# Immigration, crime, and economic effects: evidence dossier

Research checked 6 October 2026. Intended use: broad-audience factual reference and short sign linked to an evidence page. This is evidence assessment, not advice for targeting political audiences.

## Editorial recommendation

Use a question-led sign if the national scope matters:

**Undocumented immigration and crime: what does the evidence show?**

Use a narrower declarative sign if one factual finding is needed:

**In Texas, undocumented immigrants had lower felony arrest rates.**

Required immediately adjacent qualifier: **Compared with U.S.-born citizens, 2012–2018.** Link to the evidence and limitations. Do not shrink the geography and period into unreadable footnotes. “Had” is important: these are historical data.

Reject “Undocumented immigrants aren't dangerous criminals.” It is an absolute claim about individuals, while the evidence concerns group rates and places. Reject “Immigration never increases crime” and “deportation cannot improve safety” for the same scope problem. Even a low-rate group includes people who commit serious offenses. Individual victims' experiences and population comparisons can both be real.

The defensible synthesis is that the studies reviewed do not support a general claim that undocumented immigration produces higher overall violent-crime rates. That conclusion is neither proof of zero harm nor a precise, current nationwide estimate of undocumented offending. Keep the distinction between a person's offending and a neighborhood's crime rate visible throughout.

## Evidence ledger

### 1. Individual-status comparison: Texas felony arrests

Michael T. Light, Jingying He, Jason P. Robey (2020), PNAS. [Full paper](https://pmc.ncbi.nlm.nih.gov/articles/PMC7768760/); [DOI](https://doi.org/10.1073/pnas.2014704117).

Data: Texas criminal-history records, 2012–2018, linked to DHS biometric immigration-status information; population denominators from Center for Migration Studies, with Pew sensitivity checks. Each arrest charge is an incident, not necessarily a different person. The study excludes administrative federal holds. Its comparison is with U.S.-born citizens; naturalized citizens are included among legal immigrants.

Findings: substantially lower violent, property, and drug felony arrest rates among undocumented immigrants. Relative U.S.-born rates were over twice as high for violent offenses, over four times for property offenses, and about 2.5 times for drug offenses. Alternative status coding, population estimates, and conviction outcomes preserved the broad pattern.

Main limitation: one state and an older period. Immigration status can be missed or misclassified. Arrest charges are not proven offenses. Sensitivity tests reduce particular concerns; they do not establish perfect measurement or nationwide generalizability.

### 2. State-level longitudinal comparison

Light and Ty Miller (2018), Criminology. [Publisher abstract and DOI](https://onlinelibrary.wiley.com/doi/10.1111/1745-9125.12175); [repository](https://pmc.ncbi.nlm.nih.gov/articles/PMC6241529/).

Covers all 50 states and DC, 1990–2014. Combines estimated undocumented populations with crime and demographic/economic information. Fixed-effects regressions examine changes within states rather than merely comparing high-immigration states against low-immigration ones.

Findings: the association with violence was generally negative, although not statistically significant in every specification. Supplemental victimization analyses and instrumental-variable models offered little support for selective migration or reduced reporting as complete explanations.

Limitations: area-level estimates cannot identify the immigration status of perpetrators. Population estimates are modeled, not a census of legal status. Fixed effects remove stable differences but cannot guarantee that all changing confounders are controlled. The supplementary identification strategy depends on its assumptions. This is evidence against a general positive association in the study period, not a timeless causal law. Repository metadata has an inconsistent issue-date display; use the publisher's 2018 bibliographic citation.

### 3. Independent metropolitan evidence

Robert M. Adelman and colleagues (2021), Journal of Crime and Justice. [University publication record](https://researchconnect.suny.edu/en/publications/using-estimates-of-undocumented-immigrants-to-study-the-immigrati/); DOI 10.1080/0735648X.2020.1819375.

Uses 2014 metropolitan undocumented-population estimates from Pew and the Migration Policy Institute, 2013–2015 FBI crime data, and 2011–2015 American Community Survey characteristics. Findings generally align with no higher violence and lower property crime.

Important limitation: cross-sectional design. Differences between metropolitan areas can reflect selection, local institutions, reporting, or unmeasured characteristics. This is useful independent corroboration with a different research team; it is not a causal experiment or a direct comparison of undocumented and citizen offenders.

