a small, statistically significant increase in birth weight
for whites caused by exposure to FSP during the third trime-
ster. The results are extremely robust across specifications,
including controlling for county-specific linear time trends.
When the estimated coefficient is divided by mean birth
weight, the resulting effect size is a 0.06% to 0.08% increase
in birth weight, labeled in this and subsequent tables as ‘‘%
Impact (coef/mean)’’. As shown in panel B, the impact of
FSP exposure on birth weight is 50% to 150% larger for
blacks than whites. That, combined with a smaller average
birth weight for blacks, implies an impact between 0.1% and
0.2% on blacks (about twice the impact on whites).
Only a subset of women who give birth are likely to be
affected by FSP. While the coefficients reported are valid
estimates of the population impact of FSP, we also want to
know the impact among FSP recipients (treatment on the
treated). To calculate the implied impact on those who take
up the FSP, we divide the parameters by an estimate of the
FSP participation rate for this sample.23 We can inflate the
estimated effect by these participation rates for an estimate
of treatment on the treated. The results indicate that the
impact of FSP on participants’ birth weight (labeled
‘‘Estimate, inflated’’) is between 15 and 20 grams for whites
and 13 to 42 grams for blacks. The estimate expressed as a
percentage of mean birth weight (labeled ‘‘% Impact
inflated’’) is between 0.5% and 0.6% for whites and
between 0.4% and 1.4% for blacks.
TABLE 1.—IMPACTS OF FOOD STAMP INTRODUCTION ON BIRTH OUTCOMES, BY RACE
(1) (2) (3) (4) (5) (6) (7) (8)
Birth Weight (in Grams) Fraction below 2,500 Grams
A: Whites
Average FSP (0/1) 2.039 2.635 2.089 2.175 �0.0006 �0.0006 �0.0006 �0.0006
(0.947)* (0.896)** (1.039)* (0.975)** (0.0003)* (0.0003)* (0.0003)* (0.0004)
% impact (coef/mean) 0.06% 0.08% 0.06% 0.06% �1.02% �1.02% �0.97% �0.97%
Estimate inflated 15.68 20.27 16.07 16.73 �0.0047 �0.0047 �0.0045 �0.0045
% impact inflated 0.47% 0.61% 0.48% 0.50% �7.82% �7.82% �7.44% �7.44%
Observations 97,785 97,785 97,785 97,785 97,785 97,785 97,785 97,785
R2 0.54 0.55 0.55 0.56 0.17 0.17 0.18 0.19
Mean of dependent variable 3,350 3,350 3,350 3,350 0.06 0.06 0.06 0.06
B: Blacks
Average FSP (0/1) 3.454 4.120 5.466 1.665 �0.0015 �0.0016 �0.0019 �0.0009
(2.660) (2.317) (2.579)* (2.330) (0.0010) (0.0010) (0.0012) (0.0012)
% impact (coef/mean) 0.11% 0.13% 0.18% 0.05% �1.13% �1.22% �1.49% �0.68%
Estimate inflated 26.57 31.69 42.05 12.80 �0.0113 �0.0122 �0.0149 �0.0068
% impact inflated 0.86% 1.02% 1.36% 0.41% �8.70% �9.41% �11.48% �5.21%
Observations 27,374 27,374 27,374 27,374 27,374 27,374 27,374 27,374
R2 0.32 0.33 0.34 0.35 0.15 0.15 0.17 0.18
mean of Dependent variable 3,097 3,097 3,097 3,097 0.13 0.13 0.13 0.13
1960 CCDB � linear time X X X X X X
REIS controls X X X X X X X X
County per capita real income X X X X X X X X
Year quarter fixed effects X X X X X X X X
County fixed effects X X X X X X X X
State � linear time X X
State � year fixed effects X X
County � linear time X X
Each parameter is from a separate regression of the outcome variable on the food stamp implementation dummy. The treatment is assigned as of three months prior to birth (proxy for beginning of the third trime-
ster). The estimation sample includes means by race-county-quarter for years including 1968–1977 where cells with fewer than 25 births are dropped. In addition to the fixed effects, controls include 1960 county vari-
ables (log of population, percentage of land in farming, percentage of population black, urban, age below 5, age above 65, and with income less than $3,000), each interacted with a linear time trend, per capita county
transfer income (public assistance, medical care, and retirement and disability benefits), and county real per capita income. Estimates are weighted using the number of births in the cell and are clustered on county.
Standard errors are in parentheses. Inflated impacts divide the parameter estimate by an estimate of the food stamp participation rate for the regression sample.
22 Note that with 3,142 counties and 40 quarters of data, the maximum
number of observations would be about 125,000. As described above, we
drop cells with fewer than 25 births. This reduces the sample of blacks
much more than whites because blacks are more geographically concen-
trated. Despite dropping many counties, this sample represents 98% of
white births and 94% of black births.
23 We do not have information about food stamp participation in the
natality data or sufficient data to impute eligibility (for example, income).
Instead, we use the 1980 Current Population Survey and calculate FSP
participation rates for women with a child under 5 years old. (Participa-
tion rates look very similar if we alternatively use the presence of a child
below age 1 or 3.) The estimated participation rate for women with young
children (under age 5) is 0.13 for whites and 0.41 for blacks.
394 THE REVIEW OF ECONOMICS AND STATISTICS
The results for birth weight (and the other outcomes
described below) are very robust to adding more controls to
the model. We view the specification with state-by-year
unrestricted fixed effects as very encouraging, as we have
controlled for a whole host of possibly contemporaneous
changes to labor markets, government programs, and other
things that vary at the state-year level. While not shown
here, the county-level variables for government transfers
and pretreatment variables do little to change the results.
