LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIESON DISADVANTAGED NEIGHBORHOODS
DAVID NEUMARK , BRIAN ASQUITH and BRITTANY BASS∗
We assess evidence on the longer-run effects of minimum wages, the Earned IncomeTax Credit, and welfare on key economic indicators of economic self-sufficiency indisadvantaged neighborhoods. The evidence suggests that the longer-run effects of theEarned Income Tax Credit are to increase employment and to reduce poverty and publicassistance. We also find some evidence consistent with higher welfare benefits havinglonger-run adverse effects, and stronger evidence that tighter welfare time limits reducepoverty and public assistance in the longer-run. The evidence on the longer-run effectsof the minimum wage on poverty and public assistance is not robust. (JEL J22, J23, J38)
I. INTRODUCTION
The long-running research and policy debatesabout anti-poverty policies have tended to focuson short-term effects, rather than asking howthese policies have affected income, and eco-nomic self-sufficiency more generally, in thelonger run. In this paper, we attempt to counterthis shortcoming. We study the effects of themain anti-poverty policies in the United States
∗We thank the Laura and John Arnold Foundation and theEmployment Policies Institute for support for this research.B.A. gratefully acknowledges funding from the Alfred P.Sloan Foundation (grant G-2017-9813) and the NationalBureau of Economic Research (NBER). Any opinions orconclusions expressed are the authors’ own and do not neces-sarily reflect those of the Laura and John Arnold Foundation,the Employment Policies Institute, the Sloan Foundation,or the NBER. The funders have had no control over thecontent or conclusions of this research. We received helpfulcomments from Matt Freedman, Hilary Hoynes, Joe Sabia,and from seminar/conference participants at Bar Ilan Univer-sity, DIW-Berlin, Hebrew University, IZA, the MelbourneInstitute, Nanyang Technical University, the National TaxAssociation Annual Conference, the National University ofSingapore, the Norwegian School of Economics, SingaporeManagement University, the Tinbergen Institute, Tulane,UC-Berkeley, UCI, Université Catholique de Louvain, andthe University of Sydney. We are grateful for helpful researchassistance from Luis Munguia Corella.Neumark: Distinguished Professor of Economics, Depart-
ment of Economics, University of California, Irvine,Irvine, CA 92697, NBER, IZA, Phone 949-824-8496,Fax 949-824-2182, E-mail [email protected]
Asquith: Economist, W.E. Upjohn Institute, Kala-mazoo, MI 49007, Phone 269-385-0459, [email protected]
Bass: Assistant Professor, Department of Economics, Cal-ifornia State University, Sacramento, Sacramento, CA,Phone 910-742-2242, E-mail [email protected]
that attempt to increase income from work, or thatsubstitute for income from work and hence mightstrongly affect work incentives—minimumwages, the Earned Income Tax Credit (EITC),and welfare. We estimate the longer-run rela-tionships between these policies and measures ofeconomic self-sufficiency—most importantly,poverty and receipt of public assistance. Theunderlying potential mechanism we have inmind for differing longer-run effects of thesepolicies is that policies that encourage morework over time will lead to greater accumulationof human capital, and hence higher wages andearnings.
Most research on minimum wages focuses onthe short-term employment effects of minimumwages—typically for teenagers (see the review inNeumark and Wascher 2007) and more recentlyfor other low-wage workers, such as restaurantworkers (e.g., Dube, Lester, and Reich 2010).This evidence tells us little or nothing aboutwhether minimum wages reduce poverty even inthe short term, although that question has begunto get more attention (e.g., Dube 2017; Sabia andBurkhauser 2010). Virtually, no work has studiedthe longer-run effects of minimum wages, with
ABBREVIATIONS
ACS: American Community SurveyAFDC: Aid to Families with Dependent ChildrenCCTC: Child and Dependent Care Tax CreditEITC: Earned Income Tax CreditNCDB: Neighborhood Change DatabaseSSI: Supplemental Security IncomeTANF: Temporary Assistance for Needy Families
409Contemporary Economic Policy (ISSN 1465-7287)Vol. 38, No. 3, July 2020, 409–434Online Early publication September 29, 2019
three exceptions: indirect evidence on training(or education), which could affect earnings in thelonger term (e.g., Acemoglu and Pischke 2003);research directly estimating the effects on adultearnings of exposure to a higher minimum wageas a teenager (Neumark and Nizalova 2007); andmore recent work by Clemens and Wither (2019)reporting that binding minimum wage increasesduring the Great Recession period lowered theincome growth of affected workers.
Research on the EITC has also focusedon short-run employment effects (e.g., Meyer2010), and some work studies short-run effectson poverty (e.g., Neumark and Wascher 2011).There are just a few, mostly recent, exceptionsto the short-run focus. Dahl et al. (2009) exam-ine longer-term effects of the EITC via workincentives, estimating the impacts of a majorfederal expansion of the EITC on individualwomen’s earnings up to 5 years later.1 Morerecently, Neumark and Shirley (2017) study theeffects of exposure to a more generous EITCover women’s 20s and 30s on subsequent wagesand earnings. And taking an intergenerationalperspective, Bastian and Michelmore (2018)estimate the effect of exposure in childhood onadult outcomes, finding positive employment andearnings effects; they suggest that these resultsare driven by labor supply (and hence earnings)impacts on parents.
The EITC is sometimes viewed as a moreeffective policy than the minimum wage toincrease income from work, in large part becauseit incentivizes work. This question can be revis-ited in the longer-run perspective we adopt inthis paper, recognizing the possibility that theEITC could also have limited effectiveness ineconomically disadvantaged areas if there are notemployment opportunities to be taken advantageof by those induced to look for work by a moregenerous EITC.
Finally, although the literature on welfareis extensive and has studied both employmenteffects (e.g., Grogger 2003) and distributionaleffects (e.g., Bitler et al. 2006), there is very lit-tle work on longer-run effects. Two exceptionsare Grogger (2009) and Hotz et al. (2006), whostudy whether welfare programs that encouragedemployment (and in the latter case, training)boosted longer-run earnings. Moreover, the ques-tion has been raised of whether welfare generates
1. Card and Hyslop (2005) study longer-term effects of asimilar program in Canada. There is also some research tyingthe EITC to longer-term outcomes via effects on children. Fora review of related work, see Neumark (2016).
longer-run dependency on government programs(e.g., Murray 1984).
To obtain evidence on the longer-run effectsof the anti-poverty policies we study, it would beideal to have very long-term longitudinal data onmany cohorts of individuals and families. How-ever, such data are not available in the UnitedStates (except, in principle, if one could link taxdata over many decades).2 We do, however, havelong-term longitudinal data on small geographicareas—Census tracts—which can be consis-tently observed over time in the U.S. Censusand in later years in the American CommunitySurvey (ACS). We study the longer-run effectsof anti-poverty policies on the disadvantaged byestimating the longer-run relationships betweenthese policies and socioeconomic outcomesin the most-disadvantaged tracts relative toother tracts.
Our working definition of “longer run” in thisstudy is 10 years.3 This is a significant differencefrom the contemporaneous effects emphasized inmost research on anti-poverty policies. Relation-ships over periods even longer than 10 years areof potential interest, but the timing of much ofthe variation in the policies we study precludesreliably estimating these relationships over twoor three decades. In addition to looking at longer-run relationships over many decades, our paper isdistinguished by simultaneously examining mul-tiple anti-poverty policies, which provides directcomparisons of their relationships with longer-run outcomes and helps ensure that we do notspuriously attribute the potential effects of onepolicy to the effects of others.
To briefly summarize the results, our strongestfindings are twofold. First, the evidence suggeststhat the longer-run effects of the EITC are toincrease employment and to reduce poverty andpublic assistance, as long as we rely on nationaland state variation in EITC policy. Second,tighter welfare time limits also appear to reducepoverty and public assistance in the longer run;while the relationship with public assistanceresult may be mechanically related to loss ofbenefits, the relationship with poverty is more
2. The one exception is the Panel Study of IncomeDynamics, which Neumark and Shirley (2017) use to estimatethe long-term effects of exposure to a more generous EITC.However, this yields quite small long-term longitudinal sam-ples, and has other limitations.
3. Some of the papers discussed above define differentwindows for longer-run effects, usually dictated by the data.The same is true for us, as the data we use provide decadalmeasurements.
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 411
likely behavioral. We also find some evidencethat higher minimum wages, in the longer run,may lead to declines in poverty and the shareof families on public assistance, whereas higherwelfare benefits appear to have adverse longer-run effects, although the evidence on welfarebenefits and especially on minimum wages is notalways robust to using only more recent data, norto some other changes we consider.4
We want to be clear, at the outset, that iden-tifying longer-run effects of policy—especiallyof multiple policies—is a challenge. We mayrarely, if ever, have the kinds of compellingidentification strategies sometimes available tostudy the short-term effects of a single policy.In contrast, the most feasible and convincingapproach is likely what we have carried out in thispaper—combining differencing strategies witha detailed look at potential threats to identifi-cation, and at the sensitivity of the conclusionsto sensible alterations in the sample, the spec-ification, etc. Nonetheless, even being cautiousabout a causal interpretation of our findings, webelieve that the longer-term relationships we doc-ument provide interesting suggestive evidenceabout the likely longer-run effects of alternativeanti-poverty policies.
