The hidden arithmetic of immigration: what the research actually shows

In April 1980, Fidel Castro announced that any Cuban who wanted to leave could do so from the port of Mariel. Roughly 125,000 people took him up on it. About 45,000 landed in Miami between May and September of that year, arriving fast enough to expand the city’s low-skill labor force by approximately 7% in a matter of months. It was the kind of event that economists call a natural experiment — a sudden, exogenous shock to a local labor market, uncontrolled by policy, large enough to observe, and historically bounded enough to study. A gift, in methodological terms.

David Card studied it. He found no meaningful wage effect on Miami’s native workers — the city absorbed the arrivals without the labor market moving in any statistically detectable direction. Card published in the Industrial and Labor Relations Review in 1990, and the Mariel boatlift became one of the most cited natural experiments in the immigration economics literature: a demonstration, researchers argued, of the labor market’s capacity to absorb large inflows without crushing wages.

Then George Borjas reanalyzed the same event, using the same underlying data, and found a wage drop of 10 to 25% for Miami’s high school dropouts. He published in the ILR Review in 2017. Same boatlift. Same city. Same years. Same publicly available data. Opposite conclusions.

The temptation here is to say: look, even the experts can’t agree. The science is contested. We’re all just choosing who to believe.

Resist that. The appearance of unknowability in the immigration economics literature has been genuinely useful — not to the researchers, who are running a real methodological dispute about something specific and traceable, but to everyone who has found in the Card-Borjas disagreement a license to dismiss whatever findings they dislike. The Mariel dispute concerns a narrow question: which workers should count as substitutable for newly arrived low-skill immigrants, and over what sample and time window should you measure it. That question is unresolved. It matters for a specific sub-debate about wage effects on a specific worker population.

It does not touch the crime literature. It does not touch the innovation literature. It does not touch fiscal findings across generations. Those parts of the evidence base are substantially more settled than the public debate suggests — and they’ve been left more or less untouched by the Mariel controversy because neither side of the political debate has found it convenient to engage with them honestly.

Crime: where the evidence is clearest and the discourse most wrong

Start with a puzzle. Immigrants — particularly low-skill immigrants and undocumented immigrants — are demographically younger, more male, and less educated than host-country native populations. Age, sex, and education are three of the most robust predictors of criminal offending that criminology has established. Young men without high school diplomas commit crimes at substantially higher rates than middle-aged women with college degrees. This is not contested. If you took a group with the demographic profile of the average low-skill immigrant and asked a criminologist to forecast their arrest rate, the forecast would be substantially above native-born average.

The empirical finding is that this forecast is wrong.

Olivier Marie and Paolo Pinotti reviewed the international evidence systematically in the Journal of Economic Perspectives in 2024, synthesizing studies from Europe, the United States, and elsewhere across multiple methodological approaches. Their conclusion: despite the demographic profile, immigration does not significantly impact local crime rates. This is not a weak result buried in confidence intervals. It is the modal finding across an extensive cross-national literature.

The puzzle resolves when you look at the mechanism. Economic conditions — wages, unemployment, poverty — are the dominant causal driver of crime at the population level. A research design that finds a correlation between immigrant share and local crime rates, without controlling for the economic conditions that both attract immigrants and drive crime, is not producing a neutral finding. It is confusing a poverty effect with an immigration effect. The immigrant populations who settle in economically distressed areas are correlated with crime not because they cause crime, but because economic distress causes crime and also draws immigrant labor. Control for economic conditions and immigrant status loses statistical significance.

And then there is self-selection. Migration is physically demanding, financially costly, and socially disruptive. The population that attempts it is filtered before it arrives: people with low agency, low risk tolerance, and low ambition are systematically less likely to survive the process of migration than people with all three. For undocumented immigrants specifically, the filtering is even more severe, and it operates through a mechanism unavailable to native-born citizens: criminal conviction means deportation. A native-born worker who gets convicted of a felony serves a sentence and returns to the labor market. An undocumented immigrant faces that sentence plus permanent removal. The structural cost of crime is higher for undocumented immigrants than for any other population in the country.

