How Much Does Amnesty Strengthen the Safety Net? Evidence from the Immigration Reform and Control Act of 1986

Transcription

1 How Much Does Amnesty Strengthen the Safety Net? Evidence from the Immigration Reform and Control Act of 1986 Elizabeth U. Cascio Ethan G. Lewis * Dartmouth College and NBER March 2017 Abstract We explore how immigrant legal status affects safety net transfers using variation from the Immigration Reform and Control Act of 1986 (IRCA), which authorized the largest U.S. amnesty to date. Exploiting the timing and geographic unevenness in intensity of IRCA s legalization programs, we estimate a sizable effect of permanent residency on Earned Income Tax Credit (EITC) transfers. By contrast, we find null but imprecise effects of legal status on food stamp transfers. Fiscal costs are partially offset by increased state income tax revenues due to increased rates of income tax filing. These findings suggest that previous studies have understated the relationship between legal status and total family resources, particularly for families with children, and that legalization redistributes resources toward areas more affected by immigration. JEL codes: J61, H24, H53, H71 Keywords: IRCA, legalization, safety net, EITC * Corresponding author. Mailing address: Dartmouth College, Department of Economics, 6106 Rockefeller Center, Hanover, NH ethan.g.lewis@dartmouth.edu. We thank conference participants at the 2016 SOLE Annual Meeting and seminar participants at Montana State University, UCLA, UIUC, the University of Nottingham, and Williams College for their comments. Christian Dustmann provided valuable feedback on an early version of this research. We also thank William Paja and Chris Brown for outstanding research assistance and gratefully acknowledge funding from Dartmouth College. All errors are our own.

2 I. Introduction An estimated 11.5 million unauthorized immigrants live in the U.S. today (Hoefer, Rytina, and Baker, 2012). Few of the unauthorized are children, but many unauthorized adults have children who are U.S. citizens. Over 2009 to 2013, an estimated 4 million U.S. citizens half under the age of five lived with at least one unauthorized parent (Capps, Fix, and Zong, 2016). Despite their citizenship, these children face the disadvantages of unauthorized status, including informal barriers to participation in poverty-alleviating programs for which they are eligible, such as the food stamp program (FSP), 1 as well as statutory restrictions on access to other programs, such as the federal Earned Income Tax Credit (EITC), a refundable tax credit for citizens and permanent residents with positive earned income. That U.S. born children of unauthorized immigrants lack complete access to these programs in particular represents a significant hole in the social safety net. Both the EITC and the FSP occupy central roles in modern U.S. anti-poverty policy. The maximum EITC credit today represents between 30% and 40% of earnings in two-child families that receive it a substantial income transfer. In 2014, the program served 27.5 million families at a total cost of about $67 billion, and together with other smaller refundable tax credits, lifted more than 5 million children out of poverty (Short, 2014). The additional income from the EITC has also been shown to improve health at birth (Hoynes, Miller, and Simon, 2015) and the test scores of older children (Dahl and Lochner, 2012). Though the FSP is less effective in reducing child poverty, it rivals the EITC in size. 2 In utero and childhood exposure to the near-cash transfers under the FSP have also been found to improve infant and later-life health as well as economic 1 The FSP has been called the Supplemental Nutrition Assistance Program, or SNAP, since the 2008 Farm Bill. 2 In 2014, the FSP served 22.7 million households at a total cost of almost $70 billion and lifted 2 million children out of poverty (Short, 2014). Unlike the EITC, the FSP is a social assistance program that provides in-kind benefits for food purchases using means tests that have remained relatively constant over time. Food consumption of FSP recipients appears to respond to FSP transfers as it would to pure cash transfers (Hoynes and Schanzenbach, 2009). 1

3 self-sufficiency for women (Almond, Hoynes, and Schanzenbach, 2011; Hoynes, Schanzenbach, and Almond, 2016). Do legal reprieves for unauthorized migrants increase take-up of these core social safety net programs? Despite the fact that low earnings should allow many of the newly-legalized to meet program eligibility requirements, this is an empirical question. First, take-up of these programs may be low. Obtaining the EITC, for example, requires both filing a tax return and having some knowledge of the program rules; in practice, only 80% of eligible taxpayers participate. 3 Second, even with complete take-up, program eligibility may be short-lived, as previous research suggests that gaining legal status increases earnings (Koussodji and Cobb- Clark, 2002; Kaushal, 2006; Amuedo-Dorantes, Bansak, and Raphael, 2007). We estimate the effect of legal status on EITC and FSP transfers using variation from the Immigration Reform and Control Act of 1986 (IRCA). The last major comprehensive immigration reform, IRCA provided a pathway to legal permanent residency to three million unauthorized immigrants living in the U.S. at the time the largest U.S. amnesty to date. 4 It was largely unanticipated when signed into law on November 6, passed due only to a fragile coalition rapidly assembled at the end of 1986 after 15 years of failed attempts at immigration reform (Baker, 1990). Then, like now, opposition to amnesty was fierce among a significant share of politicians, and the increased enforcement measures that opponents demanded in exchange for support were anathema to existing supporters. Also like now, most affected immigrants were from Central America, of working age, and employed, and most of their children were citizens. 5 3 See accessed March 27, Based on a field experiment conducted in coordination with the IRS, Bhargava and Manoli (2015) find that targeted mailings that raise awareness and simplify information about the EITC increase take-up. 4 The last sizable U.S. amnesty was the 1997 Nicaraguan Adjustment and Central American Relief Act (NACARA). 5 Being a non-citizen Central American immigrant is arguably a good proxy for being an unauthorized immigrant as of Applying this proxy to Census microdata (Ruggles, et al., 2015), we calculate that 535,600 children under the age of 18 had at least one unauthorized parent in 1980; seventy-one percent of these children were citizens. 2

4 Our baseline empirical strategy takes advantage of the abrupt changes in legal status that IRCA authorized. Lacking microdata identifying the legal status of program beneficiaries, we combine administrative data on the intended residence of IRCA applicants for legal status with area panel data on the EITC and the FSP spanning 1979 to We then exploit the timing of the law alongside spatial variation in the intensity of application for legal status in the local population; we test for larger changes in outcomes after 1986 in areas where a larger share of the population applied for and mostly received temporary, and eventually permanent, legal residence. 7 Because IRCA provided agricultural workers earlier access to the FSP than the remaining applicants, we can pursue an alternative empirical strategy for FSP transfers a triple difference approach that exploits this timing in addition to differential spatial variation in the densities of the two applicant types. Identification in the baseline model is not trivial. As shown in Figure 1, the Tax Reform Act of 1986 (TRA86) authorized an EITC expansion in 1987, and the Omnibus Budget Reconciliation Acts of 1990 (OBRA90) and 1993 (OBRA93) authorized EITC expansions in 1991 and Our EITC estimates would therefore be biased if applicant density were correlated with determinants of EITC transfers, not to the legalization applicants themselves, but rather to other area residents. Our models address this concern by allowing outcomes to trend differently in areas with higher baseline non-applicant representation in EITC expansion ranges and higher initial EITC participation rates. They also allow us to test for small differences in the timing of effects: given IRS rules, impacts on the EITC should have arisen only after applicants 6 The Personal Responsibility and Work Opportunity Reconciliation Act of 1996, or welfare reform, temporarily changed the accessibility of safety net programs to legal immigrants (Bitler and Hoynes, 2013), complicating interpretation of our estimates for the FSP after Our research design may also become less credible the further the distance in time from IRCA s passage due to internal migration of the applicants. (See Appendix C.) 7 Two previous studies have approached estimation of this amnesty s impacts with the same idea in mind, but for other outcomes (Cobb-Clark, Shiells, and Lowell, 1995; Baker, 2015). 3

