PRELIMINARY
How Much Does Amnesty Stretch the Safety Net?
Evidence from the Immigration Reform and Control Act of 1986
Elizabeth Cascio
Ethan Lewis*
Dartmouth College and NBER
May 13, 2016
Abstract
This paper estimates the effect of immigrant legal status on Earned Income Tax
Credit (EITC) and food stamp transfers using variation from the Immigration Reform
and Control Act of 1986 (IRCA), which authorized the largest U.S. amnesty to date.
Our empirical approach exploits both the timing of IRCA and the geographic
unevenness of applications for legal status under the law. We find that areas with
higher applicant shares experienced relatively large increases in EITC transfers after
IRCA, both at the state level and at the metropolitan area level within three heavilyaffected states – California, Florida, and Texas. Income tax filing rates among low
earners increased alongside EITC transfers, and effects arise in years when the EITC
schedule remained unchanged. The estimates imply that achieving legal status raised
the annual EITC transfer to the average applicant by about $800 by 1996 – roughly
5% of pre-amnesty average annual earnings, and marginally more than would be
expected based on mechanical eligibility effects alone. Estimated effects of legal
status on food stamp transfers are small by comparison. The findings suggest that
legal reprieves for unauthorized parents today could have large effects on their U.S.
citizen children by making them eligible for the EITC.
*
Corresponding author: [email protected]. We thank participants at the 2016 SOLE Annual Meeting for
their comments. We also thank William Paja and Chris Brown for outstanding research assistance and gratefully
acknowledge funding from Dartmouth College. All errors are our own.
I.
Introduction
An estimated 11.5 million unauthorized immigrants live in the U.S. today (Hoefer,
Rytina, and Baker, 2012). Few unauthorized migrants are children, but many unauthorized adults
have children who are U.S. citizens. Over 2009 to 2013, an estimated 5.1 million children in the
U.S. under the age of 18 – 79% them U.S. citizens – lived with at least one unauthorized parent,
and among the citizens, nearly half were under the age of five (Capps, Fix, and Zong, 2016).
Despite being citizens, these children face the disadvantages of unauthorized status, and during a
critical developmental period (Yoshikawa and Kholoptseva, 2013). Among these disadvantages
is a lack of complete access to social programs that can alleviate poverty. In addition to facing
informal barriers to participation in the programs for which they are eligible, such as food
stamps, most of these children do not benefit from cash transfers under the federal Earned
Income Tax Credit (EITC), a refundable tax credit for families with positive earned income.
The EITC has come to occupy a central role in U.S. anti-poverty policy over the past
several decades, growing from a program reaching around 2 million families in the early 1980s
to the far-reaching program that it is today. In 2013, the program served nearly 29 million
families at a total cost of about $68 billion, and together with other smaller refundable tax
credits, lifted an estimated 4.63 million children out of poverty (Short 2014). The additional
family 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). While the 1996
advent of Individual Taxpayer Identification Numbers (ITINs) has provided a conduit for
unauthorized immigrants to comply with federal tax law, it does not enable them to claim the
EITC. Yet, the mechanical eligibility of unauthorized parents for the EITC has the potential to be
quite high, and they may change their labor supply in response to the EITC’s incentives.
1
Evaluating the impact of immigrants’ legal status on EITC transfers would thus
illuminate a critical hole in the existing social safety net, and how proposed legal reprieves might
provide a remedy. In this paper, we estimate this effect using variation from the Immigration
Reform and Control Act of 1986 (IRCA), the last major comprehensive immigration reform.
Among other provisions, IRCA provided a pathway to permanent residency to more than 2.7
million unauthorized immigrants living in the U.S. at the time – the largest U.S. amnesty to
date.1 Like now, the vast majority of those granted legal status were from Central America, of
working age, and employed. Also like now, most of their children were citizens.2 We use the
abrupt changes in legal status authorized by IRCA to estimate the effect of legal status not only
on the EITC, but also on the Food Stamp Program (FSP), which rivals the EITC in size but is
more accessible to U.S. citizens with unauthorized immigrant parents.3
As is the case in most research attempting the estimate the effects of amnesty, a key
estimation challenge we face is a lack of microdata with information on both legal status and the
outcomes of interest. To address this issue, we combine administrative data on intended place of
residence of the applicants for legal status under IRCA with administrative area panel data on the
EITC and the FSP. We then take a difference-in-differences approach, exploiting the timing of
the law alongside variation across space in the degree to which local populations applied for
legal status. Our empirical models test for sharp, differential changes in outcomes after 1986 in
areas where the share of the population that applied for temporary legal status (most of whom
1
The last sizable U.S. amnesty was the Nicaraguan Adjustment and Central American Relief Act of 1997. Several
pieces of legislation that would have given legal status to certain immigrants have been introduced since that time,
but none have made it through Congress.
2
Being a non-citizen Central American immigrant is a good proxy for being an unauthorized immigrant as of 1980.
Applying this proxy to Census microdata, 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.
3
In 2014, the FSP served 22.7 million households at a total cost of almost $70 billion, and in 2013, it lifted an
estimated 2.35 million children out of poverty (Short, 2014). The near-cash transfers under the FSP have been found
to improve health at birth (Almond, Hoynes, and Schanzenbach, 2011). Childhood exposure to the FSP also
improves later-life health, and for women, economic self-sufficiency (Hoynes, Schanzenbach, and Almond, 2016).
2
received it) was relatively large.4 In the absence of spillovers, this aggregate approach yields the
same impacts of amnesty that would be obtained from a difference-in-differences model
estimated on individual-level data using the rest of an area’s population – citizens and authorized
immigrants combined – as a comparison group.
Identification in this model is not trivial. Most importantly, the EITC expansion
authorized by the Tax Reform Act of 1986 (TRA86) took effect in 1987, the same year in which
applications for legal status were first accepted and some of the first applications were approved.
If applicant density were correlated with determinants of EITC transfers to other area residents,
our estimates would be biased. To address this concern, all of our empirical specifications allow
for differential trends by pre-existing correlates of EITC transfers. We also take advantage of
variation in applicant density at two levels of geography where biases are likely to be of opposite
sign – across states and across metropolitan areas within the three heavily-affected states of
California, Florida, and Texas. Using state income tax statistics from California, we are
furthermore able to explore whether the distribution of tax-filers shifted toward families with
lower earnings, the expectation if legal status increased the probability of filing an income tax
return for the first time.5 Whether the restrictions that IRCA placed on FSP take-up are borne out
in the data also provides a valuable check on the internal validity of our research design.
The estimated effects of legal status on EITC transfers are remarkably similar across the
state and metropolitan area analyses. Areas with higher applicant shares experienced relatively
large increases in EITC transfers after IRCA, but not prior. These effects arise later than 1987
4
A couple of previous studies have approached estimation of this amnesty’s impacts with the same idea in mind
(Cobb-Clark, Shiells, and Lowell, 1995; Baker, 2015), but for other outcomes. An alternative approach taken in the
literature on IRCA has been to compare trends in outcomes of the legalized population in data that pertain to the
legalized population alone to trends in outcomes of a comparison group constructed from the NLSY (Kossoudji and
Cobb-Clark, 2002; Amuedo-Dorantes, Bansak, and Raphael, 2007; Amuedo-Dorantes and Bansak, 2011).
5
Neither Florida nor Texas has a state income tax, rendering impossible a similar analysis for these states.
3
and more generally in years when the EITC schedule did not change, with the timing suggesting
that permanent residency – rather than mere application or approval of temporary legal status –
was the key driving factor. Supporting this interpretation, state income tax filing rates among low
earners in California increased alongside EITC transfers through the end of the transition to
permanent residency, then plateaued. The estimates imply that achieving legal status raised the
annual EITC transfer to the average applicant by about $800 by 1996 – roughly 5% of their preamnesty annual earnings, and marginally more than would be expected based on mechanical
eligibility effects alone. Estimated effects of legal status on food stamp transfers are small by
comparison and sensitive to the business cycle, and follow the differential patterns by type of
amnesty applicant (agricultural or not) predicted by the legislation.
This paper makes several contributions. We are the first to present credible estimates of
amnesty on safety net transfers. We are also the first to examine impacts of IRCA legalization on
all amnesty applicants, a benefit of our empirical strategy. For data reasons, the existing
literature has focused on wage and employment impacts through 1992, and only for the 60% of
applicants who were not agricultural workers (Koussodji and Cobb-Clark, 2002; AmuedoDorantes, Bansak, and Raphael, 2007; Amuedo-Dorantes and Bansak, 2011). Our findings leave
room for modest behavioral responses to the EITC to mediate these effects, but they also suggest
that estimating employment and wage effects at the peak of a recession, even with the benefit of
a comparison group, may misrepresent the impacts of legalization. Our findings also imply that
wage effects alone substantially understate the impacts of legalization on total family resources.
Further, while more suggestive, our findings regarding the timing of IRCA’s effects on
the EITC suggest that temporary legal reprieves for unauthorized immigrants, such as DAPA, 6
6
DAPA, which stands for Deferred Action for the Parents of Americans and Lawful Permanent Residents, was
proposed by President Obama in November 2014. The program was to extend three-year temporary work permits
4
might be inadequate for closing the gap in EITC benefit access for the U.S. citizen children of
unauthorized immigrants; permanent residency may be necessary. If existing literature on the
childhood benefits of the EITC is any guide (e.g., Dahl and Lochner, 2012; Hoynes, Miller, and
Simon, 2015), the foregone benefits for these children could be substantial.
II.
Background on the EITC and the FSP
A.
The Earned Income Tax Credit
The EITC is a refundable tax credit available to families with positive earnings and –
until 1994 – only to families with children. Being a refundable tax credit, families receive as an
income transfer any credit in excess of their tax liability. In terms of structure, the EITC
increases in earned income (the “phase-in” region), then plateaus over a range of earnings (the
“maximum credit” region) before declining at some rate to zero (the “phase-out” region). By
1996 – the last year we consider – the maximum credit reached $5,365 (2014 dollars) for a
family with two children, and two-child families with earnings up to $42,994 were eligible for
any EITC, as shown in Figure 1.7 For two-child families receiving the maximum credit, it
represented between 30% and 40% of family earnings – a substantial income transfer.
The parameters of the EITC have changed dramatically over the period of interest. Figure
1 gives trends between 1979 and 1996 in the real values of two aspects of the EITC schedule –
the maximum credit (Panel A) and the maximum earnings eligible for any credit (Panel B). High
inflation eroded the generosity of the EITC over the early 1980s, but policy changes drove the
changes in the years that followed. TRA86 authorized an increase in the maximum credit and
and stays from deportation to the unauthorized parents of U.S. citizen (and legal resident) children, but its
implementation was suspended in February 2015 following a legal challenge by 26 states.