This provides further evidence that the food stamp rollout is
exogenous, thereby validating the research design. Finally,
we also find the results robust to adding county linear time
trends (with some reduction for blacks). On the downside,
the poor explanatory power of our control variables in pre-
dicting the timing of FSP (described in section II) means
that the precision of our impact estimates is not noticeably
improved by including these regression controls. For the
remainder of the tables, we adopt the specification with
state-by-year fixed effects as our base case specification.
Results (not presented here) are the same if log of birth
weight is used as the dependent variable instead.
Columns 5 through 8 repeat the exercise, this time with the
fraction low birth weight (less than 2,500 grams) as the depen-
dent variable. Exposure to FSP reduces LBW by a statistically
significant 1% for whites (7–8% when inflated by participa-
tion rate) and a less precisely estimated 0.7% to 1.5% for
blacks (5% to 12% when inflated by participation rate).
To further investigate the impact of the FSP on the distri-
bution of birth weight, we estimated a series of models
relating FSP introduction to the probability that birth weight
is below a given gram threshold: 1,500; 2,000; 2,500;
3,000; 3,250; 3,500; 3,750; 4,000; 4,500 (Duflo 2001). We
use the specification in column 3 with state-by-year fixed
effects; the estimates and 95% confidence intervals are pre-
sented in Figure 3 (we plot ‘‘% Impacts [coef/mean]’’ not
inflated by program participation). Figure 3A displays the
results and confidence intervals for whites. We find that the
largest percentage reduction in probability of birth weight
below a certain threshold comes at very low thresholds of
1,500 and 2,000 grams. The impacts become gradually
smaller as the birth weight threshold is increased to 2,500
grams and above, until there is no difference for births
below 3,750 grams. Results are larger for blacks (figure
3B), showing a 6% decrease in the probability of a birth less
than 1,500 grams, and an impact that declines at higher
birth weights.24
Online appendix table 4 presents estimates for three addi-
tional outcome variables: the fraction of births that are less
than 1,500 grams, have gestation length less than 37 weeks
(preterm births), and are female. These results show that
FSP leads to a small and statistically insignificant decrease
in preterm births and the fraction of births that are female.
While small they are and statistically insignificant, this is
consistent with recent work finding that prenatal nutritional
deprivation tips the sex ratio in favor of girls (Mathews,
Johnson, & Neil, 2008).25
One limitation of these results is that microdata on births
by county are available only starting in 1968, at which point
almost half of the population was already covered by the
24 In order to gauge the magnitude of these effects, it is useful to com-
pare the estimated effects to those implied by the previous literature. Cra-
mer (1995) finds that a 1% change in the income-to-poverty ratio leads to
a 1.05 gram increase in mean birth weight. The Hoynes and Schanzen-
bach (2009) estimates of the magnitude of food stamp benefits are $1,900
annually for participants (in 2005 dollars). Scaling those to match the
units available in the literature (and treating FSP benefits as their face-
value cash equivalent) implies that food stamps increased the family
income-to-poverty ratio of participants by 15%. The implied treatment-
on-treated effect would therefore be approximately 16 grams, which is
quite similar to the effects found in table 1.
FIGURE 3.—EFFECTS OF FSP IMPLEMENTATION ON DISTRIBUTION OF BIRTH WEIGHT,
PERCENTAGE IMPACTS (COEFFICIENT/MEAN)
The graph shows estimates and 95% confidence intervals for the estimate of the impact of FSP imple-
mentation on the fraction of births in the county-quarter cell that is below each specified number of
grams. The specification is given by column 3 in table 1.
25 In results not shown here, we find that birth-weight models are little
changed by controlling for gestation (known as an IUG model). We also
estimated models where the dependent variable is the fraction of births
below a gestation-varying threshold (known as small-for-gestational-age
models; Fenton, 2003). These models yielded results very similar to the
LBW regressions.
395INSIDE THE WAR ON POVERTY
FSP. In online appendix table 5 we use data from 1959 to
1977 to examine the impact of the FSP rollout on low birth
weight and very low birth weight. To push the period back
to 1959, we are limited to use of data at the state-race-year
level (see the discussion in section V). Controls include
state and year fixed effects, REIS variables, and state-speci-
fic linear time trends; standard errors are clustered on
state.26 We first present results for 1968 to 1977, where the
data are identical to those used in table 1 but are collapsed
to the state level. The results show imprecise but qualita-
tively similar effects of FSP measured with this noisier
treatment variable. (For example, the county analysis in
table 1 shows a �1.0 percent impact on LBW for whites
and �1.5 percent for blacks compared to �0.4 percent for
whites and �1.6 percent for blacks for the state and year
data in online appendix table 5). We then show the results
for the full period (1959–1977) and the post-pilot program
period (1964–1977). Whenever estimating models for the
full FSP ramp-up period, we look separately at the period
from 1964 because the pilot counties were clearly not exo-
geneously chosen. Using these earlier (but more aggre-
gated) data, we get qualitatively similar (and statistically
indistinguishable) results across the different time periods,
suggesting that missing the pre-1968 period in our main
results may not qualitatively affect our conclusions.
A. Impacts by Likelihood of Treatment
We next explore whether the impacts of the FSP are lar-
ger among subsets of the sample that are more likely to be
affected by the FSP. The natality data include education of
the mother and presence of the father, but because of miss-
ing data (not all states collected this information in earlier
years), we lose a substantial fraction of the sample (see,
online appendix table 1). Nonetheless, we have estimated
models by age of mother, education of mother, and pre-
sence of the father (results not shown). Overall, the results
showed that the impacts are larger for older mothers (age
25 and over). None of the education results are statistically
significant. This analysis did reveal that black mothers with
no father present experience much larger impacts than all
black women. This is consistent with the high participation
rates among this group (0.70 compared to 0.50 for all
blacks).
In lieu of detailed demographic variables, in table 2 we
break counties into quartiles based on 1970 poverty rates,
where we expect larger impacts in high-poverty counties.