5 became permanent residents a transition that began in earnest in the non-eitc expansion year of 1990, as shown in Figure 2. To reinforce our conclusions, we also take advantage of variation in applicant density at two levels of geography across states and across metropolitan areas within the three heavily affected states of California, Florida, and Texas. This analysis makes several contributions. We are the first to present estimates of the effect of legal status on safety net transfers using exogenous, policy-driven variation. The existing evidence on immigration and public benefits is descriptive and has generally not made distinctions by legal status; it has also not paid much attention to the EITC. 8 Past work on IRCA has also focused on impacts between application and 1992 and has been silent on impacts for the 40% of applicants who were agricultural workers. We estimate impacts on an annual basis, extend the window of observation to 1996 encompassing more years of exposure to permanent residency and consider both seasonal agricultural workers and long-term unauthorized residents, who made up the remaining 60% of applicants. Previous studies of legalization have also focused on employment and earnings. 9 Our estimates provide insight into another channel through which legalization may increase the resources of families with children the safety net. We find estimated effects of legal status on EITC transfers that are similar across the state and metropolitan area analyses and across robustness checks. Areas with higher applicant shares experienced relatively large increases in EITC transfers after IRCA, but not prior. These effects arose well after 1987 indeed not until transitions to permanent residency began in 1990 reflecting IRS requirements of immigrants claiming the EITC. Consistent with a causal interpretation, California state income tax filing rates increased alongside EITC transfers, with 8 For a review of this literature, see Bitler and Hoynes (2013). 9 Studies of the wage and employment effects of the IRCA amnesty include Koussodji and Cobb-Clark (2002), Amuedo-Dorantes, Bansak, and Raphael (2007), and Amuedo-Dorantes and Bansak (2011). Kaushal (2006) studies the wage and employment impacts of NACARA. 4

6 the increases driven by low earners. 10 Our preferred estimates imply that permanent residency increased annual EITC transfers by about $800, or roughly 5% of pre-irca average annual earnings, by By contrast, the findings for FSP transfers are not strongly indicative of a positive impact of legal status, though the estimates are less precise than would be ideal. A natural question to ask, given our findings, is whether granting EITC access to legal permanent residents imposes a new fiscal burden. 11 This question cannot be answered without knowing how EITC receipt affects tax contributions in both the short and long run. As noted, the additional income from the EITC may have increased the human capital of affected children, raising their tax contributions in adulthood; we leave exploration of this possibility to future research. But EITC-induced increases in tax participation and consumption may have led to higher tax contributions even in the immediate term. We estimate that the EITC-induced rise in tax participation alone would have increased California state income tax revenues by about $60 per legalized resident annually starting in Our back-of-the-envelope calculations suggest that EITC-induced boosts to consumption increased annual sales tax revenues per legalized resident as well, albeit by less. 12 Thus, even in the short run, EITC eligibility for permanent residents appears to reduce the fiscal burden of immigration where it is actually concentrated at the state level, and particularly in California (National Academy of Sciences, 2016) We are able to perform this analysis for California because the state has reported personal income tax statistics in narrow income bands at the county level annually for a long time period. These data allow us to detect effects on tax filing and tax contributions in income ranges where the newly legalized immigrants were likely concentrated. By contrast, statistics on federal income tax revenues at the local level, namely the IRS Statistics of Income data, have shorter time series and are not detailed by income level. Neither Florida nor Texas has a state income tax, also rendering impossible a similar analysis for these states. 11 As others (e.g., Lee and Miller, 2000) have noticed, the fiscal burden of immigration is a small proportion of the federal budget. The approximate $2 billion in increased EITC payments that we find, for example, is less than 0.1% of the $2.2 trillion 1986 federal budget (both in 2014 dollars; see Bureau of Economic Analysis, 2017). 12 The California income tax statistics also provide suggestive evidence that legalization increased earnings, which would have had independent impacts on state and federal income tax contributions. 13 As the National Academy of Sciences report and previous research have consistently found, the primary fiscal burden of immigration derives from the fact that immigrants tend to be heavy users of the public school system, which is particularly true in California (Coen-Pirani, 2011), and not from their use of federal safety net programs. 5

7 II. Empirical Strategy A randomized controlled trial (RCT) would be the ideal way to estimate the effects of legal status. In an RCT, legal status would be randomly assigned among unauthorized individuals who apply for it. The model of interest would be given by: (1) yict t t Ai ict, where y ict represents an outcome of interest (e.g., EITC transfers) for working age person i in area c in year t, A i is an indicator for whether i gains legal status in t*, and ε ict captures unobservables. With the study sample limited to unauthorized immigrants and legal status randomly assigned, it should be the case that θ t = 0 for all years t < t*. That is, on average, there should be no difference in outcomes between the treatments and controls before legalization. After legalization, or for t t*, θ t then captures the causal impacts of legal status. In the case of IRCA, legal status was not randomly assigned, but rather granted to large share of those who applied for it. IRCA had two legalization programs. The Legally Authorized Workers (LAW) program allowed immigrants who could document continuous residence in the U.S. since before January 1, 1982 to apply for temporary legal status, which consisted of work and travel authorization, between May 1987 and May The Special Agricultural Workers (SAW) program accepted applications for temporary legal status between May 1987 and November 1988 from those who could demonstrate 90 days of work on certain USDA-defined seasonal crops in the year ending May 1, 1986, with no additional residency requirement. About 40% of all applications came through the SAW program, and about 90% of all applicants were successful in achieving temporary legal status. 6

8 Figure 2 traces the status of all applications under the LAW and SAW programs combined over time. 14 The figure confirms that all applications were submitted by late It also shows that over half of applications for temporary legal status were accepted by the end of 1988, but acceptances continued through 1992; transitions to permanent residency then occurred mainly between (fiscal years) 1989 and By the 1992 fiscal year, 88% of initial applicants nearly all of those who achieved temporary legal status had become legal permanent residents, and the figure does not rise much thereafter. This timing reflects IRCA s provisions: after meeting some additional requirements (learning English and passing a civics test), LAW applicants were able to apply for permanent residency 18 months after approval of temporary status, whereas SAW applicants were granted permanent residency almost automatically one or two years after temporary status was granted. 15 Naturalization did not really begin until 1994, but by the 2001 fiscal year, only about 30% of applicants had become naturalized citizens. The identification strategy afforded by this policy variation is difference-in-differences, represented by the model: (2) yict 0 1Ai Dt 0 Ai 1Dt ict, where D t = [t t*] is a post-legalization indicator. The coefficient of interest is now θ 1, which captures differential trends in outcomes between those who received legal status versus those who did not. Identification in model 2 does not rely on an assumption of identical expected outcomes, as differences in pre-legalization outcomes levels are captured by the parameter θ 0. Instead, estimates will be unbiased if the trend in outcomes for the comparison group, 14 Data come from the Legalization Applications Processing System (LAPS), which provides anonymized longitudinal data on all 3.04 million LAW and SAW applications through Fiscal year statistics on permanent residence come from various editions of the Statistical Yearbook of the Immigration and Naturalization Service; for naturalization, they are from Rytina (2002). Appendix Figure A1 shows trends in the status of LAW and SAW applications separately. See Appendix A for more details on these data sources. 15 The first 350,000 applicants who could demonstrate having worked on farms with qualifying crops for each of the three years ending May 1, 1986 were on the faster track (one year) to receive permanent residency. 7