II. RESEARCH STRATEGY
Our econometric strategy is to use long-termpanel data to obtain evidence on the longer-runrelationships between anti-poverty policies andeconomic outcomes in Census tracts that are ini-tially disadvantaged, relative to other tracts. Toexplain the approach, denote tracts by c, states bys, counties by j, and years by t. Denote by Ycstour economic outcomes; we focus on the povertyrate and the share of households on public assis-tance, but study other outcomes as well.5 Denoteby Pcst a vector of policies that can vary by stateand year (and very modestly by county). And
4. Note that the evidence on welfare benefits does notimply that more generous welfare benefits do not help recip-ients, but rather that more generous benefits may reduce theextent to which these recipients become economically self-sufficient.
5. Aside from policy concerns, our focus on poverty andpublic assistance is motivated by data limitations. As dis-cussed below, the data we use provide tract-level aggregates.Although we also estimate effects on average earnings andemployment rate measures, we cannot, for example, estimateeffects on earnings and employment of separate groups (suchas single mothers) to better understand the estimated effectson family-level outcomes such as poverty. In future workusing microdata we may do more to unpack the effects onthese outcomes for subgroups.
denote by DISbc a measure of initial disadvantage
defined at the tract level; DISbc is a dummy vari-
able indicating that a tract was in the top quartileof a measure of socioeconomic disadvantage (i.e.,the most-disadvantaged quartile) in the baselineperiod (b). For most of our analysis, we focus ondisadvantage defined by the share of the popula-tion in poverty, although we also explore differentmeasures of disadvantage (based on education,race, and single motherhood).
As control variables, we also include Censustract fixed effects (CTc), to account for time-invariant heterogeneity across Census tracts. Wealso include a full set of interactions betweencounty dummy variables (COj) and year fixedeffects (YRt). These interactions control veryflexibly for local shocks to economic out-comes that could potentially be correlated withthe policy variables. We cannot, of course,include tract-by-year interactions becausethese would capture all of the variation in thedependent variables.
We also always include a control for thepotential effects on tracts of long-term changesin the structure of jobs in the aggregate econ-omy.6 We use the approach, originating withBartik (1991), of applying national time-serieschanges in aggregated sectoral employment tothe tract or other subareas, based on the tract’sor subarea’s sectoral composition in the baselineperiod. While it is most natural to think of this interms of industry, in the Neighborhood ChangeDatabase (NCDB) we use, we can only do this foroccupation.7 To define this control variable, letsubscript k index occupations. Denote by SEcskltotal employment in tract c, state s, occupation k,and baseline period l (which for each year t is the10-year lag), denote by AEkt aggregate (national)employment in each period t in occupation k, anddenote by AEkl aggregate employment in occu-pation k in the baseline period l. Then tract (orsubarea) employment based solely on aggregatedevelopments is predicted in each period after l
6. For example, it is widely agreed that declines in manu-facturing hit narrow areas where manufacturing was concen-trated (think the South Side of Chicago, or Flint, Michigan),as highlighted in the seminal work of Wilson (1990) or Autor,Dorn, and Hanson (2013).
7. The NCDB does not provide tract-level information onthe number of persons working in a specific industry. Instead,it includes employment in nine categories of occupations (forpersons 16+): professional and technical occupations; exec-utives, managers, and administrators; sales; administrativesupport and clerical; precision production, craft, and repair;operators, assemblers, transportation, and materials; nonfarmlaborers; service; and farm workers or forestry and fishing.
412 CONTEMPORARY ECONOMIC POLICY
by applying the national changes to the baselinecomposition, as in
(1) PSEcst =∑
k
SEcskl ×(
AEkt − AEkl
AEkl
). 8
For our baseline analyses, we extract from theNCDB measures of Y for 1980, 1990, 2000, and2010, and measures of DISb for 1970.9 We spec-ify our model to estimate the longer-run impactsof the anti-poverty policies in P on initially dis-advantaged tracts relative to other tracts. This isa “substitute” for directly estimating effects oninitially disadvantaged individuals and families,which the data precludes; the assumption under-lying the strategy, of course, is that initially disad-vantaged tracts have much higher concentrationsof initially disadvantaged individuals and fami-lies. The model we estimate is
Ycst = α + {DISbc · Pcst} · β(2)
+ {DISbc · Pcs,t−10} · βL
+ CTc · δ′ + {COj · YRt} · ω
+ θ · ln(PSEcst) + εcst.
In Equation (2), the parameters β and βL
capture the contemporaneous and 10-year lagrelationship between the outcomes we study andthe policies in P. The main effects of policy varia-tion on non-disadvantaged tracts (with DISb = 0)are subsumed in the county-by-year fixed effects,because policy generally varies at the state level(and very slightly at the county level, which wehave coded to the tract level, and which is why P
8. This control is entered in logs because the level can dif-fer so much across tracts. Although not reported in the tablesthat follow, the estimated coefficients of this control variableon earnings, employment, and poverty are of the expected sign(increasing employment and earnings, and reducing poverty)and statistically significant. The estimated coefficient on pub-lic assistance receipt is positive, rather than negative—not inthe most obvious expected direction, although to be fair weare not aware of studies that use a Bartik control except tolook at employment-related outcomes. One possible reasonfor the public assistance result is that the Bartik control doesnot necessarily imply that higher-wage jobs grew, and theremay have been changes in public assistance that made it morelikely to get public assistance while working at low-wage jobs(most notably, welfare reform). This is consistent with whatwe find in separate models by sex, where the positive effect ofthe Bartik variable on employment is nearly twice as large forwomen as for men. We also verified that the results are veryrobust to excluding this control.
9. DISb can be measured for later years, but we workwith 1970 as our baseline in almost all of our analyses. Asexplained in the data section below, the 2010 measures areactually 2006–2010 measures based on the ACS.
has a c subscript).10,11 The estimates of β and βL
capture the relative change in Y in disadvantagedtracts, versus more-advantaged tracts, that areassociated with the policy variation P.
Considered this way, β and βL are akin totriple-difference parameters. A basic triple-difference specification (ignoring the minorcounty variation in welfare benefits) wouldinclude main effects of the policy variables (notinteracted with the indicator for disadvantagedtracts), year fixed effects, state fixed effects, theindicator for disadvantaged tracts, and interac-tions between this indicator and the year and statefixed effects. Many of these are subsumed in thericher control variables in Equation (2). Specif-ically, including the county-by-year fixed effectssubsumes main policy effects, and the tract fixedeffects subsume the indicator for disadvantagedtracts as well as the interactions between thisindicator and state fixed effects. The modelwould still include the year-by-disadvantagedtract interactions, which would imply that theeffects of policy would be identified only fromstate-level variation; for example, differentialeffects of federal EITC variation in disadvan-taged relative to advantaged areas, common to allstates, would be absorbed in these interactions.It turns out, however—as we show later—thatthe estimated relationships with the EITC areextremely imprecise when we include the year-by-disadvantaged tract interactions, owing torelatively little state variation. Hence, our mainestimates do not include these interactions, andrely on federal as well as state EITC variation.12
However, the inclusion of the county-by-year
10. Welfare benefits have a limited degree of within-state,cross-county variation in a handful of states (as discussedbelow).
11. The inclusion of the county-by-year interactions andthe focus on estimating the effects on most-disadvantagedtracts is related to recent work on the identification of min-imum wage effects (Allegretto, Dube, and Reich 2011; Dubeet al. 2010; Neumark, Salas, and Wascher 2014). This workhighlights the question of whether region-specific economicshocks are correlated with minimum wage changes. How-ever, when the county-by-year interactions are included,identification of β and βL comes solely from within-countyand year variation, and the bias from potential correla-tions between state-level or county-level economic con-ditions and the (possibly endogenous) variation in mini-mum wages or other policies at the state or county levelis eliminated.
12. The key papers in the EITC literature—establishingpositive employment effects for low-skilled mothers—alsouse federal variation (Eissa and Liebman 1996; Meyer andRosenbaum 2001). The same is true of the longer-term anal-yses discussed in the Introduction.
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 413
interactions controls for geographic heterogene-ity in shocks at a very granular level.
Aside from the controls we have discussed,the main model we use is parsimonious. It maybe most appropriate not to control for othercharacteristics of the population that may havechanged over time (such as educational levels),because skill levels may be endogenous (e.g.,Agell and Lommerud 1997). On the other hand,there may be differential migration responses topolicy in more- versus less-disadvantaged areas,and insofar as our strategy is to obtain evidenceon effects on individuals and families from varia-tion in outcomes across geographic areas, it mightbe important to control for these compositionalchanges. We present estimates of models thatallow for compositional shifts, and find that theresults are robust.
Naturally, to assess the robustness of ourresults and to gauge potential sources of bias, wealso estimate other variants of our specification.We discuss these modifications of our analysis inthe empirical section of the paper.
III. DATA
A. Neighborhood Change Database
Our data on economic outcomes and othermeasures by tract come from the NCDB,13
which provides tract-level aggregates on the keyoutcomes we study—earnings, employment,poverty, and public assistance.14 Importantly,the NCDB provides consistent tract definitionsover time. In particular, it includes historicaltract populations, demographic characteris-tics, and socioeconomic characteristics in 2010Census tract geography, providing consistentlongitudinal measures of these variables.15
13. For a description of the data, see http://www.geolytics.com/USCensus,Neighborhood-Change-Database-1970-2000,Products.asp (viewed February 13, 2017).
14. From 1970 to 2000, the measure of public assis-tance in the NCDB (which comes from the decennialCensus) includes Supplemental Security Income (SSI),AFDC/TANF, and General Assistance (sometimes calledGeneral Relief)—which usually refers to programs that pro-vide income support to adults without dependents. For theperiod ending in 2010, the NCDB data come from the ACS(as explained more below); the ACS definition of public assis-tance includes TANF and General Relief.
