Overview

Undocumented immigrants in the U.S. likely receive lower wages as a result of not having legal immigration status. As such, legalizing these immigrants could lead to improved labor market outcomes, including a greater workforce participation rate and higher wages. This paper uses U.S. census data to estimate the change in earnings that current undocumented immigrants could receive if granted amnesty.

Accounting for the difference in wages between legal and undocumented immigrants that is not explained by individual characteristics, as well as for potential improvements in English proficiency that could result from an amnesty program, I estimate that the wages of undocumented immigrants in the U.S. would grow by approximately 4%-5%. This translates to roughly $14 billion per year in additional labor market earnings. I also estimate that the average undocumented household would qualify for $1,175 in income from the earned income tax credit (EITC) after receiving legal status.

Introduction

Approximately one-quarter of all immigrants in the United States — around 12 million people — lack legal immigration status (Baker 2021). While these undocumented immigrants participate heavily in the labor market, a lack of legal status likely harms their earning prospects.

For example, a lack of legal immigration status directly narrows the range of available occupations: Jobs that require an occupational license will be difficult or impossible for an undocumented immigrant to perform. Many jobs require driver’s licenses, which, in many states, are not available to undocumented immigrants.[1] Some employers may also be wary of hiring undocumented immigrants, especially for public-facing positions with higher visibility. Indirectly, lacking legal status may disincentivize undocumented immigrants from acquiring country-specific human capital that is valuable in the labor market (notably, English language ability) due to greater uncertainty about their expected length of stay in the United States.

Not surprisingly, the issue of undocumented immigration has attracted significant political interest for many years. One proposal to address it is a widespread amnesty program, like the Immigration Reform and Control Act (IRCA) of 1986, which granted legal status to over 2 million people. The potential for improved labor market outcomes, both in the short and long terms, provides an economic rationale for enacting a similar amnesty program today.

In this paper, I provide an estimate of the expected improvement in wages that current undocumented immigrants might enjoy after receiving amnesty. First, I compare the wages of undocumented immigrants to legal immigrants, controlling for differences in their observable characteristics. I use data from the American Community Survey (ACS), primarily from 2015-2019 — i.e., focusing on the years just prior to the onset of the COVID-19 pandemic to avoid issues related to data collection during that time period. Following the approach described in Borjas (2017), I identify “likely legal” and “likely undocumented” immigrants from the ACS based on individual characteristics, such as country of origin, receipt of Medicaid, etc. Using this individual-level legal status indicator, I show that although undocumented immigrants receive much lower wages than legal immigrants, nearly all of this gap is due to differences in individual characteristics, notably education level and English proficiency. Conditional on these characteristics, I find a gap of only 3%, approximately, in wages between legal and undocumented immigrants.

Second, I estimate the degree to which English language learning might accelerate among immigrants who receive amnesty, which in turn would likely lead to higher wages. Newly legalized immigrants might desire to invest more strongly in English language ability due to longer expected stays in the United States. To estimate how much additional English proficiency we might expect from an amnesty program, I first compare English proficiency levels of undocumented immigrants with those of otherwise similar legal immigrants, finding that undocumented immigrants have significantly lower levels of English ability. I then revisit the evidence from IRCA to see if English ability improved for immigrants legalized under that program. Using the 1990 and 2000 censuses, I find that IRCA did appear to lead to a meaningful improvement in English proficiency among qualifying immigrants, equal to around half of the current conditional gap in English proficiency between legal and undocumented immigrants. However, this increase in English proficiency would only raise wages by approximately 1%; even if the entire (conditional) English proficiency gap were eliminated, we would only expect to see a 2% increase in wages.

Third, I estimate the size of the earned income tax credit (EITC) that newly legalized immigrants might expect to receive. Households headed by currently undocumented parents do not qualify for the EITC; as such, amnesty would provide these households — especially low-income households with multiple children — with a substantial increase in household income through the EITC. Using household data from the ACS, I estimate that, on average, undocumented households would qualify for $1,175 per year in EITC payments.

Overall, my results suggest that although there is scope for the legalization of undocumented immigrants to improve their labor market performance, the size of this improvement is likely to be modest: Although undocumented immigrants have significantly lower wages than legal immigrants, the vast majority of this discrepancy is driven by differences in productive characteristics — primarily, education level — on which an amnesty program would have little effect. I estimate that undocumented wages would rise by a total of 4%-5% as a result of an amnesty program, which would translate to around $14 billion per year in additional earnings. Qualifying for the EITC would represent a meaningful improvement in the incomes of current undocumented immigrants, especially those with the greatest need.

However, it is worth emphasizing that these estimates should be treated with caution, given the difficulty of identifying undocumented immigrants in survey data and forecasting both how undocumented immigrants would respond to amnesty as a group, and how the economy as a whole, including current legal immigrants especially, would be impacted. Most of the literature that explores the potential returns of an immigrant amnesty program examines prior programs, such as IRCA, whereas this paper’s goal is to estimate the returns from a hypothetical amnesty program several decades after the most recent widespread immigrant amnesty. This caveat noted, and assuming that my procedure for imputing immigrant status is reasonably accurate, my results suggest that the returns from an amnesty program are likely to be modest, given that the legal-undocumented wage gap, conditional on individual characteristics, is quite small.

The paper is structured as follows: To provide historical context on the topic of immigrant amnesty, both in the United States as well as internationally, I review the literature on the economic returns from previous amnesty programs in Section 2. In Section 3, I discuss my count of the undocumented population. Section 4 discusses the data and methodological considerations. Section 5 provides the results, and Section 6 concludes.

Historical Evidence on Economic Returns From Amnesty

Immigration Reform and Control Act (IRCA) of 1986

Perhaps the best-studied and most well-known amnesty program, especially in the U.S. context, is the Immigration Reform and Control Act of 1986. Notably, this act made it illegal for employers to knowingly hire undocumented immigrants. But the main provision of the act, at least for the purposes of this paper, is that it provided amnesty to over 2 million undocumented immigrants: Those who arrived prior to 1982 — four years before the act was signed into law by President Ronald Reagan — with basic knowledge of U.S. civics, English proficiency, and no criminal history were eligible for amnesty. As it is today, Mexico was the largest source of undocumented immigrants when IRCA was passed, and immigrants from Mexico were by far the largest recipients of amnesty from IRCA.[2]

Numerous academic studies have reviewed IRCA’s economic outcomes for amnesty recipients, aided in part by the U.S. Department of Labor’s Legalized Population Survey (LPS), a study of over 6,000 immigrants who received legal status through IRCA in the late 1980s.

