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The Price Effects of Family Caps on Fertility Decisions of Poor WomenRadha Jagannathanab; Michael J. Camassoc; Carol Harveyd

a Bloustein School of Planning and Public Policy, Rutgers University, New Brunswick, NJ b Office ofPopulation Research, Princeton University, Princeton, NJ c Department of Agricultural Food andResource Economics, Rutgers University, New Brunswick, NJ d School of Biological and EnvironmentalSciences, Rutgers University, New Brunswick, NJ

Online publication date: 27 July 2010

To cite this Article Jagannathan, Radha , Camasso, Michael J. and Harvey, Carol(2010) 'The Price Effects of Family Capson Fertility Decisions of Poor Women', Journal of Social Service Research, 36: 4, 346 — 361To link to this Article: DOI: 10.1080/01488376.2010.494084URL: http://dx.doi.org/10.1080/01488376.2010.494084

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Journal of Social Service Research, 36:346–361, 2010Copyright c© Taylor & Francis Group, LLCISSN: 0148-8376 print / 1540-7314 onlineDOI: 10.1080/01488376.2010.494084

The Price Effects of Family Caps on Fertility Decisionsof Poor Women

Radha JagannathanMichael J. Camasso

Carol Harvey

ABSTRACT. Family Caps have been a popular welfare reform policy designed to discourage womenon welfare from bearing additional children. It has been thought that the principal mechanism throughwhich a Cap achieves its objective of lower birth rates is the financial pressure placed on women by thedenial of cash benefits. Our study uses instrumental variables Probit modeling to directly measure thecontribution that price makes to Cap impact on births. We reexamine data from the New Jersey FamilyDevelopment Program (n = 8,393) experiment and find that only a very small percentage (about 2.5%)of the overall Family Cap effect reported in earlier studies can be attributed to price. Moreover, the priceeffect holds only for short-term Black welfare recipients. We speculate that much of the unexplainedFamily Cap treatment effect stems from a message of social pressure and disapproval toward welfarereceipt and childbearing on welfare. We offer a possible direction for future research which woulddirectly measure the social disapproval component.

KEYWORDS. Family Cap, social experiment, price effect, IV Probit, fertility impacts

INTRODUCTION

Public assistance has long been implicated asa cause of the higher-than-average rates of child-bearing observed in the population of welfare-eligible women (Becker, 1991, 1996; Murray,1993). It has been maintained by the critics ofthe old Aid to Families with Dependent Children(AFDC) that benefit levels, and perhaps moreimportantly the incremental benefit increases

Radha Jagannathan is an Associate Professor at Rutgers University, Bloustein School of Planning andPublic Policy, New Brunswick, NJ, and a Visiting Scholar at Princeton University, Office of PopulationResearch, Princeton, NJ.

Michael J. Camasso is a Professor at Rutgers University, Department of Agricultural Food and ResourceEconomics, New Brunswick, NJ.

Carol Harvey is the Assistant Director for Administration at Rutgers University, School of Biological andEnvironmental Sciences, New Brunswick, NJ.

Address correspondence to: Radha Jagannathan, Associate Professor, Bloustein School of Planningand Public Policy, Rutgers University, 33 Livingston Avenue, New Brunswick, NJ 68901 (E-mail:radha@rci.rutgers.edu).

triggered by each additional birth, encouragedwomen to conceive children even if the con-ceptions occur outside marriage (Haskins, 2001;Jagannathan & Camasso, 2003).

In 1992, New Jersey became the first state to“uncouple” benefit increments from births con-ceived while the mother was receiving publicassistance. This policy, known variously as theFamily Cap or Child Exclusion Provision, de-nied additional cash benefits to any child born

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Family Caps and Fertility Decisions of Poor Women 347

10 or more months after a woman entered thewelfare rolls. Because women must have had atleast one child to qualify for welfare benefits,the Cap could only affect higher-order births. InNew Jersey, if the child was the second born,the benefit loss was $102 a month; the loss was$64 a month for any higher-order births. All“capped” children remained eligible for otherbenefits such as food stamps and Medicaid in aneffort to soften the financial impact on the af-fected child(ren). Following New Jersey’s lead,22 additional states have incorporated some formof a Family Cap into their welfare reform pro-grams (Harvey, Camasso, & Jagannathan, 2000).Like New Jersey’s Family Cap, nearly all ofthese state Cap policies remain in effect today,functioning much the same today as they did inthe mid-1990s.

Virtually all of the research conducted bysocial scientists on the effectiveness of FamilyCaps in lowering birth rates has framed the re-search question as a woman’s response to theprice considerations of conceiving an additionalchild. This inclination has been fueled by apolicy literature and a popular press that oftencouches discussions of child exclusion provi-sions under such titles as “New Jersey’s $64Question” (Goertzel & Hart, 1995), “The Priceof Virtue” (Brinig & Buckley, 1999), or “Doingthe Math on the Welfare Family Cap” (Vobejda& Havemann, 1997).

But are benefit losses the dynamic whichcauses Family Caps to reduce births, if indeedthey reduce births at all? It is our contention thatthe denial of additional benefits is only one ofthe mechanisms triggered by Family Caps thatinfluences a woman’s fertility decisions. Equallyor perhaps more important is the moral exhor-tation to live a life free of welfare dependency(Kocieniewski, 2003), what some social scien-tists have called the “message effect” (Blank,2001; O’Neill & Hill, 2001). The message in-herent in Family Cap legislation clearly identi-fies a birth while on welfare as an indication of awoman’s disregard for her child’s social and eco-nomic well-being (Harvey et al., 2000). Perhapsinstead of “doing the math,” women respondto the Cap by “doing what is expected” in anunfriendly policy environment (e.g., have fewerbirths).

The notion that Family Caps influencefertility behavior through multiple motivationalmechanisms begs the question of who respondsto potential benefit loss and who is driven by abroader social message. The growing literatureon social capital (Becker, 1996) and socialapproval (Bertrand, Luttmer & Mullainathan,2000; Murray, 1993; Nechyba, 2001) providessome guidance here. It would be expectedwithin this framework that women whosesocial capital is influenced by peers and otherswith extensive public assistance experienceswould be reluctant to risk disapproval by thesepeers. Responses to the Cap in such instanceswould be halting, with the demand for childrenmore likely to be a function of expectedprogram penalties. Conversely, women withlittle experience on public assistance wouldbe expected to have less personal and socialcapital invested in a pre-Cap system of welfarebenefit increments and should heed the adviceof social responsibility more readily, resultingin fewer nonmarital births. In this article, weseek to determine how much of the Family Capfertility effect can be attributed to the monetarypenalties that women are confronted with whenthey have a second or subsequent child whilereceiving welfare. We then use our treatmentestimates to help us understand how much of theFamily Cap effect may be the result of social ornonmonetary factors such as social pressure ordisapproval.