Both mechanisms — economic controls and selection — show up in the data.

Michael Light, Jingying He, and Jason Robey published a study in PNAS in December 2020 using Texas Department of Public Safety arrest records from 2012 to 2018. Texas checks the immigration status of all arrestees, making it one of the few states where you can actually separate undocumented immigrants from legal immigrants and native-born citizens in arrest data. The findings: relative to native-born US citizens, undocumented immigrants are over twice as unlikely to be arrested for violent crimes. The pattern holds across felony categories. Legal immigrants fall between undocumented immigrants and native-born citizens — lower crime rates than native-born Americans, higher than undocumented immigrants, which is exactly what the selection argument predicts: legal immigrants face some but not all of the structural deportation cost that depresses crime among undocumented populations.

Alex Nowrasteh of the Cato Institute analyzed conviction and arrest records across the period 2013 to 2022 using Texas Department of Public Safety data, published in Cato Policy Analysis No. 977 in June 2024. The Cato analysis is not a peer-reviewed journal article; it is a policy analysis from an advocacy-adjacent research institute. The numbers it produces: undocumented immigrant homicide conviction rate of 2.2 per 100,000; legal immigrant rate of 1.2 per 100,000; native-born rate of 3.0 per 100,000. Two independent administrative datasets — one using arrest records from 2012 to 2018, one using conviction records from 2013 to 2022; one peer-reviewed, one a policy analysis — point the same direction. That convergence is worth sitting with. It’s not one study replicating another, because they’re not doing the same thing. Different measurements of the same phenomenon, arriving at the same place.

None of this means immigrants don’t commit crimes. The finding is a population-level statistical result: the group commits crimes at a lower rate than the native-born average. Individuals within any group vary.

The "null by design" problem

There is a structural problem with the most common research design in the immigration-crime literature, and it runs in the opposite direction of what critics of immigration research usually claim. Sascha Riaz, writing in the British Journal of Political Science in 2026, analyzed the workhorse empirical approach: aggregate criminal offenses to a geographic unit, regress local crime rates on local immigrant share, interpret the coefficient. The problem is architectural. Immigrant populations are typically small fractions of the total population in any given area — 10%, 15%, sometimes 20% in high-immigration zones. If immigrants commit crimes at a rate meaningfully different from native-born residents, that difference gets arithmetically diluted before it enters the regression. It becomes a whisper inside a large noise term.

Riaz ran Monte Carlo simulations calibrated to real-world immigration and crime data. The result: these designs only achieve adequate statistical power — power sufficient to reliably detect a true effect — when the crime differential is implausibly large. Moderate differences, the kind that would be policy-relevant, fall below detection threshold.

This matters for how you read the crime literature. A design biased toward detecting nothing that nonetheless produces negative correlations — immigrants associated with lower crime — is producing stronger evidence than the p-value alone suggests. The result broke through an architecture that was stacked against finding it. The strongest designs in the literature: administrative records linked to individual immigration status (the Texas data), cross-national systematic reviews, natural experiments with sharp identification. Those designs consistently point the same direction.

Innovation: what the research shows that the debate ignores

The same self-selection mechanism that explains the crime finding — migrants filtered for agency, ambition, and risk tolerance — operates in the innovation literature too, but there’s a second layer. The US immigration system itself imposes additional filters on who enters the innovating workforce. The H-1B visa, the O-1 for extraordinary ability, the EB-2 national interest waiver, the F-1 student visa that feeds into OPT employment — these channels systematically select for technical credentials, demonstrable achievement, and, in the case of O-1 and EB-2, explicit evidence of exceptional contribution to a field. Elite US universities add another filter, drawing internationally competitive students who then often enter the US labor force through their institutional networks.

Self-selection describes who attempts migration. Institutional filtering describes who the US admission system accepts from that pool. Both filters are running simultaneously and both are visible in the patent and startup data.