The literature has consistently found a positive effect of amnesty on the economic outcomes of newly legalized immigrants. Rivera-Batiz (1999), using the LPS and the 1990 U.S. census, documents that, prior to legalization, legal Mexican immigrants had wages that were 41% higher than undocumented Mexicans. Further, although undocumented Mexicans had lower levels of education and English proficiency, less than half of this large wage gap was attributable to individual characteristics. Newly legalized undocumented immigrants (both men and women) experienced significant wage growth following amnesty, driven mostly by legal status itself and less so by changes in individual characteristics.

Kossoudji and Cobb-Clark (2000), also using the LPS, explore how amnesty impacted occupational mobility. Prior to amnesty, undocumented Mexican immigrants had high occupational mobility, but within a restricted set of traditionally immigrant-concentrated occupations. After amnesty, legalized immigrants moved up the occupational ladder. These results highlight that legalization, by opening more occupations to previously undocumented immigrants, is a channel through which wages could grow.

Kossoudji and Cobb-Clark (2002) also study the effects of IRCA amnesty on wages, again using the LPS as well as the 1979 National Longitudinal Survey of Youth (NLSY). The NLSY sample consisted of Latino men and provided a comparison group to help isolate the effect of amnesty on wages, controlling for other factors. They find a substantial wage penalty for being undocumented, ranging from 14%-24%, and that amnesty resulted in wage growth of approximately 6%.

Amuedo-Dorantes, Bansak, and Raphael (2007) examine the gender dimension of IRCA, once again using the LPS and the 1979 NLSY to construct a comparison group. They find that among IRCA recipients, employment rates fell for both men and women relative to the comparison group. Newly legalized women were more likely to exit from the labor market, suggesting weaker labor force attachment after amnesty. However, they estimate — after correcting for selection into employment using marital status and family size — that between 1987 and 1992, the wages of legalized immigrants grew 9% more than the comparison group for men and 21% more for women, again suggesting that legalization led to a meaningful increase in wages among newly legalized workers.

Lozano and Sorensen (2011) estimate the value of legal immigration status utilizing a two-step procedure to identify undocumented immigrants. First, they compare Mexican immigrants who arrived just prior to qualifying for IRCA (1980-1981) with those who arrived just after and thus did not qualify for IRCA (1982-84). Second, they use data from the Mexican Migration Project — a survey conducted in migrant-sending communities in Mexico that contains information about legal immigration status in the United States — to estimate the relationship between demographic characteristics and legal status. They combine these estimates with 1990 and 2000 U.S. census data and predict the likelihood that the individual in the census is a legal immigrant. They employ a triple-difference approach and find that IRCA resulted in a 20-log-point increase in long-run earnings among Mexican immigrants, mostly due to increases in occupational wages. As suggested by Kossoudji and Cobb-Clark (2000), Lozano and Sorensen (2011) also find evidence that job mobility is a key driver of post-amnesty wage growth.

Pan (2012) also uses the U.S. census to study the effects of IRCA, but examines human capital in addition to earnings. Using the 1990 and 2000 censuses and focusing on Mexican and Central American immigrants, he finds that arriving prior to 1982 — and thus qualifying for IRCA — resulted in an increase in the probability of English proficiency of around 4% for men; for women, the difference was not statistically different from zero. Though a relatively modest change, this increase in English proficiency is consistent with greater investment in human capital following legalization.

Finally, Cascio and Lewis (2019) study the effects of IRCA on the receipt of the earned income tax credit. They find that, although little additional revenue was collected in taxes as a result of IRCA, the program did raise family incomes — especially for families with children, who are eligible for a greater credit — by allowing these families to qualify for the EITC.

Deferred Action for Childhood Arrivals (DACA)

While IRCA was by far the largest amnesty program in U.S. history, the Deferred Action for Childhood Arrivals program more recently provided partial amnesty to nearly 2 million undocumented immigrants. Introduced as an executive action by President Barack Obama in June 2012, DACA, under the guise of “prosecutorial discretion,” allowed immigrants who met program requirements to avoid deportation and be granted a work permit. To be eligible for DACA, immigrants must have arrived before the age of 16, been under the age of 31 on June 15, 2012, be enrolled in school or have a high school degree (or equivalent), and have no major criminal convictions. Although beneficiaries of DACA have not been granted permanent residency or a path to citizenship, the program has provided them relief from the threat of deportation as well as legal authorization to work.

As a form of quasi-amnesty, the experience of DACA recipients may inform the effects of a broader amnesty program. Two considerations are worth noting, however. First, DACA recipients, by design, are young, arrived in the U.S. at a relatively young age, and have at least a high school level of education; as such, the DACA-eligible population differs meaningfully from the general population of undocumented immigrants, who tend to be older and less educated and arrived at a later age. Second, the legality of the DACA program has been in question since its inception, with several states quickly filing lawsuits to challenge it and President Donald Trump seeking to end it early in his presidency.[3] It is plausible that DACA recipients may benefit more from an amnesty program than older recipients, given their young age and the longer window of time to reap the benefits of greater occupational mobility and higher investments in country-specific human capital. But to the extent that recipients of DACA have had (reasonable) suspicion that the program may not continue indefinitely, the impact of DACA on labor market outcomes may be muted compared to a broad, permanent amnesty program such as IRCA.

Keeping these caveats in mind, it is informative to explore the impacts of DACA on the labor market outcomes of recipients. Pope (2016) uses ACS data from 2005-2014 to separate DACA-eligible immigrants from DACA-ineligible immigrants of a similar age. Comparing the outcomes of these groups after DACA was implemented, he finds an increase in labor force participation and a reduction in unemployment for the DACA-eligible group, though little effect on school enrollment. Amuedo-Dorantes and Antman (2017), however, find that DACA reduced the probability of school enrollment for eligible recipients, consistent with immigrants lacking legal status moving away from employment and toward schooling, while Kuka, Shenhav, and Shih (2020) find that DACA resulted in a significant increase in both high school attendance and graduation.

Ortego, Edwards, and Hsin (2019), using a model of work, college, and nonemployment, estimate that DACA increased GDP by 0.02% — which, though a small amount overall, amounts to $7,454 per legalized worker. They find that DACA increased wages by 12% for recipients. Borjas and Cassidy (2019) find that by 2016, the wage gap between legal and undocumented immigrants fell by 4.5 percentage points for those who were DACA-eligible, representing most of the 6.8% wage penalty at the time DACA was implemented.

Villaneuva and Wilson (2023) track the impacts of DACA on both job and geographic mobility. They find that relief through DACA led to a roughly 20% increase in the cross-state mobility of likely recipients, with moves into above-median average-wage public use microdata areas (PUMAs) increasing more than moves into below-median average-wage PUMAs. As emphasized by Kossoudji and Cobb-Clark (2000) and Lozano and Sorensen (2011) for IRCA recipients, Villaneuva and Wilson (2023) also find that DACA recipients enjoyed an increase in their median occupational earnings, as well as a movement into occupations that require occupational licensing, notably teaching and nursing. This result again emphasizes the role of occupational mobility in the returns from amnesty.