9 represented by α 1, is an accurate representation of what would have happened for the legalized population absent the status change. 16 In our context, a lack of existing microdata that identify both immigrant legal status and the outcomes of interest precludes estimation of model Taking averages of model 2 at the area-by-year level (across all working age people) yields a model closer to our specification: (3) yct 1Ac Dt 0 Ac 1Dt ct 0, where y ct represents an average outcome in area c in year t, and A c represents the fraction of the area s working age population receiving legal status. If model 2 is correctly specified, the difference-in-differences coefficient in model 3, estimated using aggregate data, is equivalent to the effect of legal status at the individual level from model 2 using data from the same population. This is intuitive: if legal status increased the likelihood that an immigrant received EITC income, for instance, areas with higher legalized population shares should have experienced larger increases from before to after legalization in EITC transfers per capita. Estimation of model 3 is feasible as long as applicants were not evenly distributed geographically, making spatial variation a critical component of our empirical approach. Figure 3 shows, by state, the ratio of working-age applicants to total working-age population (as of 1986), our key measure of policy intensity (A c ) going forward. Only three states California, Florida, and Texas both have enough metro areas and exhibit enough within-state variation in policy intensity to support a within-state analysis (Appendix Table A1). Figure 4 shows the variation in policy intensity across metro areas in these states, which account for 72% of applicants. We 16 This approach has been taken in past studies of the wage and employment impacts of IRCA s legalization, but for LAW applicants only and using native-born Hispanics in the NLSY79 as the comparison group (Kossoudji and Cobb-Clark, 2002; Amuedo-Dorantes, Bansak, and Raphael, 2007; Amuedo-Dorantes and Bansak, 2011). 17 The survey data used in Table 1, Panel B (introduced below) contain information on FSP but not EITC receipt of IRCA applicants. 8

10 focus on working-age (ages 15 to 64) shares because working-age immigrants comprised over 90% of applicants, as shown in Table 1 Panel A, and the EITC is targeted on work. 18 California alone was home to the majority of applicants. About 1.5 million working-age applicants listed California as their intended state of residence, representing about 53% of working-age applicants nationwide and 8.2% of all working-age Californians in Texas was a distant second, with about 415,000 working-age applicants (14.6% of the national total), an estimated 3.8% of the state s working-age population. Though less populous and thus not home to a large share of the applicants nationwide, other southwestern states Arizona, New Mexico, and Nevada round out the top five states in terms of policy intensity. The remaining states listed include two broad groups other states in the West (Idaho, Oregon, and Washington) and populous states (Illinois, Florida, and New York). While this cross-state variation proves useful, only 0.94% of the working-age population in the country overall (excluding California) applied for legal status, and the standard deviation in applicant share across states (1.13 percentage points) is much smaller than within California, Florida, and Texas (4.33 percentage points). It is important to note that because our outcomes data do not include demographic breakdowns, model 3 implicitly uses everyone else of working age in an area as the comparison group, not just those at risk for legalization, as was the case in the hypothetical RCT. By including everyone else in an area in the comparison group, the implicit counterfactual is one of increasing EITC transfers that the unauthorized population would have been denied absent IRCA (Figure 1). As a result, our approach could understate the true effect of legalization for the EITC. On the other hand, the legalized population ages over time, but the rest of the population does 18 Here we also rely on the LAPS data. For the metro area figures, we start with 1990 SMSA definitions, making minor modifications to address suppression of some counties in the LAPS data. Appendix Table A1 shows that the vast majority of applicants in these three states are in identifiable metropolitan areas. See Appendix A. 9

11 not. Given the relative youth of applicants, our estimates could be larger than we would have found in panel microdata. We explore the extent of these competing biases in Section VI. In addition, model 3 is the reduced-form of an individual-level model with spillovers, one where A c has the same direct effect on outcomes regardless of an individual s own legal status. 19 Thus, even well-identified estimates of θ 1 in model 3 potentially capture spillovers of amnesty on other local populations. However, existing theoretical and calibration-based evidence (e.g., Chassamboulli and Palivos, 2014; Chassamboulli and Peri, 2015) suggest that the earnings and employment spillovers of amnesty for local populations and by extension spillovers to the safety net are likely quite small. 20 Assuming that A c had a different spillover effect depending on individual-level legal status, we can also gauge the importance of these spillovers empirically using aggregate data. This exercise also suggests spillovers were likely small (see Appendix B). These caveats aside, our empirical approach using aggregate data offers some benefits over a difference-in-differences model estimated on individual-level data. In practice, individuallevel data with information on IRCA legal status pertains only to LAW applicants and to limited years (time of application and 1992). Using our empirical approach, we can estimate the overall effects of both the LAW and SAW programs and at different points in time. Focusing on the LAW program alone may misrepresent IRCA s impacts overall, given differences in the two legalization programs (Appendix Figure A1) and their applicant characteristics (Table 1). Distinctions in IRCA law between the LAW and SAW programs also allow for an alternative way to estimate the effects of legal status in aggregate data. Regardless of applicant type, applicants with a valid social security number and (full-year) permanent resident status 19 That is, suppose that the individual-level model were yict Ai Dt Ac Dt Ai Ac Dt ict Taking averages of this model at the area by year level, we arrive at model 3, but now 1 1 and IRCA also included increased border security and new employer sanctions for knowingly hiring undocumented workers. Our estimates may pick up direct effects of these measures on local populations to the extent that their impacts varied by A c. Existing literature provides little reason to believe this was the case. (See Appendix B.) 10

12 were eligible for the EITC. However, LAW applicants were ineligible for some programs of social assistance furnished under Federal law on the basis of need, including food stamps, for five years after temporary admission. 21 As shown in Appendix Figure A1, the majority of LAW applicants (about 64%) became temporary residents in the 1988 fiscal year, 6% became temporary residents in the 1987 fiscal year, and 20% in in the 1989 fiscal year. Thus, if changes in legal status affected FSP transfers, areas with a higher density of SAW applicants should have experienced larger increases in FSP transfers per capita between (roughly) the 1989 and 1993 fiscal years, conditional on unrestricted time-varying impacts of overall applicant share. In effect, this triple-difference approach uses LAW applicants (not yet eligible for benefits, so effectively still unauthorized) as a comparison group for SAW applicants. This is valuable, since SAW and LAW applicants were arguably more similar to each other than they were to the rest of the local population. Table 1 shows characteristics of the two applicant groups based on the universe of applications (Panel A) and survey data (Panel B). 22 Applicants in general were overwhelmingly Hispanic (Mexican in particular), male, and of working age, though SAW applicants were more extreme along all of these dimensions. SAW applicants also earned less than LAW applicants ($8.61 per hour) and had lower levels of human capital (with a 93% high school dropout rate). However, even LAW applicants were low human capital and low earning relative to the population at large, many having incomes in the eligibility range for both the EITC and the FSP. Significant shares also had children in the household, another eligibility requirement of the EITC during most of the period of interest. On top of that, applicants were overwhelmingly in childbearing years, 80% aged 18 to 44 and 75% under age 35 (not in table). 21 Exceptions were laid out for education and child welfare programs, the disabled, pregnant women, and children. Neither SAW nor LAW applicants were immediately eligible for Aid to Families with Dependent Children. 22 The basic demographics in this table come from the LAPS, and the more detailed data come from two anonymized surveys described at length in Appendix A: (1) the Legalized Population Survey (for LAW applicants) and the National Agricultural Workers Survey (NAWS) (for SAW applicants). 11