Shai Bernstein, Rebecca Diamond, Abhisit Jiranaphawiboon, Timothy McQuade, and Beatriz Pousada analyzed US patent records from 1990 to 2016 in NBER Working Paper 30797 (2022), covered in the NBER Digest in March 2023. The numbers require sitting with. Immigrants are 16% of the US inventor population but generated 23% of all US patents filed during this period; quality-weighted — by stock market reaction to patent grants — the share rises to 25%. Include collaboration effects — patents produced by native-born inventors working with immigrant co-inventors, or influenced through network connections — and immigrants are responsible for 32% of total US patent output. Against a population share of 14–15%, they’re generating innovation at more than twice their presence in the country would predict.

The collaborator finding is the sharpest result in the study. When an immigrant co-inventor died, the productivity of their co-inventors fell by 17%. When a native-born co-inventor died, the drop was 9%. Immigrants aren’t merely adding to the total; they’re load-bearing within knowledge networks — linking research traditions, technical approaches, and collaborative relationships that native-born inventors couldn’t access independently. The loss of an immigrant co-inventor disrupts more, which says something specific about what role they’re actually playing.

In computers, communications, electronics, and medicine, immigrant inventors author approximately 30% of patents while comprising about 20% of the relevant workforce — 50% higher output per inventor than the national average. The entrepreneurship data is consistent: immigrants founded roughly 24% of new US businesses in 2019, up from 19% in 2007, reaching close to 29% by 2020 according to employer-household dynamics data compiled in the NBER Bulletin on Entrepreneurship (October 2024). Among venture-backed and AI-related firms, that share exceeds 40%.

Research by Zhao Jin, Amir Kermani, and Timothy McQuade — NBER Working Paper 33804, not yet peer-reviewed — analyzed nearly 91,000 US startups. Companies with mixed founding teams employ 20% more people after three years than native-only ventures; a second analytical method puts mixed-founder startups 44% larger and 35 percentage points more likely to secure funding. The direction is consistent with what the patent literature already establishes about immigrant-native collaboration effects.

Immigrants filing patents are also 10% more likely to cite international sources and twice as likely to collaborate with foreign inventors. Foreign researchers cite US-based immigrant patents 10% more often than native-authored ones. The network effect runs both ways.

This describes a specific immigrant population — the high-skill, institutionally filtered subset that arrived through US visa channels over this specific period. Different admission criteria would produce a different innovating population. The finding is real, well-documented, and large. It is also contingent on the selection regime that produced it.

Fiscal balance: real complexity, honest accounting

The crime and innovation literatures say something fairly clear. The fiscal literature says something genuinely complicated, and understanding what makes it complicated is itself useful — the complexity is structural, not manufactured by researchers covering for inconvenient findings.

The most comprehensive review of fiscal impacts is the 2016 National Academies of Sciences report, “The Economic and Fiscal Consequences of Immigration.” The summary finding is not the one that appears in either side’s public-facing arguments.

First-generation immigrants are net fiscal costs, primarily at the state and local level, primarily because of the cost of educating their children. This is not a small or disputable finding. K-12 education is expensive, immigrant families tend to be larger than native families, and the fiscal burden lands on school districts and state governments. A governor or state budget director who describes first-generation immigration as a fiscal cost to their government is accurately describing their budget reality.

The second generation — those children, grown into working adults — is “among the strongest economic and fiscal contributors” in the US economy, in the NAS report’s words. They pay more taxes than either their parents or the native-born average. The lifecycle picture across two generations is substantially positive.

The education gradient within the first generation is as large as any finding in the literature and almost never appears in public debate on either side. NAS 2016 estimates that a college-educated immigrant arriving at age 30 generates a net federal fiscal contribution of more than $800,000 over a 75-year horizon. A high-school dropout arriving at the same age generates a net fiscal cost of approximately $117,000 over the same period. Nearly a million-dollar difference. Age at arrival matters too: a 21-year-old with a high school diploma carries an estimated net present value of around +$126,000, a figure that declines as arrival age increases, because later arrivals contribute fewer working-age years before drawing on retirement-related programs.