Nicaraguan Adjustment and Central American Relief Act (NACARA)

Though affecting a smaller population than either IRCA or DACA, the 1997 Nicaraguan Adjustment and Central American Relief Act (NACARA) also provided amnesty to a select group of immigrants. This program targeted immigrants from Nicaragua, Cuba, Guatemala, and El Salvador, as well as immigrants from former Soviet bloc countries, and was available to nearly half a million immigrants.

Kaushal (2006), using data from the U.S. Census Bureau’s Current Population Survey (CPS) from 1996-2002, finds that NACARA raised the wages of recipients by 3% and their weekly earnings by 4%. Further, the effects showed significant heterogeneity by education level, with those without a high school degree showing little to no change in wages or earnings, while recipients with a high school diploma or higher degree enjoyed a 5% increase in wages. Kaushal finds only modest effects on the employment rates of recipients.

International Evidence

Undocumented immigration is a phenomenon common to many immigrant-receiving nations, and so, not surprisingly, there are several amnesty programs in other countries worth studying. Devillanova, Fasani, and Frattini (2018) explore the effects of a 2002 amnesty program in Italy that resulted in over 700,000 applications. This amnesty required employment, and the application was filed by employers, not applicants themselves. Expectedly, this amnesty program resulted in a significant increase in the probability of being employed.

In 2004, the Spanish government implemented an amnesty program that legalized approximately 600,000 immigrants. Monras, Vazquez-Grenno, and Moreno (2018) find that the amnesty increased the mobility of immigrants to low-immigrant provinces: For each legalized immigrant, they estimate that 0.36 immigrants left provinces with a high-immigrant population. This is consistent with evidence from IRCA and DACA that emphasizes the importance of geographic mobility after amnesty.

Measuring the Undocumented Population

Identifying undocumented immigrants using publicly available data is difficult, and necessarily done with error: Some legal immigrants might be identified as undocumented and vice versa. Nevertheless, a methodological approach is needed to proceed with forming an estimate for the wage returns from amnesty.

This paper follows the approach used in Borjas and Cassidy (2019), who use data from the ACS. Their methodology is closely based off the method used by Borjas (2017), which itself ultimately derives from the so-called “residual method” pioneered by Jeffrey Passel and Robert Warren. In brief, the residual method proceeds by first estimating, using U.S. immigration data, how many legal immigrants are likely to be in the country at a given time. Meanwhile, U.S. government surveys (notably, the CPS, U.S. census, and ACS) provide estimates for the actual size of the immigrant population each year. Comparing these two values provides an estimate for the size of the undocumented immigrant population. A drawback of this approach is that it does not provide information about whether an individual immigrant is likely to be legal or undocumented, which precludes performing individual-level analyses.

This residual method was extended further and used to produce an individual-level identifier of likely undocumented immigrants (Passel and Cohn 2014). Borjas (2017) — using the Annual Social and Economic Supplement (ASEC) of the CPS file constructed by Passel and others, which contained their “likely undocumented” variable — reverse engineers this process and identifies the relatively small number of variables (e.g., country of origin) that were most relevant in labeling immigrants as either legal or undocumented in Passel’s CPS file. He uses these characteristics to assign “likely legal” status and “likely undocumented” status to individuals.

The methodology proceeds as follows: All immigrants are initially assumed to be undocumented. If any of the following conditions hold, then they are instead classified as legal, and those who do not satisfy any of the following remain classified as undocumented.

1. The person arrived before 1980.
2. The person is a citizen.
3. The person receives Social Security benefits, Supplemental Security Income (SSI), Medicaid, Medicare, or military insurance.
4. The person is a veteran, or is currently in the U.S. armed forces.
5. The person works in the government sector. 
6. The person was born in Cuba (as practically all Cuban immigrants were granted refugee status).
7. The person’s occupation requires some form of licensing (such as physician, registered nurse, air traffic controller, or lawyer).
8. The person is a likely H-1B visa-holder, as determined by the following: 1) the immigrant works in an occupation that commonly employs H-1B visa holders (such as computer programmer); 2) the immigrant has resided in the United States for six years or fewer (i.e., the maximum length of time an H-1B visa is valid); and 3) the immigrant is at least a college graduate.
9. The person’s spouse is a legal immigrant or citizen.

By completing this procedure for each immigrant, I created a variable that indicates whether an individual is “likely legal” or “likely undocumented.” For brevity, I excluded “likely” throughout the paper and labeled these immigrants either “legal” or “undocumented,” although I acknowledge that this procedure will invariably produce errors.

Data and Methodology

In this section, I describe the data used in my analysis, as well as the methodological approach I used to form my estimates for the wage returns from an immigrant amnesty program.

Data: U.S. Census

My primary source of data is the 2015-2019 U.S. American Community Survey, downloaded from the Integrated Public Use Microdata Series (a database that provides census and survey data from around the world) (IPUMS; Ruggles et al. 2023). Though data from more recent ACS years was available when writing this paper, the onset of the COVID-19 pandemic created significant issues with data collection. Thus, my primary results rely on the most recent pre-COVID five-year ACS sample.

For my estimation sample, I include only immigrants (i.e., I drop all native-born Americans). I focus only on immigrants since I wish to compare undocumented and legal immigrants and use this comparison as a basis for estimating the potential impact of an amnesty program on their earnings. Put differently, the group of individuals that I expect undocumented immigrants would most resemble after receiving legal status would be current legal immigrants, and hence they are the most natural comparison group.

My sample includes immigrants aged 18-64. My full sample includes both those who are in and out of the labor force. However, when analyzing wages, weeks worked, or usual hours worked, I focus on a subsample of immigrants who report positive annual wage income, positive weeks worked, and positive usual hours worked.

Notes on Methodology

The methodological approach used in this paper is intended to compare outcomes between undocumented and legal immigrants, including wages, labor force participation, and English proficiency. Undocumented and legal immigrants differ on many critical dimensions ­— including education level, years in the U.S., and country of origin — that could potentially influence my outcomes of interest (notably, wages). For example, compared to legal immigrants, undocumented immigrants are significantly more likely to not have a high school level of education. Controlling for these characteristics allows for a more direct comparison of the potential impact of legal status on my key outcome variables, and thus for measuring the potential effects of an amnesty program.

Some notes of caution are important to discuss. Controlling for a rich set of characteristics, such as education, age, etc., does not necessarily imply that the remaining differences in, say, wages, can be entirely attributable to legal status. Indeed, it is possible that there are some characteristics, like education level, that differ systematically between our groups and are strongly related to our outcomes of interest, but I am not able to control for this due to the lack of data; that is, my analysis may suffer from omitted variable bias.