13 III. Estimation Framework A. Econometric Model Our baseline empirical strategy, which we apply to EITC outcomes, thus relies on both the timing of IRCA, captured by D t, and variation across states and metro areas in the intensity of application, captured by A c. In practice, we allow 1987 to be the first year in which IRCA could have had an impact (t* = 1987) a conservative approach given that legalization applications were not even accepted until May of that year, and transitions to permanent residency happened several years later. For A c, we use the measure of policy intensity described in Section II the ratio of the area s working age applicants to its working-age population in We use applications filed rather than rather than applications approved because the underlying application data only provide information on (intended) county of residence at the time of application (see Appendix A). As discussed, however, about 90% of applications filed were ultimately approved for temporary status, and 88% approved for permanent residency, so we rescale our estimates accordingly when discussing magnitudes. 23 We also do not actually estimate model 3, but rather a much less restricted version of it that substitutes area and year fixed effects for the direct effects of A c and D t and allows for flexibility in the timing of effects. This is the event-study model (4) yct Dt Ac c t ct 1986, where D t τ is a dummy variable set to one if the year of observation t is equal to specific year τ, and zero otherwise (or D t τ = 1[t = τ]); the 1986 interaction term is omitted to identify the model. The year fixed effects, α t, account for shocks to outcomes shared by all areas at a given point in 23 Migration within the U.S. across states or metropolitan areas would influence the appropriate scaling factor. However, the relationship between admissions per capita and applications per capita is very close to what would be expected in the absence of internal migration at the state level, where we have data on both (see Appendix C). 12

14 time (e.g., general business cycle effects in addition to policy changes). In our analysis of metropolitan areas, we instead control for state-by-year fixed effects, so as to account for statespecific (policy or economic) shocks to local outcomes. The area fixed effects, γ c, then absorb all sources of potential bias, observed and unobserved, which are fixed within an area over time. The θ τ s are thus the parameters of interest in model 4, capturing the precise timing of differential changes in EITC-related outcomes for areas with higher values of A c relative to the omitted year 1986, the year in which IRCA was passed but the application process had not yet begun. The θ τ s otherwise span the entire period of interest. Estimating this model, we are thus able to test whether areas of higher policy intensity were already experiencing different trends in outcomes before IRCA s passage; for estimates to identify the effect of legal status, this should not be true. We are also able to test for significant changes in EITC transfers across years when the schedule did not change (Figure 1), but the legal status of IRCA amnesty applicants did (Figure 2). 24 The key identifying assumption in model 4 is that, in the absence of IRCA s legalization provisions, areas with higher applicant shares would not have experienced different trends in EITC outcomes in 1987 and later. Estimates of the θ τ s would thus be biased if areas with higher applicant shares had other population characteristics making aggregate EITC outcomes more susceptible to the EITC expansions shown in Figure 1, such as higher shares of the native-born with earnings in the EITC expansion range. We attempt to remove any such biases by allowing for differential trends in outcomes in model 4 by characteristics of the pre-existing local earnings distribution and by pre-existing EITC participation rates. If this approach works, it should be the 24 The timing of observed changes in EITC transfers may be somewhat weak supporting evidence of causation if behavioral responses to changes in the EITC schedule take time to play out (e.g., Eissa and Liebman, 1996). Significant increases in EITC transfers over adjacent years when the EITC schedule changed could also still reflect legalization: in the absence of legal status, these immigrants would not have been eligible for these benefits. 13

15 case that the first effects on the EITC are visible when applicants transition to permanent residency, which is well after 1987 and not coincident with the EITC expansions. Indeed, for LAW and SAW applicants combined, these transitions started in earnest in the 1990 fiscal year (see Figure 2). For estimating the effects of legalization on FSP transfers, we employ the tripledifference approach earlier outlined. In this case, the model of interest is ~ L (5) yct Dt Sc Dt Ac c t ct, where S c represents the ratio of SAW applicants to total 1986 working age population in area c. In this model, the coefficients of interest are on the D τ t x S c interactions, which give differential trends in outcomes in areas with more SAW applicants versus areas with more LAW applicants, relative to the omitted year, If legal status (including temporary status) increased FSP transfers, it should be the case that ~ 0 for (roughly) 1989 τ 1993 (fiscal years). The identifying assumption in model 5 is weaker than that in model 4, requiring only that areas with higher SAW applicant shares, holding constant overall applicant shares, had no reason aside from IRCA to have experienced different trends in outcomes between 1989 and If spillovers are the same across the two applicant types, Model 5 also allows us to overcome any bias from spillovers in model 4. Unfortunately, however, this model can only reveal impacts of legal status for FSP transfers and for SAW applicants in the short term. B. Preliminary Evidence on Identifying Assumptions Did areas of higher policy intensity in fact have systematically different shares of the rest of the local population likely to be eligible for and likely to take up an expanded EITC? If so, 25 This is the case because A c = L c + S c, where L c is the ratio of LAW applicants to 1986 working-age population. 14

16 estimates of model 4 would not identify the effect of legal status. We explore this possibility by compiling and analyzing statistics on the local earnings distribution in calendar year 1979 (calculated using data from the 5% 1980 Census Public Use Microdata Sample (PUMS) (Ruggles, et al., 2015)) and on local EITC transfers per working age person in fiscal year 1986 (from the Bureau of Economic Analysis (BEA) and the Census Bureau). 26 The former proxy for eligibility for an expanded EITC, whereas the latter capture both eligibility and take-up (e.g., stemming from program knowledge). 27 In our 1980 Census calculations, we exclude (families with) any adult non-citizen Central American immigrants, to focus on populations not directly affected by the amnesty. Table 2 summarizes these characteristics, 1986 FSP transfers, and the pre-irca educational composition of the adult population for states (excluding California) and for metropolitan areas (California, Florida, and Texas) and describes their relationship with applicant share, A c. We exclude California from the state-level analysis because it is an outlier in terms of applicant share, as shown in Figure 3. All statistics are weighted by 1986 working-age population, and the regressions based on metro area-level data include state fixed effects to reflect the inclusion of state-by-year fixed effects in the corresponding specifications to follow. The bivariate models (columns 2 and 5) show that applicant share is significantly related to pre-existing educational attainment and program transfers. 28 Since these variables are highly 26 See Appendix A for further description of the data. In the 1980 Census calculations, the bottom income category would have been ineligible for the EITC. The second category roughly corresponds to families that would have been in the phase-in or maximum credit regions of the EITC prior to TRA86 (and IRCA). The third category captures families that would have been eligible for the expanded EITC under TRA86, while the last corresponds (again roughly) to families that would have been newly affected by OBRA90 and OBRA93. In 2014 dollars, the upper bound on the last income category is $48, For tax year 1996 (the first for which our data overlap), per-capita state EITC transfers are positively associated with Chetty, Friedman, and Saez s (2013) state-level sharp bunching measure conditional on the 1980 income measures included in Table 2, Panel A; the partial correlation between the two variables is 0.63 (excluding Washington DC and weighting by working-age population). 28 Standard errors are clustered on state in columns 2 and 3 and by metro area in columns 5 to 7. 15

17 correlated with one another, columns 3 and 6 present estimates from a regression of applicant share on all of the variables in Panels A and B simultaneously; the last column then shows estimates from a multivariate regression like that in column 6, but focusing on prediction of the local SAW applicant share (S c ) conditional on A c, to mirror model 5. F-statistics and associated p-values from tests of their joint significance are at the bottom of the columns. Throughout, the coefficients are jointly significant, but less so at the metropolitan level. For metropolitan areas, the partial correlations with S c are also both weaker statistically (both individually and jointly) and smaller in magnitude than those with A c (column 7 versus column 6). Still, in all regressions to follow, we control for interactions between all of these variables and the same year dummies with which A c is interacted. IV. Legal Status and the EITC A. State-Level Analysis While our preferred estimates come from the metro area-level analysis, a benefit of the state-level analysis is that EITC claim counts are not available for levels of geography below the state. We compile state-level information from two sources published tabulations from the IRS Statistics of Income (SOI) and our own tabulations from the IRS SOI individual tax model (ITM) data, which are annual 1% samples of individual federal tax returns. 29 We also use EITC transfers to state residents reported by the BEA, which provide the foundation for our metro area-level analysis. Here and throughout, the BEA data pertain to fiscal years and the IRS data to tax years, and we normalize by working age population to allow for the micro-level interpretation of our estimates described in Section II. 29 Relative to the published IRS data, calculations from the ITM can be affected by income suppression. However, the ITM data span more years in the pre-irca period and allow us to calculate statistics not consistently published the number of tax-filers receiving actual EITC refunds (amounts in excess of tax liability) and refund amounts. 16

