THE “SORT OF” AMERICANS: AMERICAN CHILDREN
OF UNDOCUMENTED MIGRANTS
Anne Le Brun
Harvard University
January 2016
Abstract
Does a migrant parent’s documentation status affect American offspring’s educational
outcomes? I exploit the exogenous discontinuity in likelihood of legal status generated by
the 1986 Immigration Reform and Control Act (IRCA), which stated that immigrants
proving continuous residence in the U.S. since 1/1/82 could legalize. In reduced form results using 2000 census data, I find American 14 year-olds whose parents were likely IRCA-eligible immigrants are 8.6 percentage points more likely to have reached high
school than peers with likely ineligible immigrant parents. One key channel through
which parental status seems to affect children’s education is through father’s labor market outcomes.
Anne Le Brun
Department of Economics
Harvard University
1805 Cambridge Street
Cambridge, MA 02138
[email protected]
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I. Introduction
Does a migrant parent’s undocumented status affect U.S.-born offspring? This question
matters for the over four million American children of undocumented migrants.1 It also matters
for policymakers interested in immigration reform. At the end of 2014, President Obama announced a plan for Deferred Action for Parents of Americans (DAPA) that would allow undocumented immigrants to temporarily remain and work in the United States. Could this small step
towards legalization benefit American-born children?2
Opponents of a path to legalization often depict it as unfair amnesty and raise concerns
about moral hazard. Proponents of legalization point to the impracticality of deporting 11 million
undocumented migrants. They emphasize the potential benefits to the U.S. labor market, and to
migrants themselves. When proponents of legalization talk about the American families of migrants, it is usually to underscore the inhumanity of separating U.S.-born children from their parents, and to emphasize the deep roots that some migrants have in their host community. For instance, in justifying DAPA, president Obama alluded to the “cruelty of ripping children from
their parents’ arms” (Obama 2014). Seldom is the argument for legalization made in terms of the
potential economic benefits to the four million American children who are offspring of undocumented migrants. A comprehensive evaluation of immigration reform, and of the value of executive actions such as those of November 2014, should attempt to account for the economic benefits to Americans of their parents’ legalization.
Lack of parental documentation can harm offspring in many ways. The government can
deport undocumented migrants, depriving children of their caretakers. Even absent removal, its
possibility can keep undocumented parents from enrolling their American children in programs
like SNAP or Medicaid (Watson 2014). Fear of parental deportation could generate harmful anxiety in parents and children alike (Satinsky et al. 2013). A growing literature shows that undocumented and/or non-naturalized migrants earn lower wages than their documented and/or natu!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
1
The Pew Hispanic Center (2011) estimates that in 2010 there were north of 4.5 million American children of undocumented migrants in the U.S., up from 2.1 million just 10 years ago. Given this growth rate and higher fertility
rates among Latinos than the broader U.S. population, it seems likely that by now, the figure is closer to 6 million or
higher.
2
DAPA is a far cry from permanent legalization, thus, my estimates of the impact of parental legalization are likely
greater than any benefits children could perceive from temporary relief from parental deportation.
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ralized counterparts (Pan 2012; Amuedo-Dorantes and Bansak 2011; Kossoudji and Cobb-Clark
2002) and research suggests they suffer worse working conditions, with lower bargaining power
and less job autonomy (Yoshikawa 2011; Gentsch and Massey 2011; Kandilov and Kandilov
2010; Bratsberg et al. 2002). These obstacles to improving their socio-economic status can impair parents’ ability to care and provide for their children. Finally, lack of documentation might
inhibit parents’ opportunities and commitment to acquire U.S.-specific skills, without which they
are less equipped to contribute to their children’s American education. It seems plausible that
some combination of the above channels might have a lasting negative impact on the American
children of undocumented migrants.
Establishing the causal relationship between parental legal status and children’s educational and labor market outcomes is difficult. First, few datasets link undocumented parents with
their American children, and simultaneously provide information on the children’s long-term
outcomes. Second, undocumented migrants might differ systematically from their documented
and/or naturalized counterparts in unobservable ways that could correlate with their children’s
own characteristics and outcomes. To my knowledge, only one paper to date explores the causal
relationship between parental undocumented status and American offspring’s educational or labor market outcomes. Using a sample of 312 children drawn from the Los Angeles Family and
Neighborhood Survey (LAFANS), Pan (2011) finds that American and foreign-born children of
undocumented migrants score lower on math and English achievement tests than American and
migrant children of documented migrants.
I add to this slim literature with an identification strategy that, like Pan (2011), relies on
the Immigration Reform and Control Act (IRCA) signed in 1986. This law allowed migrants
who could prove continuous U.S. presence since January 1, 1982 to apply for temporary legal
resident status (eventually candidates could become legal permanent residents, and finally naturalized Americans). The IRCA introduces a discontinuity in the likelihood of legal status: an undocumented migrant who arrived in the U.S. in 1981 is much more likely to have achieved legal
status by 2000 than an identical migrant who arrived in 1982. Using this regression discontinuity
design and data from the 2000 Census, I provide evidence that in California, parental arrival prior to January 1982 raises educational attainment among 14 year-olds – in particular, among the
offspring of likely initially undocumented parents, children whose parents were IRCA-eligible
are 8.6 percentage points more likely to have reached high school by age 14 than the offspring of
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ineligible parents. I focus on 14 year-olds because they were born the year that the IRCA was
signed. Hence, they were born before immigrants could differentially change their fertility behavior in response to the IRCA. At the same time, they were born the year their parents found
out about their IRCA eligibility.
Relative to Pan (2011), I use a dataset that is three times bigger, with greater geographic
coverage. Another strength of this study is that I address in more depth a key identification concern, namely the fact that the IRCA-eligibility cut-off coincides with the 1981-82 recession in
the United States. This coincidence raises the following concerns: if children of post-1981 immigrants have worse educational outcomes in 2000, this could be because recession-time immigrants have worse labor market trajectories, or because immigrants self-select differently in recession years. I provide evidence against these possible interpretations with alternative regression specifications, and with a falsification test that uses data from 1970s and 1990s recessions in
the United States. I also provide more direct evidence on some of the potential channels through
which legal status may affect children’s outcomes, and my analyses focuses specifically on the
impact of parental status on American children, whereas Pan (2011) includes undocumented
immigrant children in her analysis.
The paper proceeds as follows. The second section provides background information on
the IRCA, on the potential harms to American children from having undocumented parents and
the empirical evidence so far. The third section outlines my empirical framework. The fourth and
fifth sections present the data and results. In the sixth section, I address challenges to my identification strategy. In particular, I provide evidence that the results are not driven by differential
recession-year migrant selection or migrant labor market trajectory, nor are they likely to be
driven by fraud or selective return migration. I close the paper with an outline of next steps.
II. Background and Evidence So Far
This section sets the context for my analysis. I first provide details on the IRCA, then explain how parental legal status might matter, and finally briefly review existing evidence.
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IRCA Background3
Unexpectedly signed on November 6, 1986, the IRCA contained three main provisions.4
First, it provided a path to naturalization for eligible undocumented immigrants. Second, it instituted sanctions against employers who knowingly hired undocumented workers.5 Finally, new
resources were supposed to boost border enforcement. This paper focuses on the first of the three
provisions.
Two kinds of undocumented immigrants qualified for the IRCA’s path to naturalization:
(a) immigrants continuously present in the U.S. as of January 1st, 1982 (section 245A applicants)
and (b) special agricultural workers (SAW) who could demonstrate having completed at least 90
days of agricultural work within the twelve months before May 1986, or 90 days of agricultural
work in each of the three years 1984 through 1986.6 A little more than half of the three million
IRCA applicants were section 245A applicants and the rest were SAW applicants. I focus on
non-agricultural workers because there is significant evidence of fraud in the SAW provision of
the IRCA (I discuss IRCA fraud in greater detail in section VI below).