To put our research question to empirical test,we use data from a classical experimental designwith 8,393 New Jersey welfare recipients ran-domly assigned to treatment and control groups.Random assignment and control over the Fam-ily Cap treatment has advantages over the cross-state comparisons that are common in this lit-erature. First, the problem of unmeasured influ-ences correlated with welfare benefit levels andfertility outcomes is largely avoided. Second, thedesign can directly tie benefit levels and incre-ments to women without resorting to deviceslike average or fixed household size that can in-crease measurement error. Actual benefits paidvary with household size, number of welfare-eligible household members, other sources ofincome, and other state-specific factors that canaffect an individual woman’s fertility decisions

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348 R. Jagannathan et al.

in real time, helping us to isolate any pure effectof a Family Cap.

THE RESEARCH ON WELFAREBENEFITS AND FERTILITY

Virtually all of the prior studies of welfarebenefit effects and fertility behavior use eithercross-state, time-series comparisons of aggre-gate Vital Statistics data or micro-data fromlarge-scale population surveys such as the PanelStudy of Income Dynamics, the Survey of In-come and Program Participation, the Public UseMicrodata Sample, or the Current PopulationSurvey (CPS). It is useful to classify this recentliterature into three broad groupings: 1) stud-ies that examine the welfare benefit-fertility re-lationship but that do not draw parallels to aFamily Cap; 2) studies that examine the benefit-fertility relationship and view findings as sug-gestive of potential Family Cap effects; and 3)studies that directly measure an operating Fam-ily Cap. Studies in the first category have beenreviewed elsewhere (Moffitt, 1995, 1998), so weonly briefly touch on the more recent work pub-lished since 1993. A good deal of research hasfocused on state differences in benefit levels orchanges in benefits and their effects on births.Although many of these studies (Brinig & Buck-ley, 1999; Clarke & Strauss, 1998; Hoffman &Foster, 2000; Jackson & Klerman, 1996; Lund-berg & Plotnick, 1995; Murray, 1993; Robins &Fronstin, 1996; Rosenzweig, 1999) report sig-nificant, if modest, relationships, some studiesdo not find any welfare effect on births (see, forexample, Acs, 1996). These researchers, how-ever, do not speculate on the implications of theirfindings for any Family Cap effect. In summa-rizing the recent literature on benefit levels andchanges, it would be fair to reprise the conclu-sion drawn by Moffitt (1998, p. 50) in his earlierreview of the welfare benefit-fertility link:

A majority of the newer studies show thatwelfare has a significantly negative effecton marriage or a positive effect on fertilityrather than none at all. Because of this shiftin findings (from earlier studies), the cur-rent consensus is that the welfare system

probably has some effect on these demo-graphic outcomes.

The second group of studies is typically ex-aminations of incremental benefits with the re-searchers providing insights on how their find-ings are indicative of (unmeasured) Family Capeffects. Averett, Argys, and Rees (2000) andPowers (1994) conclude from their analyses thata Family Cap has the potential to lower non-marital fertility. Grogger & Bronars (2001) andFairlie & London (1997) state the Family Cap islikely to have a negligible effect.

Drawing conclusions about Family Cap im-pact from studies of benefit levels or benefitchanges is not as straightforward as it might ap-pear. Benefit levels may be endogenous (i.e., theactual effect of state birth rates, rather than theircause; Moffitt, 1998; Schettini-Kearney, 2004).Benefit levels of states tend to be highly corre-lated with marginal benefit levels in those samestates, making it difficult for researchers to deter-mine which component is truly driving any fertil-ity effect (Camasso, 2004). Cross-state compar-isons are also subject to unobserved differences,which may cause benefit levels and fertility tocovary across states, irrespective of any welfarepolicy changes (Hoynes, 1997; Nechyba, 2001).

More recently, studies have used an actualor potential exposure to a Family Cap insteadof incremental benefit changes. In these studies,Family Cap is measured as the presence or ab-sence of the policy across states and/or times.Dyer and Fairlie (2004), for example, use CPSdata from 1989 to 1999 to examine the impactof Family Cap policies on birth rates of “single,less educated women with children aged 15-45”in five states and find nonsignificant and nega-tive Family Cap coefficients for three of the fivestates and nonsignificant but positive coefficientsfor the other two states.

Horvath-Rose and Peters (2001) comparebirth data from Vital Statistics for Family Capand Non-Cap states from 1984 through 1996while also controlling for the potential influenceof other welfare reform interventions, includ-ing time limits and work requirement waivers.These researchers report declines in the nonmar-ital birth ratios for women aged 20 to 49 years

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Family Caps and Fertility Decisions of Poor Women 349

in Family Cap states that are 9% to 12% lowerthan comparison states.

Schettini-Kearney (2004) also uses VitalStatistics to examine the impact of Family Capon births but focuses her analyses on womenaged 15 to 34 for the years 1989 to 1998. Thisresearcher reports that there is no evidence thatFamily Caps lower fertility in models with stateand month fixed effects, but also acknowledgesa series of “curious” significant positive Fam-ily Cap effects. Caps, for example, are foundto increase birth rates among unmarried Blackwomen who are high school dropouts, Whitewomen who dropped out of high school, andBlack unmarried teens.

Kaushal and Kaestner (2001) use CPS datafrom the March 1995 to 1999 series to focus onthe impact of Family Caps and time limits onfertility among unmarried women with at leastone child. These researchers find that only in theinstance when a state adopts both a Family Capand time limits is there a significant impact onbirths. Kaushal and Kaestner (p. 716) point out,however, that those estimates are positive, “in-dicating that welfare reform increased fertility, aresult that counters almost all theory.”