The results are quite striking: the gains are concentrated in
the highest-poverty counties. Large, statistically significant
effects are present in the highest-quartile poverty counties,
while smaller and insignificant effects are presents in the
lowest-poverty counties. (Due to the relatively large stan-
dard errors, we cannot reject that they are equal.)
There is some suggestion in the historical accounts that
the impact might be different across geographic regions or
might differ by race across regions. In particular, participa-
tion in the program in the early years (after the county’s
initial adoption of FSP) was probably higher in urban coun-
ties and in the North. Barriers to accessing food stamps
might have also differed between North and South and may
have interacted with race (Citizens’ Board, 1968). Table 3
shows that the impact of FSP is larger and more statistically
significant for both blacks and whites in urban counties.
Interestingly, blacks appear to have larger effects outside
the South, while whites appear to have larger effects in the
South. These differences parallel the regional trends: Blacks
TABLE 2.—IMPACT OF FOOD STAMP INTRODUCTION ON BIRTH OUTCOMES, BY QUARTILE OF POVERTY RATES
(1) (2) (3) (4)
Low-Poverty Counties (Lowest Quartile) High-Poverty Counties (Highest Quartile)
Birth Weight Low Birth Weight Birth Weight Low Birth Weight
Average FSP (0/1) 1.871 �0.001 3.409* �0.0012*
(2.013) (0.001) (1.750) (0.0006)
% impact (coef/mean) 0.06% �1.23% 0.10% �1.50%
Observations 8,339 8,339 56,055 56,055
R2 0.78 0.38 0.56 0.26
Mean of dependent variable 3333 0.07 3303 0.08
Subsample population 0.23 0.23 0.26 0.26
1960 CCDB � linear time X X X X
REIS controls X X X X
County per capita real income X X X X
Year � quarter fixed effects X X X X
County fixed effects X X X X
State � year fixed effects X X X X
Each parameter is from a separate regression of the outcome variable on the food stamp implementation dummy. The treatment is assigned as of three months prior to birth. The estimation sample includes means
by county-quarter for years including 1968–1977 where cells with fewer than 25 births are dropped. Controls include county, year � quarter and state � year fixed effects, 1960 county variables (log of population,
percentage of land in farming, percentage of population black, urban, under age 5, over age 65 and with income less than $3,000), each interacted with a linear time trend, per capita county transfer income (public
assistance, medical care, and retirement and disability benefits), and county real per capita income. Estimates are weighted using the number of births in the cell and are clustered on county. Standard errors are in par-
entheses. Inflated impacts divide the parameter estimate by an estimate of the food stamp participation rate for the regression sample. Quartiles are assigned using 1970 county poverty rates (weighted using county
population).
26 To construct state-level FSP treatment, we use the 1968 counts of
number of births by county-month and calculate (for each state and year
using the program variables) the percentage of births in the state that were
in counties with FSP in place three months prior to birth.
396 THE REVIEW OF ECONOMICS AND STATISTICS
saw larger reductions in low birth weight (and neonatal
mortality) in the North, while whites saw larger declines in
the South. The FSP impacts by South/non-South, however,
are less precisely estimated than the results by urban/nonur-
ban.27
B. Investigation of the Timing of Impacts
To explore the possible channels for the impacts of the
FSP transfer, table 4 reestimates the mean birth weight
models varying the timing of the exposure to the FSP. The
baseline specification—reprinted from column 3 of table
1—assigns the policy introduction as three months prior to
birth, to proxy for beginning of the third trimester. Columns
2 and 3 of table 4 moves assignment of FSP treatment to
two and three quarters before birth, respectively. Moving
the treatment from third to second trimester reduces the
impact of FSP substantially, though there is still a statisti-
cally significant impact on birth weight for blacks. Further-
more, assigning treatment at three quarters before birth
(proxy for conception) yields even smaller and statistically
insignificant impacts. The results in columns 4 and 5 show
that conditional on third-trimester exposure, additional
exposure earlier in the pregnancy has no additional benefits.
Similar results are found for fraction low and very low birth
weight. Recalling from section IV that the medical litera-
ture suggests that nutrition has its greatest impact on birth
weight during the third trimester, we view these estimates
as suggestive that nutrition is playing an important channel
for the FSP transfer’s benefits. In addition, these results pro-
vide evidence that our model is not simply capturing a spur-
ious correlation between FSP introduction and trends in
infant outcomes at the county level.28
To further test for spurious trending in the county birth
outcomes that might be loading on to FSP, we include a
one-year lead of the policy variable for each of the birth
outcome variables in online appendix table 6. There is no
impact of the policy lead, and the results for the main policy
variable are qualitatively unchanged.