### 4. New publication, old observation window: neighborhoods

Charis E. Kubrin, Derek Christopher, Cheyenne Hodgen, Xiaoshuang Iris Luo, John R. Hipp (published 10 August 2026), Journal of Urban Affairs. [University repository](https://escholarship.org/uc/item/2gs6z9tc); [publisher](https://www.tandfonline.com/doi/full/10.1080/07352166.2026.2699123).

About 11,500 urban neighborhoods, 2010–2018. Restricted Census microdata and an imputation procedure estimate undocumented residents. Neighborhood fixed-effects models relate changes in population composition to changes in crime, with controls for other characteristics and immigrant groups.

Findings: growing undocumented shares were associated with lower property crime and no statistically detectable overall violent-crime change. Disaggregation matters: aggravated assaults declined, while robberies increased. The authors discuss possible victimization mechanisms; these data do not establish who committed those robberies.

Limitations: imputed status, urban coverage, reported crime, observational identification, and a pre-pandemic observation period. A 2026 publication must not be labeled “2026 crime data.” Do not omit the robbery result to manufacture uniformity. No statistically detectable association is not proof the true effect equals zero.

### 5. Drug-specific nonuniformity

David Green (2016), Social Science Quarterly, DOI 10.1111/ssqu.12300. [Publisher abstract](https://onlinelibrary.wiley.com/doi/abs/10.1111/ssqu.12300).

Pooled state-level 2012–2014 violent-crime and drug-arrest data are compared with estimates of immigrant, Mexican, undocumented, and undocumented Mexican populations using correlation and multivariate regressions. The publisher abstract directly confirms no positive violent-crime association, but a small statistically significant association between the overall undocumented population and drug-related arrests. It separately reports no evidence linking Mexican or undocumented Mexican populations to either outcome. These are different population definitions, not contradictory statements.

The full coefficient tables were not accessible in this pass; publish the qualitative abstract result, not an unverified effect size. Drug arrests also reflect policing and detection. Do not turn one subgroup's null finding into a universal null result.

### 6. Government-sponsored report is not an independent replication

Light (January 2024), *Unauthorized Immigration, Crime, and Recidivism: Evidence from Texas*, NIJ grant report, NCJ 308552. [Full report](https://www.ojp.gov/pdffiles1/nij/grants/308552.pdf).

The report's Texas rate comparisons still use 2012–2018. It also examines criminal-justice outcomes and recidivism. Its limitations warn that incomplete deportation tracking forces recidivism analysis onto a small selected subset of released offenders. Treat claims about equal recidivism cautiously.

A government summary of this research, the PNAS paper, a university press release, and news stories about it are not four independent studies. Maintain a “shared dataset/research lineage” note on the site. The NIJ report is useful methodological detail, not fresh post-2020 population evidence.

### 7. Convictions are another measurement layer

Light and colleagues (2024), *Citizenship, legal status, and misdemeanor justice*, Criminology. [Paper](https://onlinelibrary.wiley.com/doi/10.1111/1745-9125.12387).

This is a case-processing study, not an estimate of each group's underlying offending rate. Texas status analysis covers 2012–2018; the broader California/Texas citizenship analysis covers 2006–2018. With observed case and defendant controls, undocumented Texas misdemeanor defendants were more likely to be convicted and incarcerated after arrest than citizens. That is a conditional justice-system outcome, not evidence that undocumented residents offend more often.

Editorial implication: a conviction measure helps address some arrest objections but still reflects legal representation, plea decisions, case attrition, and sentencing institutions. Do not describe convictions as a perfect census of criminal behavior.

## The competing Texas analyses

### Administrative source warning

[Texas Department of Public Safety criminal illegal noncitizen data](https://www.dps.texas.gov/section/crime-records/texas-criminal-illegal-noncitizen-data).

DPS publishes counts, not an automatically comparable per-capita rate. Its notes describe incomplete identification and additional people identified while in prison. The scope is Texas arrests for state offenses, and it omits comparable lawful-foreign-national data from this presentation. The page changes over time; archive the exact release used for a chart. A cumulative count over many years cannot be compared to a one-year population denominator to produce an annual risk.