7
We restrict attention to 1996 and prior for data reasons at this time, but for reasons clarified below, our research
design becomes more problematic the further we extend the analysis in time. A consequence of this data restriction
nevertheless is that welfare reform had barely been instituted nationwide by the end of our period. Usefully,
however, welfare reform had no impact on legal immigrants’ EITC access, though it did curtail FSP benefits to legal
immigrants until 2002. See Bitler and Hoynes (2013).
5
dramatically increased the range of earnings that qualified for any credit, returning maximum
qualifying earnings to their 1979 level (and more) in real terms. The Omnibus Budget
Reconciliation Acts of 1990 (OBRA90) and 1993 (OBRA93) expanded the program further.
OBRA90 introduced separate schedules for families with one versus two or more children
starting in 1991, and OBRA93 made those differences starker starting in 1994, while also
introducing a small EITC for childless tax filers. Across these policy changes, the phase-in
subsidy rate increased monotonically, from 10 or 11 cents on the dollar from 1979-86, to 14
percent for 1987-90, to up to 40 percent for families with two or more children in 1996.
By offering more than a dollar of income for every dollar earned, the EITC provides
substantial (static) work incentives in the phase-in region, unambiguously encouraging labor
force participation, as well as more hours of work, assuming that the substitution effect
dominates. On the other hand, if leisure is a normal good, the labor supply incentives are
unambiguously negative in the maximum credit and phase-out regions. These negative incentives
are thought to fall mainly on secondary earners, such as married women (Eissa and Hoynes,
2004), though a lack of knowledge about the EITC’s structure may inhibit this type of response
(Chetty and Saez, 2013; Chetty, Friedman, and Saez, 2013).
There are thus two broad channels by which a change in legal status will generate EITC
transfers to (previously unauthorized) immigrants: (1) by making them eligible for the EITC
without any change in (labor supply) behavior, provided they file tax returns – mechanical
eligibility (Ashenfelter, 1983); and (2) through changes in labor supply in response to the EITC’s
incentives. Given that knowledge of the EITC’s structure appears important for generating
credit-maximizing behavior, it is tempting to believe that the behavioral responses will be on the
extensive (employment) margin, or in the phase-in region more generally, where knowledge of
6
the exact structure of the credit is less important. 8 Past research on IRCA has nevertheless found
negative labor supply effects for women (Amuedo-Dorantes, Bansak, and Raphael, 2007;
Amuedo-Dorantes and Bansak, 2011), consistent with EITC incentives for secondary earners,
and the legalized population already has high employment rates, as we show below.
B.
The Food Stamp Program
While also a federal program of roughly the same size, the FSP differs from the EITC in
many ways. First, the FSP does not provide cash assistance, but rather in-kind benefits
(vouchers) for food purchases. These benefits are conceived of as “near cash,” however, as
recipients appear to respond to food stamps much as they would to a pure cash transfer (Hoynes
and Schanzenbach, 2009). Second, unlike the EITC, the FSP is a social assistance program; it is
also universal. Neither positive earnings nor the presence of children are eligibility criteria: food
stamps are available to all eligible individuals and families that meet means tests.
Also unlike the EITC, these means tests have remained relatively constant over time,
except for inflation adjustments. Families with (gross) incomes at or below 130% of the federal
poverty line qualify for assistance. The FSP is potentially as generous as the EITC, but not so far
up into the income distribution: in 2014, the maximum qualifying monthly gross income for a
family of four was $2,552, and the maximum monthly benefit was $668. However, the average
household receiving food stamps in 2014 received a monthly benefit of only about $256. This
reflects both variation in household size and the fact that transfers are reduced by 30 cents for
every dollar earned. The average household receiving food stamps during the period of interest
had very similar benefit levels in real terms.9
8
Previous research has found that the EITC encourages work, particularly among single mothers (Eissa and
Liebman, 1996; Meyer and Rosenbaum, 2000, 2001; Hoynes and Patel, 2015).
9
For example, average household monthly benefits were $257 and $267 in 1989 and 1996, respectively.
7
While the 30% benefit reduction rate is lower than that under other social assistance
programs, like Aid to Families with Dependent Children (AFDC), it does provide a work
disincentive, particularly for single women (Hoynes and Schanzenbach, 2012). Gaining
eligibility to the FSP via legalization therefore provides labor supply incentives that work against
those of the EITC for those with weak labor force attachment. Nevertheless, the FSP has always
been available to the U.S. citizen children of unauthorized immigrants, and thereby to their
parents (if only indirectly). We therefore anticipate less of an impact on legalization on FSP
transfers than on EITC transfers.
III.
Background on IRCA
A.
Legal Provisions
IRCA was largely unanticipated when it was signed into law on November 6, 1986.
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 those who already supported legalization. IRCA also passed only after 15 years of
failed attempts to pass legislation to address unauthorized immigration. Indeed, bills similar to
IRCA had been introduced in the two prior Congresses and did not pass; the ultimate passage
came from a fragile coalition rapidly assembled at the end of 1986 (Baker, 1990).
IRCA had two major legalization provisions. The first, “Legally Authorized Workers”
(LAW) program allowed workers who could document continuous residence in the U.S. since
before January 1, 1982 (among other criteria) to apply for temporary legal status, which
consisted of work and travel authorization. The application period ran from May 1987 to May
1988. After meeting some additional provisions (learning English and passing a civics test),
successful LAW applicants could then apply to become permanent residents 18 months later.
8
The second, “Special Agricultural Workers” (SAW) program accepted applications for
temporary legal status from those who could demonstrate 90 days of work on certain USDAdefined “seasonal” crops in the year ending May 1, 1986 (with no additional residency
requirement), during the application period May 1987 to November 1988. If application for
temporary status was successful, SAW applicants would likely be granted permanent residency
one to two years later.10 Of all applications, about 40% came through the SAW program, and
90% were successful in achieving temporary legal status.11
The timing of IRCA’s implementation is the first critical component of our identification
strategy. Figure 2 traces the status of applications under both programs combined over time. Data
come from the Legalization Applications Processing System (LAPS), which provides
longitudinal data on all 3.04 million LAW and SAW applications through 1992, and figures by
fiscal year through 2001 are reported by Rytina (2002). The figure confirms that all applications
were submitted by late 1988. It also shows that over half of the adjustment to temporary legal
status had happened by the end of 1988, though it continued through 1992. Transitions to
permanent residency occurred mainly between 1989 and 1991, consistent with the provisions
laid out above. By 1992, 88% of initial applicants – nearly all of those who achieved temporary
legal status – had become permanent residents. Naturalization did not really begin until 1994, but
by the 2001 fiscal year, only about 30% of applicants had become naturalized citizens.
An important aspect of the legislative compromise underlying IRCA was the set of
restrictions it placed on eligibility for social assistance. First, the law stipulated that applicants
10
The first 350,000 applicants who could also 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.
11
IRCA’s legalization provisions may technically not be considered an amnesty given the costs imposed on
applicants. Beyond those described above, for example, applicants had to pay a sizable fee at the point of application
for temporary legal status. Successful LAW applicants also had to pay another fee when they applied for permanent
residency. For SAW applicants, the transition to permanent residency was almost automatic. Because the SAW
program was part of the eleventh hour compromise that got IRCA through Congress, it was not subject to as much
vetting – a possible reason why it had less stringent requirements of applicants (Baker, 1990).
9
would not be eligible for AFDC until five years after being granted temporary legal status. LAW
applicants were also more broadly ineligible for “any program of assistance furnished under
Federal law on the basis of need,” for five years, although several exceptions were laid out for
educational and child welfare programs, the disabled, pregnant women, and children. Given
Figure 2, successful applicants under either program should thus have been ineligible for AFDC
until 1992 at the earliest, and only SAW applicants may have had earlier eligibility to other
federal aid, such as the FSP. However, successful applicants under either program would have
been theoretically eligible for the EITC once they had a valid social security number. Whether
IRCA appears to have had impacts at the appropriate times by program is a useful test of the
internal validity of our research design.12
In order to build the consensus needed to include legalization provisions, IRCA also
included new enforcement measures, including increased funding for border security and new
employer sanctions for knowingly hiring unauthorized workers. It is not clear how these
additional provisions affect our estimates. On one hand, immigrant enforcement efforts have
been found to reduce Medicaid participation rates among eligible immigrants (Watson, 2014),
suggesting that similar “chilling effects” could arise for other programs for which the legalized
population is eligible.13 On the other hand, IRCA’s employer sanctions have been found to
increase wage discrimination against Hispanic workers relative to non-Hispanic workers (Bansak
and Raphael, 2001).14 Given the high Hispanic share among amnesty applicants, any such
12
We would like to examine impacts on AFDC, but we lack adequate data for doing so.
In our context, such effects are likely to come from interior enforcement. Time-series analysis suggests that IRCA
had little impact on flows from Mexico (Woodrow and Passel, 1990; Orrenius and Zavodny, 2003), and there is little
evidence to suggest border security affects the rate of border crossing (Gathmann, 2008). However, increased border
enforcement does seem to raise apprehensions (Hanson and Spilimbergo, 1999).
14
Bansak and Raphael (2001) exploited the brief period in which sanctions applied only to non-agricultural
employers; Hispanic workers’ non-agricultural wages fell relative to agricultural wages relative to the same double
difference for non-Hispanics during this period. Other theoretical and empirical work also suggests that increased
interior enforcement likely lowers wages (Cobb-Clark, Shiells, and Lowell, 1995; Chassambouli and Peri, 2015).
13
10
discrimination should lower earnings among the legalized, perhaps increasing program
eligibility. Regardless, any future immigration reform incorporating amnesty would likely
include enforcement measures, suggesting our estimates are policy relevant.
B.
Applicant Characteristics
The impacts of IRCA’s legalization provisions on safety net transfers will depend not
only on the provisions themselves, but also on applicant characteristics. The first column of
Table 1 summarizes applicant characteristics provided in the LAPS data, while Table 2
summarizes the more detailed data contained in two surveys: (1) the Legalized Population
Survey (LPS), which collected data in 1989 from a sample of about 6,000 LAW applicants ages
18 and over still residing in the U.S.; and (2) National Agricultural Workers Survey (NAWS),
which collected data on agricultural workers in the 1989 fiscal year. In the NAWS, we limit
attention to the 970 respondents who were both ages 15 to 64 and had a pending application for
legalization (presumably as a SAW) at the date of the survey.
