Minimum Wage

What the evidence says

The employment literature on minimum wage increases does not point in one direction. A large share of panel studies using state or national data find that minimum wage increases decrease teen and youth employment, with elasticities that cluster in a fairly narrow band: Neumark (2006) reports elasticities of -0.10 to -0.20 for teenagers, Neumark (2013) reports elasticities near -0.3 and a range of -0.15 to -0.64 across Census divisions, and Neumark's 2004 cross-national panel finds youth elasticities of -0.16 to -0.25. A 2025 meta-analysis of published studies (Fernandez Salguero) reports a median own-wage employment elasticity of -0.13 overall and -0.17 for teenagers specifically. Against this, natural-experiment case studies find no disemployment effect or a positive one: Card's 1993 New Jersey/Pennsylvania comparison found fast-food employment 13 percent higher in New Jersey after its minimum wage rose, Card's California study found an implied teen employment elasticity of about +0.35, and Katz and Krueger's Texas fast-food study found elasticities of 1.70 to 2.65. Dube (2016) and Cengiz (2019) sit between these camps: both find no statistically significant change in the stock of low-wage employment following a minimum wage increase — Cengiz finds the overall number of low-wage jobs was "essentially unchanged" (+2.8%, not significant) five years out, with job losses just below the new minimum (-1.8% of pretreatment employment) matched by job gains at or just above it (+2.1%).

Where studies find a negative employment effect, it is not evenly distributed. Cengiz (2019) finds an employment elasticity of about -1.4 in tradeable-sector and manufacturing jobs, but an effect "close to 0" in nontradeable sectors such as restaurants and retail, which employ most U.S. minimum-wage workers. A set of Chinese regional panel studies (Fang 2015 / the associated 2015 paper) finds negative elasticities in the more developed Eastern region (-0.154 to -0.234 current, larger lagged effects) and the Central region, but no statistically significant effect in the less-developed Western region. The same body of work finds low-skilled workers (high school or below) show adverse elasticities of -0.054 to -0.080, while high-skilled workers (a placebo group) show no measured effect.

Beyond employment counts, the evidence is more consistent on wages and turnover. Dube (2016) finds a 10 percent minimum wage increase raises average weekly earnings for teens by 2.2 percent, while decreasing separations (elasticity -0.233 for teens, -0.225 for restaurant workers), hires, and turnover (-2.0 percent for teens), with no measured change in non-employment duration — a pattern the study attributes to "search models with endogenous separations" rather than to net job destruction. Cengiz (2019) finds average wages of affected workers rose 6.8 percent, with spillovers extending to workers earning up to $3 above the new minimum (about 40 percent of the total wage increase), concentrated among incumbent workers rather than new entrants. Vergara (2022) finds the entire welfare gain for low-skill workers (elasticity ~0.1) runs through the wage-conditional-on-employment margin, with no measured effect on hours, employment, or labor-force participation, and a precise zero effect on high-skill workers' welfare — a placebo result consistent with several of the disemployment studies' own placebo checks on high-skilled workers.

Minimum wage increases also show measured effects beyond the labor market itself. Vergara (2022) finds a 0.36 elasticity of reduced corporate profits in low-skill-labor-intensive industries (retail, food, low-skill health services), no measured profit effect in manufacturing or non-exposed services, and a 0.31 to 0.39 elasticity decrease in income-maintenance benefit spending — a fiscal externality — with no measured effect on medical transfers or federal income tax liabilities. Borg (2022) finds a 10 percent increase in workplace minimum wage raises rents at residence ZIP codes by 0.69 percent, with landlords capturing roughly 10 cents of every dollar the minimum wage generates for workers. On health outcomes, Fitch (2026) finds minimum wage increases of at least $1 above the federal floor are associated with a sustained decline in homicide mortality (-0.22 per 100,000 person-years vs. never-exposed states), concentrated in firearm-involved homicides and among 18- to 25-year-olds, and Merrill-Francis (2026) finds a $1.00 state minimum wage increase above the federal minimum is associated with a 1.4 percent decrease in firearm suicides. Cognitive function shows little measured effect overall (Lee 2026: no association among all workers or higher-wage workers), with a positive effect only appearing among low-wage and part-time worker subgroups at a 6-year lag.