18 Figure 5 presents estimates of the θ τ in model 4, excluding California, for the BEA and IRS measures of state EITC amounts per working age person (in 2014 dollars, Panel A) and IRSreported counts of EITC refunds and claims per working age person (Panel B). For presentation purposes, we multiply each of the latter (and A c ) by 100. All of the regressions include state and year fixed effects, state unemployment rates, and interactions between year dummies and each of the variables in Table The capped vertical lines around the estimates represent their 95% confidence intervals; inference accounts for clustering on state, and regression estimates are weighted by 1986 state population. Consider first the estimates in Panel A for EITC amounts. Regardless of data source, estimates of all of the θ τ s for 1985 and earlier are close to zero and relatively precisely estimated, implying that states with higher applicant population shares were not already experiencing relatively strong upward trends. For all measures except published EITC claims per capita, 1990 is then the first post-irca year in which there is a marked difference in per-capita EITC measures relative to 1986 for states with higher applicant shares. Though the coefficients themselves tend to be somewhat imprecise, this pattern suggests a positive impact of permanent legal status on EITC transfers. Table 3 presents estimates from a restricted version of the event-study model underlying Figure 5 to clarify the roles played by IRCA s legalization programs and EITC schedule changes. In this restricted model, we leave model 4 otherwise unchanged but pool the year dummies on the A c (and baseline characteristic) interactions into eight groups, forcing the impacts of legal status to be the same within each. In particular, we divide the pre-irca period 30 Controlling for time-varying measures of local employment conditions comes at some risk of over-controlling, as changes in legal status could affect these outcomes. However, these controls are potentially important when we apply our approach to examine the impacts of legal status on FSP transfers, which are relatively sensitive to the business cycle (Bitler and Hoynes, 2016). 17

19 into two sub-periods 1979 to 1982 and 1983 to 1986 and the post-irca period into six subperiods 1987 (application, but implementation year for TRA86), 1988 to 1989 (when most initial applications were approved), 1990 (when transitions to permanent residency had begun in earnest), 1991 to 1992 (when most remaining applications for permanent residency were approved, but the EITC also expanded), 1993 (the earliest potential year of access to the FSP programs for LAW applicants), and 1994 to 1996 (when the EITC formula changed once again). The first two columns correspond to the estimates in Panel A of Figure 5. The interaction coefficient is first statistically significant in 1990, but only for the BEA measure (column 1). That is, only in 1990 when applicants began to attain status as legal permanent residents in large numbers can we conclude with some confidence that the gap in EITC transfers per working age person between states with higher and lower applicant shares was larger than it was in the immediate pre-irca period (1983 to 1986). Moreover, the coefficients for and 1990 are statistically different (p=0.05) despite the constancy of the EITC schedule over that period. On the other hand, there was not a statistically significant increase in EITC amounts between 1986 and 1987, despite the change in EITC schedule. Findings based on published EITC claims data in column 4 follow a somewhat similar pattern, and a similar but less precise pattern of findings emerges from the ITM measures for EITC refunds in columns 2 and In terms of magnitudes, the 1990 interaction coefficient in column 1 implies that state EITC transfers per working age person rose by on average $2.57 more between and 1990 for each additional percentage point increase in state applicant share. Absent spillovers on the remaining state population, this estimate implies that working-age applicants for legal status 31 Column 4 shows a significant increase in claims in However, this result does not hold for the number of refunds (column 3) or the overall size of claims (columns 1 and 2), suggesting that our controls for eligibility in the rest of the local population may be inadequate for capturing people who qualify only for small amounts of the EITC (which likely result in lower tax liability but not a refund) after the 1987 expansion. A key feature of TRA86 was to expand the qualifying income range for the EITC (Figure 1, Panel B). 18

20 experienced on average $257 greater increases in annual EITC transfers between and 1990 than other state residents. Scaling up this estimate to reflect the 44.7% transition rate into permanent legal status by 1990, we arrive at the implied effect of (permanent) legal status $576 in EITC transfers. By 1993, the cumulative transition rate into legal status stabilized at 88%, so this effect is $537 ($4.719 x 100 / 0.878) in 1993 and $786 ($6.923 x 100 / 0.881) in The last gain in EITC transfers reflects the effects of the 1994 change in the EITC schedule for the legalized permanent resident population: permanent legal status increased the chances of claiming the EITC by roughly the same amount (43 percentage points) from 1993 forward. B. Metro Area-Level Analysis Our state-level analysis of the EITC is limited from an identification perspective: the estimates are potentially biased by state-specific shocks, and there is considerably less variation in policy intensity across than within states. We therefore turn now to our preferred metro arealevel analysis. Here, we must rely on the BEA data on EITC transfers. For California, however, we have also developed proxies for low-income tax filing rates from state income tax statistics published by the California Franchise Tax Board (CAFTB) the number of state returns claiming the California Renter s Credit (through 1992) and the number of state returns in the bottom quartile of California s 1979 distribution of (real) adjusted gross income (AGI). 32 Shifts in the distribution of state returns toward low earners in the post-irca period provide additional evidence that the causal mechanism is legalization, as they suggest anticipated increases in taxfiling rates among the newly legalized. For many, claiming the EITC for the first time would have coincided with filing an income tax return for the first time The underlying data source the Annual Report of the CAFTB gives the number of returns filed in narrow bins of AGI (e.g., $2,000 increments in the 1986 report). Similar data are not available for federal returns, or for Florida or Texas. See Appendix A. 33 During the period of interest, Individual Taxpayer Identification Numbers (ITINs) did not exist. 19

21 Figure 6 presents the full event-studies, while Table 4 presents the accompanying restricted estimates; all of the regressions include metro area and state-by-year fixed effects, metro area employment-to-population ratios, and interactions between year dummies and each of the variables in Table 2. We also weight by 1986 (metro area) working-age population and cluster standard errors on metro area. The findings for EITC transfers per working age person are similar in magnitude to those yielded from the state analysis, particularly by the end of the period. Estimates shown in column 1 imply an effect of legal permanent residence on EITC transfers of $274 ($1.224 x 100 / 0.447) by 1990, $334 (2.812 x 100 / 0.843) by , $471 (4.139 x 100 / 0.878) by 1993, and $823 (7.248 x 100 / 0.881) by The estimates are, moreover, much more precise than they were using state-level variation. Figure 6 Panel B and the remaining columns of Table 4 then show the estimates for the two CAFTB measures earlier described. Again, 1990 appears to be a turning point in the effects of IRCA s legalization programs, pointing to the importance of legal permanent residency. For the bottom quartile variable, the interaction coefficient is first statistically significant in 1990, and despite earlier post-irca statistical significance for the Renter s Credit variable, there is a large increase in its magnitude between 1989 and That the effects for the bottom quartile variable do not increase after 1990 also suggests that increases in effects for EITC transfers over the remaining years were more a function of changes to the EITC schedule than to EITC participation, as was the case in the state-level analysis. We perform several specification checks on these estimates in Table 5. Unweighted estimates of this baseline specification are broadly similar to the weighted estimates (column 1). Focusing on California, which affords the richest variation and also provides the data on state income tax returns, also does not change our substantive conclusions (column 2). We explore the 20