The approach used in this paper implicitly assumes that, controlling for differences in individual characteristics, differences between legal and undocumented immigrants are attributable to their different legal status, and that by removing this difference (i.e., implementing an amnesty program), these two groups should, conditionally, be the same. But it is entirely possible that, even without the legal differences between these groups, there will still be differences in wages. The reason for this is that both groups are selected samples of their source country, i.e., not a random sampling of individuals from their country of origin. The immigration process selects individuals who would likely perform relatively well in the U.S., perhaps due to differences in skills or connections with friends and family, or who have a relative preference for living in the U.S. compared to their source country. These selection pressures differ between immigrants who are in the U.S. legally versus those who are undocumented; as such, these groups might differ systematically in ways that are difficult to observe. It is entirely possible that, conditional on characteristics such as education level and age, undocumented immigrants could perform better than legal immigrants after receiving amnesty, and thus my results might understate amnesty’s true payoff. Naturally, my results could also overstate the payoffs.

Another issue relates to survey nonresponse bias and how that may impact the estimates of the labor market returns resulting from an amnesty program. Specifically, though undocumented immigrants may be less likely to respond to surveys such as the U.S. census and the CPS, among those who do respond, there may be selection bias. Undocumented immigrants who are at particularly high risk of deportation, or who at least have a greater fear of deportation, may be less likely to respond to government surveys than other undocumented immigrants. They may also benefit more from an amnesty program that resolves their immigration status. Under these conditions, which seem plausible, my estimated returns from amnesty will be understated.

These concerns are serious and certainly should not be taken lightly. As such, the results in this paper should be interpreted as approximations, subject to potentially large errors. Continued empirical work on this topic should help to provide more robust estimates of the potential returns from amnesty.

Results

Summary Statistics

I begin with a basic comparison of legal and undocumented immigrants in my sample. Table 1 shows key summary statistics, separated by legal status and gender. There are striking differences between the groups.

Table 1 — Descriptive Statistics

 

Notably, among both men and women, undocumented immigrants have a much lower level of education: Over a third of undocumented immigrants lack a high school degree, compared to only 16%-17% of legal immigrants. English language fluency is also significantly lower among undocumented immigrants, with 55%-58% of legal immigrants and only 34%-36% of undocumented immigrants reporting speaking English very well or speaking only English. Undocumented immigrants are also approximately four years younger on average and have been in the U.S. for approximately five fewer years.

Among the employed sample, undocumented and legal immigrants work a similar number of hours and weeks per year, although among undocumented women, the number of weeks worked per year is slightly lower. The most notable difference is in wage and annual wage income: Among men, legal immigrants outearn undocumented immigrants by around $20,000 per year, while among women, the gap is smaller but still substantial at approximately $13,000.

Wage Differentials

Table 1 illustrates a large gap between legal and undocumented immigrants in wages, but also shows large differences between these groups in important characteristics, notably education level and English language ability. To get a better sense of how much a lack of legal status may impact wages, I estimate the following Mincerian wage regression:

log w_i = β_XX_i + β_LL_i + ɛ_i

Here, w_i is the wage of person i, X_i is a vector of individual characteristics, and L_i is a dummy variable that equals one if the individual is a legal immigrant, and zero otherwise. I include in vector X_i education level (five categories), English language proficiency (four categories), state of residence, age and years since migration (both as third-order polynomials), and birthplace. The coefficient of interest is β_L, which is my measure of the returns from legal immigration status and hence, the preliminary estimate of the returns from an amnesty program.

I compare the coefficient on the legal variable, β_L, before and after the inclusion of the individual controls (i.e., X_i). Instead of sequentially adding characteristics and observing how the coefficient on legal status changes — which can cause misleading interpretations of the data — I follow the methodology from Gelbach (2016) to decompose the change in the legal coefficient into the covariate group. Essentially, this approach tells us how much of the gap in wages between legal and undocumented immigrants can be attributed to education level, English proficiency, years since migration, etc.

The results are shown in Table 2, again separately for men and women. The top portion of the table shows the wage difference between legal and undocumented immigrants without any controls (“Difference”), the amount of that difference that can be explained by the individual controls (“Explained”), and the amount that remains unexplained (“Unexplained”). For men, the difference in wage is 0.297 log points, while for women it is 0.305 log points. Adding our controls, I find that the wages of legal immigrants are 2.8% higher for men and 2.5% higher for women (see row “Unexplained” in Table 2). These results suggest that, though undocumented immigrants earn substantially lower wages than legal immigrants, nearly all of this difference can be attributed to differences in individual characteristics, and only a relatively modest gap of under 3% persists when accounting for these differences.

Table 2 — Undocumented Wage Penalty Decomposition

 

 

The bottom portion of Table 2 decomposes how much each covariate group contributes to the change in the legal variable coefficient, i.e., how much each group contributes to the explained portion of the legal-undocumented wage gap. Not surprisingly, differences in education level play by far the largest role for men and women, explaining over a third of the wage gap for both genders. To be precise, differences in education level explain 12.4 percentage points of the total wage gap between legal and undocumented men and 10.6 percentage points of the wage gap for women. English language proficiency is the next largest contributor, explaining 6.0 percentage points of the gap among men and 5.4 percentage points of the gap among women. Years since migration, birthplace, and age also contribute significantly to the wage gap for both men and women, though typically less than half of the amount explained by education.

The previous regression results estimated the wage penalty to undocumented status based on the conditional mean; however, it may also be instructive to see how legal status affects wages at different income levels across the wage distribution. I do this by estimating quantile regressions at four quantile values: 0.2, 0.4, 0.6, and 0.8, again for men and women respectively. In short, instead of estimating the conditional mean, as is the case with ordinary least squares, a quantile regression estimates a conditional quantile. This approach allows me to estimate how amnesty might impact wages for workers at different parts of the wage distribution. The results are shown in Figure 1.

Figure 1 — Undocumented Wage Penalty Across the Wage Distribution

 

For both men and women, we observe that the effect of legal status grows as you move up the wage distribution: At the 20th percentile, it results in increases of 2.6% for men and 1.8% for women, while at the 80th percentile, it results in increases of 4.5% for men and 3.2% for women. These results indicate that, conditional on the set of individual controls, the penalty for being undocumented is greater for those higher in the wage distribution. As such, we might expect that amnesty would benefit these individuals more than those near the bottom of the distribution.

Overall, I find that there is a modest but positive premium for having legal immigrant status, conditional on standard individual controls, and thus there is likely some scope for improved wages resulting from an immigrant amnesty program. In the next few sections, I look deeper into the data and explore how legal status relates to occupational attainment, labor force participation, hours worked, and English language ability.