As described above, we use the month that the county
implemented the FSP to measure food stamp availability
during these pregnancies. If there was a lag in ramping up
county food stamp programs, then our difference-in-differ-
ence estimates will underestimate the true (eventual) pro-
gram impacts. The administrative ramp-up was aided by the
fact that the new FSP offices were often set up in the same
building as the county welfare office. To directly evaluate
the ramp-up in FSP operations, figure 4 shows food stamp
caseloads per capita by year relative to start year (the case-
load data are available only by year). The figure separately
plots caseloads for counties beginning operations in the first
half versus second half of the caseload reporting year. This
TABLE 3.—IMPACTS OF FSP INTRODUCTION ON INFANT OUTCOMES, BY GEOGRAPHY
(1) (2) (3) (4) (5) (6) (7) (8)
South Non-South Urban Counties Nonurban Counties
Birth Weight LBW Birth Weight LBW Birth Weight LBW Birth Weight LBW
A: Whites
Avearage FSP (0/1) 2.403 �0.0011 1.771 �0.0003 2.364 �0.0008 0.508 �0.0002
(1.612) (0.0005)** (1.322) (0.0004) (1.247)* (0.0004)** (1.615) (0.0006)
% impact (coef/mean) 0.07% �1.57% 0.05% �0.48% 0.07% �1.13% 0.02% �0.25%
Observations 44,194 44,194 53,591 53,591 32,282 32,282 65,503 65,503
Subsample population 0.29 0.29 0.69 0.69 0.73 0.73 0.25 0.25
B: Blacks
Average FSP (0/1) 3.527 �0.0023 7.003 �0.0009 8.371 �0.0034 �0.745 0.0023
(3.134) (0.0014)* (3.992)* (0.0022) (2.846)** (0.0013)** (5.219) (0.0023)
% impact (coef/mean) 0.11% �1.76% 0.23% �0.69% 0.27% �2.59% �0.02% 1.74%
Observations 20,837 20,837 6,537 6,537 13,090 13,090 14,284 14,284
Subsample population 0.49 0.49 0.45 0.45 0.77 0.77 0.17 0.17
1960 CCDB � linear time X X X X X X X X
REIS controls X X X X X X X X
County per capita real income X X X X X X X X
Year � quarter fixed effects X X X X X X X X
County fixed effects X X X X X X X X
State � year fixed effects X X X X X X X X
Each parameter is from a separate regression of the outcome variable on the food stamp implementation dummy. The treatment is assigned as of the three months prior to birth. The estimation sample includes
means by county-quarter for years including 1968–1977 where cells with fewer than 25 births are dropped. Controls include county, year � quarter and state � year fixed effects, 1960 county variables (log of popula-
tion, percentage of land in farming, percentage of population black, urban, under age 5, over age 65, and with income less than $3,000), each interacted with a linear time trend, per capita county transfer income
(public assistance, medical care, and retirement and disability benefits), and county real per capita income. Estimates are weighted using the number of births in the cell and are clustered on county. Standard errors
are in parentheses. Inflated impacts divide the parameter estimate by an estimate of the food stamp participation rate for the regression sample. Subsample population reports the percentage of total births that are
included in the regression. Urban counties are defined as those with greater than 50% of the 1960 population living in an urban area.
27 We define the county as urban if more than 50% of the 1960 popula-
tion in the county lives in an urban area.
28 Note that the reduction in the magnitude of the birth-weight impact
may explain the difference between our results and those of Currie and
Moretti (2008). Their study of birth outcomes in California assigned the
FSP treatment nine months prior to birth and found comparatively limited
impacts on birth weight. Another explanation for larger effects in the third
trimester is if initial FSP participation is concentrated there (rather than
earlier).
397INSIDE THE WAR ON POVERTY
figure suggests that rapid ramp-up was achieved and that
the ramp-up is only slightly faster in the counties with more
lead time (implementation earlier in the year). Further, note
that over half of the ‘‘steady-state’’ caseload is achieved in
the first year, even for counties that begin operation late in
the reporting year.
TABLE 4.—SENSITIVITY OF BIRTH WEIGHT OUTCOMES TO CHANGING THE TIMING OF THE POLICY INTRODUCTION
(1) (2) (3) (4) (5)
Main Policy Effect:
FSP—Beginning of
Third Trimester
FSP—Beginning of
Second Trimester
FSP—Beginning of
First Trimester
FSP—Beginning of
Third Trimester
FSP—Beginning of
Third Trimester
Second Policy Effect: – – –
FSP—Beginning of
Second Trimester
FSP—Beginning of
First Trimester
A: Whites
Average FSP (0/1) 2.085 1.696 1.288 2.556 2.434
(1.020)** (1.024)* (0.993) (1.640) (1.268)*
Average FSP (0/1) – – – �0.533 �0.454
Second policy variable (1.650) (1.232)
Observations 97,785 97,785 97,785 97,785 97,785
R2 0.55 0.55 0.55 0.55 0.55
Mean of dependent variable 3,350 3,350 3,350 3,350 3,350
B: Blacks
Average FSP (0/1) 5.447 4.704 2.071 5.334 8.108
(2.532)** (2.464)* (2.396) (4.596) (3.444)**
Average FSP (0/1) – – – 0.130 �3.515
Second policy variable (4.450) (3.268)
Observations 27,374 27,374 27,374 27,374 27,374
R2 0.34 0.34 0.34 0.34 0.34
Mean of dependent variable 3,097 3,097 3,097 3,097 3,097
1960 CCDB � linear time X X X X X
REIS controls X X X X X
County per capita real income X X X X X
Year � quarter fixed effects X X X X X
County fixed effects X X X X X
State � year fixed effects X X X X X
Dependent variable is equal to birth weight in grams. Each parameter is from a separate regression of the outcome variable on the food stamp implementation dummy. The specifications vary by changing the tim-
ing of food stamp implementation. Base case is in column 1, where the timing is as of three months prior to the birth (to proxy for beginning of the third trimester). The alternative specifications include timing as of
six months (second trimester) or nine months (first trimester) prior to birth. In specifications 4, we estimate jointly the treatment effects at the third and second trimesters, and in column 5, we estimate jointly the
impacts measured at the third and first trimesters. All of the other control variables and sample definitions are described in the notes to table 1.
FIGURE 4.—PERCENTAGE OF COUNTY POPULATION ON FOOD STAMPS BY NUMBER OF YEARS SINCE PROGRAM START
The graph is an unweighted regression of county-year food stamp caseloads on a series of dummy variables tracking year relative to county FSP implementation year. County caseload is expressed as a share of the
1960 population. Source for caseload data is USDA (various years).
398 THE REVIEW OF ECONOMICS AND STATISTICS
C. Event Study
The pattern of estimates in table 4 suggests that the FSP
treatment effect is identified by the discrete jump in FSP at
implementation and its impact on birth weight. In particu-
lar, we showed in table 4 that as the timing of the treatment
is shifted earlier in pregnancy, the estimated FSP effect on
birth weight decreased substantially in magnitude. If instead
identification were coming from some other trends in
county outcomes that are correlated with FSP start month,
then we would expect less sensitivity in the results to the
trimester to which the FSP treatment is assigned. However,
there remains a concern that our results are driven by trends
in county birth outcomes that are correlated with FSP
implementation in a way that county linear trends do not
capture.