The path from IRCA eligibility to naturalization took several years: while it reviewed applications, the Immigration and Naturalization Service (INS)7 granted applicants a temporary
work authorization card with photo identification.8 The INS then granted approved applicants
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3
Unless otherwise specified, the information on IRCA in this section is drawn from U.S. Department of Justice
(1992).
4
Orrenius and Zavodny (2001) write: “Immigration reform, including amnesty for undocumented immigrants, was
proposed in Congress in 1981, and the Senate passed various bills in 1982, 1983 and 1985. The House of Representatives, however was less willing to back immigration reform, primarily because of concerns about the amnesty proposal. On September 26, 1986, the House voted not to take up the immigration reform bill but then, in a ‘stunning
reversal,’ passed the measure on October 9.” (p.5)
5
The employer sanctions do not seem to have had much bite - employers could claim they had not knowingly hired
an undocumented migrant as long as an immigrant showed “documentation” which could be a fake social security
number, for instance. Different sources hint at the lack of enforcement of these provisions (see, for example,
Brownell, 2005)
6
Those who could prove having completed 90 days of seasonal agricultural work in each of the three years 19841986 were immediately granted permanent legal status, while those who could only prove 90 days of seasonal agricultural work within the last year were first granted temporary legal status.
7
The INS was swallowed in 2003 by the newly created Department of Homeland Security, with its functions divided between Immigration Control and Enforcement (ICE), USCIS (US Citizenship and immigration Services) and
CBP (Customs and Border Protection).
8
The application window for Section 245A applicants was 5/5/87 to 5/4/88. That for SAW applicants was 6/1/87 to
11/30/88.
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temporary legal status. The vast majority of IRCA applications were approved (INS 1992).9 Over
90% of the IRCA’s roughly 2.7 million legalizations took place between 1988 and 1991 (Baker
2010; U.S. Department of Justice 2000).10 Nineteen months thereafter, candidates had a one-year
window to apply for legal permanent resident (LPR) status. Five years later, LPRs could apply
for citizenship (INS 1992). By 2009, roughly 1.1 million IRCA applicants had naturalized (Baker
2010), with the bulk of those naturalizations appearing to have taken place between 1995 and
2001 (Rytina 2002).11
Potential Channels
Among children of undocumented migrants below age six, 91% are American citizens
(Yoshikawa 2011, p. 14). Relative to other U.S. citizens several factors may disadvantage these
offspring of the undocumented.
First, undocumented migrants have worse jobs. Bratsberg et al. (2002) use panel data
with individual fixed effects to show that naturalization leads to a jump in migrant earnings and
an acceleration in the growth rate of wages. The authors argue that naturalization increases access to white-collar, unionized jobs. Several papers exploit the IRCA to estimate the impact of
legal status on wages (Pan, 2012; Amuedo-Dorantes et al. 2007; Kossoudji and Cobb Clark
2002), finding an average boost to earnings in the range of 6-15%. Not only do the jobs of the
undocumented pay lower wages, they also offer fewer benefits. Kandilov and Kandilov (2010),
use propensity score matching techniques to show that documented agricultural workers in the
National Agricultural Workers’ Survey (NAWS) are much more likely than their undocumented
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9
It is unclear whether denied applicants mostly remained in the U.S. or returned to their home country. Chishti and
Kamasaki (2014) point out that many families were “mixed status” such that some family members arrived early
enough to qualify and some did not. Many of those who arrived too late would presumably be among the rejected
applicants. Chishti and Kamasaki state that these individuals were granted an “indefinite voluntary departure”, effectively a semi-legal status that was later convertible to legal status through the 1990 “family unity program.”
10
Some 1.5 million section 245a applicants were legalized during that period, and about 966 thousand SAW applicants were (U.S. Department of Justice, 2000).
11!The fact that such a large fraction of IRCA-legalized immigrants chose to remain legalized permanent residents,
rather than apply for citizenship, raises questions about what treatment is the interesting one? Are we more interested in finding out what the impact of legalization is, or the impact of naturalization? I would argue that in the context
of the IRCA, this distinction matters less because pre-1996 migrants (i.e. immigrants who arrived prior to the 1996
Illegal Immigration Reform and Immigrant Responsibility Act), if legalized, were eligible for many of the same
benefits as citizens. However, it is true that as potential citizenship applicants, LPR immigrants might have wanted
to avoid using welfare services so as not to be deemed a “charge” to the state, an accusation that some immigrants
believe could negatively affect their odds of naturalization.!
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counterparts to have employer-sponsored health insurance. In his study of 400 mothers recruited
in public New York City hospitals during childbirth, Yoshikawa (2011) finds that those who are
probably undocumented are less likely to get overtime pay, sick days and vacation days.12 They
have less job autonomy and perform more repetitive and physically demanding tasks than likely
documented migrants and African Americans from similar socio-economic backgrounds. Yoshikawa argues that these poor working conditions can negatively affect migrant offspring’s education and behavior. Indeed, existing research suggests parental socio-economic status matters for
children’s educational/labor market outcomes (see for example Dahl and Lochner 2012 for educational outcomes, and Björklund, Lindhal and Plug 2006 for labor market outcomes).
Second, undocumented migrants are ineligible for many federal programs, such as the
EITC, WIA, Medicaid, SSI, subsidized housing, etc. Likewise, undocumented migrants can find
it harder to present the required documentation to sit a GED exam. These ineligibilities and obstacles can translate into lower socio-economic status for undocumented parents vis à vis their
documented or native peers.
Third, undocumented immigrants may have fewer incentives and opportunities to acquire
U.S.-specific human capital. Lack of fluency in English will impair parents’ ability to help their
children with homework or college applications, and will inhibit their participation in school life.
Cortes (2004) finds that refugees, who likely feel stronger ties to the U.S. than economic migrants, are more fluent in English. Pan (2012) finds that migrant legalization leads to better English skills.
Fourth, undocumented parents can be deported. In the last two years, the U.S. has removed upwards of 80,000 parents of American children per year, up from 20,000 per year previously (Satinsky et al. 2013). These deportations deprive children of one or both of their primary
financial and emotional caretakers. The impacts can be many and unpredictable, temporarily or
permanently derailing a child’s life:
“I had no idea what was happening” says Janna Hakim of the morning in
2010 when a loud knocking at her Brooklyn apartment door jolted her
awake (…) Janna, then 16, and her siblings were all born (in the U.S.).
None knew that their mother was in the U.S. illegally – or that a deportation order from years earlier meant she could be whisked away by ICE
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12
The Yoshikawa study did not directly question mothers’ legal status, but deduced likely legal status through a
series of questions about the use of resources that typically require documentation.
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agents… “It was horrible, horrible (…)” (Her) 13-year-old brother began
wetting his bed, she said, and her 15-year-old brother began hanging out
with gangs and experimenting with drugs. Her father (…) grew despondent.”
Fox News Latino (2012)
Beyond the reality of deportation, the constant fear of deportation can be damaging to
parents and children alike:
“Anabel Barron (…) was facing deportation after being stopped for
speeding and driving without a license. “I am afraid of being deported,”
she said. “But for my (American) children it’s worse. They don’t sleep the
same. They don’t eat. They don’t want to go to school because they are
afraid I am not going to be there when they get home.”
