Minimum Wage Effects Across State Borders: Dube, Lester and Reich (2010), replicated and extended to 2026

The paper's preferred specification is its equation (6). Let $y_{ipt}$ be restaurant employment or average weekly earnings in county $i$ of border pair $p$ in quarter $t$. Let $w^M_{it}$ be the county's minimum wage, $y^{TOT}_{it}$ its total private-sector employment or earnings, and $pop_{it}$ its population. The paper estimates

$\ln y_{ipt} = \alpha + \eta \ln w^M_{it} + \delta \ln y^{TOT}_{it} + \gamma \ln pop_{it} + \phi_i + \tau_{pt} + \varepsilon_{ipt}.$

Here $\phi_i$ is a county fixed effect and $\tau_{pt}$ is a fixed effect for each pair in each quarter. A county that borders several counties across the state line appears once per pair. The coefficient $\eta$ is the elasticity reported throughout this page. Because $\tau_{pt}$ absorbs everything the two counties of a pair share in a quarter, $\eta$ comes only from changes over time in the minimum-wage gap within each pair. The traditional all-county panel (the paper's equation 1) replaces $\tau_{pt}$ with a single quarter effect $\tau_t$ shared by every county in the country.

1. In the border design, the minimum wage elasticity of restaurant employment is 0.016 (s.e. 0.098). Elasticities below −0.178 are ruled out at 95 percent confidence.
2. The restaurant earnings elasticity is 0.188 (s.e. 0.060), so the minimum wage binds in this sample.
3. The traditional all-county panel gives employment elasticities of −0.176 to −0.211 on the same data. The paper reads these negatives as spatial heterogeneity in employment trends, not minimum wage effects.
4. The findings are robust to long-run effects: the sixteen-quarter cumulative employment response is −0.007 (s.e. 0.202).
5. In the border design, the labor-demand elasticity is 0.079 (s.e. 0.286). Its 95 percent interval rules out elasticities below −0.48, so minimum wages raise total earnings at these jobs.

We used the authors' data and code from their public package:

• the county-level QCEW extracts for restaurants and other low-wage sectors (four .dta files, 616 MB uncompressed);
• the pair list county-pair-list.txt, with all 1,181 contiguous cross-state county pairs;
• the quarterly minimum-wage file MW_yr_qtr_84_07.dta;
• 14 Stata do-files.

Stata was unavailable, so we ported every do-file to R, using fixest and haven. The printed standard errors follow Stata conventions that the do-files do not document. We reconstructed those conventions and checked every output against the paper's printed tables.

For the extension, we rebuilt the QCEW county-by-quarter panel for 1990Q1 to 2026Q1 from the BLS bulk files and open-data API. We also built a county minimum-wage panel for the same years. It combines the package file through 2007, the Department of Labor's state history for 2008 to 2022, and effective-dated records for 2023 to 2026. The New York and Oregon regional tiers and the border-county local ordinances are included. Before estimating anything new, we confirmed that this pipeline matches our replication of the paper's main table exactly on the paper's own years when run on the package's data. The second extension study adds BLS occupational wage medians, to measure how hard each county's minimum binds.

The paper's scientific core reproduces. All 24 coefficients of the main table (Table 2) came out at the printed values to rounding. That includes the border-pair employment elasticity of 0.016 with its 90 and 95 percent lower bounds of −0.147 and −0.178, and the earnings elasticities. The all-county negatives come out at −0.177 to −0.211 against the paper's −0.176 to −0.211. The pre-trend table, the dynamic responses, the spillover test, the placebo test and the robustness checks also match.

Table 2, key cells (published / this replication)

Notes. Standard errors in parentheses, two-way clustered by state and border segment in the border-pair rows. The all-county employment row spans the columns with and without the total private sector control; the labor-demand rows use the columns with it. The labor-demand elasticity is the employment elasticity divided by the earnings elasticity, now more often called the own-wage elasticity of employment. It is not among the 24 coefficients, and the wider standard errors in our column are explained below. The paper's ratios come from a joint estimation step the package does not include, so they differ from the simple ratio of the printed cells.