15. The NCDB counts are reallocations of the Cen-sus’ reported counts, using a combined area and populationapproach. Areal weights are determined from publicly avail-able maps for all recent Census geography so that it is possibleto calculate the area overlay between tracts in different Cen-sus years. To account for the uneven distribution of population
The NCDB includes data from the 1970, 1980,1990, and 2000 Census, and from the five-yearrollups of the 2006–2010 ACS (which we some-times refer to as “2010”).16 The NCDB excludessome variables otherwise publicly available fromthe Census (in the “Summary Files”), such ascrosstabs on education by employment status byage group. However, these crosstabs were notpublished by the Census for 1970, and the ageranges that are reported change in each Censuswave, making reconciling them longitudinallydifficult. Thus, the NCDB remains the best publicdata set for this analysis.17
Because we estimate models covering manydecades, based on characteristics of tract resi-dents in a much earlier period (using 1970 as ourbaseline period to define DISb, for our baselineanalysis), we are restricted in the set of tracts wecan use. The 1970 NCDB data set is comprisedexclusively of counties surrounding populationcenters, because Census tracts were still in theprocess of growing out of their original usagefor measuring health and sanitary conditions atthe neighborhood level in urban areas (Krieger2006).18 The practical implication is that whenwe use 1970 as our base year for measuringdisadvantage, we drop mostly rural and suburban
within a tract, the NCDB exploits sub-tract geographic units,called Census blocks, which first exist nationwide in the 1990Census. Census blocks are not standardized by population,but their decennial population counts are known and Cen-sus block boundaries never cross tract boundaries within thesame Census year. These Census blocks form the basis formore precisely mapping populations across Census years andthen aggregating the results to the tract level. More detailson how the population reapportionment occurs at finer geo-graphic levels and is reconciled across Census waves can befound in Tatian, Hayes, and Zhang (2003).
16. Specifically, the 1970 data come from the FourthCount Summary Tape for Population and Housing; the 1980and 1990 data come from the Summary Tape Files 3A of theirrespective years; the 2000 data come from the Summary File3A and Summary File 1; and the 2010 data come from theSummary File 1.
17. One key advantage of using the NCDB is that thedata are publicly available, and the analysis therefore can bereplicated and explored further by other researchers. The min-imum wage literature, in particular, is replete with exchanges,comments, and replications of the work of others, and in ourview these exchanges and sharing of data have been a criticalpart of the research endeavor and central to the high level oftransparency to which researchers on all sides of the minimumwage debate have contributed.
18. The Census first fully tracted the nation in 2000(Krieger 2006). In 1990, the Census had tracts in all 50 statesplus Puerto Rico and U.S. outlying territories, but had onlyfully tracted six states: California, Connecticut, Delaware,Hawaii, New Jersey, and Rhode Island. Prior to that, Censustracts were only drawn for large cities (U.S. Department ofCommerce, Bureau of the Census 1994).
tracts. Appendix Table A1 shows that the NCDBsample is still reasonably representative of 1970national averages. The shares black, in poverty,employed, and receiving public assistance arevirtually indistinguishable between the NCDBand the decennial Census data. The share offamilies headed by a single mother is about twiceas high in the NCDB sample, and earnings areabout 20% higher, both of which are attributableto economic and cultural differences betweenurban and rural areas. Thus, although the datafrom 1970 Census tracts are representative ofmany features of the U.S. population, thesedifferences suggest that the results may not fullygeneralize to rural areas (and there could beother reasons policies have different impactsin rural areas). We also present a sensitivityanalysis where we start with 1980 as the base-line year, thus incorporating more tracts intoour analysis.
The longer-run perspective of our researchmakes it useful to have data covering manydecades, and our specifications include 10-yearlags, so that the first sample year we can usewith the NCDB is 1980. Although some of therelevant policy variation goes back to before1940 (the minimum wage was created by the FairLabor Standards Act in 1938), Census tracts canonly be identified in a small subset of areas for1940 and 1950.19 Thus, only beginning in 1960can one use any Census data at the tract level toobtain a comprehensive look at the United Statesas a whole, but to date, the 1960 Census is notincluded in the NCDB.
With regard to the policies we study, theinability to use the earlier years is not much of adisadvantage. Most of the variation in the federalminimum wage, and all of the variation in stateminimum wages, occurred much later—mostfederal variation after 1960, and state variationbeginning in the late 1980s, and coverage ofworkers by the federal minimum wage was notvery broad until the beginning of the 1960s.20
The other policies we study arise and begin tovary later—welfare in the 1960s and again withwelfare reform in the 1990s, and the EITC at thefederal level in the 1970s and at the state levelin the 1980s. Thus, the constraint of starting our
19. Census tract coverage and publicly available infor-mation prior to 1960 is limited. Only 45 cities were consis-tently given Census tracts before 1960 (Bogue 2000a, 2000b,2000c).
20. See http://www.dol.gov/whd/minwage/coverage.htm(viewed February 13, 2015) and http://www.dol.gov/whd/minwage/chart.htm (viewed February 13, 2015).
analysis in 1980 (with DISb measured in 1970)is not too limiting.
B. Anti-Poverty Policies
We study the potential effects of minimumwages, the EITC, and welfare. We view thesethree policies as the intersection of the policiesmost central to anti-poverty efforts, and the poli-cies most likely to affect income and work.21
Information on state minimum wages from1983 to 2014 was taken from the data used inNeumark et al. (2014). We extended the data backto 1960 relying on Quester (1981) and Sutch(2010),22 also cross-referencing dates and levelsagainst state and federal sources.23 We code theminimum wage as the higher of the state orfederal minimum wage, as is standard, because
21. Four substantial programs we do not consider arethe Supplemental Nutrition Assistance Program (SNAP, pre-viously Food Stamps), the Child and Dependent Care TaxCredit (CCTC), child support, and Medicaid. In general, weview these programs as less directly related to work incentives(and even less so to affecting income from work), and somehave less variation. For SNAP/Food Stamp benefit levels, onlyAlaska and Hawaii differ from federal guidelines. Prior to July1, 1974, there was some spatial variation through rollouts ofwhen Food Stamps became active, although most urbanized,predominantly low-income, and high black share counties hadthe program by 1970 (Almond, Hoynes, and Schanzenbach2011), which severely limits variation in SNAP/Food Stampbenefits (in this case based on rollout). Since welfare reform inthe 1990s, SNAP/Food Stamps has had work, search, or train-ing requirements, and hence potentially affects work incen-tives through those mechanisms, although limited researchsuggests it does not, but is instead largely a supplement towages (for those able to work); see Rosenbaum (2013) andMoffitt (2015). The CCTC is a non-refundable credit, unlikethe EITC, and hence is thought to provide weak benefits tolow-income families for whom the question of economic self-sufficiency is most salient. Child support is the financial sup-port paid by parents to support a child or children of whomthey do not have full custody. The Child Support Enforce-ment Amendments of 1984 required states to adopt numer-ical child-support guidelines. States can set their own childsupport guidelines, and decide what type of formula to usein determining income to establish the amount of the childsupport owed. While child support could affect labor supplydecisions, this is likely a secondary impact. Moreover, childsupport is not targeted on the disadvantaged. Medicaid hasprovided health coverage for low-income populations since1965. It is a federal mandate, with program parameters chosenby the states. Medicaid may influence labor force participa-tion, since eligibility is graduated by income, but there is notstrong evidence that Medicaid disincentivizes work (Baickeret al. 2014; Meyer and Rosenbaum 2001; Strumpf 2011).
22. The main information in the latter is in the appendixof the working paper, at http://www.nber.org/data-appendix/w16355/Appendix%20A%20State%20Laws.pdf (viewedFebruary 15, 2017).
23. If there was a conflict between sources, we chose theinformation in Quester (1981), to maintain consistency whenconstructing the panel.
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 415
FIGURE 1State-Level Minimum Wage
Variation (Nominal)
0
5
10
15
20
25
30
35
40
0.00
1.00
2.00
3.00
4.00
5.00
6.00
7.00
8.00
9.00
1970 1980 1990 2000 2006-2010
No. sta
te M
Ws >
federa
l
No
min
al m
inim
um
wage
Minimum Maximum Average No. > federal
Note: The minimum, average, and maximum minimumwage (measured on the left-hand axis) are shown for thedecennial Census years and the average over the 5 yearscorresponding to the ACS data. The minimum valuesmeasure the federal minimum wage. The gray boxes indicatethe number of states with a minimum wage above the federallevel (measured on the right-hand axis). Data on state-levelminimum wage variation come from Neumark et al. (2014),Quester (1981), and Sutch (2010).
lower state minimum wages, if they exist, applyto a tiny fraction of workers. In the analysis, welag the minimum wage 1 year for all outcomesexcept employment, because in the Census datathese outcomes are measured in the previousyear; we do the same for the other policies, forthe same reason. Finally, we use the log of theminimum wage.24
Figure 1 shows the minimum, average, andmaximum minimum wage (measured on the left-hand axis); the minimum values measure thefederal minimum wage. The gray boxes indicatethe number of states with a minimum wage abovethe federal level (measured on the right-handaxis). As the figure indicates, this latter numberis trivial early in the sample, but the number ofstates with higher minimum wages rises sharplyin the 2000s, to over 30.
Information on the EITC comes from adatabase of historical parameters maintained by
24. We use real ($2014) minimum wages (and do thesame for earnings), although in the regression model, withthe log transformation and year effects, the deflator is irrele-vant. Historically, there has been some debate in the researchliterature over whether to define the minimum wage relativeto an average wage measure. In recent work, this approachhas fallen out of favor, and the log of the minimum wage isused instead. The data on minimum wages can be accessed athttp://www.socsci.uci.edu/~dneumark/datasets.html (viewedFebruary 15, 2017).