The OECD evidence from European countries is consistent: immigrants admitted through labor channels — employment-based admission rather than family reunification or asylum — tend to be net fiscal contributors. The finding is sensitive to how each country defines “labor migrant,” but the directionality across countries is stable.

The time-horizon problem is at the root of most public confusion about immigration’s fiscal effects. Static analyses — immigrant households in any given year — consistently show costs: school-age children, lower initial earnings, social services concentrated in early settlement years. Dynamic analyses over multi-generational horizons consistently show net positive contributions. This is not a contradiction. It is two analysts answering two different policy questions. A state budget office asking about next year’s education expenditure gets a negative answer — correctly. A Social Security actuary asking about long-run pension solvency gets a positive answer — also correctly. Citing one while suppressing the other is advocacy dressed as analysis.

The federal/state accounting problem

The fiscal arithmetic of immigration operates against an accounting architecture that almost guarantees confusion. State and local governments bear the primary upfront cost of educating immigrant children — the largest single line item in the fiscal ledger for first-generation immigration. The federal government recollects relatively little of those education costs, because K-12 education is overwhelmingly a state and local function.
But the long-run fiscal payoff from that education investment — decades of income and payroll taxes from productive adults, Social Security contributions, Medicare contributions — flows primarily to the federal government, not to the state and local governments that paid the educational bill. Dallas Fed Working Paper 1704 (2017), "New Findings on the Fiscal Impact of Immigration in the United States," by Pia Orrenius and Madeline Zavodny, analyzed this structural mismatch. The paper finds that fiscal impact is negative at the local level but positive at the federal government level, with state and local governments bearing the bulk of education costs while federal revenues capture most of the long-run tax contribution.

A governor who calls immigration a fiscal drain may be accurately describing their jurisdiction's experience while drawing a false conclusion about the aggregate. The mismatch is not evidence that immigration is a net fiscal cost nationally. It is evidence that the division of fiscal responsibilities between levels of government has created a structural accounting problem in which costs and benefits land in different ledgers.

Wages: aggregate finding, distributional reality

The fiscal section required explaining structural complexity. The wages section requires something harder: naming concentrated losers while the aggregate finding looks benign. The previous sections went where the evidence is strongest — and wages are where honest engagement becomes most costly to give, because the honest account requires naming specific harm that advocates regularly omit from the literature they claim to represent.

The meta-analytic picture first. Simonetta Longhi, Peter Nijkamp, and Jacques Poot synthesized 348 wage estimates from 18 empirical papers in their meta-analysis published in the Journal of Economic Surveys (2005) and in subsequent papers through 2010. The average wage elasticity across this body of evidence is −0.1: a 10-percentage-point increase in the immigrant share of the workforce is associated with approximately a 1% decrease in native wages. The employment elasticity is even smaller at −0.02. By any standard of economic measurement, these are small numbers. A 10-point increase in immigrant share is an enormous supply shock — far larger than what most economies have experienced in any given decade. The wage response is barely visible.

The NAS 2016 report summarizes the consensus: “When measured over a period of 10 years or more, the impact of immigration on the wages of native-born workers overall is very small. To the extent that negative impacts occur, they are most likely to be found for prior immigrants or native-born workers who have not completed high school — who are often the closest substitutes for immigrant workers with low skills.”

Giovanni Peri, writing in the Journal of Economic Perspectives in 2016, examined US data from 1990 to 2006 and found small negative short-run wage effects on native high school dropouts (around −0.7%) and on average native wages (−0.4%), with positive long-run effects for both (+0.3% and +0.6%). The mechanism is task specialization: even within the same nominal skill category, immigrant and native workers tend to occupy different roles, creating complementarities rather than pure substitution. An immigrant construction worker and a native construction worker operating on the same site may be doing sufficiently different tasks — physical labor versus supervisory coordination — that they are less substitutable than their shared occupational label suggests.