### CIS critique

[Center for Immigration Studies, October 2022 report](https://cis.org/sites/default/files/2022-10/texas-crime.pdf); [author's 2024 explanation of the dispute](https://cis.org/Richwine/Catos-Brazenly-False-Claim-About-Our-Illegal-Immigrant-Crime-Research).

CIS argues that delayed identification of undocumented prisoners understates prior estimates, especially recent observations and less-serious offenses. It reports higher estimates using additional prison identification. This is a genuine measurement issue to disclose; it is not answered by simply calling the organization ideological. The raw person-level reconciliation needed to settle every disputed number was not independently reproduced here.

### Cato response and newer span

Alex Nowrasteh (June 2024), Cato policy analysis 977. [Full analysis](https://www.cato.org/policy-analysis/illegal-immigrant-murderers-texas-2013-2022).

Cato uses revised Texas data, including later status identification, and emphasizes homicide because identification is more complete. For 2013–2022 it reports homicide conviction rates of 2.2 per 100,000 undocumented immigrants versus 3.0 for U.S.-born people; its unrounded calculation is 26% lower. It flags other-offense data quality. Denominators use a modified residual population estimate, and “unknown or other” arrestees are treated as native-born.

Cautions: a policy analysis rather than a peer-reviewed replication; status classification and denominator assumptions remain important. Its 2013–2022 period and counting choices differ from the PNAS study, so do not combine figures as though they came from one table. Do not recompute the reported percent using rounded 2.2 and 3.0 values. Cato and CIS disagree about classification/double-counting; the responsible presentation explains the dispute rather than claiming our own raw-data audit resolved it.

## What the site should teach readers to distinguish

These are editorial/statistical safeguards, not additional empirical claims:

1. **Counts versus rates.** A larger population can have more total incidents even with a lower per-person rate. Specify both when a policy question needs both.
2. **Charges, people, arrests, convictions, incarceration, and victimization.** Never relabel one as another. Multiple charges can involve one arrest/person. Incarceration also depends on sentence length.
3. **Status versus birthplace versus nationality.** “Foreign-born,” “noncitizen,” “Mexican,” “asylum seeker,” and “undocumented” are not interchangeable categories. Naturalized citizens are citizens and foreign-born.
4. **Group averages versus individual prediction.** A population association cannot establish an individual's innocence or dangerousness.
5. **Offender rates versus area crime.** Crime occurring in an immigrant neighborhood need not be committed by immigrants; immigrants can be victims.
6. **Association versus causation.** Prefer “associated with” for observational area studies. A causal estimate must name the intervention, design, assumptions, period, and population.
7. **Recorded versus unrecorded harm.** Reporting, policing, clearance, prosecution, and migration/deportation can change observed outcomes. A reporting sensitivity analysis narrows uncertainty; it does not eliminate it.
8. **Historic evidence versus current arrivals.** None of the core crime-rate studies directly answers a 2026 question about all post-2021 entrants. Avoid pretending either the older findings or a salient recent case alone answers that question.
9. **Administrative violations versus public safety offenses.** If discussing criminal versus civil immigration rules, commission a separately verified legal explainer; do not use “illegal” as proof of violent criminality or assert that all unauthorized presence involves the same legal conduct.
10. **Average versus adjusted comparisons.** A crude rate describes actual population composition. Age/sex-adjusted rates answer a different question. Both can be useful, but labels must make the distinction.

## Concise economic-claim map

### “Undocumented immigrants pay no taxes”

Contradicted by tax-contribution evidence. [ITEP's 2024 report](https://itep.org/undocumented-immigrants-taxes-2024/) estimates $96.7 billion in federal, state, and local taxes for 2022, using population/tax microsimulation rather than an IRS count by status. Payroll incidence includes employer and employee shares; property-tax incidence includes renters. Its report excludes DACA recipients from these estimates. State the year and “estimated.” ITEP's policy perspective should be disclosed alongside the method. Tax receipts alone are not net fiscal benefit: spending must also be counted. Do not label this “$97 billion in income taxes” or “$97 billion every year today.”