Joyce, Kaestner, Korenman, and Henshaw(2004) restrict their analyses to women 15 to34 and limit their sample of low-income, un-married women (women more likely affected bya Family Cap) to 18 states. The authors concludethat there have been no major reproductive re-sponses due to a Family Cap. Like Schettini-Kearney (2004), these authors find statisticallysignificant positive effects of Family Caps onbirths both within Cap states and in cross-statecomparisons.

Sabia (2008), using aggregate state-level dataon births from the National Center for HealthStatistics for the period of 1984 to 1998, reportsthat Family Caps are associated with a reduc-tion in nonmarital birth rates of between 5% and6%. Mach (2001) uses data from the CPS forthe years 1989 to 1998 to determine if a Fam-ily Cap influences birth rate of women aged 18to 44 years. In addition to measuring the Capas a simple dummy variable, Mach attempts toaugment this specification with a measure of ef-fective benefit loss. She links households in CPSfrom year to year in an attempt to more realis-

tically model exposure to Cap penalties whichtypically target births conceived while on wel-fare. Mach also performs separate analyses forwelfare users and nonusers and finds that theFamily Cap reduces births among welfare recip-ients by 10%. She also reports that a $50 in-crease in the benefit penalty yields a substantialdecrease in births among welfare recipients.

Although Family Cap effects have typicallybeen measured with simply presence or absencedummies, results are usually reported as sensi-tivities to expected cash penalties. Kaushal andKaestner (2001, p. 718), for example, concludefrom their analyses that the absence of a signif-icant birth effect may indicate that cash assis-tance is not an important determinant of fertil-ity. For Schettini-Kearney (2004), her dummyvariable coding of the Family Cap is equivalentto an effect of incremental welfare benefits onfertility. Such an inference assumes that Capswork solely on the basis of the threat of cashpenalty.

Of course, the examination of multiple mech-anisms through which a Family Cap might work(i.e., responsiveness to expected cash penaltyvis-a-vis response to expected social disap-proval) would require multiple treatment spec-ifications (Angrist, Imbens, & Rubin, 1996;Gennetian, Bos, & Morris, 2002). Of the studieswe have reviewed, only Mach (2001) attempts toundertake such analysis with her augmentationof a Family Cap dummy with maximum andincremental welfare benefit estimations. How-ever, when cross-state studies of Family Capimpact use cash benefit amounts to more realis-tically assess the influence of monetary penalty,as Mach attempts to do, they face the additionalproblem of interstate difference in benefit lossoffsets that are frequently used to compensatecapped households. In New Jersey, for exam-ple, cash assistance is viewed as countable in-come, and food stamp amounts are decreased byabout $0.30 for each additional assistance dol-lar received. The opposite is also true: If thehousehold loses dollars due to a capped child,the food stamp allotment increases by $0.30 foreach lost cash assistance dollar. Specifications ofbenefit loss which do not adjust for these state-specific offsets risk substantial measurementerror.

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350 R. Jagannathan et al.

METHODOLOGY AND DATA

Conceptual Framework

As our conceptual starting point, we hypoth-esize that a Family Cap affects fertility throughboth a money loss response and through avoid-ance of social disapproval. We initially treatfertility decisions within an economic frame-work where the family is assumed to maximizeutility (which includes the number of childrenas an argument) subject to constraints on its re-sources of money and time (Becker, 1991, 1996;Cigno, 1991).

Nechyba (2001) maintains that the frequencyof out-of-wedlock births in a community deter-mine the level of social approval enjoyed by awoman if she herself becomes a single mother.Following Becker (1996) and Coleman (1990),it would be expected that women with highstocks of social capital invested in communitynetworks that condone a reliance on public as-sistance would ignore the advice (threat) of aFamily Cap and its message of personal respon-sibility for childbearing decisions. Any changein preference here would have to rely on a FamilyCap’s capacity to reduce personal capital stocksof actual benefits, since social norms are typi-cally slow to change (Coleman; Murray, 1993).Conversely, a Cap would be hypothesized to re-inforce community norms that disapprove of areliance on public assistance to support chil-dren. Women embedded in such social networkswould be expected to view the Cap’s messageas resonating with their individual and socialpreferences, further stimulating predisposed be-havior. Although we do not directly observe ormeasure community network effects in this ar-ticle, we believe our attempt to isolate the puremonetary effects of the Cap moves us in thedirection of a better understanding of possiblecommunity effects.

Experimental Design and ModelEstimation

Our test of a Family Cap monetary penaltyhypothesis is undertaken using a classical exper-imental design with randomization of subjectsinto experimental and control groups. This de-

sign was a requirement of the Administration forChildren and Families for New Jersey’s welfarereform that was undertaken from October 1992through December 1996. The reform, knownas the Family Development Program (FDP),contained only two components (waivers) thatcould be categorized as high intensity (Kaushal& Kaestner, 2001) or tough initiatives (Harveyet al., 2000; Schiller, 1999) with the potential foraffecting fertility: a Family Cap and an enhancedwork (Job Opportunities and Basic Skills;JOBS) program. Previous research by Camasso(2004) showed that nearly all the fertility effectsof FDP resulted from the Family Cap provision.

Experimental design has a number of ad-vantages over cross-state comparisons, not theleast of which is a clear counterfactual condi-tion (LaLonde, 1986; Orr, 1999). In the NewJersey experiment, evaluation samples weredrawn from the 10 largest welfare counties thataccount for 85% of the state’s welfare case load.Women were drawn from two distinct groupswithin each county’s welfare population:

� Families who were active on public wel-fare (AFDC) when the Family Cap wasimplemented on October 1, 1992, labeled“ongoing cases”; and

� Families who were certified for welfare re-ceipt between October 1, 1992, and De-cember, 1994, labeled “new applicants.”

Assignment to experimental and controlgroups was based on the last four digits of thewelfare payee’s social security number. The ex-periment was designed to randomly select 9,000cases from the case load with 6,000 to be as-signed to the experimental group that followedthe same rules as the overall case load since theFDP reform went into effect statewide in Octo-ber 1992. Controls were to comprise 3,000 casesrequired to follow pre-FDP (AFDC) rules. Thefinal sample fell short of the targeted 9,000 casesand contained a slightly larger number of ongo-ing cases and fewer new cases (the latter due toa slower-than-expected rate of new case entry).The final disposition of the 8,393 cases selectedis shown in Table 1.