Note: The minimum, average, and maximum EITCphase-in rate (measured on the left-hand axis) are shownfor the decennial Census years and the average over the5 years corresponding to the ACS data. The minimum valuemeasures the federal EITC. There was no EITC in 1970, andno state variation until after 1990. Information on the EITCcomes from a database of historical parameters maintainedby the Tax Policy Center.
the Tax Policy Center.25 We use the percentagesupplement in the federal EITC for a family withtwo children on the phase-in range (F2%), whichcan be amplified by the state EITC, usuallyspecified as a percentage supplement to the fed-eral EITC (S%). Thus, our combined variable isF2%·(1+ S%), where F2% and S% are measuredon a scale from zero to one.26
Figure 2 shows the EITC variation, displayedin a similar way as Figure 1. There was no EITCin 1970, and no state variation until after 1990.By the end of the sample period 23 states hadan EITC supplement, and the maximum supple-ments increase the phase-in rate by over 15 per-centage points.
We include two measures of welfare generos-ity or stringency. From 1962 to 1996, the U.S.joint federal and state social assistance programwas known as Aid to Families with DependentChildren (AFDC). The program was reformedby Congress in 1996 and rebranded as Tempo-rary Assistance for Needy Families (TANF). Ourfirst measure is the maximum payment for a fam-ily of three, usually held to be one adult and
25. See http://www.taxpolicycenter.org/sites/default/files/legacy/taxfacts/content/PDF/historical_eitc_parameters.pdf(viewed October 11, 2016).
26. State credits are fully refundable (as is the federalcredit), except for Delaware, Maine, Rhode Island, and Vir-ginia. This would suggest that our estimates could slightlyunderstate the effects of refundable credits.
two dependent children.27 Second, for the post-welfare reform period, we include a dummy vari-able for whether tight time limits were imposed.There were no time limits until welfare reformin 1996, after which 10 states adopted limits ofless than 60 months (in 2000, ranging from 21to 48 months, but generally about 2 years), andmost of the remaining states adopted time limitsof 60 months. We use a time limit dummy vari-able that is equal to zero for all states before wel-fare reform, and, after welfare reform, switches toone for states that imposed tight time limits (lessthan 60 months), to capture states that more sub-stantially tightened eligibility for welfare.28,29
All information on TANF comes from theUrban Institute’s Welfare Rules Database.30 ForAFDC, various sources were utilized.31 Somestates had benefit amounts that varied by subarea.Only for Illinois, Louisiana, Vermont, and Vir-ginia were the regional benefit levels and geogra-phies reported with enough consistency to recon-struct their longitudinal series, and even then, wehad to fill in missing years.32 For the remain-ing states with region-specific benefit amounts, in
27. We are typically able to measure benefits this way, butin some cases, we can only determine the level of benefits fora family of two. We always use the former when possible.
28. We also explored distinguishing between states thatimposed tighter time limits and those that imposed limitsof 60 months (versus none), although the results were notaffected.
29. To be sure, there are many possible measures of wel-fare reform one could use (Fang and Keane 2004). However,including many measures would be problematic because ofmulticollinearity, perhaps especially in our framework. Timelimits seem like a good choice to capture the effects of welfarereform. A small but consistent literature has shown that wel-fare time limits were a significant element of welfare reformdistinguishing TANF from AFDC (Moffit 2007), and thatthey were responsible for decreasing welfare caseloads (e.g.,Grogger 2009).
30. See http://wrd.urban.org/wrd/Query/query.cfm (vie-wed February 16, 2017).
31. U.S. Department of Health and Human Services(1973) publications (Characteristics of State Plans [vari-ous years]) provided program parameters for 1973–1976,1978–1985, and 1988–1990. For 1994 and 1996, programparameters came from U.S. House of Representatives pub-lications (Green Book [various years]). For 1969 and 1970,publicly available information was incomplete. The U.S.Department of Health, Education, and Welfare (n.d.) publica-tions on selected state maximum welfare payments were usedwhere available. For program parameters for years with miss-ing data, the annualized growth rate between the two observedyears that bracketed the missing year or years was calculated,and the benefit amount for the missing year or years wasassumed to equal the previous year’s amount times one plusthe annualized growth rate.
32. For these states, in years where the publications indi-cated that there was regional variation in benefit amounts butdid not report them, we used the following method to esti-mate the missing amounts. First, if for a year t with missing
FIGURE 3Welfare Benefits (Nominal) for Family of Three
0
100
200
300
400
500
600
700
800
900
1000
1970 1980 1990 2000 2006-2010
2hti
w3
fo
ylimaf
,stife
ne
bylt
no
M
child
ren
Minimum Maximum Average
Note: The minimum, maximum, and average monthlynominal welfare benefits for a family of three are displayedfor the decennial Census years and the average over the5 years corresponding to the ACS data. All informationon TANF comes from the Urban Institute’s Welfare RulesDatabase. For AFDC, various sources were utilized.
most cases the publications reported the highestpayment amount across regions, and this is whatwe used. However, in a few cases the publicationsdid not consistently state which region or amountthey were reporting, so we could be overstating orunderstating the benefit amount in certain years.
Figures 3 and 4 display information on the twowelfare measures we use. Figure 3 graphs nom-inal benefit levels. There is substantial variationacross states. Figure 4 displays information ontime limits.
C. Measuring Disadvantage
For our main analyses, we measure disad-vantage as the share of the population living inpoverty in the baseline year. However, we alsoshow key results for three alternative measures ofdisadvantage: the share of the population with ahigh school degree or less; the share of the pop-ulation that is black; and the share of familiesheaded by single mothers.33 The results are gen-erally robust.
data, years t-1 and t + 1 were observed and were the same,then year t was assumed to be the same as those years. If onlyone region’s amount was reported, we assumed the yearlygrowth rate was the same across regions, and extrapolatedto the missing year/region on that basis. For years whereno region-specific amounts were reported or specified, weused documents from the next year forward and used impliedgrowth rates between known years to interpolate the missingamounts.
33. This is the share of families and subfamilies. Whiletracts with large Hispanic populations are also of interest andlikely, on average, to be disadvantaged, Hispanic ethnicity hasnot been measured consistently over the long time span westudy.
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 417
FIGURE 4Welfare Time Limits
0
5
10
15
20
25
30
35
40
1970 1980 1990 2000 2006-2010
Num
ber
of sta
tes
60-month time limit Shorter time limit
Note: The number of states with a 60-month welfare timelimit and the number of states with less than a 60-monthwelfare time limit (shorter time limit) are displayed for thedecennial Census years and the average over the 5 yearscorresponding to the ACS data. There were no time limitsuntil welfare reform in 1996. All information on TANFcomes from the Urban Institute’s Welfare Rules Database.
Figure 5 provides information on the geo-graphic distribution of tracted areas as of 1970,and of our disadvantage measure. The figureshows areas tracted in 1970, with differentialshading for tracts in the four quartiles of the sharedisadvantaged—based on the share in poverty.The darkest shading is for the highest quartile ofthis share—that is, the most disadvantaged tracts.As the figure shows, a small geographic area wastracted; however, the tracted areas include mostof the U.S. population.34
IV. RESULTS
A. Descriptive Statistics
Table 1 reports descriptive statistics. Recallthat these are means across tracts, not individu-als or households. The top panel reports means(and standard deviations) for the outcomes westudy. The earnings variable is average earn-ings per household, which we construct in theNCDB from data on earnings per household with
34. The sum of the tracted population in 1970 was148,456,474 (found from the NCDB) against a total U.S. 1970population of 203,302,031 (U.S. Department of Commerce,Bureau of the Census 2002), or 73% of the U.S. population.Using the same sources, the figures are 80% and 99.99% ofthe population for 1980 and 1990, respectively.
workers, and the computed share of householdswith earnings. The employment rate is simply theemployment-to-population ratio at the tract level.The poverty rate measure is on a per person ratherthan per household or per family basis. Both trackU.S. statistics closely, despite being tract-levelobservations.35
The share on public assistance is lower thanthe poverty rate (although it is a per householdmeasure, and the poverty rate is lower at the fam-ily or household than at the individual level).It drops sharply in the final years of the sam-ple (the 2006–2010 period covered by the ACS)because SSI is excluded in the ACS data. Thischange should not influence our results materi-ally, because the definitional change should becaptured in the year effects (including interac-tions) that are included in the model;36 moreover,we find that results are very similar for povertyand for public assistance—and the change in thedata affects only the latter.
The second panel reports descriptive statisticsfor our four outcome measures for the disad-vantaged tracts. As we would expect, earningsand employment are lower, and poverty and theshare on public assistance are higher. The bottompanel reports the disadvantage measure for 1970.We report the mean as well as the 75th per-centile of this measure; the latter is the cutoff fordefining DISb.
B. Baseline Regression Results
We report baseline results for earnings,employment, poverty, and public assistancein Table 2.37 The table reports estimates ofEquation (2), reporting the estimates of the
35. See, for example, https://data.bls.gov/timeseries/LNS12300000 (viewed February 16, 2017) and http://www.census.gov/data/tables/time-series/demo/income-poverty/historical-poverty-people.html (viewed February 16, 2017).
36. The table does not show a decline from 1990to 2000. While AFDC/TANF rolls declined over thisperiod, participation in SSI grew by an amount thatoffsets a large share of this decline (see, e.g., FigureIND 4, https://aspe.hhs.gov/report/welfare-indicators-and-risk-factors-fourteenth-report-congress, viewed November29, 2017).
