The Review of Economics and StatisticsVOL. 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 initiativeof the War on Poverty: the introduction of the modern Food Stamp Pro-gram (FSP). Using variation in the month FSP began operating in eachU.S. county, we find that pregnancies exposed to FSP three months priorto birth yielded deliveries with increased birth weight, with the largestgains at the lowest birth weights. We also find small but statistically insig-nificant improvements in neonatal mortality. We conclude that the sizableincrease in income from FSP improved birth outcomes for both whitesand African Americans, with larger impacts for African Americanmothers.
IN this paper, we evaluate the health consequences of asizable improvement in the resources available to Ameri-
ca’s poorest. In particular, we examine the impact of theFood Stamp Program (FSP), which in 2007 provided $34billion in payments to about 13 million households, oninfant 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 onhealth outcomes. Second, building on work by Hoynes andSchanzenbach (2009), we argue that the FSP treatmentrepresents an exogenous increase in income for the poor.Our analysis therefore represents a causal estimate of theimpact of income on health, an important topic with littleconvincing evidence due to concerns about endogeneityand reverse causality (Currie, 2009).
We use the natural experiment afforded by the nation-wide rollout of the modern FSP during the 1960s and early1970s. Our identification strategy uses the sharp timing ofthe county-by-county rollout of the FSP, which was initiallyconstrained by congressional funding authorizations (andultimately became available in all counties by 1975). Speci-fically, we use information on the month the FSP beganoperating in each of the roughly 3,100 U.S. counties andexamine the impact of the FSP rollout on mean birthweight, 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 thestate-level variation often leveraged by economists to eval-uate transfer programs, previous FSP research has typicallyresorted to strong assumptions as to the comparability ofFSP participants and eligible nonparticipants (Currie,2003). Not surprisingly, the literature is far from settled asto what casual impact (if any) the FSP has on nutrition andhealth.
Hoynes and Schanzenbach (2009) use this county rolloutto examine the impact of the FSP on food consumptionusing the PSID. They found that the introduction of the FSPincreased total food spending and decreased out-of-pocketfood spending. Importantly, consistent with the predictionsof canonical microeconomic theory, the magnitude of theincrease in food expenditures was similar to an equivalent-sized income transfer, implying that most recipient house-holds were inframarginal (that is, they would spend moreon the subsidized good than the face value of the in-kindtransfer). As one of the largest antipoverty programs in theUnited States—comparable in cost to the earned income taxcredit (EITC) and substantially larger than TemporaryAssistance to Needy Families (TANF)—understandingFSP effects is valuable both in its own right and for whatit reveals about the relationship between income andhealth.1
We focus on birth outcomes for several reasons. First,families represent an important subgroup of the food stampcaseload. 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 ofCalifornia, Davis and NBER; Schanzenbach: Northwestern Universityand NBER.
We thank Justin McCrary for providing the Chay-Greenstone-McCrarygeography crosswalk and Karen Norberg for advice on cause-of-deathcodes. This work was supported by a USDA Food Assistance ResearchGrant (awarded by the Joint Center for Poverty Research at NorthwesternUniversity and University of Chicago), the Population Research Center atthe University of Chicago, and USDA FANRP Project 235, ‘‘Impact ofFood Stamps and WIC on Health and Long Run Economic Outcomes.’’We also thank Ken Chay, Janet Currie, Ted Joyce, Bob LaLonde, DougMiller, 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, AnkurPatel, and Charles Stoecker provided excellent research assistance, andUsha Patel entered the regionally aggregated vital statistics data for 1960through 1975.
The online appendix referred to throughout the article is available athttp://www.mitpressjournals.org/doi/suppl/10.1162/REST_a_00089.
1 The cost of the FSP was $33 billion in 2006 (compared to $24 billionfor TANF, $33 billion for the EITC, and $5.4 billion for WIC, the SpecialSupplemental 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 thelate 1960s and early 1970s. Third, to the extent that the FSPimproved birth outcomes, later-life health outcomes ofthese cohorts may have also benefited (Barker, 1992; Black,Devereux, & Salvanes, 2007). Finally, the vital statisticsdata used in this project are ideally suited for analyzingFSP rollout: the birth (death) microdata contain the countyof birth (death) and the month of birth (death). This, com-bined with the large sample sizes (for example, more than 1million birth records per year in the data set), allows us touse the discrete nature of the FSP rollout with significantstatistical power.
We find that infant outcomes improve with FSP introduc-tion. Changes in mean birth weight are small, increasingroughly 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 amongthe treated by 7% for whites and between 5% and 11% forblacks. Changes in this part of the birth weight distributionare important because they are closely linked to other new-born health measures. Although not all treatment effects arestatistically 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 reductionin neonatal mortality, although these results rarely reachstatistical significance. We find very small (but preciselyestimated) impacts of the FSP on fertility, suggesting thatthe results are not biased by endogenous sample selection.All results are robust to various sets of controls, such ascounty fixed effects, state-by-year fixed effects, and county-specific linear trends. Moreover, FSP impact estimates arerobust to and little changed by county-by-year controls forfederal spending on other social programs, suggesting ourbasic identification strategy is clean. Finally, we present anevent study analysis that further supports the validity of theidentification strategy.
Food stamps are the fundamental safety net in theUnited States. Unlike other means-tested programs, there isno additional targeting to specific subpopulations. Currentbenefits average about $200 per recipient household permonth. Our analysis constitutes the first evidence thatdespite the fact that if did not target pregnant mothers (oreven women), introduction of the FSP improved newbornhealth.