Inasmuch as the Family Cap was enactedstatewide simultaneously with the start of theexperiment, case workers and administrators did

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Family Caps and Fertility Decisions of Poor Women 351

TABLE 1. Final Disposition of Cases Used inthe Experiment

Sample Group Case Type Number of Cases

Experimentals New 2,233Ongoing 3,268

Controls New 1,285Ongoing 1,607

Total 8,393

not have to conduct a special orientation for ex-perimental cases. Program administrators did,however, face the task of ensuring that approxi-mately 3,000 controls who were exempt from theFamily Cap and other provisions of the FDP con-tinued to follow pre-reform rules. Absent prob-lems such as differential attrition and controlgroup contamination, any post-assignment dif-ferences in fertility behavior can, in principle,be interpreted as the effect of the Family Cap.Previous analysis of these potential confoundsrevealed that such problems presented minimalthreat to the experiment’s integrity (Camasso, Ja-gannathan, Harvey, & Killingsworth, 2003; Ja-gannathan, Camasso, & Killingsworth, 2004).

The decision to stratify the sample into newand ongoing cases stems from the work of Baneand Ellwood (1986). These researchers wereamong the earliest to recognize that the welfare

TABLE 2. Differences Between New and Ongoing Cases in (a) Welfare Spell Length and (b)Welfare Chronicity

New Cases Ongoing Cases

Experimental Group Control Group Experimental Group Control Group

(a) Spell LengthMean quarters 6.4 6.5 10.8 10.9Median quarters 6 6.1 11.9 12.1Total person-quarters 13,479 7,460 31,349 14,853Total cases∗ 1,918 1,087 2,856 1,377

(b) Chronicity% short-time users (6 quarters or fewer) 49.1 51.5 26.5 27.8% chronic users (14 quarters or more) 9.5 9.8 43.3 41.5% returners/cyclers 41.4 38.7 30.2 30.7

∗Fewer total cases are used in the fertility analysis than appear in Table 1 because female payees older than 45 years of age were excludedas not being at risk.Note. Chi-square tests reveal no statistically significant differences between the experimental group and the control group in either welfarespell length (panel [a]) or welfare chronicity (panel [b]).

population contained groupings of recipientswho were likely to respond to welfare reformquite differently. Women who use welfare forshort spells were viewed as having a higher mar-ket value for their time as evidenced by theircontinuing if not steady pattern of employmentcompared with more long-term welfare users.With higher opportunity costs, short-term wel-fare users are more likely, for example, to substi-tute labor market work for childbearing and aretherefore more likely to exhibit a more elastic re-sponse to welfare reform’s monetary provisions.In Table 2, we present evidence from a spell-length analysis of new and ongoing cases whichindicates that the two groups differ dramaticallyin their reliance on public assistance.

Ongoing cases spent, on average, about twiceas much time on assistance during the experi-mental period as new cases (panel [a]). Panel (b)confirms that substantially higher percentages ofongoing cases received welfare for 14 quartersor more compared with new cases. It should benoted that random assignment ensures that thereare no significant differences between the ex-perimental and control groups within each casetype, either in spell length or chronicity. Webelieve these data indicate that ongoing casescomprise a population of chronic or long-termrecipients while new cases closely mimic theacute or short-term users who Bane and Ellwood(1986) maintain are “less” heavily invested in the

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352 R. Jagannathan et al.

public assistance system and the social networksthat support long-term welfare use.

Typical modeling of randomized experimentsinvolves a simple regression specification:

Yit = a + bEit + cXit + eit (1)

where “Y” is the outcome of interest (e.g., fer-tility); “E” is a dummy variable representing ex-perimental status, equal to 1 for experimentalparticipants and equal to 0 for controls; “X” is avector of other observed characteristics; “e” is arandom error term; and the i and t subscripts de-note individuals and time periods, respectively.By virtue of random assignment, “E” and “e” areuncorrelated and an unbiased effect of the exper-iment on the outcome is given by the parameter“b.”

There are at least two potential problems withthe simple specification in Equation (1). First,the experimental effect parameter “b,” if sig-nificantly different from 0 and if exhibiting thecorrect sign, tells us that the experimental treat-ment worked but does not tell us how or why(i.e., the experiment here is treated as a “blackbox”). Second, the simple specification assumesthat all experimental subjects received the sametreatment and does not allow for the possibilityof different experimental group members expe-riencing different (amounts of) treatments andtherefore gives at best an average intention-to-treat (ITT) estimate. To go beyond the black box,it is necessary to separate or “unbundle” the ef-fect of the Family Cap policy into componentsresponsible for any “black box” effect.

In the general welfare literature, the monetaryeffect of welfare benefits on fertility behavior istypically assessed from quasi or natural experi-ments and modeled as:

Yit = a + bBit + cXit + eit (2)

where “Y” is a measure of fertility, “B” is thelevel of welfare benefits (or in some cases, themarginal benefit paid for an additional child),and “X” and “e” are the same as in Equation(1). The i here, however, indexes states, becausethe variation in “B” is brought about by varyingbenefit levels (increases) across states, a vari-ation that is crucial for the identification of the

welfare benefit effect parameter “b.” Absent ran-domization, we cannot be sure of the exogeneityof “B,” and to the extent that “e” incorporates un-observed cross-state differences in fertility thatare correlated with “B,” the welfare effect pa-rameter “b” will be biased. The obvious solutionto this problem is to find some source of vari-ation in benefits “B” that is uncorrelated withunobservables “e.” The Family Cap experimentin New Jersey offers a unique opportunity todo this by providing the vehicle for generatingclean variation in B since the random assign-ment dummy should be highly predictive of theexpected benefits received by a treatment or con-trol subject. Thus, “E” in Equation (1) serves asan instrument for “B” in Equation (2).

We investigate the “price” effect of a FamilyCap on births using instrumental variable Probitmodels. The basic regression specifications havethe form:

Y∗it = βBit + γ Xit + uit (3.a)

Bit = �1Xit + �2Eit + eit (3.b)

where subscripts i and t respectively index awoman on welfare (age 15 through 45) and time,measured in quarters; “B” is the endogenous in-cremental benefit variable; “X” is a vector ofexogenous variables; “E” is the random assign-ment dummy used here as the instrument; “Y”represents the outcome variable (births) for casei in time t ; “Y∗” the unobserved outcome index,with the observed outcome Yit = 0 if Y∗

it < 0 and1 if Y∗

it ≥ 0; (uit ,eit) ∼ N(0, �); and �1 and �2

are matrices of reduced-form parameters. Theparameter of interest here is β, the “pure” priceor benefit effect of the Family Cap, or the re-sponse of recipients to the size of the penalty afamily faces when there is a capped birth.