This proposition can be evaluated more directly in an
event study analysis. Specifically, we fit the following equa-
tion,
Yct ¼ aþ
X8
i¼�6
pi1ðsct ¼ iÞ þ gc þ dt
þcXct þ /c � tþ ect; ð2Þ
where sct denotes the event quarter, defined so that s ¼ 0
for births that occur in the same quarter as the FSP began
operation in that county, s ¼ 1 for births one quarter after
the FSP began operation, and so on. For s � � 1, pregnan-
cies were untreated by a local program (births were before
the program started). The coefficients are measured relative
to the omitted coefficient (s ¼ �2).29 Our event study
model includes fixed effects for county and time, county
REIS variables, and county-specific linear time trends.
In order to eliminate potential compositional effects, we
restrict the sample to a balanced panel of counties having
births for all fifteen event quarters: six quarters before
implementation and eight quarters after. Because our natal-
ity data begin with January 1968, this means we exclude
from the event study analysis all counties with an FSP
before July 1969.
Figure 5 plots the event and quarter coefficients from
estimating equation (2) on the fraction of low-birth-weight
births. The figure also reports the number of county and
quarter observations in the balanced sample and the differ-
ence-in-difference estimate on this sample.30 Panel A
reports estimates for blacks and panel B for whites. These
figures show an absence of a strong pretrend and evidence
of a trend break at the quarter the FSP is introduced, imply-
ing an improvement in infant outcomes. That such a prompt
increase in birth weight is observed with FSP inception
indicates that potential confounders would have to mimic
the timing of FSP rollout extremely closely. Not shown
here, the event study results are nearly identical if we
exclude the county controls, providing further evidence of
the exogeneity of the treatment. We view this as more evi-
dence of the validity of our identification strategy.31
D. Further Robustness Checks
The main results are robust to various additional specifi-
cation checks. One potential concern is that the FSP intro-
duction is correlated with unobserved county health invest-
ments (such as the expansion of access to hospitals in the
South as in Almond, Chay, and Greenstone 2007) and our
REIS controls fail to pick this up. To test this, we use the
natality data to estimate the impact of FSP implementation
on the fraction of births in a hospital or attended by a physi-
cian. These results indicate very small and statistically
insignificant improvements with FSP implementation
(online appendix table 7).
Finally, the same forces that improve infant health could
also lead to greater survival of low-birth-weight fetuses. In
addition, the FSP may lead to increased fertility among dis-
advantaged women (if children are a normal good). Both
factors, through endogeneous sample selection, could bias
the estimates downward. We consider this by evaluating
whether FSP introduction is associated with any change in
live births. The dependent variable is the number of births
in the race, county, and quarter divided by the number of
women aged 15 to 44, and the regressions are weighted by
the population of women in each cell. Table 5 presents sev-
eral estimates, which vary depending on the timing of the
FSP treatment: between three quarters prior to birth (proxy
for conception) and seven quarters prior to birth (one year
prior to conception). Across the table, we find positive but
very small and statistically insignificant effects of FSP on
births. When these point estimates are inflated by the FSP
participation rate, the estimate of the treatment on the trea-
ted is about 1% for whites and 2% for blacks. When we
stratify the results by quartiles of county poverty rates, we
also find small and statistically insignificant impacts among
those living in the highest poverty counties (online appen-
dix table 8).
VIII. Mortality Results
Table 6 shows the main results for neonatal mortality rate
for 1968 to 1977. We present three outcomes: death rate for
all causes, deaths possibly due to nutritional deficiencies,
29 Because of the discrete nature of the event study model, the s’s are
formed by aggregating months to a quarter. For example, if the FSP
started (or birth occurred) in January, February, or March 1970, then the
FSP started (or birth occurred) in 1970 quarter 1. Therefore when s ¼ 0
(birth quarter ¼ policy commencement quarter), the pregnancy could
actually have been treated for between zero and three months.
30 The difference-in-difference estimate is comparable to the results pre-
sented in table 1. We present them here because the samples used for the
event study differ from the main results (due to balancing of the sample).
31 Similar patterns are observed when the dependent variable is average
birth weight (online appendix figure 2) and the share of births below
1,500 grams (available on request).
399INSIDE THE WAR ON POVERTY
and other deaths (for definition see the data section and
online appendix table 2). Because neonatal deaths are
thought to be related primarily to prenatal conditions (parti-
cularly prior to major technological advances in neonatal
care in the 1970s and 1980s), we time the FSP treatment as
of a quarter prior to birth (to proxy for the beginning of the
third trimester). In these models, we drop any race-county-
quarter cell where there are fewer than fifty births. Results
are weighted by the number of births in the cell.
The neonatal mortality rate averages about twelve deaths
per 1,000 births for whites and nineteen for blacks, with
about half of the deaths where the cause of death indicates
those possibly affected by nutritional deficiencies. The
results for whites and blacks show that the FSP leads to a
reduction in infant mortality, with larger impacts for deaths
possibly affected by nutritional deficiencies. None of the
estimates, however, are statistically significant. Overall, the
effect of the treatment on the treated (percentage impact,
FIGURE 5.—EFFECTS OF FSP IMPLEMENTATION ON LOW BIRTH WEIGHT: RESULTS FOR EVENT STUDY ANALYSIS
Each figure plots coefficients from an event-study analysis. Coefficients are defined as quarters relative to the quarter the FSP is implemented in the county. The sample is a balanced county sample, where a county
is included only if there are six quarters of pre- and eight quarters of post-implementation data. The specification includes controls for county, county � linear time, quarter, 1960 county controls interacted with time,
county per capita transfers, and county real per capita income. The ‘‘diff-in-diff treatment effect’’ is comparable to the results presented in table 1. We present them here because the samples used for the event study
differ from the main results.