Thompson and Cohen (2014)
Parents’ access only to poor jobs, ineligibility for federal programs, low incentives to
learn English, deportation, and the fear and stress related to potential deportation, can translate
into worse outcomes for the American children of undocumented migrants.
Evidence So Far
The evidence so far on the impacts of parental documentation status on children is sparse.
From the sociology field, in a cross-section of Southern California adults who are children of
immigrants or childhood arrivals themselves, Rumbaut (2008) finds that having non-citizen parents is correlated with lower educational attainment and a higher likelihood of teenage pregnancy. These OLS estimates may suffer from significant omitted variable bias: the same factors that
determine whether a parent is able to legalize might also correlate to a child’s outcomes.
In his longitudinal ethnographic study of 400 migrant and African American mothers in
New York City, psychologist Yoshikawa finds that individuals who are less likely to be documented are also less likely to use center-based care for their children, and he finds that the use of
center-based child care is associated with higher cognitive test scores in the 36 month-old tod-
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dlers in his study (Yoshikawa 2011). Like Rumbaut, Yoshikawa does not address the issue of
omitted variables.13
Two papers in the field of economics have started to address the question of impact of parental legal status on children’s outcomes. Watson (2014) uses deportations over the years 19942003 in 25 clusters of states as a measure of immigration law enforcement intensity. She finds
that a rise in enforcement leads to lower enrollment rates in Medicaid among eligible American
children of non-citizens: parents’ fear of their own deportation keeps them away from the enrollment offices despite their children’s eligibility for Medicaid.14 One could imagine that similar
fears also keep migrant parents from enrolling their children in SNAP or other forms of welfare
for which the children are eligible.
Second, Pan (2011) uses the LAFANS to focus on a sample of 312 children ages 3-17 in
Los Angeles, some American and some immigrant. Using a similar identification to the one I
employ in here, she finds that mothers’ undocumented status leads to lower test scores among
offspring.15
III. Empirical Framework
Undocumented immigrants might differ from documented migrants and naturalized
Americans in unobservable ways that could correlate with their children’s outcomes. For example, among undocumented migrants, those with highest ability might be likelier to seek and gain
documented status. Their children are likelier to do well in school and in the labor force than the
children of less able immigrants, regardless of parental legal status. In that case, an OLS regression of children’s outcomes on parental legal status would overstate the positive causal effect of
parents’ possession of legal status on children’s outcomes.
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13
The study does not dwell on the strong correlation between likelihood of documentation and strength of networks
prevalent in his data: most of his undocumented mothers are Mexican. Mexicans have only recently started to migrate to New York, and thus have thin social networks there. It is unclear therefore whether the negative impacts that
Yoshikawa attributes to Mexicans’ lack of documentation status might at least in part be due to their lack of networks.
14
Yoshikawa (2011) likewise finds that “children who were eligible for programs that could have enhanced their
development, were very often not enrolled in the programs by their ineligible parents” (p.138).
15
One other paper in the field of economics is somewhat related to this topic. Avatabile, Clots-Figueras and Masella
(2014) find that Germany’s granting of birthright citizenship to the children of migrants leads to increased parental
investment in the children. !!
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The 1986 IRCA generates a source of discontinuity in migrants’ likelihood of being documented. Among the non-agricultural workers that are the focus of this paper, undocumented
migrants who arrived prior to January 1, 1982 should be likelier to gain documentation (indeed
naturalization) by 2000 than immigrants who arrived after January 1, 1982.
Because not all pre-IRCA migrants naturalize or even legalize, and not all post-IRCA
migrants are undocumented, this is a fuzzy regression discontinuity design. Hence, results from
the following reduced form regression deliver estimates of the intent to treat:
(1)
!!,! = !! + !! !"#!!"#$! + !! (!" − 1981)! + !! (!" − 1981)!! + !!,! !
where Y is child i’s educational outcome in county c, Pre IRCA is a dummy equal to one if child
i’s parents migrated to the U.S. before the cut-off for IRCA eligibility, YI is the parents’ year of
immigration, and Xi is a vector of baseline socio-economic and demographic characteristics of
child i (a gender dummy, and dummies for mother’s educational attainment).16 Some specifications also include MSA fixed effects, and some allow for different time effects and effects of
baseline characteristics for pre- versus post-IRCA immigrants. Variants of regression (1) provide
the main results of this paper.17
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16
Results are similar when I control for father’s education instead of mother’s.
could also use the pre IRCA dummy as an instrument for naturalization (or for LPR status, if that variable were
available in the data) in order to estimate the local average treatment effect in two stages. However the endogenous
regressor of interest, naturalization or legal status, requires special care both because it is binary and because some
individuals are likely to misreport their true naturalization status. Indeed, Van Hook and Bachmeier (2013) argue
that in the American Community Survey (and thus also likely in the census), misreporting of naturalization status is
high among Mexican men. It is very unlikely that truly naturalized immigrants would lie about their status, but it is
easily believable that undocumented immigrants responding to the 2000 census falsely claim to be naturalized.
Hence, if N* is an individual’s true naturalization status and N is the noisy measure of it, such that:
17!I
(2)
N i = N i* + ui
it seems quite likely that there will be a negative correlation between N* and the error term. Any instrument positively correlated with N* will thus also be negatively correlated with ui, and the exclusion restriction will be violated. In the presence of misreporting bias, the first stage is biased towards zero while IV estimates are biased away
from zero. Hausmann, Abrevaya and Scott-Morton (1998) provide an approach to the misreporting problem in the
case of a continuous variable. For now, I believe that the complications of IV estimation in the presence of misreporting bias with a binary variable, make the HASM approach more obfuscating than illuminating to the project. !
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IV. The Data
The empirical analysis relies on data from the IPUMS 5% sample of the 2000 census.
The key strength of the census is that for children still living with their parents, it provides information both on the parents (e.g. country of birth and year of arrival in the United States) and
on the children (namely educational achievement). However, the data presents several challenges. This section outlines both the sample definition and the limitations of the data.
Sample Definition and Summary Statistics
The children of interest are those whose parents migrated without documents or overstayed a visa in the years before and after the IRCA eligibility cut-off (January 1, 1982). I focus
on the educational outcomes of children who in 2000 are 14-17 years old. These children were
overwhelmingly born by 1986, and conceived prior to the signing of the IRCA. Children conceived after IRCA implementation might be the result of differential migrant fertility behavior by
eligibility status: for instance, it is possible that among IRCA-ineligible immigrants, only the
most (least) able still decide to bear children after the IRCA is signed. In this case, a comparison
of younger children born of pre-1982 migrants to those of post-1982 migrants would understate
(overstate) the negative impact of undocumented status.
Among children 14-17 years old, I pay closest attention to 14 year-olds, and expect results to be strongest for them: children who are 15-17 in 2000 were born in the U.S. in 19831985. This means that regardless of parental year of arrival, these children spent the first few
years of their lives as children of undocumented migrants, whose parents had no hope/idea that
the IRCA would be signed at the end of 1986. To the extent that investments in children build on
themselves (à la Heckman 2006), and that early investments matter disproportionately, a comparison of 17 year-olds by parents’ year of migration will understate the impact of undocumented
status, given that all of these 17 year-olds spent the first few years of their lives as offspring of
undocumented migrants. In addition, the older the child being considered, the smaller the sample
of IRCA-ineligible parents: for example, 17 year-olds in 1983 are for the most part born of individuals who migrated to the U.S. prior to 1982.