Occupational Attainment

The occupational attainment restrictions undocumented immigrants face may lead to significant economic costs to both these workers and the economy as a whole. Occupational license requirements and the need to have a driver’s license makes employment in certain occupations difficult for undocumented immigrants. Moreover, undocumented immigrants may avoid jobs that involve contact with the public, fearing a greater risk of detection and deportation. In fact, Lozano and Sorensen (2011) estimate that IRCA led to an increase of approximately 20 log points in the earnings of eligible immigrants, due primarily to the types of jobs they were able to obtain. As such, it is worthwhile to both document the extent to which undocumented immigrants differ in their occupational attainment relative to legal immigrants and to provide an estimate of how wages might improve among undocumented immigrants due to occupational changes resulting from amnesty.

There are a number of ways to measure occupational attainment. One parsimonious method is the task-based approach: This methodology assigns a vector of task requirements to each occupation by describing the types of activities performed on the job. There is an extensive literature that makes use of this task-based approach, including in the immigration context.[4] A key advantage of this methodology is that it helps to dramatically simplify the analysis of occupational differences by reducing hundreds of occupations to a small vector of tasks. It also allows for a measure of similarity between occupations based on the similarity of the tasks performed in each occupation.

The source of task information is the U.S. Department of Labor’s Occupational Information Network (O*NET), a database that contains detailed characteristics of the tasks required to perform various occupations. There are many ways to simplify O*NET’s rich information into a small, manageable vector; I follow Imai, Stacey, and Warman (2019) and Cassidy (2019) and use three job “tasks”: analytical, interactive, and manual.[5] Examples of the job requirements include deductive reasoning, number facility, and analytical thinking for the analytical task; oral comprehension, written comprehension, and speech recognition for the interactive task; and static strength, stamina, and handling moving objects for the manual task.

After the task assignment procedure is completed, each occupation code has a three-dimensional vector of tasks that describe that occupation. Now, for each worker in my ACS sample, I assign a job task based on their occupation code. (Note that one major limitation of this approach is that, because task assignment is done at the occupation level, no within-occupation variation in the job task is permitted; unfortunately, data that contains job task information at the individual level is rare, and to my knowledge, no data is available that includes individual-level job task information as well as some reasonable measure of likely legal immigrant status.[6]) Lastly, the task requirements are scaled so that, in my sample, each task has a mean of zero and standard deviation of one.

As with the exercise performed in Section 5.2, I calculate the unconditional differences in task requirements between legal and undocumented immigrants. I then calculate the differences, controlling for the same individual characteristics as before, and I decompose the relevance of each characteristic group in explaining the change in the legal coefficient between the base and full model. These estimates are performed separately for men and women. Results are shown in Table 3.

Table 3 — Undocumented Task Differences Decomposition

 

On average, legal immigrants work in occupations with significantly higher analytical and interactive task requirements and significantly lower manual task requirements. The analytical and interactive task differences are much greater among women than men, although the manual task differences are narrower among women. Recall that the tasks have a mean of zero and a standard deviation of one; thus, for the analytical task, the difference between legal and undocumented immigrants is over one-third of a standard deviation for men (0.39) and over half of a standard deviation for women (0.54). The interactive task differences are even greater, at nearly half a standard deviation for men (0.48) and 0.62 of a standard deviation for women, while the manual task differences are 0.45 and 0.34 standard deviations lower for undocumented men and women, respectively. For added context, the differences in analytical, interactive, and manual task requirements between high school graduates and bachelor’s degree holders are approximately one standard deviation for each task; thus, these results suggest substantial occupational differences by legal status.

Of course, as with the differences in wages, the unconditional task differences do not tell the whole story. Adding the same set of controls included in the wage estimations in Section 5.2, the task differences between legal and undocumented immigrants shrink substantially, although they do persist: For men and women, respectively, with controls, they are 0.07 and 0.16 for the analytical task, 0.11 and 0.19 for the interactive task, and -0.07 and -0.05 for the manual task. Consistent with the earlier wage results, education plays the largest role in explaining the change in the legal coefficient between the base and full model, followed by English proficiency and birthplace (which play quantitatively similar roles), while years since migration plays only a minor role.

What can these task differences tell us about the impact of amnesty on wages? A simple exercise that can shed light on amnesty’s effect on wages by means of changing occupation would be to assume that, upon legalization, the conditional task requirements of legal and undocumented immigrants would equalize. Of course, this is unlikely for a number of reasons, including the cost of job mobility, occupation-specific human capital, etc. But nonetheless, this exercise will provide at least a ballpark estimate for how changes in job tasks resulting from amnesty may affect wages.

To perform this estimate, I repeat the Mincerian log wage regressions from Section 5.2, but in addition to the original set of controls, I add controls for analytical, interactive, and manual task requirements. I run these estimations on legal immigrants only, under the assumption that, once amnesty is provided, the returns to job tasks among newly legalized immigrants will resemble the current returns to job tasks of legal immigrants.[7] Combining the coefficients on the job task variables from this regression with the conditional task requirement gaps from Table 3, I form an estimate for the change in log wage resulting from equalizing job tasks. The results are shown in Table 4, where again the estimations are performed separately for men and women. The returns are much higher for analytical tasks than for interactive or manual tasks, a consistent finding in the literature.[8]

Table 4 — Log Wage Regressions with Occupational Tasks

 

Overall, the results are modest: For men, equalizing conditional job tasks between legal and undocumented immigrants would raise wages by 1.6%, with nearly the entire amount driven by the analytical task. For women, wages would rise by 3.8%, again driven almost entirely by the analytical task.[9] As with all the estimates in this paper, these results are highly speculative. But given the improbability of job tasks fully equalizing following amnesty, these results should be considered toward the upper bound. It should also be noted that it would be incorrect to interpret these results as impacts of amnesty beyond the results found for wage differences in Section 5.2; rather, it is likely that the wage gaps are driven in part from differences in occupational attainment, and closing the task requirement gap would be a channel through which the wages of undocumented immigrants would converge toward those of legal immigrants.

Labor Force Participation and Hours Worked

Borjas (2017), using the CPS and a legal status assignment procedure nearly identical to the one utilized in this paper, finds that undocumented men have a higher labor force participation rate than legal immigrant men, while undocumented women have a lower labor force participation rate than legal immigrant women. As discussed extensively already, legal and undocumented immigrants differ along many dimensions, and some of these differences may contribute to differing labor force participation rates. However, there may yet be variation between the groups left unexplained by individual characteristics, and as such, an amnesty program could lead to a change in labor force participation. Recall that both Amuedo-Dorantes, Bansak, and Raphael (2007) and Amuedo-Dorantes and Antman (2017) found that IRCA and DACA, respectively, may have led to reductions in labor force participation among legalized immigrants. Thus there is precedent for amnesty impacting this important labor market outcome. And if labor force participation increases among undocumented immigrants due to amnesty, that should result in higher household labor income.