400 THE REVIEW OF ECONOMICS AND STATISTICS
inflated) for all causes is about 4% for whites and between
4% and 8% for blacks. These estimates are roughly in line
with the birth weight–neonatal mortality rate relationship
estimated by Almond et al. (2005): for whites, we estimate
a very similar birth weight-mortality relationship, although
the relationship between birth weight and mortality we esti-
mate for blacks is substantially stronger than in Almond
et al. (2005). Finally, we view the results for ‘‘other deaths’’
TABLE 6.—IMPACT OF FSP ON NEONATAL MORTALITY RATE (DEATHS PER 1,000 LIVE BIRTHS)
(1) (2) (3) (4) (5) (6) (7) (8) (9)
All Deaths Deaths Linked to Nutrition Other Deaths
A: Whites
Average FSP (0/1) �0.0625 �0.0158 �0.0806 �0.0492 �0.0784 �0.0376 �0.0133 0.0626 �0.0430
(0.1050) (0.1194) (0.1242) (0.0771) (0.0839) (0.0913) (0.0834) (0.0936) (0.0960)
% impact (coef / mean) �0.52% �0.13% �0.67% �0.79% �1.25% �0.60% �0.23% 1.09% �0.75%
% impact, inflated �4.01% �1.01% �5.17% �6.04% �9.63% �4.62% �1.79% 8.39% �5.76%
Observations 73,577 73,577 73,676 73,577 73,577 73,676 73,577 73,577 73,676
R2 0.16 0.16 0.18 0.10 0.11 0.13 0.12 0.12 0.15
Mean of dependent variable 12.00 12.00 12.00 6.26 6.26 6.26 5.74 5.74 5.74
B: Blacks
Average FSP (0/1) �0.3898 �0.0067 �0.6551 �0.4128 �0.3098 �0.4233 0.0231 0.3032 �0.2317
(0.4095) (0.4610) (0.4793) (0.2865) (0.2953) (0.3334) (0.2729) (0.3348) (0.2977)
% impact (coef / mean) �2.06% �0.04% �3.46% �4.58% �3.43% �4.69% 0.23% 3.06% �2.34%
% impact, inflated �4.47% �0.08% �7.52% �9.95% �7.47% �10.20% 0.51% 6.65% �5.08%
Observations 17,655 17,655 17,695 17,655 17,655 17,695 17,655 17,655 17,695
R2 0.42 0.44 0.43 0.34 0.36 0.36 0.26 0.29 0.28
Mean of dependent variable 18.94 18.94 18.94 9.02 9.02 9.02 9.91 9.91 9.91
1960 CCDB � linear time X X X X X X
REIS controls X X X X X X X X X
County per capita real income X X X X X X X X X
Year � quarter fixed effects X X X X X X X X X
County fixed effects X X X X X X X X X
State � linear time X X X
State � year fixed effects X X X
County � linear time X X X
Each parameter is from a separate regression of the neonatal mortality rate (deaths in first 28 days per 1,000 live births) on the FS implementation. The treatment is assigned as of three months prior to birth (proxy
for beginning of the third trimester). The sample includes means by race-county-quarter for years including 1968–1977 where cells with fewer than fifty births are dropped. In addition to the fixed effects, controls
include 1960 county variables (log of population, percentage of land in farming, percentage of population black, urban, below age 5, over age 65, and with income less than $3,000), each interacted with a linear time
trend, per capita county transfer income (public assistance, medical care, and retirement and disability benefits), and county real per capita income. Estimates are weighted using the number of births in the cell and
are clustered on county. Standard errors are in parentheses. Inflated impacts divide the parameter estimate by an estimate of the food stamp participation rate for the regression sample.
TABLE 5.—IMPACT OF FSP INTRODUCTION ON FERTILITY RATE (BIRTHS PER 1,000 WOMEN AGES 15–44)
(1) (2) (3) (4) (5)
FSP Implemented as of X Quarters prior to Birth
3 Quarters 4 Quarters 5 Quarters 6 Quarters 7 Quarters
A: Whites
Average FSP (0/1) 0.013 �0.004 0.007 0.031 0.035
(0.078) (0.074) (0.071) (0.074) (0.070)
% impact (coef/mean) 0.06% �0.02% 0.04% 0.16% 0.18%
% impact, inflated 0.50% �0.14% 0.28% 1.22% 1.40%
Observations 120,293 120,293 120,293 120,293 120,293
Mean of dependent variable 19.40 19.40 19.40 19.40 19.40
B: Blacks
Average FSP (0/1) 0.211 0.157 0.276 0.307 0.227
(0.221) (0.206) (0.193) (0.190) (0.183)
% impact (coef/mean) 0.80% 0.60% 1.05% 1.17% 0.86%
% impact, inflated 1.75% 1.30% 2.29% 2.54% 1.88%
Observations 44,044 44,044 44,044 44,044 44,044
Mean of dependent variable 26.24 26.24 26.24 26.24 26.24
1960 CCDB � linear time X X X X X
REIS controls X X X X X
County per capita real income X X X X X
Year � quarter fixed effects X X X X X
County fixed effects X X X X X
State � year fixed effects X X X X X
Each parameter is from a separate regression of the outcome variable on the food stamp implementation dummy. The columns vary by the timing of the FSP implementation. The estimation sample includes means
by race-county-quarter for 1968–1977. Controls include county, year-by-quarter and state-by-year fixed effects, 1960 county variables (log of population, percentage of land in farming, percentage of population
black, urban, under age 5, over age 65, and income less than $3,000), each interacted with a linear time trend, per capita county transfer income (public assistance, medical care, and retirement and disability benefits),
and county real per capita income. Estimates are weighted using the population in the cell and are clustered on county. Standard errors are in parentheses. Inflated impacts divide the parameter estimate by an estimate
of the food stamp participation rate for the regression sample.