Table 1 shows that applicants for temporary legal status under both programs combined
(Panel A) were overwhelmingly Hispanic, male, and of working age (ages 15 to 64 for our
purposes). Nearly 87% of all applicants were Hispanic, only 32% were female, only 5.5% were
under the age of 15, and less than 1% were aged 65 or older.15 Nearly three quarters of applicants
were from Mexico. LAW applicants (Panel B) were also different from SAW applicants (Panel
C). Relative to SAW applicants, LAW applicants were less likely to be working age (almost
89.4% versus 99.5% for SAWs) and more likely to be female (nearly 43% versus 18% for
SAWs). The two programs had equal Hispanic shares, but Mexican representation was lower
15
Today’s unauthorized immigrants are estimated to have a lower Mexican share (59%) than in 1986, made up for
by the rising share from other Central American counties and several Asian countries. Women also appear to be a
larger share of the recent unauthorized (47%). The recent unauthorized are also less concentrated in California, part
of the broader pattern of immigrants, especially Mexicans, spreading to other parts of the U.S. (Card and Lewis,
2007). These shifts had already largely occurred by 2000. See Hoefer, Rytina, and Baker (2012).
11
among the LAW applicants (about 70% versus 82% for SAWs). As shown in Table 2, LAW
applicants in the LPS have a similar demographic profile, though SAW applicants in the NAWS
have a higher Mexican share. All in all, though, the demographic similarity to the universe of
applicants suggests that the survey statistics might be more broadly representative.
The remainder of Table 2 summarizes economic characteristics of LAW and SAW
applicants in these survey data. Across the U.S. overall, 80 percent of LAW applicants reported
having been employed at the time of the application, and conditional on employment, they on
average worked full time – a little more than 40 hours per week. Their median hourly wage
(excluding zeros) was $11.08 (2014 dollars), a figure above the federal minimum wage in 1987
($6.98), but at only about the 22nd percentile of the national wage distribution.16 By contrast, all
SAW applicants were working (by definition), and among those employed on an hourly basis
(75%), the median hourly wage (in 1989) was $8.61 (2014 dollars) – a figure between the 10th
and 11th percentiles of the national wage distribution. To provide further context, Figure 3 plots
kernel density estimates of the (log) wage distributions for LAWs, SAWs, and the working-age
population nationally as of 1987-88. Hourly wages of applicants not only lower medians, but
also lower variances. This is consistent with their relatively homogeneous and low levels of
human capital: 72% of LAWs were high school dropouts, as were 93% of SAWs.
These statistics suggest that a large share of applicants for these programs had incomes in
the eligibility range for both the EITC and the FSP. Significant shares also had children in the
household (57% and 37% for LAWs and SAWs, respectively), another eligibility requirement of
the EITC during most of the period of interest. As a benchmark for understanding the
16
We calculated the national distribution from the 1987 and 1988 Current Population Survey (CPS) Merged
Outgoing Rotation Group files, limiting the sample to 16-64 year olds not in school and “Windsorizing” hourly ages
between $2 and $200 (in 2014 dollars).
12
magnitudes of our estimates, we will later use this and other information in these data sets to
predict EITC transfers to this population after legalization assuming no labor supply response.
C.
Geographic Distribution of the Applicants
The second critical component of our identification strategy is spatial variation in the
intended residence of the applicants. Figure 4 depicts the distribution of the working-age LAW
and SAW applicants across states; Table 3 provides more detail. Here we also rely on the LAPS
data, which provide intended state of residence for all 3.04 million applicants and intended
county of residence for the 2.78 million applicants that listed counties with more than 100,000
people (as of the 1990 Census) or more than 25 applications; given these suppression rules, we
focus our within-state analysis on metropolitan areas. The table lists states in descending order
by the ratio of working-age applicants to total working-age population (as of 1986), which will
be our key measure of policy intensity going forward. To keep the table concise, we restrict
attention to the 11 top applicant-generating states, which are represented by the darkest shading
in Figure 4. Each of these states had an applicant to population ratio of over 1 percent, and
together, they represented nearly 91% of all applications.
As both the figure and the table make clear, 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 a staggering 8.2
percent of all working-age Californians as of 1986. Texas was a distant second, with about
415,000 applicants of working age (14.6% of the national total) and an estimated 3.8 percent of
state’s working-age population affected. 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, each with applicant shares of
13
2.6 to 3.6 percent. 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).
Because California is a clear outlier among states, we drop it from our analysis taking
advantage of cross-state variation in policy intensity. In a separate analysis, however, we will
take advantage of variation in applicant density across metropolitan areas within California, as
well as within two other top applicant states – Florida and Texas.17 The last two columns of
Table 1 and Table 2 (Panel A only) also show that, with the exception of having a relatively high
Hispanic (Mexican) share, California, Florida, and Texas look fairly similar in terms of applicant
characteristics to the U.S. overall – not surprising since together they account for 72% of
applicants. Table 3 also shows that there is much more variation in policy intensity within
California, Texas, and Florida, than across states. Indeed, only those three states have both
enough metropolitan areas and exhibit enough within-state variation in policy intensity to
support a within-state analysis. This variation is shown visually in Figure 5.
IV.
Research Design
A.
Estimation Challenges
Generally speaking, the effect of interest is that of immigrant legal status. A randomized
controlled trial (RCT) would be the ideal way to estimate this effect. In an RCT, legal status
would be randomly assigned among unauthorized individuals interested in obtaining it. With
randomization, individuals receiving legal status (the treatment group) would be on average the
same as those remaining unauthorized (the control group) in terms of all characteristics likely to
17
We start with 1990 SMSA definitions to define metropolitan areas. In California, we add San Luis Obispo, which
attained status as a metropolitan area shortly after the 1990 Census. We also lose one 1990 California SMSA – Yuba
City – because its constituent counties (Yuba County and Sutter County) are not identified in the LAPS data.
Similarly, in Texas we lose San Angelo, Sherman-Denison, and Victoria, and in Florida, we lose Fort Walton Beach
because their constituent counties are suppressed in the LAPS data. However, Table 3 shows the vast majority of
applicants in these three states are in identifiable metropolitan areas.
14
influence outcomes. The control group should thus accurately represent the counterfactual –
what would have happened for those receiving legal status had they remained unauthorized – and
the effects of amnesty would be identified by the simple difference in mean outcomes between
the treatment and control groups.
This is not how IRCA worked, however, and even if it were, the data needs to estimate
experimental treatment effects are quite stringent. Indeed, although the situation could be
different had such an RCT had been carried out, we know of no existing microdata that identify
both immigrant legal status and (both of) the outcomes of interest, and thus our own analysis will
rely on data aggregated to the area (by year) level.18 Nevertheless, this hypothetical experiment
provides a useful benchmark for understanding what we are able to estimate given the available
policy variation and data.
For the hypothetical RCT, the model of interest would be given by:
(1)
y ict   t   t Ai   ict ,
where yict represents an outcome of interest (e.g., EITC or FSP transfers) for working age person
i in area (state or metropolitan area) c in year t, Ai is an indicator for whether person i gains legal
status, and εict captures unobserved contributors to variation in outcomes. With the study sample
limited to unauthorized immigrants and legal status randomly assigned, it should be the case that
 t  0 for all years t < t*, where t* represents the year that legal status is achieved. That is, on
average, there should be no difference in outcomes between the treatments and controls before
legalization. After legalization, or for t ≥ t*,  t then captures the causal impacts of legalization.
In the case of IRCA, however, legal status was not randomly assigned. In this case, a
simple point-in-time differences-in-means, as in model 1, could provide biased estimates of the
18
Both the LPS and the NAWS contain some information on FSP participation, but not the EITC. We return to a
discussion of these data in Section VI.
15
impacts of legalization in the presence of self-selection into application. A difference-indifferences framework could be more sensible. Starting with model 1 and letting Dt  t  t * be
a post-legalization indicator, such a model is represented by:
(2)
y ict   0  1 Ai  Dt   0 Ai   1 Dt   ict .
The coefficient of interest is now 1 , which captures differential trends in outcomes between
individuals who receive legal status versus those who do not. Identification in model 2 thus no
longer relies on the assumption of identical expected outcomes in levels, as potential differences
in pre-legalization levels of outcomes are captured by the parameter  0 . Rather, estimates should
be unbiased to the extent that the trend in outcomes for the comparison group – represented by
the parameter 1 – is an accurate representation of what would have happened for the legalized
population absent the status change.
Our approach to estimating IRCA’s impacts, while essentially difference-in-differences,
must furthermore be carried out using area-level aggregate data due to the data limitations noted
above. By aggregating across the entire area working-age population, we are implicitly using all
other individuals in an area as a comparison group, not just those “at risk” for legalization.
Taking averages of model 2 at the area-by-year level (i.e., across all working age people), we
arrive at:
(3)
y ct   0  1 Ac  Dt   0 Ac   1 Dt   ct ,
where y ct represents an average outcome in area c in year t, and Ac represents the fraction of the
area’s population receiving legal status. The difference-in-differences coefficient in model 3,
estimated using aggregate data, is thus equivalent to that in model 2 when estimated on
individual-level data from the same (entire area working age) population. Hence, if legalization
16
increased the likelihood that an immigrant received food stamp transfers, 1 should be positive,
and areas with higher legalized population shares should have experienced larger increases from
before to after amnesty in food stamp transfers per capita.
It is important to note, however, implicitly using everyone else in an area as the
comparison group affects interpretation of our estimates in two important ways. First, our
approach could understate the true effect of legalization for the EITC. The implicit
counterfactual is one increasing EITC transfers, but these are not expansions the unauthorized
population would have been able to access absent legalization. Second, the legalized population
ages over time, but the implicit comparison group does not. A limitation inherent in relying on
aggregated data, this means that all else constant, the estimates will be larger than what we could
have achieved in panel microdata. We discuss how this affects interpretation in Section VII.
Further, it is important to note that estimates of 1 in model 3 do not distinguish between
the direct effects of legalization (on the legalized population) and its spillover effects on other
local populations. For example, if the true individual-level model is one where Ac has a direct
effect on outcomes regardless of an individual’s own legal status, the difference-in-differences
coefficient in model 3 will also pick up this spillover.19 While an interesting possibility, the
(limited) research base gives little reason to expect much impact of legalization beyond the
legalized immigrants themselves. We return to this point in our discussion of the estimates.
B.
Empirical Model
Our identification strategy thus relies on both the timing of IRCA, captured by Dt , and
variation across counties in the expected “intensity” of the law’s impacts, captured by Ac . In
19
Formally, suppose that the individual-level model were
yict   0  1 Ai  Dt   1 Ac  Dt   0 Ai   0 Ac  1Dt   ict .
Taking averages of this model at the area by year level, we arrive at model 3, but now 1  1   1 and  0   0   0 .
17
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. For Ac , we use the measure of policy intensity described above – the ratio of the
area’s working age applicants to its working-age population in 1986. Thus, the numerator of the
policy intensity measure is applications filed rather than the number of applicants for which
temporary legal status (or permanent residency) was ultimately granted, since approval could be
endogenous. As discussed in Section III, however, about 90% of applications filed were
ultimately approved, so we rescale our estimates accordingly when discussing magnitudes.
We also do not actually estimate model 3, but rather a less restricted version of it that
substitutes area and year fixed effects for the direct effects of Ac and D t :
(4)
y ct   Ac  Dt   c   t   ct .