Borjas’s estimates are substantially larger. A 10% immigration-induced labor supply shock, in his framework, reduces average native weekly wages by approximately 3 to 4%. The methodology treats the US labor market as a single integrated system segmented by educational attainment — workers at the same education level nationwide competing regardless of geography. His critics argue this is implausible: labor markets are local, workers don’t move freely across the country in response to immigration-induced wage pressure, and the approach bundles together workers who may never compete with each other. The disagreement is real and traceable. It is not scientific chaos.

The Mariel boatlift methodology dispute

Card's 1990 paper — published in the Industrial and Labor Relations Review — found no wage effect following the boatlift. Borjas's 2017 ILR Review paper found a 10 to 25% wage drop for Miami's high school dropouts from the same event and the same underlying data. The divergence traces to one decision: which workers to include in the sample.

Borjas restricted his analysis to non-Hispanic men aged 25 to 59 — the population he argued was most directly competing with the arriving low-skill Cuban workers. Card's original 1990 study and Peri and Yasenov's 2015 reanalysis used broader samples, including women and workers aged 16 to 61, excluding only ethnic Cubans. Neither restriction is arbitrary. Each reflects a theoretical assumption about labor market structure — specifically, about which workers are substitutable for newly arrived immigrants with low skills.

Borjas's critics raised a specific empirical objection: his restricted sample showed an anomalous increase in the proportion of Black workers in Miami following the boatlift — something that couldn't have been caused by Cuban arrivals, since his sample excluded Hispanics. The more likely explanation, his critics argued, is simultaneous Haitian immigration to Miami in the same period contaminating his comparison group in ways that Borjas's design couldn't distinguish from the boatlift effect.

The lesson is not that immigration research is unreliable. The lesson is that the disagreement is about something traceable — which workers count as substitutes for newly arrived low-skill immigrants — and that tracing it reveals an unresolved theoretical question about labor market structure. That question matters. But it is not scientific incoherence. It is a real methodological dispute with documentable referents on both sides.

What both Borjas and the meta-analytic consensus agree on — even as they disagree about size — is the distributional shape of whatever wage effect exists. It falls on prior immigrants and the least-educated native workers. The NAS statement is unambiguous on this point. Peri confirms it with a different methodology. Even Borjas is making a claim about a specific subgroup, not workers in general.

Immigration generates an aggregate surplus. Output increases, prices fall for goods and services produced by immigrant labor — construction, agriculture, food service, care work. The surplus is real. It is not distributed uniformly. It flows to employers (lower labor costs), to consumers (lower prices for goods intensive in immigrant labor), and to high-skill native workers whose work complements rather than competes with low-skill immigrant labor. A lawyer in a city with a large immigrant service workforce benefits from cheaper restaurant meals and lower construction costs. The construction worker who used to have less competition before those immigrants arrived does not.

That competitive pressure, even at the modest magnitudes the meta-analysis suggests, lands on the least politically organized people in any rich democracy: prior immigrants facing labor competition from newer arrivals, and native-born workers without high school diplomas whose position was already precarious. The immigration dividend is invisible to most households — lower prices spread thinly across hundreds of millions of people, showing up as marginally cheaper meals and slightly lower construction quotes. The competitive cost to a specific low-wage worker in a specific market is concentrated and legible. It shows up as a lost shift, a stagnant hourly rate, a foreman job that didn’t materialize.

This asymmetry — diffuse gains, concentrated losses — is the standard political economy explanation for why policies that raise aggregate welfare produce intense opposition. The intensity of the immigration debate among working-class communities is not irrational. It is the rational response of people bearing concentrated costs that aggregate statistics erase.

Now look at what major pro-immigration economic arguments actually say. Documents that explicitly claim to summarize what the research shows on wages — fact sheets, economist op-eds, policy briefs invoking NAS 2016 as their authority — typically present the aggregate finding and stop: small or negligible effect on native wages overall. That finding is accurately stated. What those documents consistently omit is what the NAS 2016 report states in the same passage, directly following the aggregate finding: “To the extent that negative impacts occur, they are most likely to be found for prior immigrants or native-born workers who have not completed high school.” Not in a different chapter. Not buried in technical appendices. In the same sentence block as the finding they do cite. The document they invoke as authoritative says both things. Their public summaries carry one.