37. There are small numbers of tracts or years with miss-ing data on some outcomes; for example, a tract may havemissing employment information in 1980, but complete earn-ings, poverty, and public assistance information in that year.Rather than restrict to a balanced panel, we use all the datawe can. If we used a balanced panel across outcomes, wewould have 204,740 tract-by-year observations (for 51,185tracts) for each outcome, about 2,000 fewer than in each ofthe columns in Table 2. Results are very robust to using thebalanced panel (results available upon request).
FIGURE 51970 Disadvantage by Tract, Based on Share in Poverty, for Areas Tracted in 1970
Note: Figure shows the geographic distribution of tracted areas as of 1970 for the share in poverty with differential shadingfor tracts in the four quartiles of the share in poverty, based on the NCDB data. The darkest shading is for the highest quartileof this share—that is, the most disadvantaged tracts. Information on tracted areas in 1970 for the share in poverty comes fromthe NCDB.
coefficients β, the contemporaneous relationship,and βL, the longer-run relationship, on the vari-ables DISb
c ·Pcst and DISbc ·Pcs,t− 10, respectively.
The estimates of the longer-run relationshipsanswer the question, “Conditional on the currentpolicy, how different are contemporaneous out-comes when the current policy has been in placelonger?” That is, what is the potential longer-runeffect of the policy?
The estimates for average household earn-ings are in column (1). There is a positive butstatistically insignificant contemporaneous rela-tionship between minimum wages and earnings,but the 10-year lag relationship is negative andstatistically significant (and of offsetting magni-tude). Because earnings and the minimum wageare measured in logs (as are the EITC and welfarebenefit variables), the estimated coefficients can
be interpreted as the elasticities with respect tothe minimum wage in the most-disadvantaged(high-poverty) tracts, relative to other tracts.This way of specifying the model allowscomparisons with minimum wage-earningselasticities reported in other studies—althoughtypically these other estimates are for low-skilledindividuals and focus only on short-term, con-temporaneous effects. Contemporaneous wageelasticities in the 0.1–0.2 range are not uncom-mon (e.g., Allegretto et al. 2011).38 The 0.12estimate in column (1) is within this range.
There is statistically significant evidence of apositive short-run relationship of the EITC withearnings, but no evidence of a longer-run effect.
38. There are exceptions. In a recent study of the Seattleminimum wage, Jardim et al. (2017) find negative effects onearnings.
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 419
TABLE 1Descriptive Statistics on Outcomes and Tract Characteristics
Share of households on public assistance 14.8 14.7 14.5 4.49(11.8) (12.2) (11.1) (5.22)
[12,968] [12,974] [12,971] [12,846]Panel III: Measures of disadvantage, 1970
Mean (SD) 75th percentileInitial share in poverty 10.9 13.7
(9.72)[51,923]
Notes: Table reports means for tract-level measures. Standard deviations are shown in parentheses. Sample sizes are shown inbrackets. The statistics in Panel I are for the samples used for the respective outcome’s regression. The public assistance definitionexcludes SSI for 2006–2010.
As discussed below, there is also evidence of apositive longer-run relationship of the EITC withemployment. The absence of an earnings impactmay reflect the fact that the EITC increases laborsupply, which can depress market wages (Leigh2010). Finally, there is no evidence of statisticallysignificant longer-run (or contemporaneous) rela-tionships of either welfare benefit levels or timelimits with average household earnings.
Results for the employment rate are reportedin column (2). There is evidence of a positiverelationship with minimum wages in the shortrun, with an implied elasticity of 0.23. This resultcontrasts with a good deal of evidence in the
broader literature on the employment effects ofminimum wages. But the estimates here are fordifferent groups—residents of tracts that weredisadvantaged many decades back—as opposedto the low-skilled and usually very young work-ers considered in most of the minimum wageliterature. The longer-run estimated employmentrelationship is negative but not significant (withan elasticity of −0.11).
We find a positive longer-run relationshipof the EITC with employment, with an impliedelasticity of 0.026. We find no statistical evidenceof a contemporaneous relationship. The pointestimate of the contemporaneous impact is
420 CONTEMPORARY ECONOMIC POLICY
TABLE 2Effects of Anti-Poverty Policies on Average Earnings per Household, Employment Rate, Share in
Poverty, and Share on Public Assistance in Areas with High Share Poverty at Baseline (1970),1980–2010
Notes: The specification corresponds to Equation (2) in the text; only the coefficients of DISbc ·Pcst and DISb
c ·Pcs,t− 10 arereported. The longer-run effects are highlighted in boldface. Earnings are defined as average earned income per household (in$2014). All outcomes, and the minimum wage, EITC, and welfare benefits variables, are in logs. (The EITC phase-in rate is scaledfrom zero to 100, with one replacing zero, prior to taking logs.) Thus, the estimates of the minimum wage, EITC, and welfarebenefits coefficients can be interpreted as elasticities for the disadvantaged tracts (i.e., those in the top quartile of disadvantage),relative to other tracts. The welfare time limits variable is a dummy variable, so its estimated effect approximates the percentagechange in the outcome in disadvantaged tracts when welfare time limits are shorter. ***, **, or * indicates statistically significantlydifferent from zero at the 1, 5, or 10% level. Standard errors are clustered by state.
negative, which differs from the EITC literaturefocused on low-skilled, often single mothers.Again, this difference may reflect the fact thatresults for disadvantaged places can differfrom what has been found using individual- orhousehold-level data on the most affected groups.
For the welfare variables, we find no statisti-cally significant evidence of longer-run relation-ships with employment. This contrasts with theview that more generous welfare (higher bene-fits, or no or longer time limits) creates workdisincentives. There is evidence of a significantnegative short-run relationship with tighter timelimits, again contrary to the intended effect.
For two reasons, our most important resultsare for poverty and the share on public assistance.First, these are the direct “targets” of anti-povertypolicies. And second, evidence on the longer-run effects of anti-poverty policies on povertyand receipt of public assistance tells us moreabout the effects of these policies on economicself-sufficiency. It is important to keep in mindthat because both poverty and receipt of publicassistance depend on the value of family income
relative to thresholds, and because effects onfamily income depend on who is affected by thepolicies we consider, we should not necessarilyexpect a tight correspondence between effectson these outcomes and the prior earnings andemployment results.
Nonetheless, we should expect similar resultsfor poverty and public assistance, so we discussthese results together. The evidence on mini-mum wages in column (3) suggests that higherminimum wages reduce poverty in the longerrun, with an elasticity of −0.10, although theestimate is not statistically significant. There isalso evidence of a longer-run reduction in theshare of households on public assistance, coupledwith evidence of a contemporaneous relation-ship in the same direction. Most past researchon the short-run effects of the minimum wageon poverty has not found a significant effect(e.g., Sabia and Burkhauser 2010), althoughthe point estimates tend to be in the directionof reducing poverty, and more recently Dube(2017) finds evidence of significant povertyreductions. Recent research has not found that
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 421
higher minimum wages reduce participation inpublic assistance programs in the short-term(Sabia and Nguyen 2017).
The estimates also suggest significant short-run and longer-run effects of the EITC inreducing both poverty and the receipt of publicassistance. The longer-run implied elasticitiesare −0.05 and− 0.09, respectively. Note thatthe public assistance measure does not includethe EITC, and EITC payments do not countin the poverty measure, so that these resultsindicate that the EITC reduces poverty and thereceipt of other public assistance via behavioralchanges—before taking account of the EITC(paralleling findings in Neumark and Wascher2011).
Finally, the estimates indicate that more gener-ous welfare benefits increase poverty and publicassistance receipt in the longer run, with bothelasticities around 0.16. The result for receiptof public assistance may be somewhat mechani-cally linked to the level of benefits, given benefitformulas as well as take-up effects, and the sameis potentially true of time limits. However, thefact that the results are so similar for povertymakes it more likely that we are detecting behav-ioral effects. We also find that tighter time limitsappear to reduce poverty and public assistance inthe longer run. Note that these potential effects ofour two welfare measures are not reflected in pos-itive relationships with earnings or employment.This is not necessarily a contradiction, however;as noted earlier, because these outcomes arebased on threshold definitions, there can bechanges in the distribution but not the level ofearnings, and these distributional changes canchange the share poor or receiving public assis-tance. Moreover, time limits could reduce publicassistance receipt without necessarily increasingearnings or employment. However, one might bea bit more cautious about the estimated longer-run estimates for welfare benefits and time limitsbecause of the absence of positive longer-runrelationships with earnings or employment.
C. Additional Analyses
We now turn to a number of additionalanalyses that hew closely to our preferred spec-ification, but assess the robustness or sensitivityof the results using that specification, includingto important variations in the “treated” and“control” tracts that potentially help identifyeffects on the disadvantaged. In Appendix B,we discuss three other sets of results that help
establish the specification in Table 2 (and closevariants thereof) as our preferred specification.In our view, there are number of choices aboutprecisely how to specify the model or sample.Our preferred choices are reflected in the baselineestimates we just discussed. But knowing howsensitive the results are to some of these choicesnaturally affects the confidence with which oneshould view our findings.
Results for Women Versus Men. Our analysis ofthe effects of the EITC is quite different fromthe more typical analysis that focuses on theshort-run effects of the EITC on the employmentof disadvantaged women (generally proxiedby low skill).39 We can use the NCDB data toestimate separate longer-run coefficients on theEITC for women and men. (We cannot do this forother outcomes, and indeed this disaggregationwould make less sense for a household-levelmeasure.) As reported in Table 3, we find thatthe estimated employment coefficient is largerfor women than for men. This is what theprior literature—focusing on employment ofless-skilled women—would lead us to expect.