II. Introduction of the Food Stamp Program
The modern FSP began with President Kennedy’s 1961announcement of a pilot food stamp program that was to beestablished in 8 impoverished counties. The pilot programswere expanded to 43 counties in 1962 and 1963. The suc-cess with these pilot programs led to the Food Stamp Act of1964 (FSA), which gave local areas the authority to start upthe FSP in their county. As with the current FSP, the pro-
gram was federally funded, and benefits were redeemable atapproved retail food stores. In the period following the pas-sage of the FSA, a steady stream of counties initiated suchprograms, and federal spending on the FSP more thandoubled between 1967 and 1969 (from $115 million to$250 million). Support for requiring counties to participatein 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 allcounties offer FSP by 1975.
Figure 1 plots the percentage of counties with an FSPfrom 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 asteady 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 dateof FSP adoption (darker shading denotes a later start-update). Our basic identification strategy considers the monthof FSP adoption for each county the FSP ‘‘treatment.’’3
For our identification strategy to yield causal estimates ofthe program, it is key to establish that the timing of FSPadoption appears to be exogenous. Prior to the FSP, somecounties provided food aid through the Commodity Distri-bution Program (CDP), which took surplus food purchasedby the federal government as part of an agricultural pricesupport policy and distributed those goods to the poor. The1964 Food Stamp Act allowed counties to voluntarily setup an FSP, but the act also stated that no county could runboth the FSP and the CDP. Thus, for counties that pre-viously ran a CDP, adoption of the FSP implies terminationof the CDP.4 The political accounts of the time suggest thatdebates about adopting the FSP pitted powerful agriculturalinterests (which favored the CDP) against advocates for thepoor (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 thefood stamp caseload, but represents the percentage of the U.S. populationthat 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. Seeonline appendix table 3.
4 This transition in nutritional assistance would tend to bias FSP impactestimates downward, but we do not think this bias is substantial becauseof 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 availablewere flour, cornmeal, rice, dried milk, peanut butter, and rolled wheat(Citizens’ Board of Inquiry 1968). In contrast, food stamp benefits can beused 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 1964Food Stamp Act was achieved through classic legislative logrolling. Thefarm interest coalition (southern Democrats, Republicans) wanted to passan important cotton-wheat subsidy bill while advocates for the poor(northern Democrats) wanted to pass the FSA. Neither had majorities, yetthey made an arrangement, supported each others’ bills, and both billspassed.
388 THE REVIEW OF ECONOMICS AND STATISTICS
ing interests (such as southern or rural counties) may be lateadopters of the FSP. Counties with strong support for thelow-income population (such as northern, urban counties
with large populations of poor) may adopt FSP earlier inthe period. This systematic variation in food stamp adoptioncould 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), wedocumented that larger counties with a greater fraction ofthe population that was urban, black, or low income indeedimplemented the FSP earlier, consistent with the historicalaccounts. We sought to predict FSP adoption date with 1960county characteristics—those recorded immediately prior tothe 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 ofthe 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). Thisis consistent with the characterization of funding limits con-trolling the movement of counties off the waiting list to startup their FSP: ‘‘The program was quite in demand, as con-gressmen wanted to reap the good will and publicity thataccompanied the opening of a new project. At this time therewas always a long waiting list of counties that wanted to jointhe 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 strengthwhen it comes to our identification approachin that much ofthe variation in the implementation of FSP appears to beidiosyncratic. Nonetheless, in order to control for possibledifferences 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 countycharacteristics with time trends as in Acemoglu, Autor, andLyle (2004) and Hoynes and Schanzenbach (2009).
FSP introduction took place during a period of tremen-dous expansion in cash and noncash transfer programs asthe War on Poverty and Great Society programs wereexpanding. 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 areadministered at the state level, our controls for state-by-yearfixed effects should absorb these program impacts. To besure, however, our models include controls for per capitareal county government (non–food stamp) transfers.7
III. Background Literature
The goal of the FSP is to improve nutrition among thelow-income population. As such, many studies have exam-ined the impact of the FSP on nutritional availability andintake, food consumption, food expenditures, and food inse-
curity (see Currie, 2003, and Fraker, 1990, for reviews ofthe literature).
Almost all existing studies of the impact of the FSP useresearch designs that rely on comparisons of program parti-cipants to nonparticipants at the individual level. Thisapproach 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) havepointed out that if food stamp recipients are healthier, aremore motivated, or have better access to health care thanother eligible women, then comparisons between partici-pants and nonparticipants could produce positive programestimates even if the true effect is 0. Conversely, if foodstamp participants are more disadvantaged than otherfamilies, such comparisons may understate the program’simpact. 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. Theseunexpected results are almost certainly driven by negativeselection 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 withdifferent levels of benefit generosity or other programparameters. 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 FSPis a federal program for which there is very little geo-graphic variation (aside from the variation we use inthis paper) or variation in eligibility criteria or benefitlevels, so prior researchers have had to employ alternativeapproaches.
Identification issues aside, it is noteworthy that few FSPstudies examine the impact on health outcomes. We areaware of two studies. Currie and Cole (1991) examine theimpact of the FSP on birth weight using sibling comparisonsand instrumental variable methods and find no significantimpacts of the FSP. Our work is closer to that of Currie andMoretti (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, whichwas driven particularly by first births among teens and bychanges for Los Angeles County. As discussed below, thisnegative effect is possible if the FSP led to fertility changesor increases in the survival of low-birth-weight fetuses. Thetiming of FSP assignment in Currie and Moretti (2008) differsfrom ours in that they consider FSP availability at the begin-ning of pregnancy and its impact on birth weight, whereas wefocus on availability toward the end of pregnancy.8
The literature (see the review in Currie, 2009) providesfew 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 childrenup to age 5 in families, was introduced in 1974. Given the timing of WICimplementation relative to FSP, there is little concern that the introduc-tion of WIC biases our estimates of the introduction of FSP, and resultslimited to pre-1974 are qualitatively similar.