This is not a claim about intent. It is a claim about pattern. Read the documents, check what the cited sources say about distribution, observe what appears in summaries and what doesn’t. The conclusion that the omission is systematic follows from the pattern, not from attributing motive.

Borjas’s core concern — that specific workers bear real wage costs from immigration — is separable from his contested methodology. Even accepting the smaller meta-analytic elasticities rather than Borjas’s larger estimates, immigration produces real distributional effects. The statement “aggregate wages are barely affected” does not refute the distributional concern. It changes the subject. It answers a question — what happens to average wages? — that is not the question the workers at the bottom of the distribution are asking.

Restrictionists cite crime links that administrative data consistently fail to support, treat the Borjas-Card methodological dispute as license to dismiss findings they dislike across the entire literature, and deploy the uncertainty of one contested sub-debate to impute uncertainty to every other corner of the evidence base. The Mariel dispute is real. It does not reach the crime literature. It does not reach the fiscal literature. It does not reach the innovation literature. Using it to do so requires ignoring the domain of the dispute.

Pro-immigration advocates present the aggregate wage finding — small, nearly neutral effect on native workers overall — and stop. They cite NAS 2016 as authoritative while not citing what NAS 2016 says about distribution: that whatever wage impacts exist fall on prior immigrants and native workers without high school diplomas. The distributional finding appears in the documents they invoke; it does not appear in their summaries of those documents. They present the aggregate and omit the shape.

These are different patterns — worth distinguishing. The first ignores entire literatures. The second misrepresents the scope of one it explicitly claims to represent in full. They serve different political interests and commit different intellectual failures.

The finding most consistent with the restrictionist concern — immigration creates real distributional costs for specific, identifiable workers — and the finding most consistent with the pro-immigration case — crime goes down rather than up, aggregate wages are barely affected, innovation per immigrant is well above the national average, second-generation immigrants are among the strongest fiscal contributors in the economy — are not in tension with each other. They are simultaneously true in the same literature, not as a convenient synthesis but as a documented feature of what the research actually contains.

The Mariel boatlift entered this account as an epistemological paradox: same data, opposite conclusions, apparent chaos. It exits as a resolved paradox with a traceable shape. Borjas and Card are not looking at incompatible realities. Borjas’s narrow sample — non-Hispanic men aged 25 to 59 without high school diplomas — registered wage pressure following the boatlift. Card’s broader population did not. Both observations are consistent with a single underlying fact: the wage pressure from low-skill immigration is real and concentrated on the specific group of workers who compete most directly with arriving immigrants — not workers in general, but a specific subset of workers at the bottom of the education distribution.

The political debate has already made its choice about which workers to count. Restrictionists use that concentrated effect to make claims about immigration’s impact on all workers, which the literature doesn’t support. Advocates use the aggregate nullity to imply no one is harmed, which the distributional literature doesn’t support. One cites the narrow finding to talk about everyone; the other cites the broad finding to say there are no narrow findings.

The methodology dispute is about which workers to count. The political debate is about which workers count.

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Les médias

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Principales sources et références

Olivier Marie and Paolo Pinotti, “Immigration and Crime: An International Perspective,” Journal of Economic Perspectives, Vol. 38, No. 1, Winter 2024, pp. 181–200, https://www.aeaweb.org/articles?id=10.1257/jep.38.1.181

Michael T. Light, Jingying He, and Jason P. Robey, “Comparing Crime Rates Between Undocumented Immigrants, Legal Immigrants, and Native-Born US Citizens in Texas,” Proceedings of the National Academy of Sciences, Vol. 117, No. 51, December 2020, pp. 32340–32347, https://doi.org/10.1073/pnas.2014704117