My analysis repeats the approach from sections 5.2 and 5.3, except now my dependent variable is binary, equaling one if the individual is in the labor force, and zero otherwise. As before, I show the coefficient on the legal status variable for the base model and the full model, and I decompose the change in this coefficient attributed to each covariate group. The results are shown in Table 5.

Table 5 — Labor Force Participation Differences Decomposition

 

For men, I find no meaningful difference in the unconditional labor force participation of legal and undocumented immigrants; not surprisingly, adding controls does little to change the coefficient, which remains near zero. The results for women, however, are more interesting: Unconditionally, legal immigrant women have a labor force participation that is 9.0 percentage points higher than undocumented women, which, given the overall labor force participation rate of undocumented women at 60.6%, represents a 14.9% difference. However, I find no difference in labor force participation between these two groups of women in the full model. Of the 9.0 percentage point difference, around 2.6 percentage points can be attributed to years since migration and education each, while English proficiency explains 2.9 percentage points and birthplace explains 1.4 percentage points.

In sum, for men, there is currently little gap in the labor force participation rate between legal and undocumented immigrants, while for women, the gap is entirely attributable to individual characteristics. Thus, it seems unlikely that an amnesty program would have a meaningful impact on the labor force participation of currently undocumented immigrants.

Among those in the labor force and working, legal status could impact the usual number of hours worked per week. I repeat the previous analysis performed for labor force participation, except I now use usual hours worked per week as the dependent variable, and I restrict my sample to include only individuals with positive usual hours worked, weeks worked, and wage income. Results are shown in Table 6.

Table 6 — Usual Hours Worked Differences Decomposition

Source  American Community Survey, 2015-2019.
Notes  Standard errors are reported in parentheses. See notes from Table 2 for details. In this table, the dependent variable is usual weekly hours worked.

The unconditional differences in hours worked by legal status are minor, at only about a quarter of an hour per week for men and less than a tenth of an hour per week for women. Adding controls shrinks the gap for men to nearly zero, while for women, the controls result in legal immigrant women working 1.1 hours per week less than undocumented women, which, given the mean of 37 hours worked per week for women, represented a 2.7% difference. Thus, for men, an amnesty program would likely have little effect on hours worked. For women, it is plausible that hours worked might decrease, and accordingly lead to a decrease in labor income.

English Language Ability

The results described in the previous section suggest that the large wage gap observed between legal and undocumented immigrants can be attributed almost entirely to differences in socioeconomic characteristics. While certain factors, such age and birthplace, would not be changed by an amnesty policy, amnesty could eventually lead to changes in other characteristics. For example, granting legal status to current undocumented immigrants could incentivize those individuals to invest in English language fluency, since they might view their time in the U.S. as more permanent. This improved English proficiency should, in turn, result in higher wages for current undocumented immigrants.

As discussed above, undocumented immigrants have significantly lower levels of English proficiency than legal immigrants on average. However, these groups also differ on many dimensions (e.g., education level). As such, I repeat the exercise performed above on wages, job tasks, hours worked, and labor force participation, but now use a binary dependent variable that equals one if the individual either speaks only English or speaks English very well, and zero otherwise. Naturally, I exclude controls for English language ability. I estimate this model on our full sample, including individuals who are not in the labor force. Results are shown in Table 7.  

Table 7 — English Language Proficiency Differences Decomposition

 

Without individual controls, undocumented immigrant men are 22.7 percentage points less likely to be proficient in English than legal immigrant men, while the gap for women is only slightly lower, at 21.2 percentage points. Given the mean English proficiency rates among undocumented immigrants of only 35.8% for men and 33.8% for women, these differences imply that legal immigrants are 63.4% and 62.7% more likely to speak English very well or only English than undocumented immigrants, for men and women, respectively.

Adding individual characteristics narrows — but does not eliminate — these gaps: In the full specification, the gaps between undocumented and legal immigrants are 8.5 percentage points for men and 6.9 percentage points for women. Given the substantial returns in the labor force that result from English proficiency (see, for example, Bleakley and Chin 2004), an amnesty program could result in higher wages by leading to improved English ability.

Of the substantial literature on prior amnesty programs, both in the United States and abroad (discussed in Section 2), few papers speak to the impact of amnesty on subsequent acquisition of English language proficiency. One exception is Pan (2012), who uses the 1990 U.S. census to find that Latino immigrants arriving before the IRCA cutoff of 1982 were approximately 4 percentage points more likely to be proficient in English compared to those arriving after 1982, who did not qualify for IRCA. However, one concern with Pan’s (2012) results is that, even though duration of stay is controlled for, only the 1990 census is used; ideally, we would measure immigrants at a consistent time since migration, but the decadal structure of the census precludes that. Thus, to try and address this shortcoming, I revisit the effects of IRCA on English language proficiency using the 1990 and 2000 censuses.

I build on the approach from Lozano and Sorensen (2011), who use the 1990 and 2000 censuses to study the impact of IRCA using a difference-in-differences methodology. Their approach compares the outcomes of Mexican-born immigrants — the largest beneficiaries of IRCA — who arrived in 1980-1981 (and therefore qualified for IRCA) with Mexican-born immigrants who arrived in 1982-1984 (and therefore did not qualify for IRCA) using the 1990 census. But, since the IRCA-eligible group arrived earlier in the decade, differences between them and the 1982-1984 arrival cohort may be driven by duration of stay. Recall that both groups are measured in 1990, so the 1980-1981 cohort has been in the country for longer. To further expound this effect, they also use the 2000 census to include Mexican-born immigrants who arrived in 1990-1991 and those who arrived in 1992-1994 in their estimations; they assume that these cohorts would change in terms of English proficiency with duration of stay at the same rates as the 1980-1981 and 1982-1984 cohorts, respectively.

One concern with this approach is that, if the immigrant cohort that arrived in 1980-1981 had unusually high English ability compared to the 1982-1984 cohort, we could not separate that effect from the impact of IRCA, since we do not know their English ability upon arrival — only in the years 1990 and 2000. So, I include all immigrants in my analysis, and I control for year of arrival cohort, where my cohorts are: 1) 1980-1981, 2) 1982-1984, 3) 1990-1991, and 3) 1992-1994. This approach assumes that cohort-specific effects were common across source countries, though like Lozano and Sorensen (2011), I consider Mexican immigrants my “treated” group. Thus, by including immigrants from all countries, and not just Mexico, I can determine the cohort-specific effects that might contaminate my results. Of course, this is a strong assumption, though I believe it is more palatable than assuming no cohort effects were present between the 1980-1981 and 1982-1984 Mexican arrival cohorts.