The benefit (price) variable “B” for case i

in time t (Bit) is the net change in total bene-fit payments that the individual will receive ifshe gives birth to an additional child. For controlsubjects, this includes increased welfare bene-fits; for experimental subjects—those who aresubject to the Cap—it does not. In both cases,however, “B” includes the net change in othertransfer payments that results from the birth ofan additional child. Specifically, “B” depends

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Family Caps and Fertility Decisions of Poor Women 353

TABLE 3. Incremental Benefits by Eligible Household Size (Dollars)

Incremental Cash Benefits Incremental Food Stamp Benefits(for one additional child) (for one additional child)∗∗

Incremental Change in HouseholdSize due to Birth∗ Family Cap No Family Cap Family Cap No Family Cap

From 1 to 2 eligibles 0 160 92 44From 2 to 3 eligibles 0 102 89 58From 3 to 4 eligibles 0 64 78 59From 4 to 5 eligibles 0 64 70 51From 5 to 6 eligibles 0 64 88 69From 6 to 7 eligibles 0 50 56 41From 7 to 8 eligibles 0 50 83 68

∗For several reasons, eligible household size for cash benefits may differ from the eligible household size for food stamps.∗∗Assumes maximum food stamp allotments from October 1992 to September 1993. Maximum allotments are adjusted upward to allow forinflation.

on number of children and experimental statusand includes not only welfare benefit per se butalso increment in food stamp allotment. Table 3shows the expected incremental benefits byhousehold size for the experimental and the con-trol participants and also compares the expectedincremental benefits (both cash and food stamps)with and without the Family Cap for an increasein household size due to a birth. Although thehouseholds that are subject to the Family Cap donot receive any additional cash benefits after thebirth of another child, their food stamp incre-ment (FSI) is larger than that for similar-sizedhouseholds which are not subject to the FamilyCap. This is a simplified calculation and ignorespotential complications that may be introducedby concurrent changes in other factors (e.g., re-ceipt of income from sources other than AFDCcash benefits, the imposition of sanctions andtheir impact of AFDC benefits, and so on) thatcan affect the calculation of both cash and foodstamp benefits. Also, even within a householdnot subject to the Family Cap, the number offood stamp-eligible members may not equal thenumber of AFDC cash-benefit eligibles. Othersources of income (e.g., receipt of SupplementalSecurity Income) or the imposition of sanctionsfor failure to cooperate with job training require-ments may disqualify a household member fromreceipt of AFDC cash benefits, but that individ-ual will still be eligible for food stamps.

For experimental cases, benefits equal an FSIonly since cash payments are capped. FSI is cal-

culated as:

FSI = FSmax t,n+1 − FSmax t,n (4)

FSmax here is the maximum food stamp allot-ment at time t for food stamp-eligible householdsize n. Food stamp amounts are determined bythe number of food stamp-eligible members inthe household and by the amount of income re-ceived by the household. There is a maximumfood stamp allotment for each household sizethat is set for 1 year (October through Septem-ber) and increases each year with the cost ofliving. The food stamp calculation begins withthis maximum amount adjusting it downward totake into account household income and otherfactors that affect food stamp benefits. Once thehousehold’s food stamp allotment is determined,any additional “countable” income received bythe household—and this income includes cashassistance—will result in a reduction in thefood stamp allotment. For control cases, ben-efits equal cash benefits (CB) and a FSI. Here,however, FSI is calculated as

FSI = FSmax t,n+1 − FSmax t,n − (0.30∗CB)(5)

where the maximal food stamp allotment is de-creased by $0.30 for each additional welfare dol-lar received. For example, for a control grouphousehold, the birth of a second child will re-sult in an increase of $102.00 in cash assistance

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354 R. Jagannathan et al.

but will reduce the maximum food stamp allot-ment for a family of three by $127.20 or 30% ofcash assistance grant for a total combined bene-fit of ($322 + ($315 – 0.30∗$322)), or $540.40.For an experimental group household, the birthof a second child would result in a total com-bined cash assistance and food stamp benefit of($162.0 + $315.0), or $477.00. Benefit amountsand increments are adjusted for inflation usingthe average Consumer Price Index for each quar-ter from October 1992 through December 1996.

Vector X in Equations (3.a) and (3.b) includesa linear time trend which measures the effectsof otherwise unmeasured factors that changesmoothly over time, seasonal indicator mea-sures that capture seasonal patterns in births,and biographic and demographic characteristicsof the woman receiving assistance, namely race,age, education, number of children, and mari-tal status. “X” also includes area economic andother contextual measures to adjust for location-specific criteria such as local economic con-ditions and other possible time-invariant (andotherwise unobservable) influences operating atthe county level. These covariates include a se-ries of nine dummy variables to represent thecounties in the sample. Also contained in “X”are county unemployment rates from Decem-ber 1992 through December 1996 to control forchanges in local labor market conditions dur-ing the study period. Because our data con-tains repeated observations, we employ Huber-corrected standard errors to adjust for possibleclustering effects.

Data Source and Structure

Ethical approval for the study was granted byRutgers University Institutional Review Boardin the Office of Research and Sponsored Pro-grams, Human Subjects and Animal Care, un-der Protocol #E94-107 in January of 1993. Dataon births were obtained from administrativerecords maintained by the state’s welfare as-sistance agency. These data identify births re-ported to women receiving cash assistance dur-ing a quarter. The birth outcome variable is codedeach quarter as 1 if a birth occurred, 0 if not. Allright-hand side measures in specifications (3.aand 3.b) were also gleaned from administrative

databases with the exception of county unem-ployment rates, which were obtained from theNew Jersey Department of Labor.