8 Table 3 shows the sensitivity of our impact estimates to the timing ofFSP assignment.
390 THE REVIEW OF ECONOMICS AND STATISTICS
weight. Cramer (1995) finds that mothers with more incomehave higher-birth-weight babies, although income is identi-fied cross-sectionally. Kehrer and Wolin (1979) find evi-dence that the Gary Income Maintenance Experiment mayhave improved birth weight. However sample sizes aresmall (N ¼ 404 births), and although positive effects werefound for woman as being and high risk for low birthweight (young, smokers, short birth interval), perverseeffects were found for woman classified as being of low risklow birth weight. Currie and Cole (1993), using IV andmother-fixed effects estimators, find that AFDC incomeleads to improvements in birth weight. Baker (2008) usesthe 1993 expansion in the EITC, which disproportionatelybenefited families with two or more children, finding a 7gram increase in the birth weight of subsequent children. Ingeneral, 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, weargue that our paper provides some of the best evidence todate 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 foodstamps 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 rolloutidentification approach and data from the PSID to examinethe impacts of food stamps on food expenditures; they findthat recipients of food stamps behave as if the benefits werepaid in cash. Therefore, not only can we think of the FSPintroduction as a large income transfer, we can think of it asfor the most part the equivalent of a cash income transfer.
With this framing, an increase in income could lead tochanges in infant health through many channels. We wouldexpect 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. Wehave little information on how particular subcategories offood demand change with FSP availability: Hoynes andSchanzenbach (2009) are able to measure impacts on totalfood expenditures, but cannot provide information on thequantity or quality of food consumed (or other goods).
The medical literature on the determinants of birthweight provides a useful structure for thinking about thepossible channels for the health effects of the FSP. As Kra-mer (1987a, 1987b) suggested, birth weight is usefullydecomposed 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 tobe more difficult to manipulate, though empirically moreimportant than IUG in affecting birth weight in developedcountries (Kramer, 1987a, 1987b). Maternal nutrition andcigarette 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 thethird trimester of pregnancy.9 Kramer (1987a) writes, ‘‘It isimportant to analyze additional health measures in additionto birth weight: A final reminder concerns the need forfuture 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 gestationalage are important only insofar as they affect these out-comes’’ (p. 510).
We examine impacts on neonatal mortality because it iscommonly linked to the health environment during preg-nancy; it is therefore plausible that FSP transfers may havebeen a factor. Estimates from Almond, Chay, and Lee(2005) indicate that a 1 pound increase in birth weightcauses neonatal mortality to fall by 7 deaths per 1,000births, or 24%. Postneonatal mortality, by contrast, isviewed as being more determined by postbirth factors.10
This discussion suggests that we would expect FSP toaffect birth weight and neonatal mortality but not necessarilygestational length. One obvious channel for food stampimpacts is through improvements in nutrition. The introduc-tion of the FSP transfer increases total family resources and ispredicted to increase the quality and quantity of food con-sumed, thereby leading to improvements in infant health. Theincreased transfer income could also encourage behaviors thatcould harm infant health, such as smoking or drinking.11
Health improvements may work through other channels aswell, for instance, reducing stress (such as financial stress)experienced by the mother, which itself may have a directimpact on birth weight. We explore these issues by separatelytesting for FSP impacts on length of gestation and birth weightand by exploring the sensitivity of our impact estimates to thetiming of FSP assignment by pregnancy trimester.
Overall, we expect that access to the FSP should improveinfant health. The same forces that improve infant health,however, could also lead to a change in the composition ofbirths. In particular, if improvements in fetal health lead tofewer fetal deaths, there could be a negative compositionaleffect on birth weight from the improved survivability ofmarginal fetuses. This could bias downward the estimated
9 See the literature review of Rush et al. (1980). For example, the cohortexposed to the Dutch famine in the third trimester had lower average birthweight than cohorts exposed earlier in pregnancy (Painter, Rosebooma, &Bleker, 2005).
10 The initial health at birth is generally much better among infants whodie in the postneonatal period than among infants dying in the first monthof life. For example, while 72% of all neonatal deaths had a low birthweight (below 2,500 grams), only 20% of all postneonatal deaths werelow-birth-weight infants (Starfield, 1985). Postneonatal deaths tend to becaused by negative events after birth, most often by infectious diseasesand accidents (Grossman & Jacobowitz, 1981). Further, postneonataldeaths may be more responsive to hospital access than neonatal deaths(see Almond, Chay, & Greenstone, 2007).
11 Although recipients cannot purchase cigarettes directly with FSPbenefits, the increase in resources to the household may increase cigaretteconsumption, which would work to reduce birth weight.
391INSIDE THE WAR ON POVERTY
effects of the FSP on birth weight and infant mortality.12 Inaddition, if FSP introduction leads to increases in fertilityfor disadvantaged women, this could also lead to negativecompositional effect and a subsequent downward bias onthe estimates.13 To evaluate such channels, we test forimpacts of the FSP on total births (finding no effect).
The data for our analysis are combined from severalsources. The key treatment or policy variable is the monthand year that each county implemented a food stamp pro-gram, which comes from USDA annual reports on countyfood stamp caseloads (USDA, various years). These adminis-trative FSP data are combined with two microdata sets onbirths 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 theyears preceding the beginning of the microdata. These dataare 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, thesedata are either a 100% or 50% sample of births, and thereare about 2 million observations per year. Reported birthoutcomes include birth weight, gender, plurality, and (insome state-years) gestational length. Data on the month andcounty of birth permit linkage of natality outcomes to themonth the FSP was introduced in a given county. There arealso (limited) demographic variables, including age and raceof the mother and (in some states and years) mother’s educa-tion and marital status. Online appendix table 1 providesinformation 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 usequarters (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 afterall 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 onlybeginning in 1968. By 1968, half of the population lived incounties with on FSP in place. In the interest of examiningthe full FSP rollout, we obtained annual print vital statisticsdocuments and digitized the available data. With these printdocuments, we augment the microdata with counts of thetotal number of births by county and year (not available byrace) for 1959 to 1967 and counts of births by birth weightranges by state, race and year (not available by county) for1959 to 1967.14
B. Vital Statistics Death Data
These data are coded from death certificates and areavailable beginning in 1959. The data encompass the uni-verse of death certificates (except in 1972, when they are a50% sample) and report the age and race of the decedent,the cause of death, and the month and county of death. Wecollapse the data to county-race-quarter cells covering theyears 1959 to 1977.