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The age restriction in the available data introduces a limitation: if I focus on 14 year-old
children, I cannot study whether the children of undocumented migrants are more or less likely
to graduate from high school, go to college, get white collar jobs, or other longer term economic
outcomes. I could of course use more recent ACS data to get at longer-term outcomes for immigrant offspring born in 1986. However, the ACS only provides data on a child’s parent if the two
still live under the same roof. In 2010, only a non-random minority of those born in 1986 will
still be living with their parents, so the analysis would be unrepresentative. Hence, it seems more
prudent to focus on analysis that uses the 2000 census, when children born in 1986 are only 14
and thus still living with their parents.
There are, in the census, few outcomes of potential interest for children of age 14. Because 14 is the age when most children start high school, I focus on a dummy equal to one if the
child is attending high school – in the 2000 census, 40.5% of all 14 year olds are in high school
(and the overwhelming majority of the rest are in middle school).18 This measure of academic
progress intuitively speaks to whether a student is on track for graduating from high school.19
Another non-trivial restriction in the data is the following: ideally, the analysis would focus on the children of migrants who arrived undocumented (or who overstayed visas) in the
years before and after January 1, 1982. However, the census does not provide parents’ documentation status at the time of arrival (it merely lists whether at the time of the census, the immigrant
is a citizen or not). Therefore, I restrict the sample to children whose parents are likeliest to have
been undocumented on arrival in the U.S. The Pew Hispanic Center (2011) estimates that 70% of
undocumented parents of children in the U.S. are Mexican, and another 17% are from other Latin
American countries (most notably Central America). Furthermore, California houses more undocumented migrants than any other state, by a wide margin: in 1990 (the earliest year for which
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18
Results using a dummy equal to 1 if the child is still enrolled in middle school are the mirror image of the HS results. I also explored looking at likelihood of teenage motherhood and the likelihood of attending school at all, but
the incidence of teenage motherhood and of not attending school among 14 year-olds were too low for the results to
be meaningful.
19
There are many reasons why a student may not be “on track,” and there is conflicting evidence on whether repeating a grade is good or bad for children’s eventual academic achievement. Jacob and Lefgren (2009), find that students with test scores just low enough to get them held back have the same high school graduation rate as students
whose test scores were just high enough to pass to the next grade. On the other hand, Andrew (2014) matches students in the NLSY on a vast set of characteristics (test scores, behavioral patterns, socioeconomic background variables, etc.) and finds that repeating a grade translates into a 50 percent lower likelihood of graduating from high
school. Given the paucity of relevant outcome variables in the census, I am forced to make the assumption that not
reaching high school by age 14, the “normal” starting age, is a bad omen for children’s long run educational attainment.
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data are shown), California counted 1.5 million undocumented migrants, to Texas’s 450,000.20
Thus, I restrict attention to children of Mexican and Central American immigrants who live in
California in 2000.21 In results available on request, I also further restrict the sample to children
whose parents do not have a college degree, under the assumption that college-educated parents
are much likelier to immigrate with documents (this restriction does not materially change the
results).
Finally, due to concerns of fraud among SAW applicants for legalization, I focus on
families living in metropolitan areas, whose parents, if eligible for legalization, would have likely applied under section 245A of the IRCA. The assumption is that focusing on urban families
excludes most of the agricultural workers who applied for legalization under the SAW provision
of the IRCA (I discuss fraud in more detail in section V).22
Table 1 presents summary statistics for the sample. There are 1,023 children of Mexican
and Central American migrants age 14 living in California, whose parents migrated between
1976 and 1986.23 I define parental year of migration as the earlier of the mother’s or father’s year
of migration (under the assumption that one spouse’s eligibility for IRCA is enough to confer to
the whole family benefits from legalization). “Pre-IRCA” children are children whose parental
migration date is earlier than January 1, 1982. Pre-IRCA children are significantly likelier to
have naturalized parents than are their post-IRCA counterparts. They are likelier to be enrolled in
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20
The Migration Policy Institute points out that half of all California children under age 18 today have at least one
migrant parent, and 90% of those children were born in the U.S.. This provides further support to the focus of this
paper on California children.
21
The 2000 census undercounts undocumented immigrants. However, this likely just stacks the decks against finding evidence that lack of parental documentation harms children. Chiquiar and Hanson (2005), assuming an undocumented undercount of 15% in the 2000 census, use Mexican Migration Project (MMP) data to adjust the numbers
and observable characteristics in their 2000 census sample of immigrants. The MMP gathers data from immigrants
when they are in Mexico, where they have no incentive to lie about their documentation upon migration. Using this
data, Chiquiar and Hanson estimate that the undocumented who are not captured in the U.S. census have relatively
low educational attainment, vis à vis their peers captured in the census. Thus, my sample excludes undocumented
migrants in 2000 who are on average less educated than their peers. If anything, I would imagine that these immigrants’ children have lower educational attainment on average, and that their exclusion from the sample merely biases me against finding any negative impacts from lack of documentation. !
22
This restriction is imperfect because immigrants who live in urban areas in 2000 did not necessarily live in urban
areas on arrival. Indeed, there is evidence in the National Agricultural Workers Survey (NAWS) that a substantial
fraction of IRCA-legalized farm workers eventually left agricultural work for other activities. If they move to a city
to pursue these other work opportunities, the sample I have created includes immigrants who qualified for IRCA via
the SAW provision, so merely by working 90 days in the lead up to May 1986, rather than through section 245A, by
proving continuous U.S. residence as of January 1, 1982. I can’t see a way around this imperfect assumption given
my data constraints.
23
Results presented here are for children who live with both parents. Results are similar when I include children
who live with one OR both parents.!
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high school, and less likely to be in middle school. There is some evidence that a child’s father’s
baseline characteristics and 2000 labor income differ somewhat by IRCA status. 24 I return to this
point later.
Figure 1 shows the percentage of migrant parents (of American children) who are naturalized by 2000, by year of migration, contrasting the trends for Mexican/Central American migrants to California to those for other migrants. Unsurprisingly, more recent immigrants are less
likely to be naturalized in 2000, and Mexican/Central American immigrants of almost any vintage show a lower probability of being naturalized than contemporary immigrants from other
countries.
More importantly, Figure 1 shows a noticeable drop in likelihood of naturalization for
1982 Mexican/Central American immigrants relative to their immediate predecessors. No similar
drop is observable for non-Mexican and non-Central American immigrants. Furthermore, this
drop likely represents a lower bound on the impact of the IRCA program. Indeed, over half of
the program’s beneficiaries stopped short of applying for citizenship once they had obtained Legal Permanent Resident status. If the census provided data on an individual’s legal status, rather
than just their citizenship status, figure 1 could plot the relationship between year of arrival and
probability of being legal. Such a graph would in all likelihood show a starker break between
1981 and 1982.
In any case, I interpret the visible break in Figure 1 as evidence that for immigrants likely
to be undocumented (i.e. Mexicans and Central Americans) arriving prior to the IRCA eligibility
cut-off of January 1, 1982 dramatically increases the chances of legalizing. However, there are
other possible explanations for the drop, which challenge the interpretation of the IRCA as a regression discontinuity design. For instance, the drop in naturalization coincides with a severe recession in the United States. Migrants might self-select differently in recession years, and/or may
have worse labor market outcomes if they arrive during a recession (and worse labor market outcomes might impair later efforts to naturalize). There might be IRCA fraud such that assignment
of treatment is manipulated. Finally, there might be selective return migration that differs for
IRCA-eligible and -ineligible migrants. I address these challenges in section VI, after presenting
results in the next section.
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
24
It is worth noting here that the direction is the opposite of what one would expect if one worried that the results I
observe later were driven by baseline characteristics. Furthermore, these differences in baseline characteristics appear to be driven by outliers in one year with little data.
!
14!