### “Immigration reduces the federal deficit”

Conditionally supported for a particular modeled surge. [CBO July 2024](https://www.cbo.gov/publication/60165) projected approximately $0.9 trillion less federal deficit over 2024–2034 from its 2021–2026 surge scenario. This is an older conditional forecast, not a realized gain or current 2026 forecast. Its “other foreign nationals” category includes some permitted entrants/stayers and some without permission; it is not identical to all undocumented residents. The headline estimate excludes discretionary appropriations changes and state/local budgets. The same report projects larger aggregate GDP, which does not establish an equal gain for every resident. Recheck updated migration and policy baselines before featuring the projection.

### “Immigration has no local public cost”

Contradicted for the surge examined by [CBO June 2025](https://www.cbo.gov/publication/61464). For 2023 it estimated a $9.2 billion direct net state/local cost: $10.1 billion added revenue and $19.3 billion spending. An alternative measure yielded $9.8 billion net cost. Education, shelter, and border security contributed. This is a selected surge population, year, and level of government, not the lifetime net balance of every undocumented resident. Federal gains and local costs can coexist. Do not mechanically subtract this one-year local estimate from an eleven-year federal projection.

### “Immigrants take jobs or depress everyone's pay”

Too broad. The [National Academies synthesis](https://www.nationalacademies.org/projects/DBASSE-CNSTAT-13-03/publication/23550) finds small overall long-run native-born wage/employment effects, with adverse effects more plausible for earlier immigrants and native-born high-school dropouts. Its population is immigration generally, not exclusively undocumented immigrants. Use it for broad labor-market context, not an undocumented-specific numerical assertion.

### “Undocumented immigration has only benefits / only costs”

Neither formulation survives outcome-specific assessment. [Wilson and Zhou, Dallas Fed working paper 2607, March 2026](https://www.dallasfed.org/~/media/documents/research/papers/2026/wp2607.pdf) studies primarily March 2021–March 2024 using immigration-court/administrative microdata and a two-way leave-out shift-share instrument. It estimates approximately one additional local job per unauthorized immigrant worker inflow, no statistically significant local wage decline, and higher local rents/house prices without detectable housing-supply expansion. “No significant wage decline” is not proof of no effect: the wage estimate is imprecise. Reduced per-capita labor income can partly reflect adding lower-paid workers rather than incumbent workers losing pay. Local estimates need not equal national effects. This is a preliminary working paper, not an official Federal Reserve policy conclusion. Its operational status definition includes entrants not formally admitted under immigration law; preserve the paper's category rather than assuming it matches every crime study.

## Proposed evidence-page architecture

- Exact claim and a short scoped finding, with date reviewed.
- Three visible tags: population, geography, observation period.
- “What was measured?” before the chart.
- Main Texas comparison linked directly to the primary paper; graph axis says felony arrest charges per population, never simply “criminals.” If numeric series are used, verify original figure/data, not a press-release transcription.
- Separate panels for individual-status research and area-level research.
- “Where findings differ” box including neighborhood robbery and Texas status-identification dispute.
- “What we do not yet know” box: contemporary nationwide status-specific rates and post-2021 subgroup generalizability.
- A source ledger identifying peer-reviewed study, government estimate, working paper, or advocacy/policy analysis; list shared datasets to avoid inflated source counts.
- Correction route and dated change log. Avoid a universal “TRUE/FALSE” badge for a multicomponent claim.
- Economics as its own evidence page. Do not use fiscal or employment findings to imply anything about crime.

## Update and publication gates

Before publishing a chart: reconcile numerator, denominator, offense definition, unit, year, and status categories; independently verify every plotted number; document whether age/sex adjustment was applied; and ensure alt text includes limitations. No chart has been computed or independently replicated in this research pass.

Update when: a new status-identified crime series becomes available; Texas revises identification rules or historical data; a core paper receives a correction/retraction; a post-2021 cohort analysis becomes available; independent replication materially changes estimates; or economic projections change with actual flows/policy. For estimates and legal-benefit claims, recheck the source immediately before publication.

Outstanding targeted verification: full-text Green 2016 coefficient tables if quantifying its effect; raw-data reconciliation of competing Texas analyses; supplementary methods and imputation validation of the 2026 neighborhood paper if giving a methodological deep dive; newest CBO baseline before any forward-looking fiscal headline. These do not block the narrow historical Texas headline, but do block pretending this memo establishes a precise nationwide 2026 offending rate.