Our mortality measure is the neonatal mortality rate,defined as deaths in the first 28 days of life per 1,000 livebirths. We focus on deaths from all causes, as this gives usthe most power (further cutting of the county-quarter-racecells by detailed cause of death leads to many very thincells) and is unaffected by changes in the coding of causeof death (conversion from ICD-7 to ICD-8) in 1968. Wehave attempted to identify causes of death that could beaffected by nutritional deficiencies and also present resultsfor these and other deaths.15 We consider nutritional causesboth because the FSP was targeted at those in nutritionalrisk and widespread concerns about nutritional statusamong the poor during this period. Online appendix table 2lists the broad categories for cause of death.
Our main neonatal results use the natality microdata toform 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 thedenominator for live births and therefore neonatal deathrates (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 thisincrease is accounted for by reductions in early prenatal (embryonic) mor-tality, only to appear as deaths after birth during infancy, this would implynearly a doubling of the infant mortality rate, which stood close to 2%nationally in 1970. Such an increase is not observed and would obviouslyoverwhelm any reductions in infant mortality among those who wouldhave survived until birth absent the FSP. That said, our data clearly donot allow us to distinguish between births that reflect a prevented embryo-nic or fetal death versus induced conceptions. But the magnitudesinvolved suggest that postponement of intrauterine mortality to the firstyear of life could not have been the norm or the infant mortality ratewould have risen substantially. Thus, if we take the table 5 point estimatesat 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 withrespect to additional transfers from income support programs is verysmall (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 deathclassifications. We are responsible for any classification errors.
16 We need quarterly births by race-county to match the quarterlydeaths in the numerator. We use the distribution of births by quarter foreach county in 1968 and assume that quarterly pattern holds for all years1959–1967. In practice the ‘‘seasonality’’ of births across quarters is mini-mal.
17 See National Cancer Institute, http://seer.cancer.gov/popdata/download.html.
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struct fertility rates, defined as births per 1,000 women ages15 to 44. Our main results use fertility rates by county-race-quarter for 1968 to 1977. We also use the digitized annualcounts of births by county to construct fertility rates bycounty-year (not race, not quarter) for the full period 1959to 1977.
D. County Control Variables
The 1960 City and County Data Book, which compilesdata from the 1960 Census of Population and Census ofAgriculture, is used to measure economic, demographic,and agricultural variables for the counties’ pretreatment(before FSP is rolled out) period. In particular, we use thepercentage of the 1960 population that lives in an urbanarea, 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 thecounty population. We use the Bureau of Economic Analy-sis, Regional Economic Information System (REIS) data toconstruct annual, county real per capita income, and gov-ernment transfers to individuals, including cash publicassistance benefits (Aid to Families with Dependent Chil-dren AFDC; Supplemental Security Income, SSI; and Gen-eral Assistance), medical spending (Medicare and militaryhealth 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 datafrom microfiche for 1959, 1962, and 1965 to 1968.19
We estimate the impact of the introduction of the FSP oncounty-level birth outcomes, infant mortality, and fertility,separately by race. Specifically, we estimate the followingmodel:
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, weinclude unrestricted fixed effects for county gc and time dt.
We examine the sensitivity to including state-by-year fixedeffects lst or county-specific linear time trends, which arenot shown in equation (1).
FSPct is the food stamp treatment variable equal to 1 ifthe county has a food stamp program in place. The timingof the treatment dummy depends on the particular outcomevariable used. For the analysis of births, we assign FSP ¼ 1if there is an FSP in place at the beginning of the quarterprior 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 mostimportant for determining birth weight. However, weexplore the sensitivity to changing the timing of the FSPtreatment. Neonatal deaths are thought to be tied primarilyto prenatal conditions, and we therefore use the same FSPtiming (we use the age at death and measure the FSP as ofthree months prior to birth, to proxy for the beginning ofthe third trimester). We have less guidance for the correcttiming for FSP treatment for fertility; we explore FSP avail-ability between three quarters prior to birth (to proxy forconception) and seven quarters prior to birth.
The vector Xct contains the annual county-level controlsfrom the REIS, including real per capita transfers and thelog of real annual county per capita income. CB60c are the1960 county characteristics, which we interact with a lineartime trend to control for differential trends in health out-comes that might be correlated with the timing of FSPadoption.
We consider several outcome variables in our main spe-cifications. First, using the natality data, we measure infanthealth at birth as continuous mean birth weight in gramsand fraction low birth weight (less than 2,500 grams, orabout 5.5 pounds). These measures are means withincounty-race-quarter. Second, using the mortality data, weexamine impacts on neonatal mortality rates (per 1,000 livebirths) for all causes and for those likely to be affected bynutritional deficiencies.
All estimates are weighted using the number of births inthe 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 cellswhere there are fewer than 25 (50) births.21 The results arenot sensitive to this sample selection. We also drop Alaskabecause of difficulties in matching FSP service areas withcounties.
18 Beginning in 1969, the REIS data permit more detailed categories fortabulating government transfers (including the ability to capture Medicaidspending). 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 addingmore detailed categories. The REIS data also measure food stamp transferpayments, but for obvious reasons, we do not use this as a control in ourmodel. 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 reportno spending on FSP; in the year of introduction, this falls to 1.3% and isless than 0.3% in subsequent years (online appendix table 3).