V. Results
Basic Results
With the census data, the only way to know the migratory status of a child’s parent is if
the child lives with his/her parent. So by necessity, the analysis below excludes all children
whose parents have both been deported. Assuming deportation of two parents negatively affects
children’s outcomes, the estimates below represent a lower bound on the true positive impact of
parental documentation.
According to Figure 2, children of post-IRCA Mexican immigrants are less likely to be
attending high school than the offspring of pre-IRCA migrants (as a control group, the figure also includes children of non-Mexican, non-Central American immigrants, who are on average
much likelier to migrate with documents and who therefore are much less likely to have been
“treated” by the IRCA). Thus, there seems to be some support for the idea that parental IRCA
eligibility does affect children’s educational outcomes. The children whose parents are likelier to
be documented (whether as legal permanent resident or as naturalized citizens) in 2000 seem to
have better educational outcomes at age 14 than the children of likelier undocumented parents in
2000. To explore this visual evidence further, I run regression counterparts to Figure 2. Table 2
presents results from variants of linear probability regression (1). In the simplest specification, in
column (1), 14 year-old children of pre-IRCA migrants appear 8.6 percentage points more likely
to be enrolled in high school than the children of post-IRCA migrants.25 I explore the robustness
of these results in columns (2)-(8) by including gender and parental education controls, and interactions of these terms with the “pre-IRCA” dummy; by including migration year trends, and
allowing migration year trends to differ pre- and post-IRCA; by including the unemployment
year in the year of immigration; and by excluding years one at a time. The magnitude of the coefficient of interest varies according to specification, but remains significantly positive in most
columns, whether errors are clustered by parents’ year of migration or bootstrapped. As table 3
shows, results are also robust to different windows of estimation. In results available on request,
I repeat the analysis with a probit specification
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
25! They are also, not surprisingly, 10 percentage points less likely to be in middle school, and 1.2 percentage points
likelier to be attending school – these results available on request.!
!
15!
In appendix A, I also repeat a similar analysis using years of education for 15-16 year
olds as a dependent variable and find either insignificant or negative coefficients for the preIRCA variable. For instance, Figure 3 illustrates that no clear pre/post IRCA pattern emerges for
15 year olds’ school years completed.26 One possible explanation is that regardless of parental
IRCA eligibility, 15-17 year-olds were born in 1983-1985, and thus spent the first years of their
lives as children of undocumented immigrants, prior to the announcement of the IRCA.
Causal Channels
Why are the children of undocumented immigrants less likely to have reached high
school by age 14 than the children of documented immigrants? Section II outlined several potential causal channels, and highlighted the evidence that exists already: it appears that an individual’s legal status has a bearing on his/her labor market outcomes (Pan, 2012; Amuedo-Dorantes et
al. 2007; Kossoudji and Cobb Clark 2002), English fluency (Pan 2012), likelihood of deportation, and likelihood of enrolling offspring in Medicaid (Watson 2014). Through which of these
channels does lack of parental documentation harm children? Are there other channels too?
The census provides data that allows me to control for some (but not all) of the potential
causal channels.27 In particular, I can control for parents’ English fluency, parents’ welfare use
and labor income in 2000.28 If inclusion of a particular potential causal channel leads to a loss of
magnitude and significance of the pre-IRCA coefficient, this suggests that the included variable
may indeed be a channel through which undocumented parent status affects children’s outcomes.
Table 4 presents evidence on different candidate causal channels. According to these results, parents’ English fluency and welfare use have little bearing on the children’s educational
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
26
The dummy equal to one if a person has reached high school is most relevant for 14 year-olds, as 95% of 15 yearolds with likely initially undocumented parents have reached high school (i.e. there is little variation in the variable
for 15 year-olds). That is why for children in the age group 15-17, I discuss years of education completed as the relevant metric. For 14 year-olds, years of education completed is not precisely measured: the census only reveals yearby-year grade completion for high school. For children still in middle school, the census does not distinguish between children who have completed 7th or 8th grade, for instance.
27
The census data does not allow exhaustive exploration of all potential causal channels. As already mentioned, I
cannot analyze the outcomes of children whose parents have been deported. As another example, the data tell us
nothing about parents’ or children’s mental state. Thus, it is impossible to test whether one mechanism that correlates undocumented migrants to less educated offspring is the mental and emotional toll on both generations from
the risk of parental deportation.
28!Although I take parental education as given, I could also treat parental education as a variable that might be affected by IRCA-eligibility, and thus as a potential causal channel, but as already seen in Table 2, the inclusion of
parental education as a control variable does not change the coefficient of interest.!!
!
16!
achievement at age 14. In other words, even if as Pan (2012) and Yoshikawa (2011) suggest,
parents’ undocumented status correlates to lower English fluency and lower enrollment rates in
welfare, it is not through these channels that legal status affects children’s educational attainment. On the other hand, when I control for the log of the father’s labor income in 2000, the coefficient on the pre-IRCA dummy loses magnitude and statistical significance.29 I interpret this
as evidence that the relatively poor labor market opportunities of undocumented immigrants negatively affect not only them, but also their American-born children’s education.
However, there is an alternative interpretation: immigrants who arrive in 1982-83 experience worse labor market trajectories than 1981 immigrants because they came to the United
States during a weak labor market. The negative impact of their labor market experience on their
children’s education may have nothing to do with their legal status, and everything to do with the
state of the economy in their arrival year. There is conflicting evidence on whether arrival during
a recession harms the labor market trajectory of immigrants. Åslund and Rooth (2007) find that
in the Swedish context, immigrants are scarred by arrival during a recession. McDonald and
Worswick (1998) echo these findings with Canadian data but Chiswick, Cohen and Zach (1997)
argue immigrants suffer no penalty as a result of arriving in the U.S. during a recession. I turn
now to address this and other challenges.
VI. Challenges
The believability of the above findings hinges crucially on the assumption that we can
view the IRCA through an RDD lens. I address here several challenges to that assumption.
The 1981-2 Recession
On Figure 1, the shaded rectangles show years of rising/high unemployment.30 The eligibility cut-off for the IRCA, January 1, 1982, coincides with a recession in the U.S. The drop in
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
29!There
is of course a selection issue here, namely that I only observe labor income of parents who work. This problem is particularly significant for women, given that only 50% or so of the moms in this sample report labor income.
I thus include only the log of fathers’ income as a potential causal channel, but even with fathers I should interpret
results with caution, as only 83% of fathers report income. !
30
The shaded areas are years in which the unemployment rate is significantly rising, or remains on a high plateau
after having risen significantly.
!
17!
likelihood of naturalization for 1982-83 immigrants vis à vis immediate predecessors might be
attributable to macroeconomic conditions rather than the IRCA. Maybe arriving in a year of recession puts immigrants on a worse labor market path that limits their odds of naturalization, and
importantly, might also affect their children’s educational outcomes. If this is the case, regression
(1) does not identify the effect of IRCA-eligibility, but also, confoundedly, the effects of a recession on year of arrival. This would also provide an alternative explanation for the finding in Table 4, that controlling for father’s wage in 2000 eliminates the significance of the coefficient of
interest. Indeed, father’s wage in 2000 may not be a causal channel through which parental legal
status affect children, but rather may be a consequence of father’s arrival during a recession.
This is theoretically possible, but it is worth noting that the drop in naturalization rates for
1982-83 arrivals is far larger than drops in naturalization rates for immigrants arriving during
other recessions depicted on Figure 1. It seems unlikely that the 1982 recession, alone among
recessions, would have such a large impact on naturalization rates. Nevertheless, as a first attempt to address this concern, the specification in column 5 of Table 2 controls for the unemployment rate in the year of the immigrant’s arrival.31 In results available on request, I repeat the
analysis excluding 1982 and 1983, the years of peak unemployment during that recession, qualitatively, the results are similar thought the magnitude of the coefficient on pre-IRCA becomes
somewhat larger.