The literature is thin or silent on some outcomes a reader might expect. No claim here measures effects on aggregate poverty rates, total state employment, or non-fast-food/non-retail industries outside the tradeable/manufacturing and nontradeable comparison in Cengiz. Long-run effects beyond four to five years are addressed only narrowly (Allegretto 2011 finds no difference between long-term and contemporaneous effects once spatial controls are included). And while several studies dispute whether minimum wage increases cause disemployment, none of the claims here directly measures a monopsony mechanism — it is raised only as an interpretive possibility, not tested.

Where the evidence splits

The central and largest split is over the direction and size of the minimum wage's effect on teen and youth employment. Neumark's body of work (2001, 2004, 2006, 2013) and the associated Chinese regional panel studies consistently find negative elasticities in the -0.1 to -0.3 range using fixed-effects panel and difference-in-differences designs. Card's case studies (1993 New Jersey/Pennsylvania, California) and Katz and Krueger's Texas fast-food survey find no effect or a positive effect using similar difference-in-differences logic but narrower, single-state or single-industry samples. Allegretto (2011) explicitly addresses this split: a standard fixed-effects specification reproduces the negative "consensus" elasticity of -0.118, but adding state-specific spatial trend controls renders the employment elasticity statistically indistinguishable from zero (90% CI rules out elasticities more negative than -0.052), which the paper attributes to a downward bias from uncontrolled spatial heterogeneity — a bias it finds "particularly large for African Americans." Neumark (2013) directly disputes this resolution, arguing that "methods that let the data identify the appropriate control groups" (rather than pooling all in-region states as controls) restore "stronger evidence of disemployment effects, with teen employment elasticities near -0.3." The sources thus locate the disagreement specifically in how control states and trends are chosen — an unresolved methodological dispute between the two papers, not a difference in underlying data.

A second, related split concerns time trend: the Fernandez Salguero (2025) meta-analysis finds published studies since 2010 report own-wage elasticities near zero (-0.04) versus -0.40 in studies published before 2010, attributing the shift to "an improvement in quasi-experimental methodologies and greater attention to credible identification strategies" — the same methodological fault line as above, restated across the literature as a whole rather than between two papers.

Within Card's 1993 New Jersey study itself, employment expanded at stores that initially paid the old minimum ($4.25) and contracted at stores that already paid above the new minimum ($5.00+, -2.16 FTE employees, comparable to Pennsylvania's -2.28 FTE decline). The claims explain this split by exposure: stores unaffected by the wage floor behaved like the untreated Pennsylvania comparison group, while affected stores did not show the predicted contraction.

Thresholds and dose-response

Cengiz (2019) establishes a dollar-denominated dose-response pattern in wage spillovers: after a minimum wage increase, wage effects extend to workers earning up to $3 above the new minimum, and this spillover band accounts for about 40 percent of the total wage increase generated by the policy. The same study finds job losses concentrated in the $1 wage bin just below the new minimum (a decline equal to 1.8 percent of pretreatment employment) and job gains concentrated between the new minimum and $4 above it (a gain equal to 2.1 percent of pretreatment employment), with no measured employment change further up the wage distribution.

Open empirical questions

• No claim here measures the effect of minimum wage increases on aggregate poverty rates, income inequality, or total (not sector-specific) state employment.
• The specific methodological choice driving the Allegretto/Neumark split — how control states and trend specifications are selected — is described by both sides but not adjudicated by any source here.
• Long-run effects beyond about four to five years are addressed by only one source (Allegretto 2011), leaving the durability of any employment or wage effect past that window unmeasured.
• No source here directly tests a monopsony mechanism for the positive-employment case-study results; it is raised only as an unmeasured interpretive possibility.