19 We used linear interpolation to fill in the missing years. We thankGary Kennedy of the Bureau of Economic Analysis for providing theREIS data microfiche.
20 To be precise, because we collapse the data to the county-quarter, theFSP variable can sometimes equal something other than a 0 or 1. Thenatality data are available at the monthly level, and we use that to assignFSP status as of three months prior to birth (proxy for beginning of thethird trimester). When the data are collapsed to the county-quarter, thispolicy variable is averaged among the three months of observations inthat cell. Therefore, the policy variable ranges from 0 to 1, with mostvalues 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 weightand the fraction of births that are low birth weight (LBW)for 1968 to 1977. Results are presented separately for whitesand blacks. For each outcome, we report estimates from fourspecifications with different controls. Column 1 includescounty and time (year � quarter) fixed effects, county percapita income, REIS county-level per capita transfers, and1960 county characteristics interacted with linear time. Theremaining columns control for trends in three ways: column2 with state-specific linear time trends, column 3 withunrestricted 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 meanbirth weight for births to white women. These columns indi-cate a small, statistically significant increase in birth weightfor 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% increasein birth weight, labeled in this and subsequent tables as ‘‘%Impact (coef/mean)’’. As shown in panel B, the impact ofFSP exposure on birth weight is 50% to 150% larger forblacks than whites. That, combined with a smaller averagebirth weight for blacks, implies an impact between 0.1% and0.2% on blacks (about twice the impact on whites).
Only a subset of women who give birth are likely to beaffected by FSP. While the coefficients reported are validestimates of the population impact of FSP, we also want toknow the impact among FSP recipients (treatment on thetreated). To calculate the implied impact on those who takeup the FSP, we divide the parameters by an estimate of theFSP participation rate for this sample.23 We can inflate theestimated effect by these participation rates for an estimateof treatment on the treated. The results indicate that theimpact of FSP on participants’ birth weight (labeled‘‘Estimate, inflated’’) is between 15 and 20 grams for whitesand 13 to 42 grams for blacks. The estimate expressed as apercentage of mean birth weight (labeled ‘‘% Impactinflated’’) is between 0.5% and 0.6% for whites andbetween 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: WhitesAverage 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 97,785R2 0.54 0.55 0.55 0.56 0.17 0.17 0.18 0.19Mean of dependent variable 3,350 3,350 3,350 3,350 0.06 0.06 0.06 0.06
B: BlacksAverage 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 27,374R2 0.32 0.33 0.34 0.35 0.15 0.15 0.17 0.18mean of Dependent variable 3,097 3,097 3,097 3,097 0.13 0.13 0.13 0.131960 CCDB � linear time X X X X X XREIS controls X X X X X X X XCounty per capita real income X X X X X X X XYear quarter fixed effects X X X X X X X XCounty fixed effects X X X X X X X XState � linear time X XState � year fixed effects X XCounty � 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 countytransfer 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 maximumnumber of observations would be about 125,000. As described above, wedrop cells with fewer than 25 births. This reduces the sample of blacksmuch more than whites because blacks are more geographically concen-trated. Despite dropping many counties, this sample represents 98% ofwhite births and 94% of black births.
23 We do not have information about food stamp participation in thenatality data or sufficient data to impute eligibility (for example, income).Instead, we use the 1980 Current Population Survey and calculate FSPparticipation rates for women with a child under 5 years old. (Participa-tion rates look very similar if we alternatively use the presence of a childbelow age 1 or 3.) The estimated participation rate for women with youngchildren (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 outcomesdescribed below) are very robust to adding more controls tothe model. We view the specification with state-by-yearunrestricted fixed effects as very encouraging, as we havecontrolled for a whole host of possibly contemporaneouschanges to labor markets, government programs, and otherthings that vary at the state-year level. While not shownhere, the county-level variables for government transfersand pretreatment variables do little to change the results.This provides further evidence that the food stamp rollout isexogenous, thereby validating the research design. Finally,we also find the results robust to adding county linear timetrends (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) meansthat the precision of our impact estimates is not noticeablyimproved by including these regression controls. For theremainder of the tables, we adopt the specification withstate-by-year fixed effects as our base case specification.Results (not presented here) are the same if log of birthweight is used as the dependent variable instead.
Columns 5 through 8 repeat the exercise, this time with thefraction low birth weight (less than 2,500 grams) as the depen-dent variable. Exposure to FSP reduces LBW by a statisticallysignificant 1% for whites (7–8% when inflated by participa-tion rate) and a less precisely estimated 0.7% to 1.5% forblacks (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 modelsrelating FSP introduction to the probability that birth weightis 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). Weuse the specification in column 3 with state-by-year fixedeffects; the estimates and 95% confidence intervals are pre-sented in Figure 3 (we plot ‘‘% Impacts [coef/mean]’’ notinflated by program participation). Figure 3A displays theresults and confidence intervals for whites. We find that thelargest percentage reduction in probability of birth weightbelow a certain threshold comes at very low thresholds of1,500 and 2,000 grams. The impacts become graduallysmaller as the birth weight threshold is increased to 2,500grams and above, until there is no difference for birthsbelow 3,750 grams. Results are larger for blacks (figure3B), showing a 6% decrease in the probability of a birth lessthan 1,500 grams, and an impact that declines at higherbirth weights.24
Online appendix table 4 presents estimates for three addi-tional outcome variables: the fraction of births that are lessthan 1,500 grams, have gestation length less than 37 weeks(preterm births), and are female. These results show thatFSP leads to a small and statistically insignificant decreasein preterm births and the fraction of births that are female.While small they are and statistically insignificant, this isconsistent with recent work finding that prenatal nutritionaldeprivation tips the sex ratio in favor of girls (Mathews,Johnson, & Neil, 2008).25
One limitation of these results is that microdata on birthsby county are available only starting in 1968, at which pointalmost 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 toa 1.05 gram increase in mean birth weight. The Hoynes and Schanzen-bach (2009) estimates of the magnitude of food stamp benefits are $1,900annually for participants (in 2005 dollars). Scaling those to match theunits available in the literature (and treating FSP benefits as their face-value cash equivalent) implies that food stamps increased the familyincome-to-poverty ratio of participants by 15%. The implied treatment-on-treated effect would therefore be approximately 16 grams, which isquite 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 ofgrams. The specification is given by column 3 in table 1.