22 robustness of the California finding further in column 3, where we model pre-irca trends linearly (via an interaction between A c and year). 34 Due to a statistically significant pre-irca trend (which exists in California but not in all three states combined), this approach lowers the magnitudes of the post-irca coefficients; some in the early post-irca period even become negative and statistically significant. Yet, the time pattern of the estimates is still reflects the need for permanent residency to claim the EITC. An additional threat to validity is that areas with higher applicant shares may have experienced greater shifts in population toward groups more likely to be eligible for the EITC (or for larger EITC refunds) in the post-irca period. Race/ethnicity is a correlate of EITC transfers, as is the ratio of children to working age population. The last two columns add these metro areaby-year varying demographic characteristic controls to the specification for California in column These controls diminish the magnitude of the coefficients for per-capita EITC transfers (column 4) and for the percent of returns filed in the bottom quartile of California s 1979 distribution of AGI (column 5), particularly at the end of the sample period. They nevertheless still suggest the importance of permanent residency to receiving the EITC. 36 V. Legal Status and the FSP There is reason to believe that IRCA s legalization programs should have had less of an impact on FSP transfers than on EITC transfers, as some unauthorized immigrants were already receiving FSP benefits via their U.S. citizen children. In fact, 3.7% of LAW applicants in the Legalized Population Survey (LPS) (used in Table 1) reported that someone in their family 34 The implicit counterfactual for the post-irca period in this specification is a continuation of the pre-irca trend. 35 We focus on California for this specification check because the California State Department of Finance has published annual data on population by Hispanic ethnicity and age at the county level back to 1979 (see Appendix A). By contrast, the county age-sex-race files produced by the U.S. Census Bureau only begin producing statistics by Hispanic ethnicity in The trailing off of impacts in the bottom quartile between and appears driven by earnings growth in the newly legalized population, as we show in Table 9 and discuss in Section VI. 21

23 received food stamps at the time of application for temporary status. 37 FSP participation among LAW applicants and their families in the LPS also rose to 12.4% in However, not all of this increase need reflect legalization, as FSP caseloads went up during the recession in the early 1990s. 38 The sensitivity of food stamps to the business cycle in general (Bitler and Hoynes, 2016) makes it especially important to have a good comparison group for this outcome. Model 5 provides one, since it identifies the effect of legalization by comparing LAW applicants to SAW applicants, taking advantage of SAW applicants earlier legal access to this program. For comparison, the thick line in Figure 7 Panel A represents the event-study coefficients for FSP transfers per working age person from the same specification as employed for EITC transfers (model 4); the restricted event-study estimates are shown in the first column of Table 6. This time, the restricted models reflect our expectations for the timing of differential effects between the LAW and SAW applicants. The estimates are potentially surprising negative through (and statistically significantly so in 1988), positive and statistically significant in 1994, and positive but not statistically significant in Taken at face value, these estimates imply that legalization at least initially lowered FSP participation. Vetting of their applications may have reduced fraud or encouraged LAW applicants and their families to forego some FSP benefits to which they may have actually been entitled, in which case this would be a real effect. On the other hand, the rest of the local population may be a poor comparison group for this particular outcome. Columns 2 and 3 of Table 6 thus show estimates like those in column 1, but replacing the overall applicant share in the population with the LAW applicant share and the SAW applicant share, respectively (estimated jointly); column 4 then shows the SAW-LAW difference in these coefficients, 37 Similarly, the FSP participation rate for presumed SAW applicants in the NAWS (FY89) was 10.3%. 38 Per-capita FSP transfers rose nationally by nearly 50% between 1987 and 1992, with nearly all of that increase happening over 1990 to

24 estimated using model 5. The full event studies are shown in Figure 7, Panels A and C. In the restricted event-study model, the SAW-LAW coefficient differences are positive and statistically significant through 1988, and though no longer significant, remain of similar magnitude for the remainder of the period. None of the post-irca coefficients are statistically different from one another. Table 7 performs robustness checks on these estimates that mirror those performed in Table 5 for EITC transfers. While still noisy, the estimates are somewhat more in line with expectations if IRCA had a positive impact on FSP transfers. For example, when restricting attention to California (column 2), which provides much of the identifying variation, as well as when allowing for linear pre-irca trends (column 3) and controlling for demographic characteristics (column 4) within California, we can reject that the coefficients for and 1994 are the same, and the coefficient difference is in the expected direction. Yet, we cannot reject equality of the coefficients for 1988 and All in all, we do not view these results as providing strong evidence of an impact of IRCA on FSP transfers. Estimates from model 4 are generally statistically insignificant and small by the end of the sample period. And coefficient estimates from model 5 that should be significantly different from one another for FSP transfers are not. In addition, application of model 5 to EITC transfers in columns 5 through 8 of Table 6 and Panels B and D of Figure 7 (full sample) and column 5 of Table 7 (California only) reveal no differential impact; this supports a causal interpretation, since we only expect to see one insofar as relevant economic characteristics of the two groups differ. To be clear, though, the estimates from model 5 are noisy enough that we cannot rule out effects as large as we estimated for the EITC in some years. 23

25 VI. Interpretation A. Benchmarking Magnitudes We have provided a variety of evidence that immigrant legal status particularly, achieving legal permanent residency increases the probability of receiving income support through the tax system. How big are these estimates relative to expectations? To provide a rough benchmark for interpretation of magnitudes, we simulated transfers to applicants based on their baseline economic characteristics (Table 1 and associated data), assuming no behavioral response to the incentives of the EITC and (initially) a 100% take-up rate. We then calculated what our coefficients would have looked like in the presence of these purely mechanical effects by predicting changes in EITC amounts in the comparison group based on the earnings distribution and family structure of citizens and non-citizen non-central American immigrants in the 1980 Census. We then repeated the exercise allowing for aging of the legalized population and for a more realistic 80% take-up rate for both the treatment and comparison groups. Table 8 shows these calculations; for reference, the first column gives estimates from our preferred metro area-level specification (Table 4, column 1). The baseline calculation in column 2 holds key EITC determinants fixed at their pre-authorization levels and suggests that mechanical effects stabilize in 1993 to explain between 40 and 60 percent of our coefficient estimates. However, imposing the fertility changes reported in survey data for LAWs between 1987 and 1992 on all pre-authorization respondents (column 3), we can explain more than the remainder of the coefficient estimates at a 100% take-up rate. Allowing for across-the-board 5% earnings growth (column 4) slightly less than the wage impacts of IRCA reported in previous studies 39 reduces the mechanical share of the estimates, though it does remain close to 100%. 39 The most credible wage estimates, which include a comparison group, for which legal status is observed, and which include data from both before and after the IRCA amnesty, range from 6% for men (Kossoudji and Cobb- 24

26 These calculations suggest that mechanical effects may explain much of our estimates. But they also assume that all newly eligible taxpayers receive the EITC. Imposing the more realistic take-up rate of 80% (column 5), the mechanical share of the estimates falls (not surprisingly) to about 80%. This finding suggests that there is some scope for behavioral responses to the EITC s labor supply incentives to have contributed to our estimates. Unfortunately, the behavioral response of this population to the EITC is not identifiable, since EITC access and legal status changed simultaneously. 40 However, consistent with a labor supply response to the EITC on the part of secondary earners (Eissa and Hoynes, 2004), Amuedo- Dorantes, Bansak, and Raphael (2007) find that female LAW applicants left the labor force as a result of legalization. Another way of benchmarking the estimates is to calculate what we would have found had we been able to compare the legalized population to a population with similar baseline characteristics that remained unable to access the EITC. In practice, this is just the simulated EITC for the treatment group, and it represents what we would have gotten from the hypothetical experiment described in Section II if there were no causal effects of legalization on earnings or fertility and no behavioral response to the EITC. Column 7 shows these calculations, assuming again an 80% take-up rate, scaled in dollar terms to reflect the effect of legal status at the individual level. These are very similar to the implied effects of our estimates per legal permanent resident shown in column 6 for comparison (like above, calculated as column 1 coefficient/legal permanent resident transition rate x 100). This suggests that our estimates may Clark, 2002) to 9% for men and 21% for women, correcting for selection into employment (Amuedo-Dorantes, Bansak, and Raphael, 2007). These estimates focus on LAW applicants as observed in the LPS, using native-born Hispanics in the NLSY79 as a comparison group. 40 Even reduced-form labor supply impacts may not be measurable using our approach. Annual measures of labor supply at local geography are only available in the Current Population Survey, which has both limited sample sizes and limited geographic identifiers in this period. 25