These quarterly data were then pooled to forman unbalanced panel that included observationsfor each quarter a woman was enrolled on wel-fare during the study period. A sample case ob-servation was included in the analysis for thosequarters in a year that the case was listed on thewelfare rolls. We do not have information on fer-tility outcomes when cases are not on the rolls;hence, the design does not allow us to estimateaverage treatment effects (ATE; i.e., the aver-age effect of FDP if all members in the experi-mental group received complete and continuousexposure to FDP inputs). However, the designdoes provide the empirical basis to compute ITTestimates based on the available observations,assuming that differential attrition and controlgroup contamination are not present in the ex-periment.

Potentially, we had 17 quarterly observationsfor each ongoing case with fewer observationsfor new cases selected into the sample after thefourth quarter of 1992. During the evaluationperiod, many recipients left welfare for varyingperiods. If and when these individuals returnedto the rolls, they retained their original caseidentification number, random assignmentstatus, and case type and were again includedin the sample. As can also be seen from Table2 panel (b), the returners or cyclers comprisedabout 40% in the new case group and 30%in the ongoing case sample. It is important tonote that there were no significant differencesbetween the experimental and control groups inthe proportion of short-time, chronic or return-ers/cyclers. Women who stayed on the rolls forsome or all 17 quarters and who may have givenbirth beyond the study period are essentiallyright censored and are not counted beyond De-cember 1996. This structuring of data produceda total of 66,992 person-quarter observations.

Sample Characteristics

The characteristics of the experimental sam-ple at time of entry into the experiment arepresented by treatment status and case type inTable 4.

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Family Caps and Fertility Decisions of Poor Women 355

TABLE 4. Sample Characteristics by Experimental Status and Case Type

Ongoing Cases New Cases

Characteristic Experimental Control Experimental Control

PercentageCounty of Residence:

Atlantic 4.13 4.40 7.14 5.97Camden 13.54 14.39 12.08 12.17Cumberland 3.95 4.15 5.81 4.61Essex 30.40 30.55 21.28 19.81Hudson 18.93 17.54 15.06 15.67Mercer 4.59 5.53 6.50 7.48Passaic 6.35 6.98 9.75 10.18Union 6.57 6.22 7.09 6.68

Race/Ethnicity:White 14.59 15.96 19.63 20.60Black 50.67 53.10 44.27 44.72Hispanic 33.46∗∗ 29.33 32.06 30.35Other 1.11 1.32 2.88 2.86

Age:Younger than 20 1.02 0.69 9.29 9.5520–24 15.36 13.95 16.75 15.2725–29 22.42 23.95 20.59 21.8830–34 21.09 20.93 19.77 19.8935–39 19.18 17.66 14.32 12.2540–44 10.55 10.25 7.51 8.4345 and older 9.28 10.94 6.77 6.84

Education:Less Than High School 40.10 40.70 31.60 31.36High School 38.81 38.05 45.01 43.35College 8.97 9.60 12.87 15.46Other 0.77 0.66 0.25 0.61

Marital Status:Never Married 64.52 67.73 58.91 57.57Married 7.27 6.77 13.78 13.10Widowed 0.97 0.83 0.58 0.42Separated/Divorced 27.24 24.67 26.73 28.91

Employed 14.46 14.39 13.64 14.24Mean

Age 32.47 31.75 30.30 30.36Number of Eligible Children 1.88 1.82 1.66 1.68Earned Income Averaged Over

Entire Sample 124.47 134.24 127.42 135.64Those Working 852.98 910.44 893.67 904.78

Number of Cases 3, 243 1, 591 2, 185 1, 257

∗∗p < .05.

The overall sample was approximately 50%Black, 17% White, and 33% Hispanic. Themean age was 32 years with a majority ofwomen between 20 and 39 years of age. About37% of the sample did not finish high schoolwith about 40% holding a high school diploma.Sixty-three percent of the sample has neverbeen married, and about 14% reported some

earning from work sometime during the studyperiod.

It is evident from Table 4 that new cases differfrom ongoing cases in a number of ways. Moth-ers on new cases tend to be younger, to havefewer children on welfare, and are more likely tohave completed high school and to have attendedcollege. New-case women are also less likely to

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356 R. Jagannathan et al.

TABLE 5. Variation in Marginal Benefits Resulting from Random Assignment of Recipient intoFDP Treatment and Control Groups Using IV Probit Estimation

New Cases Ongoing Cases

Instruments All Cases Whites Blacks Hispanics All Cases Whites Blacks Hispanics

Assignment –58.33 –54.65 –54.71 –55.31 –51.52 –51.73 –52.10 –50.15(0.853)† (1.52) (0.952) (1.23) (0.551) (1.48) (0.740) (0.992)–68.36†† –35.77 –57.48 –44.78 –93.48 –34.85 –70.37 –50.53

Time on FDP –0.846 –0.396 –0.539 –0.478 –0.282 –0.324 –0.293 –0.246(0.098) (0.106) (0.058) (0.072) (0.020) (0.057) (0.028) (0.035)–8.621 –3.72 –9.18 –6.64 –13.75 5.69 –10.48 –6.97

Assignment × Time 0.577 ns ns ns ns ns ns nsInteraction (0.103)

5.61Intercept 140.57 136.67 139.71 137.70 132.44 134.08 133.46 129.73

(0.818) (1.481) (0.948) (1.195) (0.536) (1.435) (0.719) (0.971)171.85 92.23 147.36 115.22 246.81 93.40 185.57 133.49

VarianceExplained by Instruments 77.2% 76.6% 76.5% 77.3% 77.0% 76.7% 75.9% 76.1%

†Robust standard error.††T-value.

have never been married. Whereas slightly morethan 50% of the ongoing sample is Black, only44% of new cases are Black. Table 4 also showsthe equivalence between experimental and con-trol groups on virtually all sample characteris-tics, indicating that randomization was success-fully carried out. Of the 32 comparisons madebetween the experimental and control groups,only one difference (proportions of Hispanics inexperimental and control groups) was statisti-cally significant (p < .05).

RESULTS

We present results from the instrument vari-ables component of our IV Probit analysis onTable 5. For both new and ongoing cases andfor all race-specific analyses within these twogroups of cases, assignment status is found toexert a profound effect on marginal benefits andwould appear to satisfy the relevance as wellas the exogeneity assumptions of instrumentalvariable use. As the table also shows, assign-ment is far more predictive of benefits than istime on welfare or the interaction of assignmentand time.