Specifically, I estimate the following specification:

SpeaksEng_i = β_o + β_XX_i + β_MexMex_i + β_cohortCohort_i + β₁₉₉₀1990_i + β_Mex*1990Mex_i * 1990_i + β_Mex*EarlyMex_i * Early_i + β_{1990*Early*Mex}1990_i * Early_i * Mex_i + ɛ_i,

where X_i includes controls for age (as a third-order polynomial) and education level of individual i, Mex_i is a dummy variable that equals one if individual i was born in Mexico, and zero otherwise. Cohort_i is a vector of year of arrival cohort (described above), and 1990_i is a dummy variable that equals one if the survey year is 1990, and zero otherwise. Early_i is a dummy variable that equals one if the immigrant arrived in the early part of the decade, i.e., during cohorts 1 (1980-1981) or 3 (1990-1991), and zero otherwise. The coefficient of interest is β_{1990*Early*Mex}, which is the coefficient on the triple-interaction term of Mexicans who arrived early in the decade and are observed in 1990 — i.e., who arrived in 1980-1981 and therefore qualified for IRCA. This coefficient measures how much more English language acquisition these IRCA-qualifying immigrants experienced by 1990, partialling out the effects of arriving early in the decade, arriving from Mexico, and arriving during the 1980-1981 cohort. A positive coefficient on this variable would indicate that IRCA did, indeed, result in greater English language acquisition among qualifying immigrants.

My sample includes immigrants who arrived in one of the four cohorts defined above and who were aged 16-44 at the time of arrival. I include each cohort only once in the estimation, i.e., though cohorts 1 and 2 are interviewed in both the 1990 and 2000 census samples, I omit these cohorts from the 2000 census. Finally, I perform the estimation separately for men and women.

The results are shown in Table 8. The coefficient on my triple interaction, β_{1990*Early*Mex}, is 0.048 for men and 0.029 for women, where the results are statistically significant at the 1% level for men and the 5% level for women. Interestingly, and perhaps not surprisingly, these results are quite similar to the values from Pan (2012) of 0.039 for men and 0.014 for women (see Table 2, columns 2 and 4, in Pan 2012). In the 1990 census, among the estimation sample, the English proficiency of Mexican immigrants was only 18%-20%, approximately, and thus a 4.0 percentage point difference represents approximately a 25% increase.

Table 8 — English Proficiency Improvement Resulting from IRCA

 

How might these results translate to amnesty today? Among Mexican immigrants with the same age at migration values as the previous estimation, levels of English proficiency in the 2019 sample are similar to those in the 1990 census: Approximately 20% report being proficient in English. However, considering just those who are likely undocumented, only 14% report being proficient in English. Thus, an improvement of 4.0 percentage points in English language proficiency in the first decade following legalization may be a reasonable expectation.

Translating an improvement in English proficiency of 4.0 percentage points into wages requires an estimation for the return from English language ability in the labor market. One approach is to estimate a Mincerian wage regression and control English proficiency, but this methodology is prone to ability bias if some characteristics impact both English proficiency and ability in the labor market — which would in turn bias the estimated return from English ability upward (omitted variable bias). However, English proficiency could be measured inaccurately, perhaps especially given that it is self-reported; this would bias the estimate toward zero (attenuation bias). Bleakley and Chin (2004), using the 1990 census and an instrumental variable strategy based on age at migration of childhood immigrants, find that the ordinary least squares (OLS) estimates understate the returns from English proficiency, i.e., that the attenuation bias exceeds the ability bias.

Thus, for my estimate of the results for English proficiency, I rely on a simple OLS estimation in which I control for English proficiency. I perform this estimation on the 2019 sample of legal immigrants only with positive earned income, weeks worked, and usual hours worked, and I include the controls described in Section 2. Results are shown in Table 9. I find that the returns from English proficiency, i.e., from either speaking English very well or speaking only English, are 18.2% for men and 18.6% for women. Multiplying this value by 4.0 percentage points (the estimated improvement in English ability that would result from amnesty) yields just under a 1% increase in earnings resulting from improved English language proficiency.

Table 9 — Log Wage Regressions, Returns from English Proficiency

 

A simpler exercise would be to assume that, in the extreme, an amnesty program eliminates all of the difference in English language proficiency between legal and undocumented immigrants that persists in the presence of individual controls. Recall from Table 7 that these unexplained differences are 8.5 percentage points for men and 6.9 percentage points for women; thus, under this assumption, and given the estimated returns from English proficiency of around 18% described above, we would expect less than a 2% increase in wages from improved English language ability.

In summary, I find evidence that: 1) undocumented immigrants do have meaningfully lower English proficiency levels than legal immigrants, even in the presence of controls for individual characteristics; 2) IRCA did lead to improved English ability among likely recipients, and thus we might expect a similar improvement from a contemporary amnesty program; but 3) the overall contribution of this improved English ability to the wages of undocumented immigrants is likely to be modest, on the order of 1%-2%.

Earned Income Tax Credit

A lack of legal immigration status restricts the public services available to undocumented immigrants; as such, amnesty would unlock many previously unavailable services. It is beyond the scope of this paper to explore the impact of amnesty on the receipt of each of these services. However, the earned income tax credit (EITC) bears directly on the central question of this paper: the effect of amnesty on labor market earnings. Cascio and Lewis (2019), using data from the IRCA amnesty, provide evidence that granting amnesty to previously undocumented immigrants did indeed raise their likelihood of claiming the EITC.

In brief, the EITC subsidizes the wages of low earners, depending on family composition — specifically, the number of minor children as well as income filing status (i.e., single versus married and filing jointly). The credit phases in rapidly at low income levels, significantly raising effective wages, until it reaches a maximum credit and then plateaus, remaining constant for a range of income. Eventually, the credit begins to decline (phases out), lowering a worker’s effective wage, until the credit reaches zero. The phase-in rate, maximum credit size, and phase-out rate all depend on filing status and number of children.

The ACS data used in this study is at the household level, and thus contains sufficient information to estimate the size of the EITC credit each household would be eligible for. Of course, a number of assumptions are required, since the ACS does not include tax filing information, and the EITC eligibility of some household structures, such as those containing extended families or renters, are difficult to determine with the available information.

I perform the estimation at the household level. I include only children aged 17 and under, and for adults, I keep only heads of household and spouses, if present. I assume that all children in the household, including stepchildren, adopted children, and siblings, are dependents of the household’s head of household and spouse. Finally, I assume that if both the head of household and spouse are present, they file taxes jointly, and otherwise that single-parent households file taxes individually. Household income is calculated as the sum of the total personal income of the head of household and spouse (if present).