The following falsification test further addresses the concern that the discontinuity is the
result of the recession rather than the IRCA: if 14 year-old children of immigrants are less likely
to reach high school if their parents arrive in a recession/ high unemployment year, I should observe this not only for arrivals during the early 1980s recession that coincides with the IRCA eligibility cut-off, but also with arrivals during the other recessions visible on Figure 1. The 1990
census data that I use for this falsification test contains somewhat different variables than the
2000 census, so rather than analyze whether 14 year-olds have reached high school, I test whether for a 15 year-old, the likelihood of having completed ninth grade depends on parents’ year of
immigration. 32 I find no evidence that in the 1990 census, 15 year-old children of Mexican and
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
31
Ideally, I would like to control for how long it took parents to find jobs upon arrival in the U.S., and for their first
wages in U.S., but the 2000 census does not provide that information.
32!The 1990 census does not provide information on the grade a student is currently attending, so I cannot analyze
whether students have reached high school or not. It classifies students’ educational achievement as having passed
“5th, 6th, 7th or 8th grade,” or having passed 9th grade. From this information, it would be impossible to know, from
looking at a 14 year-old, if she has passed 8th grade and is thus “on track” for her age, or if she just passed 7th grade,
!
18!
Central American immigrants are less likely to have completed ninth grade if their parents arrived in 1970-1974 (i.e. during a recession) than if they arrived in 1965-1969 (no recession). On
the contrary, children of recession-year arrivals are more likely to have completed ninth grade
than the children of 1965-69 arrivals. Likewise, using the 2009-2011 3-year ACS data, Figure 4
shows no evidence that American children whose parents immigrated in 1990-1993 have a lower
likelihood of reaching high school by age 14 (indeed, it looks like immigrants who arrive after
the recession have children who are less likely to have reached high school by age 14). Thus, I
assume that the causal channel findings of Table 3 do not reflect the consequence of an immigrant’s arrival in a recession year.
Another concern that the recession raises is that the profile of migrants during the recession might differ from that of pre- and post-recession migrants. Figure 5, which shows parent
characteristics by year of migration, suggests that migrant selection might have changed somewhat during the years of the recession – it does appear that in 1983 (i.e. post IRCA, and at the
heart of the period of high unemployment), immigrants are somewhat more educated than in the
immediate preceding years. If anything, such a change in selection would generate a bias against
finding a positive impact of legal status on children’s outcomes, and suggests the findings of this
paper can be viewed as a lower bound on the true estimate of legal status impact on children’s
outcomes.
Unclear Break, and Fraud
Figure 1 illustrates a second challenge: while the percent of Mexican migrants who are
naturalized clearly drops between 1980 and 1983, the drop is not a clear break as of 1982. There
is a gradual decrease in 1982 and then a further decrease in 1983. The IRCA stated that anyone
immigrating after January 1, 1982 would be ineligible for legalization, so the drop in naturalization likelihood should show up fully and only for 1982 immigrants. In addition to the potential
impact of the recession already discussed, there are a few other possible explanations: first, maybe the INS exercised discretion in applying the cut-off, such that if an immigrant could provide
proof of U.S. residence as of January 1982, regardless of whether that proof dated from January
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
and so is lagging. Thus, I instead look at 15 year olds, and examine whether their likelihood of having completed 9th
grade varies with parents’ year of immigration. The other main difference between the 1990 and 2000 census is that
the 1990 census only breaks down immigrants’ year of arrival into five year bins: 1965-69, 1970-74, etc (unlike the
2000 census which provides specific year of arrival information for immigrants). !
!
19!
1st or January 31st, he/she would be considered eligible for the IRCA. There is not a lot of evidence of INS leniency on the cut-off to eligibility, but neither is there evidence refuting this possibility.
A second possibility is that January 1, 1982 has high salience in migrants’ minds, given
that it is the cut-off date for IRCA eligibility. When asked about their date of migration in 2000,
far after the fact, immigrants might remember most accurately that they just made the cut-off for
IRCA eligibility, and thus might say they arrived in the U.S. by 1982. This hypothesis is difficult
to prove or disprove.
A more obvious possibility is that immigrants lied about their arrival date when the IRCA
was implemented, in order to gain eligibility for the legalization program. This is potentially
concerning if “liars” are a select group of immigrants: it is possible that only the most able immigrants can fabricate the documentation required to prove residency as of January 1982. Two
possibilities then exist: (a) immigrants lie at the time of the IRCA, and then again the 2000 census that generates the data for Figure 1; or (b) immigrants only lie at the time of the IRCA, so in
the 2000 census they truthfully reply that they arrived in 1982. If those lying at the time tended
to be the more able immigrants, possibility (b) would tend to bias results against finding a positive impact of IRCA eligibility on children’s outcomes.33 Possibility (a) is more concerning – if a
select group of immigrants lies in 1986 and 2000, results from regression (1) might be biased
upwards – they might show that children of pre-IRCA immigrants have better educational outcomes, not because of their parents’ legal status, but because of their parents’ differing ability
levels.
The liars hypothesis is not extremely concerning for a few reasons. First, visual inspection of observable migrant characteristics by year of immigration (in Figure 5) reveals no evidence of a positive change in selection between 1981 and 1982 (the slight uptick in father’s education is visible only in 1983). The liars hypothesis also seems somewhat unlikely because as
Shaw (1989), the Assistant Commissioner for Investigation at the INS, suggests, there was a lot
more evidence of fraud among SAW applicants to the IRCA than among the section 245A applicants that are the focus here, due to the less stringent burden of proof attached to the SAW provision. “SAW fraud has developed mainly because of the SAW provisions of the new law which
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
33!since
these liars would be falsely classified as IRCA ineligible (because in 2000 they reply truthfully regarding
year of migration) when in fact they and their children had benefited from the IRCA (because in 1986 they lied
about migration year)!
!
20!
enabled an applicant to submit only an affidavit from a farmer or farm labor contractors attesting
to eligibility for the benefit. This eligibility (…) is based on either 90 days of work in agriculture
during each of 1984, 1985 and 1986, or 90 days of work in agriculture between May 1, 1985 and
May 1, 1986. Comparatively, Section 245A, the amnesty provision of the law, required extensive
documentation of the qualifying presence and consequently, ineligible aliens inclined to attempt
fraud, chose the relatively easier SAW application.”
Further suggestive evidence that immigrants did not lie about their date of arrival comes
in the form of the density of year of migration for Mexicans from 1965 to 1999. Figure 6 shows a
local (by no means global!) peak in 1980.34 Presumably, a lying migrant, under pressure to provide “extensive documentation of the qualifying presence,” would seek to minimize that burden
and would claim to have arrived just before the eligibility cut-off, not 12-24 months before. 35 In
other words, I would expect the density to show a local peak in 1981 if many immigrants were
lying.
Selective Return Migration
One final potential concern is the possibility of selective return migration. For instance, it
is possible that among IRCA-ineligible applicants, only the most (least) able decide to stay in the
U.S. In that case, the estimates here provide an under (over) estimate of the impact of documentation on children’s outcomes. Or if, among IRCA-eligible immigrants, only the most (least) able
choose to take up the legalization option and stay in the U.S., the estimates in this paper would
be an over (under) estimate of the impact of documentation on children. Using U.S. census data
from 1970 to 2000, Aguilar Esteva (2013) finds evidence that 1975-1980 Mexican and Central
American arrivals become slightly more negatively selected by 2000 (in other words the most
able migrants return to their home country) and that 1985-1990 Mexican and Central American
immigrants become slightly more positively selected over time in the U.S. (he does not provide
data on 1980-1985 immigrants). According to Aguilar Esteva then, among IRCA-eligible immi!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
34
In fact, the local maxima on the graph suggest that immigrants have a tendency to round to the nearest decade
(1970, 1980, 1990) of their arrival.