The area fixed effects,  c , absorb all sources of potential bias, observed and unobserved, that are
fixed within an area over time, such as fixed aspects of demographics or network effects in
program participation. The year fixed effects,  t , account for shocks to outcomes shared by all
areas at a given point in time (e.g., general business cycle effects in addition to policy changes).
In our analysis of metropolitan areas, we allow for state-by-year fixed effects, so as to account
for state-specific shocks to local outcomes. Doing so, we are able to remove biases from statespecific policy changes and economic shocks.
The key identifying assumption in model 4 is that, aside from IRCA’s legalization
provisions, there is no other reason to believe that areas with higher applicant shares would have
experienced different trends in the outcomes of interest from before to after 1987. Estimates of
 would be biased, for example, if the EITC expansion under TRA86 would have had
18
systematically different impacts on EITC claims for areas with higher values of Ac even in the
absence of legalization; only the common effect of TRA86 is captured in year fixed effects.
Similarly, estimates of  could be biased if areas with higher values of Ac had other
characteristics making their outcomes more susceptible to later policy changes (such as later
EITC expansions) or to the changes in the wage structure that occurred over the period.
Given these concerns about identification in model 4, we expand our approach to rely
more on the sharp timing of the law, focusing attention on the event-study specification
(5)
y ct 
 D   A


1986
t
c
  c   t   ct ,
where y ct is still an outcome of interest in area c in year t, and  c and  t remain vectors of area
and year fixed effects, respectively. Now, however, D t is a dummy variable set to one if the
year of observation t is equal to specific year τ, zero otherwise (or Dt  1t    ). The   ’s are
thus the new parameters of interest, capturing the precise timing of differential changes in
outcomes for areas with higher values of Ac relative to the omitted year – 1986, the year in
which IRCA was passed but the application process had not yet begun. The   ’s otherwise span
the entire period of interest, including pre-legalization years. 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; if the estimates are identified, this should not be true. We are
also able to test for significant changes in EITC transfers across years during which the schedule
did not change (per Figure 1), but the legal status of IRCA amnesty applicants did (per Figure 2).
Model 5 is thus helpful in attempting to rule out bias from the second set of forces
described above – those from general trends where there is no strong reason to expect a change
precisely in 1987, and from later policy reforms. However, it does not confront the fact that the
19
EITC expansion under TRA86 would have taken effect at the same time. On the one hand, that
amnesty applicants under IRCA were heavily low-income themselves means that the EITC
expansion would have been more strongly felt in areas with higher applicant shares. We consider
this to be part of the reduced-form effect of legalization, as IRCA was knowingly passed two
weeks after TRA86. On the other hand, this EITC expansion – as well as those that followed –
also has the potential to bias our estimates even within the context of model 5. For example, if
applicant-denser areas also had higher shares of citizens and authorized immigrants eligible for
an expanded EITC, our estimates would pick up the impacts of EITC expansions on these other
populations. We will attempt to remove any such biases by allowing for differential trends in
outcomes by relevant county characteristics measured prior to IRCA, introduced next.20
C.
Preliminary Evidence on Identifying Assumptions
Did areas of higher policy intensity in fact have systematically different shares of the
native and authorized immigrant population likely to be eligible for – and likely to take up – an
expanded EITC? We explore this possibility by compiling and analyzing public-use microdata
on the income distribution from the 1980 Census and 1986 levels of EITC transfers to areas per
working age person, with the numerator reported by the Bureau of Economic Analysis (BEA)
and the denominator from the Census Bureau. The former are meant to proxy for program
eligibility, whereas the latter are meant to provide insight into both eligibility and take-up (e.g.,
stemming from program knowledge).21 In the Census calculations, we exclude (families with)
20
Throughout, we also control for proxies for local economic conditions – the state unemployment rate (in the statelevel analysis) and the local employment-to-population ratio (in the metro area-level analysis). Doing so comes at
some risk of “over-controlling,” as 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 food stamp transfers, which are
relatively sensitive to the business cycle (Bitler and Hoynes, 2016).
21
To explore the plausibility of the second idea, we compared the state-level per-capita EITC transfers reported by
BEA to the measure of EITC knowledge compiled from IRS tax records by Chetty, Friedman, and Saez (2013) – the
fraction of self-employed tax filers with children who report earnings at the first kink in the EITC schedule (“sharp
bunching”). For tax year 1996 (the first for which our data overlap), per-capita EITC transfers are positively
20
any adult non-citizen Central American immigrants, who were likely to have been unauthorized
immigrants affected by the IRCA amnesty. We cannot make this exclusion in the aggregate BEA
data, but unauthorized immigrants should have low to nil take-up of the EITC.
Table 4 summarizes these pre-IRCA characteristics for states (excluding California) and
for metropolitan areas (California, Florida, and Texas) and describes their relationship with
applicant share. All statistics are weighted by Census estimates of 1986 area-level working-age
population, and the regressions based on the metro area-level data include state fixed effects, to
mirror the estimates to follow. Echoing the figures earlier presented, less than 1 percent of the
working-age population in the country overall (excluding California) applied for legal status, and
the variation in applicant shares across states was not large (Panel A, column 1). In California,
Florida, and Texas, by contrast, the application rate among working-age people was 5.9 percent,
and the variation in it nearly 4 times greater (column 4).
The first numbers in Panel B, based on the 1980 Census, represent citizen/authorized
immigrant families in an area that both have children present and fall in one of four annual
earned income ranges: $0, $1 to $4,999, $5,000 to $9,999, and $10,000 to $14,999 (in 1979
dollars). The bottom category would have been ineligible for the EITC, whereas the remaining
categories correspond roughly to income ranges of the EITC before and after IRCA.22 The
remaining rows of the panel summarize findings for 1980 levels of educational attainment of
natives/authorized immigrants ages 25 to 64, the college equivalent share in particular being a
strong predictor of subsequent rising wage inequality (Beaudry, Doms, and Lewis, 2010).
associated with sharp bunching conditional on the 1980 income measures included in Table 4 Panel B; the partial
correlation between the two variables is 0.63 (excluding Washington DC and weighting by working-age population).
22
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 $48,909.
21
Policy intensity has a significant bivariate relationship only with the bottom income
category, but in opposite directions for the state and metro area analyses. States with higher
applicant shares have lower shares of native/authorized immigrant families with both children
and no earned income (column 2), while the reverse is true across metro areas (column 5). The
next two sets of figures are consistent with these findings, as states (metro areas) with higher
policy intensity had significantly higher (lower) shares of college equivalents. Metro areas with
higher applicant shares also had higher dropout shares. Findings from the transfer data, in Panel
C, are also broadly consistent with the implied relationship between policy intensity and human
capital. For example, metro areas with higher applicant shares have higher levels of transfers not
only under the EITC, but also under the FSP.
Since many of these variables are highly correlated, columns 3 and 6 present estimates
from a regression of applicant share on all of the variables in Panels B and C simultaneously; Fstatistics and associated p-values from tests of their joint significance are found at the bottom of
the column. For states, the coefficients are highly jointly statistically significant. For metro areas,
the coefficients are also jointly significant, though the p-value is somewhat lower, and fewer
individual coefficients are significant (at least at the 5% level).23 In both cases, holding constant
the other variables, 1986 EITC transfers are at least a marginally significant predictor of higher
applicant density, whereas the second income category ($1-$4,999) is a significant predictor of
lower applicant density. However, the partial correlations with education are different, consistent
with the bivariate analysis. Combined with higher precision, the relative weakness of these
relationships at the metro level makes us prefer the estimates using that variation. Still, we
control for interactions between all of these variables and the same year dummies with which Ac
is interacted in all regressions to follow.
23
This general pattern of findings also holds across metropolitan areas within each of the three states individually.
22
V.
Legal Status and the EITC
A.
State-level Analysis
While our preferred estimates come from the metro area-level analysis, an analysis using
state-level variation is a useful starting point. Not only do some of the potential biases work in
opposite directions, but EITC claims data 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 – annual 1% samples of individual federal tax returns. Relative to the published data, our
calculations from the ITM can be affected by income suppression. However, the ITM data span
more years in the pre-IRCA period than the published data and allow us to calculate statistics not
consistently published – namely, the ratio of tax-filers receiving actual EITC refunds (amounts in
excess of tax liability) to the working age population, as well as the refund amounts received per
working age person. We also use EITC transfers reported by the BEA.24
Figure 6 presents estimates of the  in model 5, excluding California, for the two
measures of state EITC amounts per working age person (in 2014 dollars, Panel A) and the
measures of state EITC refunds and claims per working age person (Panel B). The latter are each
expressed in percent terms, as is Ac, for the presentation purposes. All of the regressions include
state and year fixed effects, state unemployment rates, and interactions between year dummies
and each of the variables in Panels B and C of Table 4. The capped vertical lines around the
estimates represent their 95% confidence intervals; inference accounts for heteroscedasticity and
autocorrelation of the error terms within states over time, and regression estimates are weighted
by 1986 state population.
24
We normalize by working age population to allow for a potential micro-level interpretation of our estimates, as
described in Section IV.A. Unfortunately, we do not have annual state panel data on the number of potential taxfiling units (e.g., families), so we must rely on population.
23
Consider first the estimates in Panel A for EITC amounts. Regardless of data source,
EITC amounts per working age person increased by more between 1986 and most post-IRCA
years for states with higher applicant shares: nearly all of the estimates of the  for 1987 and
later are positive. Though the coefficients themselves tend to be somewhat imprecise – none are
statistically significant at the 5% level until 1990 – this pattern is suggestive of a positive impact
of legal status on EITC claims. Reinforcing this interpretation, all estimates of the  for 1985
and earlier are close to zero and fairly precisely estimated, implying that states with higher
applicant population shares were experiencing neither relatively strong upward trends already,
nor relative downward trends as might be expected if the estimates were biased, given the
erosion in the real EITC shown in Figure 1.
Even so, changes to the EITC schedule, such as those between 1986 and 1987, 1990 and
1991, and 1993 and 1994, will mechanically generate higher EITC transfers, and not just in the
population of interest. To bolster the case that changes in legal status are indeed the driving force
behind these estimates, it would thus be helpful (but not dispositive) to demonstrate that
significant changes in outcomes occurred outside of these “seams” in the EITC schedule.
Fortunately, IRCA applicants’ legalization experiences – approval of initial applications,
transition to permanent residency, etc. – had landmarks in other years, as suggested by Figure 2.