25 In results not shown here, we find that birth-weight models are littlechanged by controlling for gestation (known as an IUG model). We alsoestimated models where the dependent variable is the fraction of birthsbelow a gestation-varying threshold (known as small-for-gestational-agemodels; Fenton, 2003). These models yielded results very similar to theLBW regressions.
395INSIDE THE WAR ON POVERTY
FSP. In online appendix table 5 we use data from 1959 to1977 to examine the impact of the FSP rollout on low birthweight and very low birth weight. To push the period backto 1959, we are limited to use of data at the state-race-yearlevel (see the discussion in section V). Controls includestate and year fixed effects, REIS variables, and state-speci-fic linear time trends; standard errors are clustered onstate.26 We first present results for 1968 to 1977, where thedata are identical to those used in table 1 but are collapsedto the state level. The results show imprecise but qualita-tively similar effects of FSP measured with this noisiertreatment variable. (For example, the county analysis intable 1 shows a �1.0 percent impact on LBW for whitesand �1.5 percent for blacks compared to �0.4 percent forwhites and �1.6 percent for blacks for the state and yeardata in online appendix table 5). We then show the resultsfor the full period (1959–1977) and the post-pilot programperiod (1964–1977). Whenever estimating models for thefull FSP ramp-up period, we look separately at the periodfrom 1964 because the pilot counties were clearly not exo-geneously chosen. Using these earlier (but more aggre-gated) data, we get qualitatively similar (and statisticallyindistinguishable) results across the different time periods,suggesting that missing the pre-1968 period in our mainresults 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 beaffected 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 earlieryears), we lose a substantial fraction of the sample (see,online appendix table 1). Nonetheless, we have estimatedmodels by age of mother, education of mother, and pre-sence of the father (results not shown). Overall, the resultsshowed that the impacts are larger for older mothers (age25 and over). None of the education results are statisticallysignificant. This analysis did reveal that black mothers withno father present experience much larger impacts than allblack women. This is consistent with the high participationrates among this group (0.70 compared to 0.50 for allblacks).
In lieu of detailed demographic variables, in table 2 webreak 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 inthe highest-poverty counties. Large, statistically significanteffects are present in the highest-quartile poverty counties,while smaller and insignificant effects are presents in thelowest-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 thatthe impact might be different across geographic regions ormight differ by race across regions. In particular, participa-tion in the program in the early years (after the county’sinitial adoption of FSP) was probably higher in urban coun-ties and in the North. Barriers to accessing food stampsmight have also differed between North and South and mayhave interacted with race (Citizens’ Board, 1968). Table 3shows that the impact of FSP is larger and more statisticallysignificant for both blacks and whites in urban counties.Interestingly, blacks appear to have larger effects outsidethe South, while whites appear to have larger effects in theSouth. 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 56,055R2 0.78 0.38 0.56 0.26Mean of dependent variable 3333 0.07 3303 0.08Subsample population 0.23 0.23 0.26 0.261960 CCDB � linear time X X X XREIS controls X X X XCounty per capita real income X X X XYear � quarter fixed effects X X X XCounty fixed effects X X X XState � 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 meansby 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 (publicassistance, 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 countypopulation).
26 To construct state-level FSP treatment, we use the 1968 counts ofnumber of births by county-month and calculate (for each state and yearusing the program variables) the percentage of births in the state that werein 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 neonatalmortality) in the North, while whites saw larger declines inthe 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 theFSP transfer, table 4 reestimates the mean birth weightmodels varying the timing of the exposure to the FSP. Thebaseline specification—reprinted from column 3 of table1—assigns the policy introduction as three months prior tobirth, to proxy for beginning of the third trimester. Columns2 and 3 of table 4 moves assignment of FSP treatment totwo and three quarters before birth, respectively. Movingthe treatment from third to second trimester reduces theimpact 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 statisticallyinsignificant impacts. The results in columns 4 and 5 showthat conditional on third-trimester exposure, additionalexposure earlier in the pregnancy has no additional benefits.Similar results are found for fraction low and very low birthweight. Recalling from section IV that the medical litera-ture suggests that nutrition has its greatest impact on birthweight during the third trimester, we view these estimates
as suggestive that nutrition is playing an important channelfor 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 ininfant outcomes at the county level.28
To further test for spurious trending in the county birthoutcomes that might be loading on to FSP, we include aone-year lead of the policy variable for each of the birthoutcome variables in online appendix table 6. There is noimpact of the policy lead, and the results for the main policyvariable are qualitatively unchanged.