Recall that if an individual’s spouse is a legal immigrant or a nonimmigrant, the legal status assignment procedure described in Section 3 means that the individual will also be legal; thus, either both the head of household and spouse must be classified as legal, or both must be classified as undocumented; therefore, we can think of households as being “legal” or “undocumented.” Note that undocumented parents can have “legal” children, if those children are born in the United States, but this household would still be classified as undocumented.

Results by legal status are shown in Table 10. Undocumented households would, on average, be eligible for an estimated $1,175 in EITC after receiving amnesty and thus qualifying for the credit. This value is significantly greater than that of legal households ($556), due both to lower household income (approximately $27,500 less for undocumented households than legal households on average), as well as the greater number of dependents among undocumented households (around 0.3 more per household on average). An EITC of $1,175 corresponds to a roughly 2% increase in household income among undocumented immigrants. Note, however, that this value is highly heterogeneous due to the nature of the EITC program: Among households with less than $30,000 in annual income, undocumented households would receive approximately $2,270 in EITC, which for this income group corresponds to a 15% increase in household income.

Table 10 — Estimated Average Earned Income Tax Credit Payments by Household Type

 

It is important to note that, although amnesty would allow undocumented immigrants to access the lucrative EITC program, this would be an income transfer from other taxpayers. Nonetheless, this would represent an increase in income for undocumented immigrants. There could be efficiency gains from the expanded EITC if it induced greater labor force participation: Bhardwaj (2022) finds that, following the 1996 welfare reform that restricted undocumented immigrants from receiving EITC, the labor force participation of undocumented immigrant women fell by 7 percentage points. Thus, it is plausible that reopening this tax credit to undocumented immigrants would help increase labor force participation. This increased labor force participation would lead to a further increase in income for currently undocumented households.

Conclusion

Undocumented immigrants represent a substantial fraction of the immigrants living in the United States. A large-scale amnesty program that would legalize their status is a commonly proposed policy. One of the arguments in favor of such a policy is that legalization would lead to improved labor market outcomes among currently undocumented immigrants. In this paper, I provide some speculative estimates of how large of an effect on wages we might expect from such an amnesty program.

Using American Community Survey data from 2015-2019 and imputing likely legal status using individual and family characteristics, I find that, although undocumented immigrants have significantly lower wages than legal immigrants, nearly all of this difference is driven by differences in individual characteristics, such as education level and English language proficiency. After correcting for differences in these productive characteristics, the wage gap left unexplained is under 3%. I also find that legal and undocumented immigrants have similar labor force participation rates, with or without controlling for individual characteristics, and while undocumented women have a much lower labor force participation rate than legal immigrants, accounting for individual characteristics eliminates that difference. Finally, hours worked are nearly identical for legal and undocumented immigrant men, while hours worked are slightly higher among undocumented women after controlling for individual characteristics.

Undocumented immigrants tend to work in occupations that are lower in analytical and interactive task requirements and higher in manual task requirements. Most, though not all, of these gaps disappear when controlling for individual characteristics. By simulating the effect on wages of an amnesty program that results in identical occupational task requirements, conditional on individual characteristics, I find that wages would rise by under 2% for men but by roughly 4% for women.

Undocumented immigrants are less likely to be proficient in English, even when controlling for other characteristics such as education level. Amnesty may induce immigrants to invest in productive country-specific human capital, particularly English language ability. To get a historical measure of how amnesty might affect English language acquisition, I revisit the IRCA amnesty using the 1990 and 2000 U.S. census samples. I find that, among immigrants who likely qualified for amnesty under IRCA, there was an increase of approximately 4.0 percentage points in the probability of speaking English very well, which is roughly half of the English proficiency gap left unexplained by individual characteristics. Assuming the same improvement occurs as a result of an amnesty program implemented today, this translates to an approximately 1% increase in wages; assuming complete convergence in (conditional) English ability following amnesty, wages would rise by close to 2%.

Amnesty would allow previously undocumented immigrants to apply for the earned income tax credit. Using household-level data from the ACS, I estimate that the average undocumented household would be eligible for approximately $1,175 in EITC, i.e., approximately 2% of current household income.

Overall, I estimate that the effects of amnesty on the labor market income of currently undocumented immigrants would be approximately 4%-5%, not including the income derived from the EITC. Given the estimated size of the undocumented population and their current yearly earnings, this translates to a total increase in labor income by as much as $14 billion per year.

These estimates are highly speculative and based on a legal assignment procedure that is inevitably imperfect. If the legal status were simply measured with error, as in a classical measurement error, then these estimates would suffer attenuation bias and so would be biased downward. In that case, we could expect a labor income increase from amnesty that exceeds 4%-5%. However, it is far from guaranteed that this assignment procedure is susceptible only to classical measurement error, and so assuming downward bias is not warranted.

Overall, I find that amnesty would likely lead to a modest — though not insignificant — improvement in the wages of currently undocumented immigrants. As such, it is important that the improved economic performance of undocumented immigrants be considered by policymakers when debating the value of a large-scale immigrant amnesty.

Endnotes

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[1] See “Map,” Toolkit: Access to Driver’s Licenses, National Immigration Law Center, https://www.nilc.org/issues/drivers-licenses/dlaccesstoolkit2/#map.

[2] See Warren and Passel (1987) and Passel and Cohn (2014).

[3] See “DACA Immigration Timeline,” National Immigration Law Center, https://www.nilc.org/issues/daca/daca-litigation-timeline/. 

[4] For a sample of papers that employ the task-based approach in the immigration context, see Warman and Worswick (2015), Cassidy (2019), and Imai, Stacey, and Warman (2019).

[5] I use the same task requirement vectors as Cassidy (2019) and assign tasks using the IPUMS-provided occ1990 variable. For more detailed information of how these tasks are calculated, I refer the reader to Cassidy (2019).

[6] See Autor and Handel (2013) and Cassidy (2017) for discussions on the importance of variation in job tasks within an occupation.

[7] Estimating the wage regression results on the pooled sample of legal and undocumented immigrants does not meaningfully change my results.

[8] The high returns for analytical tasks shown here are consistent with existing task-related literature, such as Warman and Worswick (2015).

[9] These calculations combine the results from the “Unexplained” row in Table 3 with the OLS coefficients from Table 4. For men, the values are: 0.070*0.214 + 0.109*(-0.020) + (-0.071)*(-0.045) = 0.0160 log points, or 1.6%. For women, the values are: 0.160*0.211 + 0.193*0.019 + (-0.054)*(-0.007) =  0.0378 log points, of 3.8%.

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This research is generously supported by a grant from the Charles Koch Foundation.

This material may be quoted or reproduced without prior permission, provided appropriate credit is given to the author and Rice University’s Baker Institute for Public Policy. The views expressed herein are those of the individual author(s), and do not necessarily represent the views of Rice University’s Baker Institute for Public Policy.