Table 5 presents estimates from a restricted version of the event-study model underlying
Figure 6 in an attempt to disentangle the roles played by legalization itself and changes to the
EITC schedule. In this restricted model, we pool the year dummies on the Ac (and control
variable) interactions into seven groups, effectively forcing the impacts of legal status to be the
same within each group. In particular, we divide the pre-IRCA period into two sub-periods –
1979 to 1982 and 1983 to 1986 – and the post-IRCA period into five sub-periods that correspond
24
roughly to the phases of IRCA’s application process – 1987 (essentially application only, 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),
and 1993 (when access to the FSP should have begun for LAW applicants), and 1994 to 1996
(when the EITC formula changed once again). The regressions continue to include vectors of
individual year and state fixed effects and state unemployment rates.
The first two columns correspond to the estimates in Panel A of Figure 6. Consistent with
earlier discussion, the interaction coefficient is first statistically significant in 1990, but only for
the BEA measure (column 1). That is, only in 1990 can we conclude with some confidence that
EITC transfers per working age person were higher than they were in the immediate pre-IRCA
period (1983 to 1986). Because there was essentially no change in the EITC formula between
1989 and 1990, this finding suggests that our estimates reflect the effect of legal status, a
conclusion reinforced by the fact that the coefficients for 1988-89 and 1990 are statistically
different (p=0.05). Likewise, there was a statistically significant increase in EITC transfers per
person between 1991-92 and 1993 (p=0.02), another non-expansion year, but not a statistically
significant increase in EITC amounts between 1986 and 1987, despite the change in EITC
schedule. A similar though less precise pattern of findings emerges from the ITM measures for
EITC refunds in columns 2 and 3. Together, these findings suggest that transitions to permanent
residency may have been important for receiving EITC benefits.
In terms of magnitudes, the 1990 interaction coefficient from the analysis the BEA data
(column 1) implies that state EITC transfers per working age person rose by on average $2.50
more between 1983-86 and 1990 for each additional percentage point increase in state applicant
25
share. Thus, in the absence of spillover effects on the remaining state population, the average
working-age applicant for legal status experienced a $250 greater increase in EITC transfers
between 1983-86 and 1990 than the average citizen/authorized immigrant. When we scale up this
estimate to reflect the 90% transition rate into temporary legal status from application, we arrive
at what we will call the effect of achieving legal status – $278 in EITC transfers as of 1990. By
1993, this effect rose to $497 ($4.48 x 100 / 0.9), and by 1994-96, it reached $750 ($6.75 x 100 /
0.9). By the same logic, the estimates imply that legal status increased the probability of claiming
the EITC by about 40 percentage points by the end of the sample period.
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 metro area-level
analysis. Her, we must rely on the BEA data on EITC transfers. For California, however, we
have also developed several proxies for low-income filing rates from state income tax statistics
published by the California Franchise Tax Board (CAFTB) 25 – the number of state returns
claiming the California Renter’s Credit (reported only through 1992) and the number of state
returns with adjusted gross income (AGI) in the bottom quartile of California’s 1979 distribution
of AGI. Shifts in the distribution of state returns toward low earners in the post-IRCA period
arguably reflect increases in tax-filing rates among the newly legalized, providing additional
evidence that the causal mechanism is legalization.
Figure 7 presents the full event-studies, while Table 6 presents the accompanying
restricted estimates; all of the regressions include metro area and state-by-year fixed effects,
25
The latter is made possible by the fact that the underlying data source – the Annual Report of the State of
California Franchise Tax Board (CAFTB) – reports the number of returns filed in narrow bins of AGI (e.g., $2,000
increments in the 1986 report).
26
metro area employment-to-population ratios, and interactions between year dummies and each of
the variables in Panels B and C Table 4.26 The findings for EITC transfers per working age
person are remarkably similar in magnitude to those yielded from the state analysis, particularly
by the end of the sample period. As shown in the column 1 of the table, the effect of legalization
on EITC transfers is $137 by 1990 ($1.24 x 100 / 0.9), $462 by 1993, and $814 by 1994-96. The
estimates are, moreover, much more precise than they were at the state level: here, we see a
significant impact by 1989 (Figure 7, Panel A), and year-specific increases in the interaction
coefficient are statistically significant not only in years when the EITC schedule did not change,
but also when it did. The first three columns of Table 7 show that similar patterns emerge across
each of the three states in the estimation sample.27 Unweighted estimates (column 4 of Table 7)
are also broadly similar, but smaller in magnitude.
We have thus found similar estimates both within and across states, as well as evidence at
both levels of geography of increases in EITC transfers in years where the EITC schedule was
not changed. The timing of observed changes in EITC transfers is, however, somewhat weak
supporting evidence of causation. On one hand, behavioral responses to changes in the EITC
schedule might take some time to play out (e.g., Eissa and Liebman, 1996). On the other, finding
significant increases in EITC transfers over adjacent years when the EITC schedule changed
could still reflect an impact of legalization: in the absence of gaining legal status, these
immigrants would not have been eligible for these benefits. The CAFTB tax participation
measures are thus quite useful. During the period of interest, ITINs did not exist; unauthorized
immigrants likely regularly had federal income tax withheld from their paychecks and W-2’s
filed by employers on their behalf, but did not file a federal income tax return out of fear or a
26
We also weight by 1986 (metro area) working-age population and cluster standard errors on metro area.
A weighted average of these estimates does not produce the figures in Table 6 column 1 because all of the control
variables are implicitly interacted with state dummies in Table 7.
27
27
lack of knowledge about how to do so. For many of these immigrants, claiming the EITC should
thus have been one and the same with filing an income tax return for the first time.
Figure 7 Panel B and the remaining columns of Table 6 show the estimates for the two
CAFTB measures earlier described. Again, 1990 appears to be a turning point in the effects of
legalization, again suggesting that transitions to permanent residency may have been critical. 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
big increase in its magnitude between 1989 and 1990. Moreover, the effects plateau around
1991, suggesting that the increased effects for EITC transfers over the remaining years were
more a function of changes to the EITC schedule than lagged responses to legal status.
Importantly, areas with higher applicant shares were not already experiencing significant upward
trends in either of these measures prior to IRCA, again supporting a causal interpretation.
VI.
Legal Status and the FSP
Recall that there is good reason to believe that legalization will have less of an impact on
FSP transfers than on EITC transfers, as some unauthorized immigrants were already exposed to
the FSP via their U.S. citizen children. And in fact, 3.7% of LAW applicants in the LPS reported
that someone in their family received food stamps at the time of application. FSP participation
among LAW applicants and their families as reported in the LPS also rose to 12.4% in 1992.
However, not all of this increase need reflect legalization, as food stamps caseloads went up
during the recession in the early 1990s. Per-capita FSP transfers rose nationally by nearly 50%
between 1987 and 1992, with nearly all of that increase happening over 1990 to 1992. The
sensitivity of food stamps to the business cycle makes it thus particularly important to have a
comparison group for this outcome.
28
For this, we turn to our research design. Here, we rely only on the metro area-level
variation, as the limitations of the state variation are likely to be more severe for this outcome.
The thick lines in Figure 8 Panel A represent the event-study coefficients for FSP transfers per
working age person (based on the same specification as we employed for EITC transfers), with
corresponding restricted event-study estimates shown in the first column of Table 8 Panel A. The
estimates are potentially surprising – negative and statistically significant through 1989, positive
starting in 1991-92, and positive and statistically significant only for 1993. The 1993 estimate
implies that legal status increased FSP transfers by on average about $300 per year. Assuming
that all received benefits for the full year, this would imply a 10 percentage point increase in the
caseloads of formally unauthorized immigrants – an effect of legal status similar to the 1987 to
1992 difference in raw FSP participation means in the LPS data. But by 1996 – well into a period
of economic expansion – the effect falls almost to zero and is not statistically significant. The
pattern of findings later in the period suggests that the legalized population is more sensitive to
the business cycle than other area residents.
But can we explain the negative impacts through 1990? Being limited to the short term,
these negative effects are potentially consistent with the restrictions on FSP access that IRCA
imposed on the applicants. Recall the individual-level interpretation of the coefficient of interest:
the effect of legal status is the differential trend between the average person receiving legal status
and the average citizen or authorized immigrant. With 1987 to 1990 being a period of modest
expansion in the FSP, a negative impact of the observed magnitude implies that FSP transfers
actually fell in absolute terms among the newly legalized through 1990. In fact, the coefficient
estimates suggest that many individuals exposed to food stamps at the time of application left the
program entirely.
29
However, these program access restrictions were only placed on LAW applicants; SAW
applicants were free to remain food stamp recipients. To test this explanation for the findings, we
therefore expanded model 5 to allow for differential trends by the both the percent of the
working age population applying for legal status as LAWs and the percent applying for legal
status as SAWs; if the explanation holds, all of the negative effects should be driven by LAWs.28
The estimates are depicted as the thinner solid (SAW) and dashed (LAW) lines in Figure 8 Panel
A and in columns 2 and 3 of Table 8. While not all of the coefficient estimates are statistically
significant, the findings suggest that the negative impacts through 1990 were indeed driven by
applicants under the LAW program, as expected. Moreover, the SAW-LAW coefficient
differences (Table 8 column 4 and Figure 8 Panel C) are statistically significant through 1990.
But the SAW-LAW gap narrowed thereafter and was completely closed by 1996.
While these findings are independently interesting, this exploration of differential effects
by legalization program provides for a useful test of the internal validity of our research design.
In the same spirit, we can test for SAW-LAW differences in the effects of legalization on EITC
transfers, where there are no legal reasons to expect a difference. And this is exactly what we
find. As shown in Panels B and D of Figure 8 and Panel B of Table 8, there appears to be no
difference in effects until 1991-92, and these differences favor SAWs, who we would predict to
have higher EITC eligibility rates given their lower prior incomes.
VII.
Discussion
Thus far, we have provided a variety of evidence that immigrant legal status increases the
probability of receiving income support through the tax system. But what is going in “inside the
black box” of the EITC estimates is not yet clear. To what extent are they purely mechanical – a
function the legalized population’s earnings and family structure? How much might they arise
28
The FSP participation rate for presumed SAW applicants in the NAWS (FY89) was 10.3%.
30
through behavioral labor supply responses to the EITC? And what about changes in earnings that
arise from other labor market responses to legalization? These need not be limited to the
legalized population; can we rule out that labor market spillovers to other area residents are a
contributing factor?
There is good reason to believe that, of all of these explanations, mechanical eligibility is
the most important. To explore this, we predicted EITC transfers for the newly legalized
population using the detailed survey information on LAW and SAW applicants from the LPS
and the NAWS, respectively.29 Taking the EITC schedules as given, we first assumed that their
earned income, presence of a spouse, and number of children remained unchanged from what
they reported in the survey. We estimated an average family earned income of $25,163 in 2014
dollars ($17,750 per working age person), and that 54%, 12%, and 33% had no kids, one kid, or
two or more kids, respectively, at baseline. We then made the predictions again but varying these
characteristics in reasonable ways to reflect aging over the ten-year period. Throughout, we use
the earnings distribution and family structure of citizens and non-citizen non-Central American
immigrants in the 1980 Census to predict changes in EITC amounts in the comparison group. We
do not subject the comparison group predictions to the same changes as we do the legalized
population, so as to mirror the specifications we estimated.