401INSIDE THE WAR ON POVERTY
(not affected by nutritional deficiencies), which are opposite
signed and much smaller in magnitude (although again sta-
tistically significant), as favorable evidence that the mortal-
ity estimates are coming from the FSP. Online appendix
table 9 separates the mortality effects by quartiles of the
county poverty rate, and while imprecisely estimated finds
a negative effect in the highest-poverty counties but a posi-
tive one in the lowest-poverty counties that were unlikely to
experience a substantial FSP treatment.
Online appendix table 10 presents results for all races for
the full period from 1959. We are unable to present results
by race here because the denominator (live births by county
and time) is not available by race prior to 1968. The first
three columns replicate the results in table 6 for 1968 to
1977 for all races. In the subsequent columns (for 1959–
1977 and 1964–1977), we find results very similar to those
for 1968 to 1977. Overall, FSP implementation leads to a
reduction in neonatal mortality, although not statistically
significantly so.
IX. Interpretation and Conclusion
The uniformity of the FSP was designed to buffer the dis-
cretion states exercised in setting rules and benefit levels of
other antipoverty programs. This uniformity was deliber-
ately preserved through the major reforms to welfare under
the 1996 Personal Responsibility and Work Opportunity
Reconciliation Act (Currie, 2003). An unintended conse-
quence of this regularity has been to circumscribe the pol-
icy variation that researchers typically use to identify pro-
gram impacts. As a result, surprisingly little is known about
FSP effects.
In contrast to other major U.S. antipoverty programs, the
FSP was rolled out county by county. This feature of imple-
mentation allows us to separate the introduction of food
stamps from the other major policy changes of the late
1960s and early 1970s. Although FSP benefits were (and
are) paid in vouchers that themselves could be used only to
purchase food, because the voucher typically represented
less than households spent on food (covering just the
‘‘thrifty food plan’’), recipients were inframarginal and ben-
efits were essentially a cash transfer (Hoynes & Schanzen-
bach, 2009).
Across the board, our point estimates show that this near-
cash transfer improved infant outcomes. In particular, we
find increases in mean birth weight for whites and blacks,
with larger impacts estimated at the bottom of the birth
weight distribution (that is, low birth weight and very low
birth weight). Consistent with expectations, we find larger
birth weight effects for black mothers and those living in
high-poverty areas—populations where FSP participation is
more common. Consistent with epidemiological studies,
FSP availability in the third trimester had the largest birth
weight impact. We conclude that despite not targeting preg-
nant women, the introduction of the FSP increased birth
weight. This finding is all the more noteworthy given the
mixed success that randomized interventions have had in
raising birth weights (Rush, Stein, & Susser, 1980; Lumley
& Donohue, 2006).
While the point estimates for gestation length and neona-
tal mortality would also suggest improved health at birth,
estimated effects are imprecise, despite the large samples
from vital statistics data. One interpretation is that statistical
power is lost when analyzing gestation length (incomplete
reporting by states) and mortality (rare). Leaving the impre-
cision issue aside, gestation length and mortality appear less
affected than the likelihood of low and very low birth
weight.
At a minimum, our results indicate that the FSP had an
immediate first-stage impact on newborns. Furthermore,
these estimated impacts (as reflected by birth weight) are
much larger in high-poverty counties. Our findings reveal
that an exogenous increase in income during a well-defined
period, pregnancy, can improve infant health. Future work
should consider whether this FSP-induced birth weight
improvement is reflected in subsequent outcomes and how
poverty and birth weight may mediate this relationship.
REFERENCES
Acemoglu, Daron, David Autor, and David Lyle, ‘‘Women, War and
Wages: The Impact of Female Labor Supply on the Wage Struc-
ture at Mid-Century,’’ Journal of Political Economy, 112 (2004),
497–551.
Almond, Douglas, Kenneth Y. Chay, and Michael Greenstone, ‘‘Civil
Rights, the War on Poverty, and Black-White Convergence in
Infant Mortality in the Rural South and Mississippi,’’ MIT Depart-
ment of Economics working paper no. 07–04: (2007).
Almond, Douglas, Kenneth Y. Chay, and David S. Lee, ‘‘The Costs of
Low Birth Weight,’’ Quarterly Journal of Economics, 120 (2005),
1031–1084.
Baker, Kevin, ‘‘Do Cash Transfer Programs Improve Infant Health: Evi-
dence from the 1993 Expansion of the Earned Income Tax Credit,’’
manuscript, University of Notre Dame (2008).
Barker, D.J.P., Fetal and Infant Origins of Adult Disease (London: British
Medical Journal, 1992).
Bastiotis, P., C. S. Cramer-LeBlanc, and E. T. Kennedy, ‘‘Maintaining
Nutritional Security and Diet Quality: The Role of the Food Stamp
Program and WIC,’’ Family Economics and Nutritional Review,
11 (1998), 4–16.
Berry, Jeffrey M., Feeding Hungry People: Rulemaking in the Food
Stamp Program (New Brunswick, NJ: Rutgers University Press,
1984).
Black, Sandra E., Paul J. Devereux, and Kjell G. Salvanes, ‘‘From the
Cradle to the Labor Market? The Effect of Birth Weight on Adult
Outcomes,’’ Quarterly Journal of Economics 122 (2007), 409–
439.
Blank, Rebecca, ‘‘Evaluating Welfare Reform in the United States,’’ Jour-
nal of Economic Literature 40 (2002), 1105–1166.
Butler, J. S., and J. E. Raymond, ‘‘The Effect of the Food Stamp Program
on Nutrient Intake,’’ Economic Inquiry 34 (1996), 781–798.
Citizens’ Board of Inquiry into Hunger and Malnutrition in the United
States, Hunger, U.S.A. (Boston: Beacon Press, 1968).