The estimated difference between men andwomen is not large, but most evidence of positiveemployment effects of the EITC for womenfocuses on unmarried women with children,whereas in the NCDB data we cannot measureemployment rates for women distinguished bymarital status and number of children.40 Thefact that we find a positive coefficient for menis interesting. The standard EITC literatureignores men, focusing mostly on single mothersfor whom incomes should be lowest and thusthe positive extensive-margin effects of theEITC strongest. However, men in low-incomefamilies—especially with spouses who do notwork—can still, in principle, respond positivelyto the positive employment incentives created bythe EITC.
Alternative Definitions of Disadvantage. Weexplored using alternative definitions of disad-vantage for classifying tracts as disadvantaged atbaseline: the share of the population with a high
39. See, for example, Eissa and Liebman (1996) andMeyer and Rosenbaum (2001).
40. We have plans to do additional work on the longer-runeffects of anti-poverty policies using confidential microdatafrom the Census and ACS. However, even then we will notbe able to focus sharply on unmarried versus married women,or women with or without children, since both of these canchange for an individual over time.
422 CONTEMPORARY ECONOMIC POLICY
TABLE 3Effects of Anti-Poverty Policies on Male and
Female Employment Rates in Areas with HighPoverty Rate at Baseline (1970), 1980–2010
Log maximum welfare benefit −0.0020 0.0102(0.0167) (0.0206)
10-year lag of log maximumwelfare benefit
0.0088 −0.0200(0.0108) (0.0126)
Welfare time limits(< 60 months)
−0.0236** −0.0322**(0.0115) (0.0127)
10-year lag of welfare timelimits (< 60 months)
−0.0257* 0.0021(0.0140) (0.0150)
Adjusted R2 0.71 0.66N 206,787 206,753Tract fixed effects Yes YesCounty x year interactions Yes Yes
Notes: See notes to Table 2. The only difference is thedependent variables.
school degree or less; the share of the populationthat is black; and the share of families headedby single mothers.41 These results are reportedin Table 4. Focusing on our key results—thelonger-run relationships with poverty and publicassistance—the estimates are quite robust. Wealways find negative estimated relationshipsbetween both the minimum wage and the EITCand poverty, although the estimates are sta-tistically significant only for the share blackdisadvantage measure (and more strongly so forthe EITC). The evidence (including statisticalsignificance) is more robust for the potentialeffects of the minimum wage and the EITC inreducing receipt of public assistance—especiallyfor the EITC. The estimated impacts of welfarebenefits and time limits in reducing poverty andpublic assistance are very robust; the magnitudesare similar across the three alternative measures
41. The correlations of the indicators for the most-disadvantaged quartiles are as follows: share poor and shareblack: 0.44; share poor and share single mothers: 0.38; andshare poor and share low-education: 0.25. The correspondingcorrelations for the actual shares, rather than the dummy vari-ables for the top quartile of disadvantage, are 0.55, 0.62, and0.26.
of disadvantage, and most of the estimatedcoefficients are statistically significant.42
Compositional Changes. As noted above, ourestimates using geographic variation mightbetter identify effects on individuals and fam-ilies if we control for compositional changes.We do this, in Table 5, by adding controls formigration—capturing the proportion that movedinto the tract from the same county, or fromanywhere else, in the previous 5 years. To cap-ture additional detail on the composition ofmigration, we add controls for the compositionof the tract population by race, education, singlemotherhood, and age.43
Comparing Tables 2 and 5, the qualitative con-clusions are generally very similar. However, onenoteworthy finding is that the estimated coeffi-cients for poverty and public assistance are typi-cally smaller in magnitude in Table 5. This is trueof the estimated longer-run coefficients on theminimum wage and the EITC in reducing povertyand public assistance, and the estimated longer-run impacts of less generous welfare benefits andwelfare time limits in reducing poverty and publicassistance. Taken at face value, this implies thatpart of the evidence suggesting beneficial effectsfound in Table 2 is attributable to changes in thecomposition of disadvantaged tracts, consistentwith policies that reduce poverty in the most-disadvantaged tracts also leading to in-migration(in relative terms, at least) of residents less likelyto be poor and on public assistance.
The question of whether anti-poverty poli-cies are beneficial or detrimental in helpingto lift the economic fortunes of particularlydisadvantaged areas is important, given thatthere is scant evidence that explicit place-basedanti-poverty programs, such as enterprise zones,increase jobs or reduce poverty in disadvantagedneighborhoods.44 Geographically-concentratedpoverty poses its own challenges above andbeyond individual poverty, perhaps mostimportantly for minorities, who tend to cluster
42. We also find robust evidence of positive longer-runemployment effects of the EITC, although also of modestreductions in average earnings.
43. We are somewhat limited in what compositional con-trols we can use over time because of the data available in theNCDB. Thus, for example, for age we can only measure theproportion aged 16–34 over our entire sample period.
44. See, for example, Neumark and Simpson (2015) andNeumark and Young (forthcoming). The latter paper does notexamine longer-run effects of explicit place-based policies,although research on this topic is in progress (Neumark andYoung, in progress).
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 423
TAB
LE
4E
ffec
tsof
Ant
i-Po
vert
yPo
licie
son
Ave
rage
Ear
ning
spe
rH
ouse
hold
,the
Em
ploy
men
tRat
e,th
eSh
are
inPo
vert
y,an
dth
eSh
are
onPu
blic
Ass
ista
nce,
inA
reas
with
Low
Edu
catio
n,H
igh
Shar
eB
lack
,or
Hig
hSh
are
ofSi
ngle
Mot
hers
atB
asel
ine
(197
0),1
980
–20
10
Ear
ning
sE
mpl
oym
ent
Shar
ein
Pov
erty
Shar
eon
Pub
licA
ssis
tanc
e
Shar
e≤
HSG
Shar
eB
lack
Shar
eSM
Shar
e≤
HSG
Shar
eB
lack
Shar
eSM
Shar
e≤
HSG
Shar
eB
lack
Shar
eSM
Shar
e≤
HSG
Shar
eB
lack
Shar
eSM
(1)
(2)
(3)
(4)
(5)
(6)
(7)
(8)
(9)
(10)
(11)
(12)
Log
min
imum
wag
e0.
0247
−0.
0730
0.00
130.
1556
***
0.14
95**
*0.
2320
***
−0.
0291
0.00
81−
0.03
25−
0.22
69−
0.30
22−
0.30
89(0
.075
9)(0
.062
7)(0
.065
1)(0
.043
7)(0
.045
1)(0
.042
6)(0
.133
9)(0
.100
9)(0
.117
9)(0
.189
5)(0
.247
9)(0
.187
9)10
-yea
rla
gof
log
−0.
0355
−0.
0872
−0.
0309
−0.
0657
−0.
0387
−0.
0600
−0.
0316
−0.
1111
*−
0.13
22−
0.28
96*
−0.
3109
**−
0.34
35*
min
imum
wag
e(0
.063
2)(0
.061
3)(0
.063
9)(0
.051
6)(0
.077
9)(0
.058
6)(0
.094
6)(0
.064
7)(0
.116
0)(0
.145
0)(0
.148
4)(0
.174
0)L
ogE
ITC
phas
e-in
rate
0.06
02**
0.04
03*
0.07
37**
*−
0.01
52−
0.01
37−
0.01
70−
0.13
43**
*−
0.15
57**
*−
0.16
46**
*−
0.15
91**
−0.
1669
**−
0.17
95**
*(0
.025
3)(0
.023
7)(0
.019
6)(0
.015
3)(0
.022
8)(0
.015
7)(0
.042
1)(0
.023
7)(0
.041
9)(0
.060
9)(0
.064
2)(0
.053
8)10
-yea
rla
gof
log
−0.
0230
*−
0.03
22*
−0.
0177
0.01
69**
*0.
0110
0.01
85**
*−
0.01
15−
0.04
09**
*−
0.01
99−
0.05
97**
−0.
0868
***
−0.
0776
***
EIT
Cph
ase-
inra
te(0
.012
2)(0
.016
4)(0
.012
3)(0
.006
0)(0
.006
6)(0
.006
9)(0
.016
6)(0
.013
5)(0
.017
0)(0
.023
5)(0
.030
9)(0
.022
5)L
ogm
axim
um0.
1161
***
0.10
68**
0.11
59**
*−
0.01
620.
0149
0.02
45−
0.11
09*
0.02
290.
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424 CONTEMPORARY ECONOMIC POLICY
TABLE 5Effects of Anti-Poverty Policies on Average Earnings per Household, Employment Rate, Share in
Poverty, and Share on Public Assistance in Areas with High Share Poverty at Baseline (1970),1980–2010, with Migration and Demographic Controls
Notes: See notes to Table 2. The only difference is the addition of migration and demographic controls. The migrationvariables refer to the previous 5 years. Only the proportion aged 16–34 is included as a control due to a lack of consistentage categories available across years in the NCDB.
residentially in poor areas.45 Moreover, researchsuggests that living in poverty areas creates extrahardships for the poor and also for the non-poorresiding in those areas, owing to less private-sector investment, higher crime, weaker labormarket networks, poor health, etc.46 Thus, if anti-poverty policies reduce poverty in disadvantagedareas, there may be positive spillover effects,as effects from disadvantaged neighborhoods
45. American Community Survey (ACS) data from 2010indicate that 50.4% of blacks, 44.1% of Hispanics, but only20.3% of whites, reside in areas where the poverty rate is 20%or higher (see Bishaw 2014, for more descriptive evidence).At the same time, poverty rate differences between thesegroups are much smaller (see https://www.census.gov/prod/2013pubs/acsbr11-17.pdf, viewed March 31, 2017).