Table 9 shows these predictions for EITC transfers, for reference giving the legal status
effect from our preferred metro area-level specification in column 1. The baseline prediction in
column 2, which holds key EITC determinants fixed at their pre-authorization levels, suggests
that mechanical eligibility stabilizes in 1993 to explain a little over half the observed effects of
legal status for EITC transfers. However, mechanical eligibility effects at pre-authorization
characteristics suggest larger effects for 1990 and prior than we actually estimate, supporting
29
We will give more details behind these predictions in an appendix in a future draft of this paper.
31
earlier evidence that becoming a permanent resident is critical to EITC participation. For this
reason, we restrict attention in the subsequent columns to predictions for 1991-92 forward.
Doing so has the additional benefit of making more realistic the changes in family structure and
earnings that we assume for the applicant pool.
And not surprisingly, their characteristics do not remain fixed at their pre-IRCA levels in
the post-amnesty period. First, applicants have more children, which should have increased their
mechanical eligibility for the EITC. To see by how much, we re-predicted EITC transfers
imposing the fertility changes reported for LAWs in the LPS between 1987 and 1992 on all preauthorization respondents to the LPS and the NAWS. These predictions, shown in column 3,
suggest that these fertility changes alone can explain more than the remainder of the estimated
effects: adding children but holding other pre-authorization characteristics fixed, the predicted
estimates are slightly larger than what we find. Time in the U.S. or general experience effects
should however have a positive impact on earnings, pulling some of the legalized population out
of EITC eligibility over time. For example, allowing for across-the-board 5% earnings growth
(column 4) reduces the mechanical share of the estimates, though it does remain above 100%.
This exercise suggests that our estimates are indeed mostly mechanical. That being the
case, it is useful to show predicted EITC transfers for the legalized population only. Holding
relevant characteristics constant at baseline levels, these figures represent what would we would
have found had we been able to compare the population receiving amnesty to a population with
similar baseline characteristics that evolved similarly over time (in terms of family structure,
earnings, etc.), but remained unable to access the EITC. In principle, this is what we would have
gotten from the hypothetical experiment described above if there were no causal effects of
legalization on earnings or fertility. Given in the last column of Table 5, these effects stabilize
32
around 80% of what we actually estimate – for example, implying an average effect of legal
status on EITC transfers of about $600 by 1996.
As described, the share of our estimates that is not purely mechanical could reflect labor
supply responses to becoming newly eligible for the EITC, or other labor market responses not
just for the newly legalized, but also the rest of the population. Unfortunately, it is difficult to
distinguish between all of these remaining explanations with a de novo empirical analysis. For
instance, it would be nice to use our research design to look for direct evidence of wage or
employment changes for both the newly authorized population and other local residents. The
scope for doing so is limited, however.30 Fortunately, existing studies provide some guidance as
to how to interpret this residual.
First, the spillovers channel is likely to be weak. A key feature of relevant theoretical
work on amnesty is that unauthorized immigrants have a higher search cost (or worse outside
option) than authorized immigrants (or natives) in a wage bargaining model (Chassamboulli and
Peri, 2015). Thus, legal status may push up immigrants’ and so similarly skilled natives’ wages,
though at the expense of employment due to higher labor costs (and lower profits). Yet, the
available calibrations suggest the spillover to natives is miniscule.31 Further, the single study that
30
Annual data are necessary, and the leading potential data – the CPS MORGs – identify only 51 of the 66
metropolitan areas in our sample and only for 1986 to 1994. We would also be forced to use ethnic Mexican status
to distinguish between the populations of interest, since neither immigrant nor legal status is identified in the CPS
prior to 1994, and it would be necessary to add the 1980 Census to have sufficient pre-IRCA data. Estimates would
also be rendered imprecise by the small cell sizes in the CPS. When we press forward with this approach anyway,
we find no significant evidence of differential changes in the log wages or employment of less educated nonMexicans after IRCA.
31
Chassamboulli and Peri (2015)’s calibrations suggest that increasing the rate at which undocumented Mexican
workers are legalized would likely increase both native-born earnings and employment. This is not an ideal model of
IRCA, however, which was a one-time amnesty. Indeed their findings appear to partly – perhaps mainly – derive
from the greatly increased flows of immigrants that result from the higher legalization rate. Although not explicitly
about unauthorized immigration, comparisons in Chassamboulli and Palivos (2014) appear closer in spirit to IRCA:
they compare labor market impacts of an immigration-induced skill mix shock when immigrants have, alternatively,
higher or the same search costs as natives. Such a shift in theory raises the expected costs of hiring workers of their
skill level, and so induces lower job entry and leads to lower employment. Despite the fact that immigrants make up
33
has examined the broader labor market impacts of amnesty found that it had a negligible impact
on aggregate wages (Cobb-Clark, Shiells, and Lowell, 1995).32 There are also other channels by
which legalization might affect existing legal residents, but the evidence suggests that these
impacts are also likely to be small.33
Second, empirical research on amnesty’s impact on labor market outcomes of the newly
legalized immigrants themselves is potentially consistent with some behavioral labor supply
response to the EITC. Applying a difference-in-differences approach to data on LAWs from the
LPS and a comparison group of Hispanics from the NLSY, Amuedo-Dorantes, Bansak, and
Raphael (2007) and Amuedo-Dorantes and Bansak (2011) both find that the employment rates of
LAWs fell as a result of amnesty (between 1987 and 1992), and particularly so for women. For
these women, transitions out of the labor force rose. Though the authors do not explicitly
mention the EITC, they point out that these women might have been encouraged to leave paid
work by new eligibility for social assistance.34 These studies however do not present estimates
for women by marital status, which would allow us to discern the EITC’s dis-employment
incentives for secondary earners. They also focus on log hourly wages, not annual earnings.35
over 10 percent of the labor market in their simulations the effects derived from changes in search costs are
generally below 0.1% (comparing columns of their table 2).
32
The authors examined a very crude outcome, production worker wages (not broken out by nativity), which shows
a negligibly larger increase after IRCA in areas with more LAW applicants compared to areas with fewer.
33
For example, by increasing their time horizon, legal status may over time induce immigrants to acquire U.S. skills
(like English). This might make them more substitutable for natives, but the elasticity of substitution between
immigrants and natives is so large (e.g., Card, 2009; Ottaviano and Peri, 2012) that this change would also likely
have a small effect on natives’ wages. Immigrants legalized under IRCA reduced their remittances (AmuedoDorantes and Mazzolari, 2010), which could theoretically lead to positive effects through higher U.S. consumer
spending. However, estimates in Olney (2015) suggest the resulting wage increase would be less than one percent.
34
For men, unemployment rates rose, one interpretation being that new eligibility for unemployment insurance (UI)
allowed men to take more time finding jobs. In an auxiliary analysis, we did find evidence that legalization
increased UI transfers using our research design, though effects were limited to the recession period. An alternative
interpretation is therefore that the legalized population is relatively sensitive to the business cycle.
35
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 CobbClark, 2002) to up to 20% for women (Amuedo-Dorantes, Bansak, and Raphael, 2007). Selection corrected wage
estimates tend to be larger, suggesting positive selection among those who leave paid employment.
34
While we hope to explore these issues in the future in search of behavioral responses to the
EITC, the necessity to restricting attention to the recessionary year of 1992 is likely to limit what
we can learn from this exercise.
VIII. Conclusion
In this paper, we find that areas with higher applicant shares under IRCA’s
legalization program experienced relatively large increases in EITC transfers after IRCA,
both at the state level and across metropolitan areas within states. Most of these effects
appear to be mechanical, though there remains some scope for a labor supply response to
EITC’s incentives on the part of the newly legalized population. Effects on FSP transfers
are small by comparison and really only apparent during the early 1990s recession,
suggesting that the newly legalized population did not create long-term food stamps
recipients.
In terms of magnitudes, our estimates imply that achieving legal status raised the
annual EITC transfer to the average applicant by about $800 by 1996 – roughly 5% of preamnesty average annual earnings. This figure could be somewhat inflated over what would
achieved in microdata with a credible comparison group. Therefore, taking instead the
$600 figure we arrived at in Section VII as an alternative estimate, our findings imply that
IRCA’s legalization program increased EITC refunds by about $1.53 billion in 1996, or
about 4% of total federal spending on the EITC in that year.
In general, our findings suggest that legal reprieves for unauthorized parents today
could have large effects on their children by making them eligible for the EITC. Though
more speculative, the timing of the EITC responses we find is consistent with permanent
residency being a key determinant of EITC participation, suggesting executive deferred
35
actions are an imperfect substitute for a true legalization program. It also suggests that
estimating the long-run impact of IRCA on applicants’ children – who are now well into
adulthood – would be valuable. Although the data challenges in producing such estimates
are likely to be immense, they are likely to be a key factor in the broader net long-run
welfare and fiscal impacts of IRCA, as well as any future legalization program.
IX.
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39
40
Notes: TR
RA86=Tax Reform
m Act of 1986; OBR
RA90=Omnibus Bu
udget Reconciliatio
on Act of 1990; OB
BRA93=Omnibus Budget Reconciliattion
Act of 199
93.
41
Notes: Nu
umbers of initial ap
pplicants and tempo
orary admissions were
w calculated by the
t authors at the yyear and month leveel from the LAPS ddata,
excluding the 2% of applican
nts whose applicatiion date was not prrovided. Numbers of
o permanent resideents and naturalized citizens were
provided by
b Rytina (2002) att the fiscal year lev
vel. To calculate cu
umulative transition
ns to permanent ressidency and citizennship, we divide thee
Rytina fig
gures by the total nu
umber of applicantss as reported in thee LAPS data.
42
Notes: Ho
ourly wages of LAW
W applicants are drawn
d
from the LPS
S and pertain to thee time of application
on. Hourly wages oof SAW applicants are
drawn from
m the NAWS and correspond
c
to the most
m recent pay perriod during the 198
89 fiscal year; piecee rate workers are eexcluded. Hourly
wages from
m the CPS are calcculated from the Merged Outgoing Ro
otation Group files.. Hourly wages aree “Windsorized” at $2 and $200 ($20114).
43
Notes: Maap plots the percentt of a state’s 1986 working
w
age populaation that applied for
f legal status unde
der IRCA in the low
wer 48 states. The
number off working-age applicants for legal stattus was calculated by the authors from
m the LAPS data, aand the 1986 workiing age population was
estimated by the Census Burreau. Working age is defined as ages 15-64
1
for consisten
ncy across the two ddata sets.