What did not reproduce is almost entirely in the standard errors and p-values, not the estimates. Two kinds of number in Table 2 combine two regressions:

• the labor-demand elasticity, the employment elasticity divided by the earnings elasticity (the percent change in jobs per percent rise in pay);
• the cross-specification p-values, which test whether two specifications give the same employment elasticity.

Their point values follow from coefficients that reproduce. But their standard errors also depend on how the errors of the two underlying estimates move together, and no single regression reports that. The paper estimated it with a seemingly unrelated regression, which fits the employment and earnings equations jointly and lets their residuals correlate. No do-file in the package runs that step. So we stacked the two equations in one regression with the paper's two-way clustering and computed the standard errors from it. This recovers the point ratios, but our standard errors are wider in every specification. In the border-pair specification, our ratio is 0.087 against the paper's 0.079, and our standard error is 0.533 against 0.286. The paper's 95 percent interval, [−0.482, 0.640], is the source of the −0.48 bound in claim 5. Ours, [−0.957, 1.132], does not rule out −0.48. (By coincidence, −0.482 is also the paper's point estimate for the border sample with a single quarter effect.) Without the authors' code we cannot tell which choice in their joint estimation produces the narrower standard errors. So the paper's −0.48 bound (claim 5 above) could not be reproduced from the package. For total earnings the threshold that matters is −1: they rise as long as the elasticity stays above it, and our border-pair interval only just excludes −1. One of the four cross-specification p-values matches (0.022). The other three come out at 0.017, 0.142 and 0.193 against the paper's 0.066, 0.011 and 0.056.

A few cells differ for other reasons. In the border-segment figure the pooled mean matches (−0.005 against −0.006). But only 40 of the paper's 64 segments were estimable from the shipped panel, so our dispersion is wider (0.078 against 0.049). The Table 6 row that stacks restaurants with retail prints 0.076 for earnings and −0.032 for employment. The shipped code computes a per-sector regression on a precombined column, not the stacked estimator its own footnote describes. Neither version reproduces the printed values. Full-service restaurant earnings came out at 0.156 against 0.187, a likely data-vintage difference. Two appendix cells near zero drift past our tolerance: −0.036 against −0.002 with state trends, and 0.074 against 0.079 in the placebo. The CPS-based hours bound, and the statistic that restaurants employ 29.9 percent of near-minimum workers, have no basis in the package at all: it ships no CPS data or tabulation code. Reproducing Table 5 required rebuilding a shipped crosswalk file that is empty, and inferring sample rules that differ cell by cell.

A reader asked, through the site, whether the no-job-loss finding holds now that cross-border minimum-wage differences are much larger. The paper raises this question itself. On page 962 the authors wrote that the results "cannot be extrapolated to predict the impact of a minimum wage increase that is much larger than what we have experienced". An estimate drawn from small minimum-wage differences need not predict what large ones do, because a larger minimum reaches further up the wage distribution. In the paper's balanced sample, the yearly mean gap among differing pairs stayed between 0.065 and 0.185 log points. Across all 1,181 pairs, as in Figure 2, it peaked at 0.204 in 2005.

The federal floor has been $7.25 since July 2009, while many states index or phase in much higher minimums. By 2026Q1, 828 of the paper's 1,181 pairs straddle a minimum-wage difference. Their mean gap is 0.481 log points. Of all 1,181 pairs, 305 exceed 0.60, roughly a $13.20 minimum against $7.25. The largest is 0.86: Washington's $17.13 against Idaho's $7.25.

We extended the paper's QCEW restaurant panel from 2006 to 2026Q1. We grouped the 1,181 pairs by the largest gap each reached over 2015Q1 to 2026Q1, fixed before any employment outcome was examined. We then re-estimated the paper's preferred specification (pair-by-quarter fixed effects with the total private sector control) on 2015Q1 to 2026Q1, excluding 2020, within each class. Classes where the earnings response is not significant are uninformative: if the minimum cannot be shown to bite, a zero employment effect means nothing. That excludes the two classes with gaps under 0.40.