27 provide a lower bound on the true effects if there was also a labor supply response on the part of the newly legalized to the EITC. B. A New Fiscal Burden? Do our findings imply that allowing EITC access to legal permanent residents is a new fiscal burden? Not necessarily. Those EITC transfers may have generated better outcomes for affected children, reducing their reliance as adults on the safety net. But even in the short term, some of the additional income from the EITC may have been returned to state (and local) governments in the form of higher sales taxes. Increases in income tax filing induced by EITC eligibility may have also raised state income tax revenues. Eligibility of legal permanent residents for the EITC could therefore function not just as a transfer to individuals, but also as a transfer to the governments of the states that bear the direct fiscal costs of immigration (National Academy of Sciences, 2016). To get a sense of the magnitude of this transfer, we return to our California income tax statistics. Looking at changes in the number of returns filed throughout the distribution of AGI not just in the first quartile we can infer effects on overall tax filing rates. Table 9 shows estimates of the model in Table 5, column 5, but for each of the four quartiles of California s 1979 AGI distribution, as well as overall (i.e., the ratio of returns filed to working age population). 41 The gains for the bottom quartile shown earlier are repeated in the second quartile (column 2), and largely reflect an overall increase in tax filing (column 5) that is, legalized immigrants coming into the tax system. Taking 1990 again as a focal point, the estimates imply a 65 percentage point (0.293/0.45 x 100) increase in the likelihood of filing a tax return a figure 41 We use the same specification as in Table 5, column 5, to account for potential pre-irca trends in the outcomes. 26

28 comparable to the 1986 mean filing rate. 42 Most of these gains are evenly split between the first and second quartile of the 1979 AGI distribution. A back-of-the-envelope calculation on the basis of these estimates implies that, absent increases in AGI, the rise in the number of tax returns starting in 1990 would have increased California tax payments by about $55 to $60 per permanent resident through Given the magnitude of the income change from the EITC, state sales taxes are also likely to have increased and not just in California by a slightly lower amount. 44 Thus, some of the income transfers to the newly legalized population through the EITC likely returned to state governments, particularly in California, even in the very short term. Importantly, Table 9 also provides suggestive evidence of earnings gains from legalization. After effects on overall tax filing rates stabilize, returns filed per capita shift upward in the AGI distribution, consistent with increases in earnings among legalized applicants (see Appendix D). In particular, between 1993 and , the 8 percentage point decline in the bottom quartile effect is offset by increases in the second and third quartile effects of 4 percentage points each. Back-of-the-envelope calculations on the basis of these estimates suggest 42 This figure is less than 100 percent because tax filing units often contain more than one working age person. 43 According to Table 9, there was an increase in returns per legalized worker of roughly 27 percentage points (~0.12/.045 x 100) in each of the first and second quartiles in In 2014 dollars, average tax payments per return in the first (second) quartile ranged between $7 and $20 ($192 and $207), implying an increase in state income tax contributions between $55 and $60 per legalized resident. Note that this is a lower bound, as it excludes the small (and statistically insignificant) increases in filing rates at higher quartiles. 44 Recall that permanent residency was associated with about a $275 increase in EITC transfers by 1990 and about an $800 increase by The average combined state and local California rate of sales tax was 6% through 1990 and 7.25% starting in Florida and Texas had sales tax rates over this period of 6% and 6.25%, respectively. For California, then, the revenue gain was on the order of $275 x MPC x 0.06 in 1990 and $800 x MPC x by 1996, where MPC represents the marginal propensity to consume items that are taxable in California. Assuming an MPC of 0.7 then implies increases of $11.55 and $40.6 per legalized resident in California in 1990 and 1996, respectively. Effects in 1996 would be slightly smaller in Florida and Texas, given those states lower sales tax rates. Note that an MPC of 0.7 might be reasonable given that IRCA s legalization appears to have induced Mexican arrivals to decrease their remittances (Amuedo-Dorantes and Francesca Mazzolari, 2010). In Europe, there is also more direct evidence that legal status increases consumption holding constant income (Dustmann, Fasani, and Speciale, forthcoming). 27

29 a gain in AGI of around 16.7% (or $3,114) over this period. 45 To be sure, AGI is not the same thing as earnings; even if it were, in our approach the legalized population is aging whereas the comparison group is not, so AGI gains could reflect returns to experience in addition to the effects of legal status. However, a gain in AGI of this magnitude is unlikely to be entirely due to experience. This is an independently interesting result, as existing literature has only estimated earnings impacts through 1992 (as opposed to 1996) and only for LAW applicants (as opposed to the overall applicant pool). It also makes clear that, by focusing on new tax payments associated with the EITC only, the above calculations miss other new tax contributions that arise from legalization. These would include not only new state sales and income tax contributions, but also new payroll tax contributions at the federal level. 46 VII. Conclusion There are estimated to be over 11 million unauthorized immigrants in the U.S. today. Many are the parents of U.S. citizens who have no legal right to the EITC, a program central in reducing childhood poverty in the modern social safety net. In this paper, we have used spatial and temporal variation from IRCA, the last comprehensive immigration reform, to explore the extent to which extending legal status to unauthorized immigrants both to the long-standing undocumented population and to seasonal agricultural workers affects EITC and FSP transfers 45 We estimate that the mean income in the bottom, second, and third quartiles of the 1979 California AGI distribution (in 2014 dollars) are, respectively, $7,891.47, $28,351.45, and $55, Thus, we take the gain in mean AGI between 1993 and as roughly -0.08*7, *28, *55, = $2, per applicant or /0.88 = $3,114 per permanent resident. If we divide by an estimate of base income of $18,636 (5% larger than the pre-amnesty earnings estimate of $17,748.56, as we used in Table 8, column 4), we get 16.7%. See Appendix D for more details. 46 Legal status-induced movements of immigrants from the uncovered to the covered sector, as well as increases in earnings among those already working in the covered sector, would also increase payroll tax revenues. In theory, for example, the $3,114 increase in AGI we found between 1993 and alone would raise payroll tax contributions by $467 (=$3,114 x 0.15). Unfortunately, we cannot study impacts on payroll tax contributions directly because the available data are a short time series, are not detailed by income level, and use imputed geography. 28

30 received. While we cannot rule out that the effects of a similar legalization program would be different today, the demographics of the likely unauthorized today overlap heavily with those of IRCA s legalization applicants, 47 and eligibility conditions and program generosity of both the FSP and the EITC are similar now to what they were in the mid-1990s. While FSP transfers appear to have been little affected by IRCA s legalization programs, we have found that areas with higher applicant shares experienced relatively large increases in EITC transfers once applicants were eligible for legal permanent residence. This is true both at the state level and across metropolitan areas within California, Florida, and Texas. Our estimates imply that permanent residency raised the annual EITC transfer to the average applicant by about $800 by 1996 roughly 5% of pre-amnesty average annual earnings. Taking the $800 figure as a lower bound, based on our calculations in Section VI, our findings imply that IRCA s legalization programs increased EITC refunds by about $2 billion in 1996, representing about 7% of total federal spending on the EITC in that year. These new EITC outlays were partially offset by increases in state income and sales tax contributions, suggesting that new EITC claims stemming from amnesty helped to relieve some of the geographically concentrated fiscal burden of immigration (National Academy of Sciences, 2016). If existing literature is any guide, the additional income from the EITC as well as earnings gains associated with legalization may have improved applicants children s test scores and health in infancy and possibly into adulthood. More directly, legalization may have removed the harmful impacts on cognitive development associated with various aspects of parents undocumented status, such as low incomes and anxiety about the risk of deportation 47 Two things that have changed are that the number of likely unauthorized is considerably larger now than it was in 1986, and they are less concentrated in California (Hoefer, Rytina, and Baker, 2012). 29