35!Orrenius (2001), using Mexican Migration Project data, estimates the rate of undocumented immigration from
1960 to 1999. She finds local peaks in 1970, 1980 and 1986. MMP data is gathered in Mexico, and thus respondents
have no incentive to lie about their dates of migration in that survey, the way one could argue they might in the U.S.
Census.
!
21!
grants, the less able would remain in the U.S. long enough to be captured in the 2000 census.
Among the ineligible immigrants, the most able would remain in the U.S. in 2000. This would
stack the deck against finding that undocumented parental status harms children.
To further examine the possibility of selective return migration for the specific population
of interest here, I look at the summary statistics for Mexican and Central Americans who arrived
in the U.S. in the 1976-1986 period, as captured by the 1990 and 2000 census. I focus in particular on immigrants who live in California and have at least one four year-old at home in the 1990
census (or at least one 14 year-old at home in the 2000 census). A comparison of the summary
statistics for these immigrants across the two census years cannot reveal whether selective return
migration took place before the 1990 census was held, i.e. between 1986 and 1990, but it would
at least show whether there was selective return migration between 1990 and 2000 (based on observables). Table 5 presents summary statistics by IRCA eligibility status, both in 1990 and in
2000. As expected, the average age and earnings for immigrants rise over time, regardless of IRCA eligibility (and pre-IRCA immigrants have higher earnings in both years). For both IRCAeligible and -ineligible immigrants, male representation rises, suggesting that women return to
the home country. Contrary to Aguilar Esteva, I find no evidence of differential changes in educational attainment by IRCA eligibility status. So either there is no selection in return migration
(based on observables) or, at worst, as Aguilar Esteva’s analysis suggests, there is selection that
biases the coefficient of interest towards zero.
VII. Conclusion and Next Steps
The evidence here complements the conclusions of Pan (2011): I find that American
children of migrants in California are less likely to have reached high school by age 14 if their
parents are likely to be undocumented. I provide evidence that the results are not driven by differential recession-year migrant selection, migrant labor market trajectory or selective return migration, I argue my findings are unlikely to be driven by IRCA fraud, and I provide preliminary
evidence on some of the causal channel candidates.
Going forward, I would like to expand on this project in the following three directions.
First, I would like to explore other potential causal channels. The census data alone does not di-
!
22!
rectly allow me to test whether fear is a causal channel. It is certainly possible that parents fearful
of deportation are less able and less likely to ensure their children’s regular attendance at school.
It is also possible that the risk of parental deportation makes American children afraid (as one of
the anecdotes quoted in this paper suggests), and this harms school attendance and/or performance. Borrowing from Watson (2014), I plan to analyze whether variations in enforcement
stringency affect the school attendance/achievement of children of likely undocumented immigrants. Such a result would suggest that just as enforcement generates a chilling effect among
undocumented immigrants in enrolling their eligible children in Medicaid, so too does it disrupt
these children’s educational attainment.
Second, I would like to find other large datasets that both (a) link children to their parents
and (b) provide information on the children’s education and labor market outcomes. I have focused here on whether 14 year olds are enrolled in high school only as a result of data constraints, and it would be useful to be able to look beyond this intermediate yardstick of educational progress, at ultimate educational attainment and labor market performance.
Finally, the results above do not hold for likely undocumented immigrants in other states
such as Texas and Illinois. This raises questions about why and how California is different. Are
differences in state policies, or in states’ enforcement of federal policies, responsible? Pham and
Hoang Van (2014) put together a state-by-state “Immigrants Climate Index” (ICI) that ranks
states according to their receptiveness to immigrants as of 2009. According to these authors (respectively a law professor and an economist), the split across states in sub-federal immigrationrelated policy and regulations took off in the mid 2000s. If this is accurate, it would seem unlikely that differences in results across states in the 2000 could be driven by differences in state-level
policy climates. Even if the ICI illustrates differences in state attitudes that predate the mid
2000s, they seem unlikely to explain differences in outcomes for children in different states. Indeed, the ICI ranks California and Illinois as the two most immigrant-friendly states, so the results of my analysis should be the same for children of immigrants in the two states. It seems
more likely that small sample sizes in the other states are driving differences in results between
California and other states. A larger, restricted-use sample of the Census data would be extreme-
!
23!
ly useful here.36 Another possibility is that immigrants in California are different from immigrants in other states, and in particular are more likely to be undocumented.
Immigration policy pertains first and foremost to people and lives, but also has farreaching consequences for the U.S. economy. To date, few policymakers have discussed the possible economic consequences for more than four million American children of having undocumented parents. The results in this paper suggest these costs could be non-negligible. This should
inform the ongoing debates on President Obama’s November 2014 executive actions and immigration reform more broadly.
!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!!
36
In the 5% sample of the U.S. census, in Illinois, there are only 11 American 14 year-olds living in urban areas
whose Mexican/Central American parents arrived in 1982. There are only three whose parents arrived in 1983…
Figures are similarly low in most years. My repeated efforts to secure access to restricted use data via the Census
Bureau’s Research Data Center were not fruitful due to the sensitive nature of the populations I study (undocumented immigrants and children).
!
24!
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Medicaid Participation. American Economic Journal: Economic Policy. 6(3): 313-38
Yoshikawa, Hirokazu. 2011. Immigrants Raising Citizens: Undocumented Parents and Their
Young Children. New York, NY: Russell Sage Foundation.
!
28!
Figure 1: Percent of Immigrant Parents Naturalized, by Year of Immigration
Note: shaded areas represent periods of rising unemployment, or years in which after rising, the unemployment remains on a high
plateau.
Figure 2: Percent of 14 Year-Olds in High School, by Parental Year of Migration
!
29!
Figure 3: 15 Year-Olds’ Years of Education, by Parental Year of Migration
Figure 4: Percent of 14 Year-Olds in High School, by Parental Year of Migration, 20092011 ACS
!
30!
Figure 5: Migrant Characteristics, by Year of Migration
(a) % of Moms Who Are HSDO
(b) % of Dads Who Are HSDO
(c) Dad’s ln(labor income) in 2000
!
31!
Figure 6: Density of Year of Migration, 1965-1999 Mexican Migrants
!
32!