As described above, we use the month that the countyimplemented the FSP to measure food stamp availabilityduring these pregnancies. If there was a lag in ramping upcounty 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 thefact that the new FSP offices were often set up in the samebuilding as the county welfare office. To directly evaluatethe ramp-up in FSP operations, figure 4 shows food stampcaseloads per capita by year relative to start year (the case-load data are available only by year). The figure separatelyplots caseloads for counties beginning operations in the firsthalf 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: WhitesAvearage 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 65,503Subsample population 0.29 0.29 0.69 0.69 0.73 0.73 0.25 0.25
B: BlacksAverage 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 14,284Subsample population 0.49 0.49 0.45 0.45 0.77 0.77 0.17 0.171960 CCDB � linear time X X X X X X X XREIS controls X X X X X X X XCounty per capita real income X X X X X X X XYear � quarter fixed effects X X X X X X X XCounty fixed effects X X X X X X X XState � 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 includesmeans 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 errorsare 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 areincluded 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 impactmay explain the difference between our results and those of Currie andMoretti (2008). Their study of birth outcomes in California assigned theFSP treatment nine months prior to birth and found comparatively limitedimpacts on birth weight. Another explanation for larger effects in the thirdtrimester is if initial FSP participation is concentrated there (rather thanearlier).
397INSIDE THE WAR ON POVERTY
figure suggests that rapid ramp-up was achieved and thatthe ramp-up is only slightly faster in the counties with morelead time (implementation earlier in the year). Further, note
that over half of the ‘‘steady-state’’ caseload is achieved inthe first year, even for counties that begin operation late inthe 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 TrimesterFSP—Beginning ofSecond Trimester
FSP—Beginning ofFirst Trimester
FSP—Beginning ofThird Trimester
FSP—Beginning ofThird Trimester
Second Policy Effect: – – –FSP—Beginning ofSecond Trimester
FSP—Beginning ofFirst Trimester
A: WhitesAverage 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 �0.454Second policy variable (1.650) (1.232)Observations 97,785 97,785 97,785 97,785 97,785R2 0.55 0.55 0.55 0.55 0.55Mean of dependent variable 3,350 3,350 3,350 3,350 3,350
B: BlacksAverage 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 �3.515Second policy variable (4.450) (3.268)Observations 27,374 27,374 27,374 27,374 27,374R2 0.34 0.34 0.34 0.34 0.34Mean of dependent variable 3,097 3,097 3,097 3,097 3,0971960 CCDB � linear time X X X X XREIS controls X X X X XCounty per capita real income X X X X XYear � quarter fixed effects X X X X XCounty fixed effects X X X X XState � 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 ofsix 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 theimpacts 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 the1960 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 FSPtreatment effect is identified by the discrete jump in FSP atimplementation and its impact on birth weight. In particu-lar, we showed in table 4 that as the timing of the treatmentis shifted earlier in pregnancy, the estimated FSP effect onbirth weight decreased substantially in magnitude. If insteadidentification were coming from some other trends incounty outcomes that are correlated with FSP start month,then we would expect less sensitivity in the results to thetrimester to which the FSP treatment is assigned. However,there remains a concern that our results are driven by trendsin county birth outcomes that are correlated with FSPimplementation in a way that county linear trends do notcapture.
This proposition can be evaluated more directly in anevent study analysis. Specifically, we fit the following equa-tion,
Yct ¼ aþX8
pi1ðsct ¼ iÞ þ gc þ dt
þcXct þ /c � tþ ect; ð2Þ
where sct denotes the event quarter, defined so that s ¼ 0for births that occur in the same quarter as the FSP beganoperation in that county, s ¼ 1 for births one quarter afterthe FSP began operation, and so on. For s � � 1, pregnan-cies were untreated by a local program (births were beforethe program started). The coefficients are measured relativeto the omitted coefficient (s ¼ �2).29 Our event studymodel includes fixed effects for county and time, countyREIS variables, and county-specific linear time trends.
In order to eliminate potential compositional effects, werestrict the sample to a balanced panel of counties havingbirths for all fifteen event quarters: six quarters beforeimplementation and eight quarters after. Because our natal-ity data begin with January 1968, this means we excludefrom the event study analysis all counties with an FSPbefore July 1969.
Figure 5 plots the event and quarter coefficients fromestimating equation (2) on the fraction of low-birth-weightbirths. The figure also reports the number of county andquarter observations in the balanced sample and the differ-ence-in-difference estimate on this sample.30 Panel Areports estimates for blacks and panel B for whites. Thesefigures 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 promptincrease in birth weight is observed with FSP inceptionindicates that potential confounders would have to mimicthe timing of FSP rollout extremely closely. Not shownhere, the event study results are nearly identical if weexclude the county controls, providing further evidence ofthe 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 theSouth as in Almond, Chay, and Greenstone 2007) and ourREIS controls fail to pick this up. To test this, we use thenatality data to estimate the impact of FSP implementationon the fraction of births in a hospital or attended by a physi-cian. These results indicate very small and statisticallyinsignificant improvements with FSP implementation(online appendix table 7).
Finally, the same forces that improve infant health couldalso lead to greater survival of low-birth-weight fetuses. Inaddition, the FSP may lead to increased fertility among dis-advantaged women (if children are a normal good). Bothfactors, through endogeneous sample selection, could biasthe estimates downward. We consider this by evaluatingwhether FSP introduction is associated with any change inlive births. The dependent variable is the number of birthsin the race, county, and quarter divided by the number ofwomen aged 15 to 44, and the regressions are weighted bythe population of women in each cell. Table 5 presents sev-eral estimates, which vary depending on the timing of theFSP treatment: between three quarters prior to birth (proxyfor conception) and seven quarters prior to birth (one yearprior to conception). Across the table, we find positive butvery small and statistically insignificant effects of FSP onbirths. When these point estimates are inflated by the FSPparticipation rate, the estimate of the treatment on the trea-ted is about 1% for whites and 2% for blacks. When westratify the results by quartiles of county poverty rates, wealso find small and statistically insignificant impacts amongthose living in the highest poverty counties (online appen-dix table 8).