44
45
Notes: Maaps plots the percen
nt of a metropolitan
n area’s 1986 work
king age population
n that applied for leegal status under IR
RCA. The number of
working-aage applicants for leegal status was calcculated by the auth
hors from the LAPS
S data, and the 19866 working age poppulation was estimaated
by the Cen
nsus Bureau. Work
king age is defined as ages 15-64 for consistency
c
across the two data sets.
46
Notes: Eaach graph shows co
oefficients (95% co
onfidence intervals)) on interactions beetween working-agge applicant populattion share and yearr
indicators. All specificationss include state fixed effects, year fixeed effects, interactio
ons between the yeear indicators and eeach of the pre-exissting
state charaacteristics listed in Panels B and C off Table 3, and state unemployment rates. Interactions witth the indicator forr 1986 are omitted tto
identify th
he model. The estim
mation sample inclludes all states exceept California. Speecifications are weiighted by 1986 working age populatioon,
and standaard errors are clusteered on state. The dotted
d
line represen
nts passage of IRCA
A in October 19866.
47
Notes: Eaach graph shows co
oefficients (95% co
onfidence intervals)) on interactions beetween working-agge applicant populattion share and yearr
indicators. All specificationss include metro areea fixed effects, staate by year fixed eff
ffects, interactions bbetween the year inndicators and each of
the pre-ex
xisting metro age ch
haracteristics listed
d in Panels B and C of Table 3, and metro
m
area employm
ment-to-population rratios. Interactions
with the in
ndicator for 1986 are
a omitted to identiify the model. Thee estimation samplee includes metropoolitan areas in Califfornia, Florida, andd
Texas. Sp
pecifications are weeighted by 1986 wo
orking age populatiion, and standard errors
e
are clustered on metro area. Thee dotted line repressents
passage off IRCA in October 1986.
48
Notes: In Panels
P
A and B, th
he thick lines B reprresent coefficients on interactions bettween working-agee applicant populatiion share and year
indicators, while the thin blu
ue lines represent co
oefficients on interractions between eaach of the working--age LAW and worrking-age SAW
applicant population
p
shares estimated
e
jointly. Panels
P
C and D plo
ot differences betweeen the SAW and L
LAW coefficients iin Panels A and B,
respectiveely, with 95% confiidence intervals. Sp
pecifications includ
de the same controlls that are listed in the notes to Figuree 7. The estimation
sample inccludes metropolitan
n areas in Californiia, Florida, and Tex
xas. Specificationss are weighted by 11986 working age ppopulation, and
standard errors
e
are clustered on metro area. Thee dotted line repressents passage of IRCA in October 19886.
Table 1. Demographics of IRCA Applicants for Legal Status: Universe Data
U.S.
Overall
(1)
States Other
than California
(2)
California, Florida,
and Texas
(3)
A. LAW and SAW Applicants Combined
Age (%):
< 15 Years Old
> 65 Years Old
Female (%):
Hispanic (%)
Mexican (%)
5.5
0.88
32.2
86.8
75.1
5.0
0.91
30.4
78.6
65.4
6.0
0.88
33.4
91.6
80.8
B. LAW Applicants Only
Age (%):
< 15 Years Old
> 65 Years Old
Female (%):
Hispanic (%):
Mexican (%):
9.4
1.19
42.8
86.8
70.2
8.7
1.21
40.1
79.0
61.0
10.0
1.19
43.9
92.4
77.1
C. SAW Applicants Only
Age (%):
< 15 Years Old
> 65 Years Old
Female (%):
Hispanic (%):
Mexican (%):
0.10
0.44
17.7
86.7
81.8
0.16
0.52
17.5
78.0
71.3
0.09
0.43
18.2
90.4
86.3
Notes: Calculations are based on the LAPS, which gives the universe of amnesty applications under both the
LAW and SAW programs. LAPS=Legalization Applications Processing System. LAW=Legally Authorized
Workers. SAW=Seasonal Agricultural Workers.
49
Table 2. Economic Characteristics of IRCA Applicants for Legal Status: Survey Data
U.S.
Overall
(1)
States Other
than California
(2)
California, Florida,
and Texas
(3)
A. Working-age LAW Applicants
(source: LPS)
Female (%):
Speaks Mostly Spanish (%)
Mexican (%)
Employed (%) *
Hours per Week|Employed *
Hourly wage ($2014), median *
Local Percentile, from CPS**
High school dropout (%)
Years of Schooling
Any Children (%)
41.9
85.4
69.3
80.2
41.5
11.08
22.31
72.3
7.95
57.1
40.1
78.9
59.0
81.1
41.8
10.55
22.90
69.4
8.18
50.8
43.1
90.4
76.3
79.6
41.2
10.89
21.96
75.9
7.62
59.7
B. Working-age SAW Applicants
(source: NAWS)
Female (%):
Mexican (%)
Paid Hourly (v. Piece Rate) (%)
Hours per Week|Paid Hourly †
Hourly wage ($2014), median †
Local Percentile, from CPS **
High school dropout (%)
Years of Schooling
Any Children (%)
17.5
94.0
75.4
46.2
8.40
10.6
92.9
5.2
36.9
17.2
90.7
71.5
45.1
7.92
8.1
92.2
5.5
30.9
n.a.
n.a.
n.a.
n.a.
n.a.
n.a.
n.a.
n.a.
n.a.
Notes: LPS=Legalized Population Survey. NAWS=National Agricultural Workers Survey (FY89).
Calculations from the LPS are based on the 6,118 respondents to the survey who were age 15-64 at the time of
application for amnesty; LPS only surveyed LAW applicants who were still in the U.S. and at least age 18 in
1989. Calculations from the NAWS are based on the 970 respondents aged 15-64 who had a pending
application for legalization (assumed under the SAW program) at the time of the FY89 survey. * At time of
application for legal status. ** Percentile of the wage in the same region in the 1987-88 Merged Outgoing
Rotation Group (MORG) files. † At the time of the survey (FY89).
50
Table 3. States with Highest Population Shares of Working-Age LAW and SAW Applicants
State
51
California
Texas
Arizona
Nevada
New Mexico
Illinois
Florida
Idaho
Oregon
New York
Washington
Applicants/
Pop Aged
15-64
% of All US
LAW & SAW
Applicants
8.21
3.78
3.62
2.82
2.67
1.99
1.94
1.57
1.51
1.39
1.20
53.1
14.6
2.75
0.67
0.89
5.25
5.07
0.34
0.92
5.90
1.26
% of States' Applicants:
In Identified
In Identified
LAW
County
Metro Area
56.2
66.6
31.8
52.1
54.0
73.9
30.4
18.6
13.3
67.0
22.7
98.1
82.2
92.0
83.7
54.1
98.3
88.7
1.7
64.0
99.1
57.9
Notes: Authors' calculations from the LAPS data and Census population estimates for 1986.
95.8
82.2
85.2
83.7
54.1
98.1
88.3
1.7
64.0
98.9
57.9
Metro Areas
Number ID'd Applicants/Pop
in State
Std. Dev.
23
24
3
2
2
11
19
1
4
11
9
4.29
2.43
4.48
0.07
3.46
1.33
1.94
0.00
1.06
1.21
2.48
Table 4. Pre-Existing Area Characteristics and their Relationship with Policy Intensity
State level (excluding CA)
Coef (se)
Coef
(se)
in
pred'n of
Mean
on A c (%) A c (%)
(sd)
(1)
(2)
(3)
Working-Age Applicants (A c , as %)
0.94
(1.13)
-
Metro area level (CA, FL, TX)
Coef (se)
Coef
(se)
in
pred'n of
Mean
on A c (%) A c (%)
(sd)
(4)
(5)
(6)
A. Policy Intensity
5.90
(4.33)
-
-
B. 1980 Characteristics: Citizens and Likely Authorized Immigrants
% of All Families:
w/ Kids and No Earned Income
w/ Kids and Earning $1-$4,999
w/ Kids and Earning $5,000-$9,999
w/ Kids and Earning $10,000-$14,999
% of Persons Ages 25-64:
College Equivalents
No HS Degree
3.25
(0.83)
3.06
(0.63)
4.28
(1.18)
5.06
(0.86)
-0.164*
(0.096)
-0.043
(0.090)
0.075
(0.154)
-0.040
(0.132)
-0.462
(0.283)
-1.374***
(0.410)
-0.053
(0.429)
-0.067
(0.285)
2.75
(0.94)
2.86
(0.85)
4.04
(1.43)
4.55
(1.05)
0.100***
-0.347
(0.034)
(1.172)
0.030
-3.592***
(0.035)
(1.312)
0.069
-0.202
(0.051)
(0.868)
0.040
0.760
(0.039)
(0.822)
27.2
(4.2)
27.4
(6.2)
1.654***
(0.457)
-0.563
(0.842)
0.137**
(0.054)
0.032
(0.056)
34.0
(6.2)
22.4
(6.4)
-0.399**
(0.187)
0.611***
(0.141)
0.143
(0.163)
0.378*
(0.200)
C. 1986 Levels of Program Participation: Full Population
Amts ($2014) per working age person:
EITC Transfers
Food Stamps Transfers
F-stat on joint significance
P-value on joint significance
# of States or Metro Areas
Additional controls:
State Fixed Effects
18.8
(6.8)
151.9
(56.5)
1.716**
(0.789)
0.959
(7.094)
0.167***
(0.050)
0.002
(0.002)
23.0
(7.6)
102.0
(77.2)
0.984***
(0.246)
5.957**
(2.701)
0.458*
(0.251)
-0.011
(0.021)
-
-
7.39
0.000
-
-
3.27
0.004
49
49
49
66
66
66
X
X
Notes: Authors' calculations from the LAPS (Panel A), 1980 Census 5% State Sample (Panel B), and the BEA's Local
Area Personal Current Transfer Receipts (Panel C). Regressions in columns 2, 3, 5, and 6 are weighted by 1986 area
population (Census estimates). Dollar figures in the 1980 Census are nominal (1979). Standard errors are clustered on
state (columns 2 and 3) and metropolitan area (columns 5 and 6), and estimates are weighted by 1986 working-age
population. ***, **, and * represent statistical significance at the 1%, 5%, and 10% levels, respectively.