Alex Nowrasteh, “Illegal Immigrant Murderers in Texas, 2013–2022: Illegal Immigrant and Legal Immigrant Conviction and Arrest Rates for Homicide and Other Crimes,” Cato Policy Analysis No. 977, Cato Institute, June 26, 2024, https://www.cato.org/policy-analysis/illegal-immigrant-murderers-texas-2013-2022

Sascha Riaz, “Null by Design: Statistical Dilution in Immigration-Crime Research,” British Journal of Political Science, Vol. 56, April 2026, https://www.cambridge.org/core/journals/british-journal-of-political-science/article/null-by-design-statistical-dilution-in-immigrationcrime-research/29595CF23A516E1993E0F71EF0094910

Shai Bernstein, Rebecca Diamond, Abhisit Jiranaphawiboon, Timothy McQuade, and Beatriz Pousada, “The Contribution of High-Skilled Immigrants to Innovation in the United States,” NBER Working Paper 30797, National Bureau of Economic Research, December 2022, https://www.nber.org/papers/w30797

“The Outsize Role of Immigrants in US Innovation,” NBER Digest, March 2023, https://www.nber.org/digest/20233/outsize-role-immigrants-us-innovation

Saheel Chodavadia, Sari Pekkala Kerr, William Kerr, and Louis Maiden, “Immigrant Entrepreneurship in the US,” NBER Bulletin on Entrepreneurship, October 21, 2024, https://www.nber.org/be/20242/immigrant-entrepreneurship-us

Zhao Jin, Amir Kermani, and Timothy McQuade, “Native-Immigrant Entrepreneurial Synergies,” NBER Working Paper 33804, 2025 (not yet published in peer-reviewed journal as of writing; findings from UC Berkeley Haas newsroom coverage at https://newsroom.haas.berkeley.edu/research/for-startup-success-teams-with-both-u-s-born-and-immigrant-founders-have-an-edge-study-shows/)

National Academies of Sciences, Engineering, and Medicine, “The Economic and Fiscal Consequences of Immigration,” National Academies Press, 2016, https://www.nationalacademies.org/read/23550

Pia Orrenius and Madeline Zavodny, “New Findings on the Fiscal Impact of Immigration in the United States,” Federal Reserve Bank of Dallas Working Paper No. 1704, April 2017, https://www.dallasfed.org/research/papers/2017/wp1704

Simonetta Longhi, Peter Nijkamp, and Jacques Poot, “A Meta-Analytic Assessment of the Effect of Immigration on Wages,” Journal of Economic Surveys, Vol. 19, No. 3, July 2005, pp. 451–477, https://papers.ssrn.com/sol3/papers.cfm?abstract_id=634622

Simonetta Longhi, Peter Nijkamp, and Jacques Poot, “Meta-Analyses of Labour-Market Impacts of Immigration: Key Conclusions and Policy Implications,” Environment and Planning C: Government and Policy, Vol. 28, 2010, https://journals.sagepub.com/doi/10.1068/c09151r

Giovanni Peri, “Immigrants, Productivity, and Labor Markets,” Journal of Economic Perspectives, Vol. 30, No. 4, Fall 2016, pp. 3–30, https://www.aeaweb.org/articles?id=10.1257/jep.30.4.3

George J. Borjas, “The Wage Impact of the Marielitos: A Reappraisal,” ILR Review, Vol. 70, No. 5, October 2017, pp. 1077–1110, https://journals.sagepub.com/doi/10.1177/0019793917692945

David Card, “The Impact of the Mariel Boatlift on the Miami Labor Market,” Industrial and Labor Relations Review, Vol. 43, No. 2, January 1990, pp. 245–257, https://journals.sagepub.com/doi/10.1177/001979399004300205

Giovanni Peri and Vasil Yasenov, “The Labor Market Effects of a Refugee Wave: Applying the Synthetic Control Method to the Mariel Boatlift,” NBER Working Paper No. 21801, National Bureau of Economic Research, December 2015, https://www.nber.org/papers/w21801