Table 6 shows the results from the IV Probitestimation of births for all ongoing cases com-bined and in a series of race-specific analyses(Equation [3a]). The effect of marginal bene-fits is not significant, consistent with previousanalyses of ongoing cases that measured treat-ment effect with a simple Family Cap assign-ment dummy.

Table 7 presents birth outcome results for newcases, showing significant effects when all newcases are pooled. The table also pinpoints thatthis new case effect emerges from the Black wel-fare recipients only.

Specifically, a dollar increase in the bene-fits increases the Probit index significantly by.0013 for all new cases and by .0022 for new-case Blacks. The corresponding marginal effect(shown in Table 8) is .0001 in both instances,implying that a dollar increase in the marginalbenefits leads to an increase in birth probabilityby .0001 for all new cases and for Blacks. How-ever, the Cap led to a decrease in the marginalbenefit of about $55 on average, reducing wel-fare benefits (considering both AFDC and foodstamps) by this amount. Therefore, the marginaleffect implies that a $55 reduction in bene-fits leads to a little more than half a percent

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Family Caps and Fertility Decisions of Poor Women 357

TABLE 6. IV Probit Regression of Births on Price for Ongoing Cases by Race

All Ongoing Cases Whites Blacks Hispanics

Coef. Std. Error Coef. Std. Error Coef. Std. Error Coef. Std. Error

Marginal Benefits 0.0002 0.0006 0.0015 0.0017 0.0004 0.0007 −0.0007 0.0011June −0.0782∗ 0.0417 0.0765 0.1383 −0.0687 0.0526 −0.1356∗ 0.0803September −0.0508 0.0452 −0.0991 0.1639 −0.0242 0.0564 −0.0820 0.0860December −0.0320 0.0393 0.0398 0.1222 −0.0127 0.0500 −0.1030 0.0767Black 0.0514 0.0481Hispanic −0.0186 0.0499< High School −0.0257 0.0530 0.0692 0.1519 −0.1056 0.0925 −0.0097 0.0724High School −0.0620 0.0557 0.0367 0.1565 −0.1375 0.0948 −0.0487 0.0786> High School −0.1693∗∗ 0.0869 −0.1062 0.2630 −0.3198∗ 0.1291 −0.0491 0.1432Single −0.0126 0.0382 0.0901 0.0918 −0.0193 0.0595 −0.0201 0.0619Age 0.0033 0.0228 0.0809 0.0730 0.0035 0.0310 0.0017 0.0417Age Squared −0.0009∗∗ 0.0004 −0.0021 0.0013 −0.0009 0.0006 −0.0009 0.0007Number of Children 0.0222∗ 0.0134 0.0073 0.0440 0.0385∗∗ 0.0157 −0.0262 0.0302County Unemployment 0.0624 0.0222∗∗ 0.0845 0.0643 0.0531∗ 0.0286 0.0806∗ 0.0451County JOBS Participation −0.0046 0.0027∗ −0.0042 0.0071 −0.0035 0.0036 −0.0074 0.0058Constant −1.7748 0.3971 −3.6154 1.1655 −1.6555 0.5257 −1.4973 0.7758

Note. All regressions include county fixed effects.Robust standard errors are reported.∗p < .1. ∗∗p < .05.

decline in birth probabilities (0.0001 ∗−55 =0.0055).

It should be noted here that the pattern ofsignificant results for the monetary component

of the Family Cap found in these analyses arevery similar to the pattern found in earlier anal-yses that modeled the Family Cap as an overalltreatment dummy variable (Jagannathan et al.,

TABLE 7. IV Probit Regression of Births on Price for New Cases by Race

All New Cases Whites Blacks Hispanics

Coef. Std. Error Coef. Std. Error Coef. Std. Error Coef. Std. Error

Marginal Benefits 0.0013∗∗ 0.0006 −0.0007 0.0015 0.0022∗∗ 0.0008 0.0009 0.0011June 0.0607 0.0527 0.0328 0.1312 0.0966 0.0720 0.0263∗∗ 0.1019September 0.2137∗∗ 0.0584 0.0993 0.1519 0.2090∗∗ 0.0794 0.3223∗ 0.1093December 0.1784∗∗ 0.0594 0.2795 0.1419∗∗ 0.1441∗ 0.0828 0.1977 0.1115Black 0.0908∗ 0.0503Hispanic 0.0151 0.0545< High School −0.0079 0.0656 −0.2962 0.1487∗∗ 0.2738∗ 0.1477 −0.0500 0.0897High School −0.0855 0.0667 −0.3026 0.1439∗∗ 0.1576 0.1493 −0.0852 0.0937> High School −0.0205 0.0800 −0.2811 0.1896 0.2585 0.1613 −0.0998 0.1352Single 0.0108 0.0427 −0.0486 0.0909 0.0969 0.0748 0.0417 0.0703Age 0.0265 0.0240 0.0908 0.0535∗ 0.0127 0.0380 0.0942∗∗ 0.0439Age Squared −0.0011∗∗ 0.0004 −0.0020 0.0009∗∗ −0.0010 0.0007 −0.0023∗∗ 0.0008Number of Children −0.0410∗∗ 0.0212 −0.0072 0.0478 −0.0330 0.0281 −0.1007∗∗ 0.0370County Unemployment 0.1993∗∗ 0.0351 0.1536 0.0794∗∗ 0.2042∗∗ 0.0512 0.2346∗∗ 0.0670County JOBS Participation −0.0127∗∗ 0.0038 −0.0160 0.0088∗ −0.0138∗∗ 0.0055 −0.0068 0.0070Constant −2.9395 0.4731 −3.0930 1.0720 −3.0034 0.7159 −4.2482 0.9063

Note. All regressions include county fixed effects.Robust standard errors are reported.∗p < .1. ∗∗p < .05.

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358 R. Jagannathan et al.

TABLE 8. Comparison of Marginal Effects of Family Cap Cash Benefits and Family Cap Dummyon Births

New Cases

All New Cases Whites Blacks Hispanics

Family Cap Dummy† −0.0035∗∗ 0.0029 −0.0077∗∗ −0.0022Family Cap (Marginal Benefits) Effect (per dollar) 0.0001∗∗ 0.0000 0.0001∗∗ 0.0001Money Effect as a % of Overall Family Cap Effect 2.4499 1.4038 1.9461 2.3046

Ongoing Cases

All Ongoing Cases Whites Blacks Hispanics

Family Cap Dummy† −0.0003 −0.0025 −0.0008 0.0012Family Cap (Marginal Benefits) Effect (per dollar) 0.0000 0.0000 0.0000 0.0000Money Effect as a % of Overall Family Cap Effect 0.2360 1.9726 2.1066 1.9475

†Estimates taken from Jagannathan and Camasso (2003); Jagannathan, Camasso, and Killingsworth (2004).∗∗p < .05.