52
Table 5. Impacts of IRCA Legalization on EITC Transfers and Claims: State-Level Variation
Dependent variable:
# Returns per working age person
Amt. per working age person ($2014)
(as %)
EITC Transfers
EITC Refunds
EITC Refund
EITC Claim
Source:
BEA
IRS SOI ITM
IRS SOI ITM
IRS SOI
(1)
(2)
(3)
(4)
Mean, 1986
18.4
A. Pre-IRCA Mean of Dependent Variable
19.4
2.82
3.96
B. Restricted Event-Study Model: Full Controls
Pre-IRCA
Ac x Years 1979-82
Post-IRCA
Ac x Year 1987
Ac x Years 1988-89
Ac x Year 1990
Ac x Years 1991-92
Ac x Year 1993
Ac x Years 1994-96
N (state x year)
P-values on F-tests:
1988-89 = 1990
1990 = 1991-92
1991-92 = 1993
1993=1994-96
0.364
(0.237)
-0.290
(0.803)
0.041
(0.079)
-
0.060
(0.501)
-0.169
(1.215)
2.503***
(0.689)
3.412**
(1.315)
4.482***
(1.644)
6.746**
(2.931)
-0.301
(0.581)
0.637
(1.202)
4.404
(2.908)
5.368**
(2.303)
7.771**
(3.661)
12.031**
(5.779)
0.029
(0.057)
0.040
(0.123)
0.285
(0.176)
0.353**
(0.152)
0.564**
(0.213)
0.399
(0.251)
0.060
(0.047)
0.246***
(0.071)
0.290***
(0.080)
0.313***
(0.097)
0.366***
(0.108)
0.380**
(0.144)
882
881
881
686
0.05
0.21
0.02
0.30
0.13
0.67
0.42
0.28
0.11
0.59
0.21
0.22
0.15
0.51
0.04
0.87
Notes: Estimation sample excludes California, which is an outlier in terms of state policy intensity (Figure 3). All
regressions include year fixed effects, state fixed effects, state unemployment rates, and interactions between year
group dummies (1979-82, 1987, 1988-89, 1990, 1991-92, 1993, and 1994-96) and each of the pre-existing state
characteristics listed in Panels B and C of Table 3. Standard errors are clustered on state, and regressions are
weighted by 1986 working-age population. ***, **, and * represent statistical significance at the 1%, 5%, and
10% levels, respectively.
53
Table 6. Impacts of IRCA Legalization on EITC Transfers and Low-Income Tax-Filing:
Metro Area-Level Variation within States (California, Florida, Texas)
Dependent variable:
Amt. per working
age person
($2014)
Source:
Mean, 1986
EITC Transfers
BEA
(1)
# Returns per working age person
(as %; California Only)
Bottom Quartile
of 1979 CA
Renters Credit
Distribution
CAFTB
CAFTB
(2)
(3)
A. Pre-IRCA Mean of Dependent Variable
23.01
23.22
14.33
B. Restricted Event-Study Model: Full Controls
Pre-IRCA
Ac x Years 1979-82
Post-IRCA
Ac x Year 1987
Ac x Years 1988-89
Ac x Year 1990
Ac x Years 1991-92
Ac x Year 1993
Ac x Years 1994-96
N (metro areas x year)
P-values on F-tests:
1988-89 = 1990
1990 = 1991-92
1991-92 = 1993
1993=1994-96
0.063
(0.126)
-0.059
(0.047)
-0.067
(0.046)
0.093
(0.100)
0.436**
(0.178)
1.237***
(0.129)
2.820***
(0.258)
4.157***
(0.411)
7.327***
(0.804)
0.027*
(0.014)
0.114***
(0.025)
0.278***
(0.046)
0.507***
(0.083)
-
-0.024
(0.025)
0.052
(0.036)
0.181***
(0.055)
0.311***
(0.049)
0.308***
(0.045)
0.270***
(0.048)
1,188
322
414
0.00
0.00
0.00
0.09
0.00
0.00
0.00
0.00
0.00
0.00
0.97
0.18
-
Notes: All regressions include state-by-year fixed effects, metropolitan area fixed effects,
metropolitan area employment-to-population ratio, and interactions between year group
dummies (1979-82, 1987, 1988-89, 1990, 1991-92, 1993, and 1994-96) and each of the preexisting state characteristics listed in Panels B and C of Table 3. Standard errors are
clustered on metro area, and regressions are weighted by 1986 working-age population.
***, **, and * represent statistical significance at the 1%, 5%, and 10% levels, respectively.
54
Table 7. Impacts of IRCA Legalization on the EITC by State and Unweighted:
Metro Area-Level Variation within States (California, Florida, Texas)
State:
Mean, 1986
Dependent variable: EITC Transfers per Working Age Person ($2014)
California
Florida
Texas
All: unweighted
(1)
(2)
(3)
(4)
23.46
A. Pre-IRCA Mean of Dependent Variable
21.54
23.22
25.16
B. Restricted Event-Study: Full Controls
Pre-IRCA
Ac x Years 1979-82
Post-IRCA
Ac x Year 1987
Ac x Years 1988-89
Ac x Year 1990
Ac x Years 1991-92
Ac x Year 1993
Ac x Years 1994-96
N (metro area x year)
P-values on F-tests:
1988-89 = 1990
1990 = 1991-92
1991-92 = 1993
1993=1994-96
-0.101
(0.188)
-0.273
(0.478)
0.296
(0.401)
0.323**
(0.141)
0.153***
(0.026)
0.477***
(0.071)
1.129***
(0.143)
2.863***
(0.305)
4.249***
(0.429)
7.425***
(0.705)
0.520***
(0.113)
0.781***
(0.203)
1.657***
(0.421)
2.654**
(1.138)
4.413**
(1.838)
7.853*
(3.845)
0.527***
(0.126)
1.466***
(0.187)
1.791***
(0.206)
3.715***
(0.446)
5.779***
(0.846)
12.142***
(2.030)
-0.334**
(0.153)
-0.297
(0.299)
0.842***
(0.174)
2.125***
(0.382)
2.959***
(0.567)
4.406***
(1.025)
414
342
432
1,188
0.00
0.00
0.00
0.00
0.02
0.22
0.03
0.11
0.00
0.00
0.00
0.00
0.00
0.00
0.00
0.01
Notes: All regressions include state-by-year fixed effects, metropolitan area fixed effects, metropolitan area
employment-to-population ratio, and interactions between year group dummies (1979-82, 1987, 1988-89, 1990,
1991-92, 1993, and 1994-96) and each of the pre-existing state characteristics listed in Panels B and C of Table 3.
Standard errors are clustered on metro area, and regressions are weighted by 1986 working-age population. ***,
**, and * represent statistical significance at the 1%, 5%, and 10% levels, respectively.
55
Table 8. Impacts of IRCA Legalization by IRCA Program:
Metro Area-Level Variation within States (California, Florida, Texas)
Ac =
Dependent variable: Transfers per Working Age Person ($2014)
By Program:
Overall
Difference:
LAW + SAW
SAW - LAW
LAW
SAW
(1)
(2)
(3)
(4)
A. Food Stamp Program
Pre-IRCA
Ac x Years 1979-82
Post-IRCA
Ac x Year 1987
Ac x Years 1988-89
Ac x Year 1990
Ac x Years 1991-92
Ac x Year 1993
Ac x Years 1994-96
N (metro area x year)
-1.014
(0.891)
-1.302
(0.949)
-0.417
(1.318)
0.884
(1.747)
-1.363***
(0.461)
-1.942**
(0.785)
-1.376
(1.089)
0.707
(1.105)
2.720**
(1.160)
0.979
(1.295)
-2.121
(1.101)
-2.993
(1.081)
-2.829**
(0.548)
-0.031
(0.334)
2.145
(0.759)
0.567
(0.340)
0.025
(0.577)
-0.002
(0.951)
1.377
(0.732)
2.194*
(0.570)
3.869
(1.507)
1.836
(1.659)
2.146*
(0.543)
2.992***
(0.130)
4.206***
(0.409)
2.225
(0.875)
1.724
(0.749)
1.269
(1.891)
1,188
1,152
1,152
1,152
B. EITC
Pre-IRCA
Ac x Years 1979-82
Post-IRCA
Ac x Year 1987
Ac x Years 1988-89
Ac x Year 1990
Ac x Years 1991-92
Ac x Year 1993
Ac x Years 1994-96
N (metro area x year)
0.063
(0.126)
-0.096
(0.289)
0.455
(0.197)
0.551
(0.484)
0.093
(0.100)
0.436**
(0.178)
1.237***
(0.129)
2.820***
(0.258)
4.157***
(0.411)
7.327***
(0.804)
0.112
(0.128)
0.490**
(0.075)
1.142***
(0.082)
2.528***
(0.089)
3.698***
(0.132)
6.650***
(0.278)
0.067
(0.177)
0.364
(0.216)
1.438***
(0.037)
3.375***
(0.190)
5.022***
(0.194)
8.672***
(0.506)
-0.045
(0.305)
-0.126
(0.289)
0.296
(0.116)
0.847*
(0.212)
1.324***
(0.131)
2.022**
(0.369)
1,188
1,152
1,152
1,152
Notes: All regressions include state-by-year fixed effects, metropolitan area fixed effects, metropolitan area
employment-to-population ratio, and interactions between year group dummies (1979-82, 1987, 1988-89, 1990,
1991-92, 1993, and 1994-96) and each of the pre-existing state characteristics listed in Panels B and C of Table 3.
In columns 2-4, the interaction coefficients for LAW and SAW applicants are estimated by the same regression.
Standard errors are clustered on metro area, and regressions are weighted by 1986 working-age population. ***,
**, and * represent statistical significance at the 1%, 5%, and 10% levels, respectively.
56
Table 9. Predictions of Mechanical Eligibility for EITC Transfers
Effects implied by
Table 6, column 1
(1)
Post-IRCA
Year 1987
Predicted mechanical effects:
Pre-authorization
Adding kids + 5%
characteristics
earnings increase
Adding kids
(2)
(3)
(4)
Simulated
experiment
(5)
57
10
130
-
-
-
Years 1988-89
48
177
-
-
-
Year 1990
137
173
-
-
-
Years 1991-92
313
222
468
442
279
Year 1993
462
247
518
488
312
Years 1994-96
814
448
902
850
593
Notes: Implied effects (column 1) multiply the coefficients in Table 6, column 1 by 100 and divide by 0.9 to reflect the transition rate
from application to temporary status. Columns 2-4 are computed from applying year-specific EITC program rules -- which depend on
family earned income and number of children -- to a representative sample of the legalized population at the time of IRCA application,
and subtracts off the change in predicted EITC awards per working age population since 1986 among citizens and non-citizen nonCentral Americans in the 1980 Census. The legalization sample comes from combining the LPS, which represents LAW applicants,
and the fiscal year 1989 NAWS respondents with a pending application for legal status, which represent SAW applicants, weighted to
reflect their proportions in applications in the LAPS (1.78/3.04 for LAW and 1.26/3.04 for SAW). In both surveys, family income is
imputed based on individual earnings (details in appendix). Column 2 reports the average expected EITC award based on these initial
demographics in this sample. Column 3 computes EITC awards after applying observed changes in number of children to 1992 by
iniitial, gender, martial status, and number of children in the LPS to the combined legalization sample. Column 4 adds children in the
same way as column 3 but also increases family incomes uniformly by the factor 1.05. Column 5 gives predicted EITC transfers for the
legalized population only (i.e., not using a comparison group). If effects were purely mechanical, these would be the figures achieved
from an experiment if there were no causal effects of legalization on earnings or fertility.