In the large-gap pairs, the answer matches the paper's. Across the 226 balanced pairs whose gap passed 0.40 (all 608 large-gap pairs average a 2026Q1 gap of 0.587 log points), the employment elasticity is −0.022 (s.e. 0.054). Its 95 percent confidence interval is [−0.128, 0.085]. The earnings elasticity is 0.121 (s.e. 0.015), so the minimum wage bites hard in these counties. The interval's lower bound, −0.128, lies above the −0.178 bound the paper itself ruled out. So the paper's conclusion extends, in the paper's own terms, to gaps two to four times larger than its average gap. The employment leads are tiny (−0.015 and −0.017, each less than a quarter of its standard error). So the higher-minimum counties were not already on different restaurant trends before the gaps opened.

Notes. All rows are our estimates; the paper has no counterpart at these gaps. The paper's preferred specification on QCEW data for 2015Q1–2026Q1 excluding 2020, with standard errors two-way clustered by state and border segment. A class bites when its earnings confidence interval excludes zero. The headline row's minimum detectable effect is 0.152, the size of loss this design would detect 80 percent of the time; the estimate itself rules out losses beyond −0.128.

A single regression that interacts the minimum wage with the gap classes asks the dose-response question formally. Does the employment effect grow more negative as the gap grows? No class differs significantly from another. The class slopes are 0.272, −0.049, −0.002 and −0.032 from the smallest class to the largest, and the test that all four slopes are equal gives p = 0.449. The contrast between the two classes over 0.40 and the two under it is −0.129 (s.e. 0.111). Between the two classes where the minimum bites, the difference is −0.030 (s.e. 0.058).

The result survives the variants we declared in advance:

• estimating only 2021Q1 to 2026Q1 gives 0.069 (s.e. 0.084);
• dropping 2021 as well as 2020 gives −0.014 (s.e. 0.058);
• dropping the California pairs once the state's $20 fast-food minimum takes effect gives −0.023 (s.e. 0.055);
• using all 608 large-gap pairs rather than the balanced 226 gives 0.002 (s.e. 0.056);
• adding a separate linear trend for every pair leaves the estimate at −0.022 (s.e. 0.039);
• dropping the total private sector control gives −0.047 (s.e. 0.054).

Every variant leaves the lower confidence bound above −0.178. The metro split is descriptive only, but all three groups are near zero: −0.029 (s.e. 0.050) for metro pairs, −0.036 (s.e. 0.108) for nonmetro, and −0.016 (s.e. 0.065) for mixed.

The longer panel also lets us re-run the paper's central diagnosis. The paper argues that designs without local controls read spatial heterogeneity as job loss. Its own years confirm that on our panel, which uses today's data vintage (see Notes): with common time effects the border sample gives −0.109 (s.e. 0.075), against −0.043 (s.e. 0.091) with the full pair-by-quarter effects. That wedge shrinks era by era and is gone today. On 2021 to 2026 the two specifications give 0.051 (s.e. 0.039) and 0.054 (s.e. 0.077), a difference of −0.003 (p = 0.95). As high minimums spread, the low-wage states that once trended differently stopped doing so. This is consistent with the paper's account of why the two designs disagreed.

A gap across a border is not the same thing as a minimum that binds. Spokane County, Washington faces Idaho across the largest gap in the data, 0.86 log points. Yet Washington's $17.13 minimum is only 0.65 of the local median wage, because Washington wages are high. Today's large gaps come mostly from high-wage states bordering low-wage ones, so bindingness rises far less than the gap. Even Spokane, at the largest gap, only reaches the lower edge of the most binding tail, ratios of 0.65 and above; most large-gap pairs sit below it. The economic content is in bindingness. Competitive models predict that the employment response turns negative as the minimum rises toward the median wage. Search and monopsony models predict a response near zero up to some threshold.