46. See the summary of the evidence in Federal ReserveSystem and Brookings Institution (2008).
can have lasting impacts on the next generation(Chetty et al. 2014). And the in-migration ofthe somewhat less-disadvantaged, as suggestedby Table 5, may provide positive spillovers onthe most-disadvantaged living in these areas,although we also need to be concerned thatthe latter are simply being displaced to otherareas—a potential with respect to explicit place-based policies as well, although one on whichthe evidence is limited (see, e.g., Reynolds andRohlin 2015).
Varying the Comparison Tracts. Next, we varythe comparison or control tracts used to try toidentify the longer-run effects of anti-povertypolicies on the most-disadvantaged tracts. First,we drop observations in the third quartile of theobservations used to define DISb. In this case, the
Notes: See notes to Table 2. The only difference is omitting observations in the third quartile of the disadvantage measure.
“control” or “untreated” tracts are more sharplydelineated from the tracts in the top quartile ofdisadvantage because we omit observations forwhich the share poor at the tract level is betweenthe median and the 75th percentile. Given thatthe policies we study would also be expected toaffect low-wage earners or low-income familiesin other tracts, the inclusion of tracts in the thirdquartile of the distribution of disadvantage couldbias our findings towards zero. Consistent withthis expectation, nearly every estimate in Table 6is larger in absolute value than the correspondingbaseline estimate in Table 2; and this is true forevery statistically significant longer-run estimatein Table 2. However, the estimates are not verydifferent between Tables 2 and 6, suggesting thatour evidence is driven by differences in outcomesthat are strongly concentrated in the tracts in thetop quartile of disadvantage.
We also show, in Table 7, that we find quitesimilar results if we estimate our model onlyfor the top two quartiles of disadvantage, esti-mating the potential longer-run effects of policyfrom changes in the most-disadvantaged tractsrelative to tracts in the third quartile. All of thelonger-run coefficients for the minimum wage,the EITC, and our two welfare variables thatwere significant in Table 2 remain statisticallysignificant, while the point estimates for the EITCand the welfare variables are smaller in absolute
value. In our view, the evidence in Table 7 bol-sters a causal interpretation of our findings, asit seems much less likely that there are differ-ent shocks hitting tracts in the top (fourth) andthird quartiles of the distribution of disadvantage,in contrast to the comparison between the topquartiles and other quartiles. And regardless ofwhether one subscribes to a causal interpretation,the results in Tables 6 and 7 show that our evi-dence on the associations between anti-povertypolicies and economic outcomes in the most-disadvantaged tracts is robust to the choice ofcomparison tracts.
Robustness to Baseline/Starting Year. We nextpresent a robustness analysis in which we moveup the baseline year in which we measuredisadvantage by one decade—to 1980—andestimate the models for 1990–2010 instead of1980–2010. If the composition of tracts changedmuch from 1970 to 1980, then a good part ofour identification of effects for “disadvantaged”tracts may not reflect tracts that are as likely tobe disadvantaged in later years, given that weuse data over four decades for our main analysis.Although there is considerable persistence in ourmeasure of disadvantage, the classification oftracts as disadvantaged in 1980 is more persis-tent than the classification in 1970. The sharesof the tracts in the top quartile of the poverty
426 CONTEMPORARY ECONOMIC POLICY
TABLE 7Effects of Anti-Poverty Policies on Average Earnings per Household, Employment Rate, Share in
Poverty, and Share on Public Assistance in Areas with High Poverty Rate at Baseline (1970),1980–2010, Top Versus Third Quartile
Earnings Employment Poverty Public Assistance(1) (2) (3) (4)
Notes: See notes to Table 2. The only difference is that the 1st and 2nd quartiles of the disadvantage measure are omitted.
distribution in 1970 that are in the top quartileone, two, and three decades later are 67.6%(1980), 59.2% (1990), and 58.8% (2000). Thecorresponding shares based on the 1980 data are71.9% (1990), 71.8% (2000), and 61.7% (2010).
The results are reported in Table 8. The resultsfor the EITC, and for welfare time limits, arerobust to this change. We still find statisticallysignificant evidence suggesting that the longer-run effect of the EITC is to reduce poverty andpublic assistance (and to increase employment,but significant only for the longer-run coeffi-cient). And we find similar evidence for welfaretime limits. In contrast, however, the results forminimum wages flip sign, as do the results forwelfare benefits. Especially insofar as policy-makers should be more interested in results basedon more current data, this evidence suggests thatwe should not draw strong conclusions about thebeneficial longer-run effects of either minimumwages or less generous welfare benefits.47
Two of the prior analyses accounted forchanges in the composition of tracts due tomigration (Table 5), or due to the passage of
47. There is some important minimum wage variationin the very early part of the sample, which could explainwhy the minimum wage effects are so different when wemove up the baseline period and the starting year for theanalysis.
time (Table 8). Our next analysis explores ahybrid of these two issues. Rather than fixing theclassification of disadvantaged tracts in a singlebaseline period (1970 in most tables, and 1980 inTable 8), we allow the classification of tracts toevolve over time. (That is, we modify Equation(2), changing the dummy variable for disad-vantaged tracts from DISb
c to DISc,t− 10).48 Thisspecification allows the composition of tracts tochange over time, which implies that we are morecertain that we are estimating 10-year lags ofpolicy effects for tracts that were disadvantaged10 years prior. At the same time, the compositionchanges could reflect long-term effects of policy,which is why we prefer the specification using afixed baseline.
The results are reported in Table 9. The resultsare generally quite similar for the EITC and wel-fare, with two exceptions. First, the estimatedlonger-run coefficients on welfare benefits aresmaller; and second, the evidence that the EITCmay reduce poverty in the longer run is weaker,although the evidence that it reduces publicassistance does not change. Evidence persistssuggesting that the longer-run effect of the EITCis to increase employment. More substantial is
48. The second and third terms in Equation (2) become{DISc,t − 10·Pcst}β + {DISc,t − 10·Pcs,t − 10}βL.
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 427
TABLE 8Effects of Anti-Poverty Policies on Average Earnings per Household, Employment Rate, Share in
Poverty, and Share on Public Assistance in Areas with High Poverty Rate at Baseline (1980),1990–2010
Earnings Employment Poverty Public Assistance(1) (2) (3) (4)
Notes: See notes to Table 2. The only difference is that the “baseline” disadvantage dummy variable DISb is defined as of10 years prior to the observation rather than in a fixed baseline year (1970 in most of our analyses)—that is, DISc,t− 10 insteadof DISb
c .
428 CONTEMPORARY ECONOMIC POLICY
TABLE 10Effects of Anti-Poverty Policies on Average Earnings per Household, Employment Rate, Share in
Poverty, and Share on Public Assistance in Areas with High Poverty Rate at Baseline (1970),1980–2010, with 10-Year Policy Leads
Earnings Employment Poverty Public Assistance(1) (2) (3) (4)
10-year lead of log minimum wage 0.0804 0.0130 −0.0495 0.1340(0.0843) (0.0537) (0.1579) (0.1501)
Notes: See notes to Table 2. The only difference is the addition of 10-year leads of the policy variables. The leading effectsare highlighted in italics.
the change in results for the minimum wage. Theevidence in Table 9 suggests longer-run effectsthat increase poverty and public assistance, withthe effect on poverty statistically significant.Coupled with the evidence in Table 8, this isanother indication that we cannot draw robustconclusions that higher minimum wages reducepoverty or public assistance in the longer run.
Allowing for Leading Effects (Pre-Trends). Ourfinal analysis addresses additional evidence—inaddition to the analysis using different quar-tiles of disadvantage for comparisons—relatedto a causal interpretation of the findings. Weadd 10-year leads of our policy variables toour models, to see whether policy changes werecorrelated with prior changes in outcomes, whichcould lead to biased estimates of policy effects.For the leads corresponding to the most recentdata in our sample, we use 2016 (for welfare)or 2017 values (for the EITC and minimumwage)—depending on data availability—which
nearly correspond to 10 years after the midrangeof the 2006–2010 period.
The results, reported in Table 10, indicatethat there are some significant partial correla-tions between our outcome variables and futurepolicy changes. For the EITC, there are positivepartial correlations for poverty and the share onpublic assistance. If both EITC generosity andpoverty/public assistance are quite persistentover time, then this leading relationship createsa bias against finding beneficial effects of theEITC. This is what we find, as controlling for theleads generates stronger beneficial longer-runeffects of the EITC on these outcomes (compareto Table 2)—thus strengthening our conclusionsfor the EITC. In contrast, this analysis some-what weakens the evidence that more generouswelfare benefits increase poverty and publicassistance, and that tighter time limits reducethem. Still, these estimated effects of welfarepolicy on poverty remain statistically significant
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 429
(only at the 10% level for time limits).49,50
Finally, although the leading effects of minimumwages are not statistically significant, includingthese leading effects eliminates the evidence ofbeneficial longer-run effects of minimum wagesin reducing poverty and public assistance receipt,and in fact leads to evidence consistent withhigher minimum wages increasing poverty in thelonger run.
V. CONCLUSIONS
Our goal in this paper is to generate evidenceon the longer-run effects of anti-poverty policieson key socioeconomic outcomes in disadvan-taged areas. We study three policies—minimumwages, the EITC, and welfare (including a keyaspect of welfare reform)—and estimate howthese policies influence earnings and employ-ment, and most important, poverty and publicassistance, in the most disadvantaged areas.The kinds of longer-run effects we study differsubstantially from almost all research on theeffects of these policies, although there are a fewexceptions that focus on longer-run effects of asingle one of these policies.
We identify tracts that are initially disad-vantaged in terms of a high share of residentswho are poor. We then estimate the longer-run relationships between these alternative poli-cies and key economic indicators of economicself-sufficiency—in particular, poverty and thereceipt of public assistance, but also employmentand earnings.