Table 1: Summary Statistics for 14 Year-Olds in Sample
All
% Male
% 14 year-olds in middle school
% 14 year-olds in high school
% 14 year-olds in school
% Whose mom/dad migrated pre 1/1/82
Parents’ migration yr – 1981
% With naturalizd parent
% With high school drop-out dad
% With high school grad dad
% With high school drop-out mom
% With high school grad mom
ln (dad’s labor income)
% With dad on welfare
% With mom on welfare
% With English-fluent dad
% With English-fluent mom
Observations
0.52
(0.50)
0.51
(0.50)
0.49
(0.50)
0.99
(0.09)
0.72
(0.45)
-0.68
(2.39)
0.46
(0.50)
0.78
(0.41)
0.19
(0.40)
0.81
(0.39)
0.17
(0.38)
10.00
(0.70)
0.02
(0.15)
0.04
(0.20)
0.52
(0.50)
0.38
(0.49)
1,023
Children of postIRCA migrants
0.50
(0.50)
0.57
(0.50)
0.43
(0.49)
0.98
(0.12)
0.00
(0.00)
2.55
(1.28)
0.39
(0.49)
0.75
(0.44)
0.23
(0.42)
0.78
(0.41)
0.20
(0.40)
9.93
(0.66)
0.04
(0.20)
0.07
(0.25)
0.51
(0.50)
0.36
(0.48)
286
Children of preIRCA migrants
0.52
(0.50)
0.49***
(0.50)
0.51***
(0.50)
1.00*
(0.07)
1.00***
(0.00)
-1.92***
(1.33)
0.49***
(0.50)
0.80**
(0.40)
0.18*
(0.38)
0.82
(0.38)
0.16
(0.37)
10.02
(0.72)
0.02**
(0.13)
0.03
(0.18)
0.53
(0.50)
0.39
(0.49)
737
Summary statistics are from a sample drawn from the 2000 census of children whose parents migrated from Mexico or Central
America between 1976-1986. Significant differences between children of pre- and post-IRCA migrants are denoted as follows: *
p<0.1; ** p<0.05; *** p<0.01.
!
33!
Table 2: Reduced Form Impact of Parent Legal Status on High School Attendance
(1)
Pre-IRCA
Clustered
errors
Bootstrapped
errors
Demographic
& mig year
controls
Different
pre/postIRCA
trends
MSA FE
UE rate
R2
N
(2)
(3)
(4)
(5)
Dependent variable: dummy=1 if child attends HS (Linear Probability Model)
0.086
0.059
0.165
0.183
0.164
(0.025)***
(0.047)
(0.051)***
(0.055)***
(0.059)**
(0.033)***
0.01
1,016
(0.060)
(0.074)**
(0.095)*
(0.077)**
X
X
X
X
X
X
X
X
X
X
0.05
1,016
0.01
1,016
0.02
1,016
0.05
1,016
Note: Robust clustered errors are clustered by year of parents’ migration. Demographic controls are male dummy, dummies for mothers’ educational attainment. Migration year controls are linear and quadratic controls for (parents’ year of
migration – 1981). UE rate is the U.S. unemployment rate in the year of migration. * p<0.1; ** p<0.05; *** p<0.01
Table 3: Parent Legal Status on High School Attendance – Varying Time Windows
(1)
(2)
(3)
(4)
(5)
Dependent variable: dummy=1 if child attends HS (Linear Probability Model)
Pre-IRCA
Clustered
errors
Bootstrapped
errors
R2
N
Years
0.086
(0.025)***
0.070
(0.024)**
0.080
(0.023)**
0.091
(0.033)*
0.085
(0.000)***
(0.031)***
(0.032)**
(0.036)**
(0.080)
(0.000)***
0.01
1,016
1977-1986
0.00
887
1978-1985
0.01
671
1979-1984
0.01
452
1980-1983
0.01
208
1981-1982
Note: Robust clustered errors are clustered by year of parents’ migration. * p<0.1; ** p<0.05; *** p<0.01
!
34!
Table 4: Reduced Form Impact of Parent Legal Status on High School Attendance, with Potential Causal Channels
(1)
(2)
(3)
(4)
(5)
(6)
(7)
Dependent variable: dummy =1 if child attends high school (Linear Probability Model)
Pre-IRCA
0.086
(0.025)***
Mom English-fluent
Dad English-fluent
0.088
(0.025)***
-0.078
(0.037)*
0.060
(0.023)**
Mom on welfare
Dad on welfare
0.081
(0.029)**
-0.082
(0.036)**
0.057
(0.022)**
-0.087
(0.069)
-0.149
(0.080)*
0.084
(0.030)**
-0.092
(0.039)**
0.057
(0.022)**
-0.081
(0.074)
-0.144
(0.082)
ln (dad’s income)
Demographic & mig
year controls
Different
pre/postIRCA trends
MSA FE
Recession controls
Constant
R2
N
0.050
(0.038)
-0.098
(0.041)**
0.039
(0.023)
-0.090
(0.095)
-0.171
(0.138)
0.080
(0.032)**
0.053
(0.063)
-0.093
(0.047)*
0.036
(0.019)*
-0.060
(0.095)
-0.160
(0.115)
0.080
(0.032)**
X
0.143
(0.135)
-0.091
(0.047)*
0.036
(0.019)*
-0.063
(0.096)
-0.162
(0.119)
0.081
(0.033)**
X
X
0.428
(0.019)***
0.01
1,016
0.426
(0.028)***
0.01
1,016
0.441
(0.032)***
0.02
1,016
0.433
(0.032)***
0.02
1,016
-0.308
(0.334)
0.03
847
X
X
-0.319
(0.421)
0.06
847
X
X
-0.295
(0.422)
0.06
847
Note: Robust errors, clustered by year of parental migration. Demographic controls are male dummy and dummies for mothers’ educational attainment. Migration year controls are
linear and quadratic controls for (parents’ year of migration – 1981). UE rate is the U.S. unemployment rate in the year of migration. * p<0.1; ** p<0.05; *** p<0.01
Table 5: Evidence on Selective Return Migration between 1990-2000
Real income (2000 US$)
Age
% Male
% High school dropout
% High school graduate
% College graduate
Observations
Pre-1982 migrants
1990
2000
13,122
16,423***
(13,544)
(24,545)
32.29
41.73***
(5.64)
(5.10)
0.52
0.49**
(0.50)
(0.50)
0.79
0.78
(0.41)
(0.41)
0.19
0.19
(0.40)
(0.40)
0.02
0.02
(0.14)
(0.14)
3,498
2,864
Post-1982 migrants
1990
2000
9,621
12,803***
(10,871)
(18,374)
30.77
40.60***
(5.93)
(5.65)
0.45
0.41**
(0.50)
(0.49)
0.76
0.75
(0.43)
(0.43)
0.22
0.21
(0.41)
(0.41)
0.02
0.04
(0.15)
(0.18)
1,272
1,165
Summary statistics are for Mexicans and Central American migrants who arrived 1976-1986, were between 15-45 years old i
1980 and have children (age 4 in 1990, 14 in 2000). Significant differences between pre- and post-IRCA migrants are denote
follows: * p<0.1; ** P<0.05; *** p<0.01.
!
36!
Appendix A: Years of education completed, by parents’ year of arrival
!
!
Pre!IRCA!
!
Age!15!
(1)!
0.120!
(0.022)***!
(2)!
70.358!
(0.045)***!
Age!16!
(3)!
(4)!
(5)!
(6)!
(7)!
70.182!
(0.108)
*!
15,333!
X!
70.289!
(0.108)***!
70.302!
(0.112)***!
0.289!
(0.030)***!
70.083!
(0.064
)!
11,841!
X!
(8)!
73.256!
(0.199)***!
N!
15,333!
15,333!
15,333!
15,333!
11,841!
11,841!
Demo!con7
!
X!
X!
X!
!
X!
trols,!lin.!&!
quadratic!
controls!
Diff.!
!
!
X!
X!
X!
!
!
X!
pre/post!
trends!
Diff.!pre!&!
!
!
!
!
!
!
!
!
post!trends!
MSA!FE!
!
!
!
X!
X!
!
!
!
Recession!
!
!
!
!
X!
!
!
!
controls!
Note:!*!p<0.1;!**!p<0.05;!***!p<0.01.!Demographic!controls!are!male!dummy,!dummies!for!mother’s!educational!attainment
!
37!
(9)!
(10)!
72.952!
(0.200)***!
72.885!
(0.205)***!
11,841!
X!
11,841!
X!
X!
X!
!
!
X!
!
X!
X!