2004; Jagannathan & Camasso, 2003). Table 8also compares marginal effects generated fromthe Cap dummy variable (Equation [1]) and ourcurrent approach of isolating the monetary com-ponent of Family Cap. The table shows thatthe monetary component comprises a very smallportion of the overall Family Cap effect on birthsand is statistically significant for only new cases,and among the new cases, only for the Blacksample. The monetary component accounts foronly about 2.5% of the overall new-case birtheffect and about 2% of the Black, new-case birtheffect found in previous studies of New Jersey’sFDP program.

DISCUSSION AND CONCLUSION

In this article, we have tried to determinehow much of the Family Cap effect can be at-tributed to the monetary penalties which womenface when they have an additional birth whilereceiving welfare. Our analyses differ from ear-lier examinations of New Jersey’s Family Cap,other experimental data analyses conducted inArkansas, Delaware, and Arizona, and virtuallyall nonexperimental studies in our use of theexpected cash benefit loss ($) to measure fertil-ity impacts. Our comparisons with the previousexaminations of New Jersey’s Cap, where thepolicy effect was measured by a simple treat-ment control-group dummy variable, allow us to

gauge how much of this effect is a function ofprice.

And although we find that assignment intoFamily Cap treatment and control groups is anexcellent instrument for marginal benefits (Ta-ble 5), we see that benefits account for a verysmall percentage of Family Cap effects reportedin earlier studies (Table 8). Only about 2.5% ofthe birth effect identified by Jagannathan andCamasso (2003; Jagannathan et al., 2004) fornew cases can be attributed to price. Further, wefind that this small price effect is confined toBlack women in the new-case subsample wherewe show that a dollar increase in welfare bene-fits increases birth probability by .0001. With theFamily Cap representing a benefit reduction of$55, however, this marginal effect translates toa decrease in the birth probability for new-caseBlack women of a little more than half a percent.

Given the evidence here that marginal bene-fits do not mediate the relationship between theFamily Cap assignment dummy and fertility be-havior, we are compelled to seek alternative ex-planations for why Family Caps appear to work.We believe that explanation lies not in the eco-nomic literature but in the broader social scienceliterature on social norms. Women in New Jer-sey, through media barrage, constant remindersfrom case managers, and immersion in an overallclimate of hostility to welfare, were stalked bythreats of adverse action and pressure to “do the

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Family Caps and Fertility Decisions of Poor Women 359

right thing.” These message effects have beenhypothesized to account for significant impactsof welfare reform on case load reduction and em-ployment (Blank, 2001; DeParle, 2004; O’Neill& Hill, 2001).

Of course, for a message to influence behav-ior, it must first resonate with the intended au-dience. There are clear indications from earlierNew Jersey studies that Family Caps have muchgreater impacts on “new cases,” who tend tohave higher stocks of personal capital invested inemployment and more social capital invested incommunity networks that are receptive to threatsof welfare sanctions and/or advice to engage in“responsible behavior.”

We draw two conclusions from our analyses.First, models matter: When an experiment or apolicy change gives different treatments to dif-ferent persons, the very popular “black box,”treatment-control approach implicit in Equation(1) may not tell the whole story. Indeed, ourresults here show that the birth declines havelittle connection to price, leaving us to hypoth-esize about the real importance of Family Cap’snoneconomic motivation.

Second, the data matter: Although we believeour results are noteworthy, we caution that theyare by no means the last word on the $64-dollarquestion, or how incremental welfare benefits af-fect fertility behavior. In particular, our data arerestricted to women on welfare. Thus, we areunable to determine the existence or magnitudeof any “entry effects” of the Family Cap. Thatis, by changing marginal benefits, the Cap mayhave either increased or reduced entry of womeninto welfare and may thus have had additionaleffects on births—yet our data do not allow usto address this question. Also, we do not studythe birth impact of the Cap when women leavewelfare. Thus, our impact estimates are not ATEbut are instead ITT effects that could be dif-ferent from ATE estimates if fertility behavioris systematically different in on- and off-welfarequarters. One remedy proposed by Bloom (2005,p. 82) to reconcile potential differences betweenATE and the typically more conservative ITT es-timates is to extrapolate ITT estimates to forman average effect of the treatment on the treated.We do not perform such extrapolation for tworeasons. We cannot assume that recipients in off-

quarters do not experience a treatment effect. Itis possible that there may be a larger impact onfertility behavior when a welfare safety net is nolonger available. Moreover, we cannot determinewhich control group members are the counter-parts of treatment group members in the off-welfare quarters (Bloom; Orr, 1999). Omissionof “entry” and “off-quarters” effects is certainlyone caveat concerning our results. In addition,external validity of our results may also be lim-ited, given that we use data from just one stateand that a different mix of political, economic,and demographic characteristics in other statesmay yield a different set of results.

The main limitation of our analyses, of course,is our inability to measure the message compo-nent of the Family Cap and estimate its effecton births directly. Data on the social disapprovalmessage designed to be delivered by the Cap arehard to come by via administrative data collec-tion, our primary data source for the analysesreported here. Future research needs to considerincorporation of survey data that ascertain atti-tudes and perceptions toward the Cap and theextent of assimilation of any social message em-bedded in the Cap. A related problem is evidentinsofar as the Family Cap may represent othercomponents that are nonmonetary besides themessage. Without explicit subject assignment tothese potentially multiple nonmonetary compo-nents, it may be impossible to “unbundle” sucheffects. Future research might also be focused ona factorial experimental design that would enablesuch uncoupling of the various Cap components.

We do believe, however, that we have ad-vanced the argument for examining the socialnorm influences of a Family Cap impact. Poorwomen appear to have modified their fertility de-cision in response to the social message that haspervaded today’s public welfare environment—a message that resonates with disapproval. Cer-tainly, this is not the last word on the “price ofvirtue,” but perhaps it may be a useful startingpoint for further discussion.

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