Cramer, James, ‘‘Racial and Ethnic Differences in Birth Weight: The
Role of Income and Financial Assistance,’’ Demography 32
(1995), 231–247.
Currie, Janet, ‘‘Food and Nutrition Programs,’’ in Robert Moffitt (Ed.),
Means-Tested Transfer Programs in the U.S. (Cambridge, MA:
NBER, 2003).
——— ‘‘Healthy, Wealthy, and Wise: Socioeconomic Status, Poor
Health in Childhood, and Human Capital Development,’’ Journal
of Economic Literature 47 (2009), 87–122.
402 THE REVIEW OF ECONOMICS AND STATISTICS
Currie, Janet, and Nancy Cole, ‘‘Does Participation in Transfer Programs
during Pregnancy Improve Birth Weight?’’ NBER working paper
no. 3832 (1991).
——— ‘‘Welfare and Child Health: The Link between AFDC Participa-
tion and Birth Weight,’’ American Economic Review 83 (1993),
971–985.
Currie, Janet, Enrico Moretti, ‘‘Did the Introduction of Food Stamps
Affect Birth Outcomes in California?’’ in R. Schoeni, J. House, G.
Kaplan, and H. Pollack, (Eds.), Making Americans Healthier:
Social and Economic Policy as Health Policy, (New York: Russell
Sage Press, 2008).
Duflo, Esther, ‘‘Schooling and Labor Market Consequences of School
Construction in Indonesia: Evidence from an Unusual Policy
Experiment,’’ American Economic Review 91 (2001), 795–813.
Fenton, Tanis, ‘‘A New Growth Chart for Preterm Babies: Babson and Benda’s
Chart Updated with Recent Data and a New Format,’’ BMC Pediatrics
3:13 (2003), http://www.biomedcentral.com/1471¼2431/3/13.
Fraker, Thomas, ‘‘Effects of Food Stamps on Food Consumption: A
Review of the Literature’’ (Washington, DC: Mathematica Policy
Research, 1990).
Grossman, Michael, and Steven Jacobowitz, ‘‘Variations in Infant Mortal-
ity Rates among Counties of the United States: The Roles of Public
Policies and Programs,’’ Demography 18 (1981), 695–713.
Hoynes, Hilary W., and Diane Whitmore Schanzenbach, ‘‘Consumption
Responses to In-Kind Transfers: Evidence from the Introduction
of the Food Stamp Program,’’ American Economic Journal:
Applied Economics 1 (2009), 109–139.
Kehrer, Barbara H., and Charles M. Wolin, ‘‘Impact of Income Mainte-
nance on Low Birth Weight: Evidence from the Gary Experi-
ment,’’ Journal of Human Resources 14 (1979), 434–462.
Kramer, Michael S., ‘‘Intrauterine Growth and Gestational Determi-
nants,’’ Pediatrics 80 (1987a), 502–511.
——— ‘‘Determinants of Low Birth Weight: Methodological Assessment
and Meta-Analysis,’’ Bulletin of the World Health Organization 65
(1987b), 633–737.
Lumley, Judith, and Lisa Donohue, ‘‘Aiming to Increase Birth Weight: A
Randomised Trial of Pre-Pregnancy Information, Advice and
Counseling in Inner-Urban Melbourne,’’ BMC Public Health
6:299 (2006), http://www.biomedcentral.com/1471¼2458/6/299.
MacDonald, Maurice, Food, Stamps, and Income Maintenance (Madison,
WI: Institute for Poverty Research, 1977).
Mathews, Fiona, Paul J. Johnson, and Andrew Neil, ‘‘You Are What Your
Mother Eats: Evidence for Maternal Preconception Diet Influen-
cing Foetal Sex in Humans,’’ Proceedings of the Royal Society 275
(2008), 1661–1668.
Moffitt, Robert, ‘‘Incentive Effects of the US Welfare System,’’ Journal
of Economic Literature, 30 (1992), 1–61.
——— ‘‘The Effect of Welfare on Marriage and Fertility,’’ in Robert
Moffitt (Ed.), Welfare, the Family, and Reproductive Behavior,
(Washington, DC: National Research Council, 1998).
Painter, Rebecca C., Tessa J. Rosebooma, and Otto P. Bleker, ‘‘Prenatal
Exposure to the Dutch Famine and Disease in Later Life: An Over-
view,’’ Reproductive Toxicology 20 (2005), 345–352.
Ripley, Randall B., ‘‘Legislative Bargaining and the Food Stamp Act,
1964,’’ in Frederick N. Cleaveland, (Ed.), Congress and Urban
Problems: A Casebook on the Legislative Process (Washington,
DC: Brooking Institution, 1969).
Rush, David, Zena Stein, and Mervyn Susser, Diet in Pregnancy: A Ran-
domized Controlled Trial of Nutritional Supplements (New York:
Alan R. Liss, 1980).
Starfield, Barbara, ‘‘Postneonatal Mortality,’’ Annual Review of Public
Health 6 (1985), 21–40.
U.S. Congressional Budget Office, ‘‘The Food Stamp Program: Income or
Food Supplementation?’’ (Washington, DC: U.S. Government
Printing Office, 1977).
U.S. Department of Agriculture, ‘‘Food Stamp Program, Year-End Parti-
cipation and Bonus Coupons Issues,’’ technical report, Food and
Nutrition Service, (various years).
U.S. Department of Health, Education and Welfare, ‘‘Vital Statistics of
the United States, Volume I’’ (1959–1967).
403INSIDE THE WAR ON POVERTY
Copyright of Review of Economics & Statistics is the property of MIT Press and its content may not be copied
or emailed to multiple sites or posted to a listserv without the copyright holder’s express written permission.
However, users may print, download, or email articles for individual use.
Order an Essay Now & Get These Features For Free:
Turnitin Report
Formatting
Title Page
Citation
Outline