31 (Yoshikawa and Kholoptseva, 2013). 48 Although the data challenges to demonstrating such effects directly are immense, they are worth trying to overcome: these effects are central to understanding the long-run net welfare and fiscal impacts of IRCA, as well as to contemplating the effects of any future legalization program. VIII. References Almond, Douglas, Hilary W. Hoynes and Diane Whitmore Schanzenbach Inside the War on Poverty: The Impact of Food Stamps on Birth Outcomes. The Review of Economics and Statistics 93(2): Amuedo-Dorantes, Catalina, Cynthia Bansak, and Steven Raphael Gender Differences in the Labor Market: Impact of IRCA s Amnesty Provisions. American Economic Review, Papers & Proceedings 97(2): Amuedo-Dorantes, Catalina and Francesca Mazzolari Remittances to Latin America from Migrants in the United States: Assessing the Impact of Amnesty Programs. Journal of Development Economics 91(2): Amuedo-Dorantes, Catalina and Mary Lopez Falling Through the Cracks? Grade Retention and School Dropout among Children of Likely Unauthorized Parents. American Economic Review, Papers & Proceedings 105(5): Baker, Scott R Effects of Immigrant Legalization on Crime. American Economic Review, Papers & Proceedings 105(5): Baker, Susan Gonzalez The Cautious Welcome: The Legalization Programs of the Immigration Reform and Control Act. Washington DC: The Urban Institute. Bhargava, Saurabh and Dayanand Manoli Psychological Frictions and the Incomplete Take-Up of Social Benefits: Evidence from an IRS Field Experiment. American Economic Review 105(11): Bitler, Marianne and Hilary Hoynes Immigrants, Welfare Reform and the U.S. Safety Net. In Card, Davd and Steven Raphael, Eds. Immigration, Poverty, and Socioeconomic Inequality. New York: Russell Sage Foundation. Bitler, Marianne P. and Hilary W. Hoynes The More Things Change, the More They Stay the Same? The Safety Net and Poverty in the Great Recession. Journal of Labor Economics, 31(1): S403-S Similarly, Amuedo-Dorantes and Lopez (2015) find evidence that increased enforcement increases grade repetition among the likely undocumented young children. 30

32 Capps, Randy, Michael Fix, and Jie Zong A Profile of U.S. Children with Unauthorized Immigrant Parents. Migration Policy Institute Fact Sheet, January. Chassamboulli, Andri and Giovanni Peri The Labor Market Effects of Reducing Undocumented Immigrants. Review of Economic Dynamics 18: Chassamboulli, Andri and Theodore Palivos A Search Equilibrium Approach to the Effects of Immigration on Labor Market Outcomes. International Economic Review 55(1): Chetty, Raj, John Friedman, and Emmanuel Saez Using Differences in Knowledge Across Neighborhoods to Uncover the Impacts of the EITC on Earnings. American Economic Review 103(7): Cobb-Clark, Deborah A., Clinton R. Shiells, and B. Lindsay Lowell Immigration Reform: The Effects of Employer Sanctions and Legalization on Wages. Journal of Labor Economics, 13(3): Cortes, Kalena Are Refugees Different from Economic Immigrants? Some Empirical Evidence on the Heterogeneity of Immigrant Groups in the United States. The Review of Economics and Statistics 86(2): May, Dahl, Gordon B. and Lance Lochner The Impact of Family Income on Child Achievement: Evidence from the Earned Income Tax Credit. American Economic Review 102(5): Dustmann, Christian, Francesco Fasani and Biagio Speciale. Forthcoming. Legal status and Consumption Behaviour of Immigrant Households. Journal of the European Economic Association. Eissa, Nada and Hoynes, Hilary Taxes and the Labor Market Participation of Married Couples: The Earned Income Tax Credit: Journal of Public Economics 88 (9-10): Eissa, Nada and Jeffrey Liebman Labor Supply Response to the Earned Income Tax Credit. Quarterly Journal of Economics 111(2): Hoefer, Michael, Nancy Rytina, and Brian Baker Estimates of the Unauthorized Immigrant Population Residing in the United States: January Office of Immigration Statistics, Policy Directorate, U.S. Department of Homeland Security. Hoynes, Hilary, Douglas L. Miller, and David Simon Income, the Earned Income Tax Credit, and Infant Health. American Economic Journal: Economic Policy 7(1):

33 Hoynes, Hilary and Diane Whitmore Schanzenbach Consumption Responses to In-Kind Transfers: Evidence from the Introduction of the Food Stamp Program. American Economic Journal: Applied Economics 1(4): Hoynes, Hilary and Diane Whitmore Schanzenbach Work Incentives and the Food Stamp Program. Journal of Public Economics 96: Hoynes, Hilary W., Diane Whitmore Schanzenbach, and Douglas Almond Long Run Impacts of Childhood Access to the Safety Net. American Economic Review 106(4): Kaushal, Neeraj Amnesty Programs and the Labor Market Outcomes of Undocumented Workers. Journal of Human Resources 14(3): Kossoudji, Sherrie A., and Cobb-Clark, Deborah A Coming Out of the Shadows: Learning about Legal Status and Wages from the Legalized Population. Journal of Labor Economics, 20(3): National Academies of Sciences, Engineering, and Medicine; Division of Behavioral and Social Sciences and Education; Committee on National Statistics; Panel on the Economic and Fiscal Consequences of Immigration The Economic and Fiscal Consequences of Immigration. Francine D. Blau and Christopher Mackie, Editors. Ruggles, Steven, Katie Genadek, Ronald Goeken, Josiah Grover, and Matthew Sobek Integrated Public Use Microdata Series: Version 6.0. Minneapolis: University of Minnesota. Rytina, Nancy IRCA Legalization Effects: Lawful Permanent Residence and Naturalization through Mimeo, Office of Policy and Planning Statistics Division, U.S. Immigration and Naturalization Service. Short, Kathleen The Supplemental Poverty Measure: Current Population Reports P Washington, D.C.: U.S. Census Bureau. Yoshikawa, Hirokazu and Jenya Kholoptseva Unauthorized Immigrant Parents and Their Children s Development: A Summary of The Evidence. Migration Policy Institute. 32

34 Notes: TRA86=Tax Reform Act of 1986; OBRA90=Omnibus Budget Reconciliation Act of 1990; OBRA93=Omnibus Budget Reconciliation Act of

35 Notes: Numbers of initial applicants and temporary admissions were calculated by the authors at the year and month level from the LAPS data, excluding the 2% of applicants whose application date was not provided. Numbers of permanent residents by fiscal year (ending October of calendar year) are from the Yearbook of Immigration Statistics (various years), and naturalized citizenss by fiscal year were provided by Rytina (2002). To calculate cumulative transitions to permanent residency and citizenship, we divide the published fiscal year figures by the total number of applicants as reported in the LAPS data. 34

36 Notes: Map plots the percent of a state s 1986 working age population that applied for legal status under IRCA in the lower 48 states. The number of working-age applicants for legal status was calculated by the authors from the LAPS data, and the 1986 working age population was estimated by the Census Bureau. Working age is defined as ages for consistency across the two data sets. 35

37 36