We have two main results that emerge acrossthe many analyses we report. First, the evidence
49. The pattern of bias for time limits is the same asfor the EITC. In column (3), there is an estimated nega-tive lead for tighter welfare time limits (significant at the10% level). Assuming the same type of persistence, thisimplies a bias towards finding that tighter time limits reducepoverty, consistent with the smaller estimate of the longer-run effect of tighter time limits once we include the lead-ing effect (in the last row of column (3)). However, thenegative leading effect for welfare benefits—assuming thesame persistence—should imply a bias against finding thatmore generous welfare benefits increase poverty and publicassistance receipt. But including the leading effects has theopposite effect. This may be related to differences in the per-sistence of welfare benefits, especially coupled with the post-welfare reform issues discussed earlier.
50. One might wonder whether the evidence of leadingeffects we find is driven in part by defining disadvantage interms of the poverty rate, which is related to poverty and pub-lic assistance outcomes (although our outcomes are measuredin later decades). However, the estimated leading effects andthe implications for the estimates were similar using the othermeasures of disadvantage from Table 4 (results available uponrequest).
suggests that longer-run effects of the EITC areto increase employment and to reduce povertyand public assistance, as long as we rely onnational as well as state variation in EITC policy.Second, tighter welfare time limits also appearto reduce poverty and public assistance in thelonger run. We also find some evidence thathigher minimum wages, in the longer run, maylead to declines in poverty and the share offamilies on public assistance, whereas higherwelfare benefits appear to have adverse longer-run effects, although the evidence on minimumwages and welfare benefits—and especially theevidence on minimum wages—is not robust tousing only more recent data, nor to other changes.In our view, the most robust relationships we findare consistent with the EITC having beneficiallonger-run impacts in terms of reducing povertyand public assistance, whereas there is essentiallyno evidence that more generous welfare deliverssuch longer-run benefits, and some evidencethat more generous welfare has adverse longer-run effects on poverty and reliance on publicassistance—especially with regard to time limits.
The comparison across anti-poverty policies isperhaps the most important evidence we provide.In our view, we have captured the main anti-poverty policies that target working-age adultsand that can affect both their work incentivesand their income from work. Given the strong,short-term pro-work incentives of the EITCestablished in other research, the evidence wefind suggesting beneficial longer-run effects ofthe EITC might seem like a natural conclusion.But it is by no means a foregone conclusion,as there is little evidence on longer-run effects,nor evidence that simultaneously looks at thesekey anti-poverty policies. And we caution thatmore work is needed to pin down EITC effects,given that our results depend on using nationalpolicy variation, while at least one paper hasfound beneficial (short-run) effects of the EITCusing only the state-level variation (Neumarkand Wascher 2011).
Our evidence on how anti-poverty policieschange economic outcomes in disadvantagedneighborhoods could connect in important waysto the intergenerational mobility literature, whichemphasizes the importance of place in longer-run economic outcomes. Moreover, it may bepossible to draw some specific policy links.For example, one key finding in this researchis that neighborhoods with larger fractions ofsingle parents are associated with poorer futureoutcomes for children (Chetty et al. 2014). This
430 CONTEMPORARY ECONOMIC POLICY
suggests that beneficial longer-run effects ofthe EITC in reducing poverty could also lead topositive intergenerational effects.
Finally, we have focused on the longer-runeffects of three key policies chosen becausethey are most likely to affect work incentives.In principle, of course, a whole set of policies,going back to early childhood interventions,could have longer-run effects on labor marketand socioeconomic outcomes of individuals,families, and neighborhoods.51 Most work, evenon short-term policy effects on labor marketoutcomes, has focused on policies in isolation,and the same is true of the much more minis-cule literature on longer-run policy effects. Wereadily acknowledge, however, that there ispotentially a great deal more to be learned fromsimultaneously considering the effects of morepolicies, including their interactions, althoughthe empirical challenges are likely to be severe.Moreover, the fact that some of our findingsdepend on the sources of policy variation weuse highlights that there are further challenges inestimating longer-run policy effects.
APPENDIX A
TABLE A11970 NCDB Versus 1970 Decennial Census Selected
Characteristics
NCDB Census
Share in urbanized areas N.A. 73.5%Share black 11.8% 11.1%Share high school graduate or less 76.9% 78.6%Share in poverty 11.1% 13.7%Share of families headed by single
Notes: Table reports NCDB and Census estimates of sev-eral sample characteristics and outcomes, drawn from theNCDB and National Historical GIS (NHGIS) organizationfor the Decennial Census data (Manson et al. 2018). NCDBstatistics are weighted by tract population. Residence inurbanized areas was not reported in the NCDB in 1970, butgiven how areas were selected for being tracted, it is reason-able to assume the figure is close to 100%.
aFor public assistance and earnings, the NCDB reportshousehold-level data. In the NHGIS data, the numerator anddenominator for public assistance are families instead ofhouseholds. The NHGIS reports aggregate earnings by sexinstead of by household, but once summed, the estimates aredirectly comparable.
51. See the extensive inventory of such policies, andresearch summaries, in Neumark (2016).
APPENDIX B
In this appendix, we discuss three other sets of resultsthat help establish the specification in Table 2 (and close vari-ants thereof) as our preferred specification. First, in AppendixTable B1, we report results paralleling those in Table 2, butincluding the minimum wage, the EITC, and the welfare vari-ables in separate specifications, rather than simultaneously.The minimum wage results are not at all robust to this alter-native analysis, suggesting a strong negative longer-run effecton employment, and strong positive longer-run effects onpoverty and public assistance. The EITC results, and moreso the welfare time limit results, are robust. The minimumwage results are particularly interesting, because it is verymuch the norm in the minimum wage literature to excludeother policies from the regression models estimated (as it is,indeed, in many similar panel data analyses of the effectsof other policies). In our context, at least, given that pre-cision of the estimates does not decline much from includ-ing the three policies simultaneously (compare Table 2 andAppendix Table B1), it is preferable to include the threepolicies simultaneously.
Second, in Appendix Table B2 we report the results (notedearlier) that we obtain estimating a more saturated modelincluding interactions between the indicator for disadvan-taged tracts (DISb) and year fixed effects. As the table shows,our estimated EITC coefficients become far less precise, espe-cially for the longer-run effects, with standard errors thatincrease by a factor of as much as 15 and lead to uninformativeconfidence intervals. Presumably reflecting this, the estimatedEITC coefficients diverge quite strongly from Table 2, withopposite signs for all of the estimated longer-run effects (allinsignificant). The precision of the estimated coefficients forthe other policies does not change much, but given that wesaw the importance of controlling simultaneously for all threepolicies for pinning down the effects of minimum wages (inAppendix Table B1), it is not surprising that the estimatedrelationships with minimum wages change dramatically inAppendix Table B2, pointing to large positive relationshipswith poverty and public assistance. Because of the impreci-sion of the estimated EITC coefficients, we do not use thismore saturated specification. As noted in the main text, wealready control for rich geographic heterogeneity in shocks toour outcomes.
Third, coding the generosity of welfare, especially post-welfare reform, is not as clear-cut as, for example, coding theminimum wage. It is difficult to capture the effects of welfarereform in a limited set of variables, as we noted earlier. Oneconcern is that the effects of welfare benefits pre- and post-reform can be quite different, because it became much harderto get benefits in the latter period (e.g., Haveman et al. 2015).Our inclusion of the (tight) time limits variable should helpon this score, as it flags states with potentially more stringentrules in the post-reform period. As another alternative, wemodified the welfare benefits variable to also include aninteraction with a post-1996 dummy variable, to allow thepotential effects of benefits to change post-reform. (Thisvariable was included in the same way as the main effects inthe preceding specifications—contemporaneous and lagged,with both also interacted with DISb.)
The results, reported in Appendix Table B3, are quiterobust. The key question concerns the effects of the welfarevariables on poverty and public assistance. The interactionsbetween the welfare benefit variables and the post-reformindicator are not significant. The estimated coefficients ofbenefits for poverty and public assistance in the pre-reformperiod remain positive and statistically significant, and the
NEUMARK, ASQUITH & BASS: LONGER-RUN EFFECTS OF ANTI-POVERTY POLICIES 431
TABLE B1Effects of Anti-Poverty Policies on Average Earnings per Household, Employment Rate, Share in Poverty, and Share on Public
Assistance in Areas with High Poverty Rate at Baseline (1970), 1980–2010, One Policy at a Time
Earnings Employment Poverty Public Assistance(1) (2) (3) (4)
I. Minimum wagesLog minimum wage 0.1162** 0.0820*** −0.1854*** −0.2951***
(0.0450) (0.0267) (0.0688) (0.0990)10-year lag of log minimum wage −0.3407*** −0.1277*** 0.6576*** 0.7314***
Notes: See notes to Table 2. The difference in this table is that each panel reports estimates of the specification using minimumwage, EITC, and welfare variables separately, rather than simultaneously.
TABLE B2Effects of Anti-Poverty Policies on Average Earnings per Household, Employment Rate, Share in Poverty, and Share on Public
Assistance in Areas with High Poverty Rate at Baseline (1970), 1980–2010, Saturated Model Absorbing Federal Variationacross Disadvantaged Versus Advantaged Tracts
Earnings Employment Poverty Public Assistance(1) (2) (3) (4)
Notes: See notes to Table 2. The only difference is the additional set of welfare benefit variables interacted with the post-welfare reform (year >1996) variable.
estimated coefficients for tighter time limits remain negativeand statistically significant. Thus, nothing in this analysisindicates we need to distinguish the effects of welfare benefitspre- and post-reform.
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