VIII. Mortality Results
Table 6 shows the main results for neonatal mortality ratefor 1968 to 1977. We present three outcomes: death rate forall causes, deaths possibly due to nutritional deficiencies,
29 Because of the discrete nature of the event study model, the s’s areformed by aggregating months to a quarter. For example, if the FSPstarted (or birth occurred) in January, February, or March 1970, then theFSP started (or birth occurred) in 1970 quarter 1. Therefore when s ¼ 0(birth quarter ¼ policy commencement quarter), the pregnancy couldactually 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 theevent study differ from the main results (due to balancing of the sample).
31 Similar patterns are observed when the dependent variable is averagebirth weight (online appendix figure 2) and the share of births below1,500 grams (available on request).
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and other deaths (for definition see the data section andonline appendix table 2). Because neonatal deaths arethought to be related primarily to prenatal conditions (parti-cularly prior to major technological advances in neonatalcare in the 1970s and 1980s), we time the FSP treatment asof a quarter prior to birth (to proxy for the beginning of thethird trimester). In these models, we drop any race-county-quarter cell where there are fewer than fifty births. Resultsare weighted by the number of births in the cell.
The neonatal mortality rate averages about twelve deathsper 1,000 births for whites and nineteen for blacks, withabout half of the deaths where the cause of death indicatesthose possibly affected by nutritional deficiencies. Theresults for whites and blacks show that the FSP leads to areduction in infant mortality, with larger impacts for deathspossibly affected by nutritional deficiencies. None of theestimates, however, are statistically significant. Overall, theeffect 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 countyis 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 studydiffer from the main results.
400 THE REVIEW OF ECONOMICS AND STATISTICS
inflated) for all causes is about 4% for whites and between4% and 8% for blacks. These estimates are roughly in linewith the birth weight–neonatal mortality rate relationshipestimated by Almond et al. (2005): for whites, we estimate
a very similar birth weight-mortality relationship, althoughthe relationship between birth weight and mortality we esti-mate for blacks is substantially stronger than in Almondet 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: WhitesAverage 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 73,676R2 0.16 0.16 0.18 0.10 0.11 0.13 0.12 0.12 0.15Mean of dependent variable 12.00 12.00 12.00 6.26 6.26 6.26 5.74 5.74 5.74
B: BlacksAverage 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 17,695R2 0.42 0.44 0.43 0.34 0.36 0.36 0.26 0.29 0.28Mean of dependent variable 18.94 18.94 18.94 9.02 9.02 9.02 9.91 9.91 9.911960 CCDB � linear time X X X X X XREIS controls X X X X X X X X XCounty per capita real income X X X X X X X X XYear � quarter fixed effects X X X X X X X X XCounty fixed effects X X X X X X X X XState � linear time X X XState � year fixed effects X X XCounty � 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 (proxyfor 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, controlsinclude 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 timetrend, 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 andare 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: WhitesAverage 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 120,293 120,293 120,293 120,293 120,293Mean of dependent variable 19.40 19.40 19.40 19.40 19.40
B: BlacksAverage 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 44,044Mean of dependent variable 26.24 26.24 26.24 26.24 26.241960 CCDB � linear time X X X X XREIS controls X X X X XCounty per capita real income X X X X XYear � quarter fixed effects X X X X XCounty fixed effects X X X X XState � 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 meansby 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 populationblack, 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 estimateof the food stamp participation rate for the regression sample.
401INSIDE THE WAR ON POVERTY
(not affected by nutritional deficiencies), which are oppositesigned and much smaller in magnitude (although again sta-tistically significant), as favorable evidence that the mortal-ity estimates are coming from the FSP. Online appendixtable 9 separates the mortality effects by quartiles of thecounty poverty rate, and while imprecisely estimated findsa negative effect in the highest-poverty counties but a posi-tive one in the lowest-poverty counties that were unlikely toexperience a substantial FSP treatment.
Online appendix table 10 presents results for all races forthe full period from 1959. We are unable to present resultsby race here because the denominator (live births by countyand time) is not available by race prior to 1968. The firstthree columns replicate the results in table 6 for 1968 to1977 for all races. In the subsequent columns (for 1959–1977 and 1964–1977), we find results very similar to thosefor 1968 to 1977. Overall, FSP implementation leads to areduction in neonatal mortality, although not statisticallysignificantly 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 ofother antipoverty programs. This uniformity was deliber-ately preserved through the major reforms to welfare underthe 1996 Personal Responsibility and Work OpportunityReconciliation 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 aboutFSP effects.
In contrast to other major U.S. antipoverty programs, theFSP was rolled out county by county. This feature of imple-mentation allows us to separate the introduction of foodstamps from the other major policy changes of the late1960s and early 1970s. Although FSP benefits were (andare) paid in vouchers that themselves could be used only topurchase food, because the voucher typically representedless 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, wefind increases in mean birth weight for whites and blacks,with larger impacts estimated at the bottom of the birthweight distribution (that is, low birth weight and very lowbirth weight). Consistent with expectations, we find largerbirth weight effects for black mothers and those living inhigh-poverty areas—populations where FSP participation ismore common. Consistent with epidemiological studies,FSP availability in the third trimester had the largest birthweight impact. We conclude that despite not targeting preg-nant women, the introduction of the FSP increased birthweight. This finding is all the more noteworthy given the
mixed success that randomized interventions have had inraising 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 samplesfrom vital statistics data. One interpretation is that statisticalpower is lost when analyzing gestation length (incompletereporting by states) and mortality (rare). Leaving the impre-cision issue aside, gestation length and mortality appear lessaffected than the likelihood of low and very low birthweight.
At a minimum, our results indicate that the FSP had animmediate first-stage impact on newborns. Furthermore,these estimated impacts (as reflected by birth weight) aremuch larger in high-poverty counties. Our findings revealthat an exogenous increase in income during a well-definedperiod, pregnancy, can improve infant health. Future workshould consider whether this FSP-induced birth weightimprovement is reflected in subsequent outcomes and howpoverty and birth weight may mediate this relationship.
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