Our second extension study writes the employment elasticity as a function of bindingness, the minimum divided by the local median wage. Area median wages start only in 2005, so the fit uses a mean-based stand-in that reaches back to 1990: 40 times the minimum, divided by the county's average weekly private-sector pay over the previous year. A line fitted on 2005 to 2026, where both measures exist, converts between them. The function itself is fitted on 1990 to 2014 only; the conversion line uses later years too. The fitted level at the sample's average bindingness is −0.026 (s.e. 0.079), and the slope is −0.007 (s.e. 0.011) per unit of the mean-based ratio: no detectable gradient. A kinked version places its best-fitting threshold at a median ratio of 0.62. But the kink's slope has a bootstrap 95 percent interval of [−25.63, 0.92], which spans zero. So no threshold is statistically identified over the data's range.

The pre-declared test holds the model out of sample: predict the 2015 to 2026 elasticity from the pre-2015 fit, then compare with the direct estimates. In the bins where today's large-gap pairs mostly fall, ratios of 0.45 to 0.65, the direct estimates of −0.019 and −0.021 land inside the prediction band. The tail at 0.65 and above is different. Only 4 pre-2015 pairs ever reached that bindingness, once their mean-based ratios are converted, so the pre-2015 data cannot discipline a prediction at the extreme tail of today's range. About 31 percent of today's large-gap pairs are in that tail. For that tail we claim nothing: the model's band there rests on only 4 pre-2015 pairs, so the effect is not yet tested, not zero.

The model makes testable predictions, and they fall in that tail, so they will be its first real test. Washington against Idaho, Florida's $15.00 step against Alabama and Georgia, Michigan's $15.00 against Indiana and Ohio, and California's fast-food sector should all show employment elasticities near −0.03. A future estimate whose own confidence interval lies wholly below about −0.19 would falsify it. The implied own-wage employment elasticity (the paper's labor-demand elasticity) at the fit's center is −0.13 (s.e. 0.40). That is consistent with the median across published studies collected by Dube and Zipperer (2024, NBER working paper).

Jha, Neumark and Rodriguez-Lopez (2024, NBER working paper) argue that many border pairs are poor comparisons. Two neighboring counties can still belong to different commuting zones, the areas within which most people both live and work. If they do, they are separate labor markets, and the authors argue this biases the border design toward zero. On County Business Patterns data for 1990–2016, their same-commuting-zone pairs give −0.160 (s.e. 0.107). On the paper's own 1990–2006 data, their commuting-zone pairs give −0.141 (s.e. 0.070), against 0.016 for all pairs.

We split the paper's 1,181 pairs by whether both counties lie in the same 1990 commuting zone, the definition the critique uses. That gives 331 same-zone pairs. We then re-estimated the paper's preferred specification separately for the same-zone and different-zone pairs, era by era, and in the large-gap pairs.

Notes. All rows are our estimates. Balanced contiguous pairs, standard errors two-way clustered by state and border segment. The 2006–2014 era starts in 2006Q3, and 2020 is excluded throughout. Large-gap pairs are those whose gap passed 0.40 log points over 2015Q1 to 2026Q1 (81 same-zone and 145 different-zone pairs).

In the paper's years our same-zone estimate, −0.129 (s.e. 0.145), is close to the critique's. It rests on 131 pairs and the small gaps of that period, so its 95 percent interval, [−0.413, 0.155], is wide. After 2006 the two groups agree in every era. In the large-gap pairs the same-zone estimate is 0.019 (s.e. 0.072), against −0.041 (s.e. 0.063) for different-zone pairs. Earnings respond strongly in the same-zone large-gap pairs (0.130, s.e. 0.028), so the minimum bites there and the zero employment response is informative. One era is weaker: in 2006–2014 the same-zone earnings interval includes zero, so that era's same-zone employment estimate says little.

The answer does not depend on which commuting-zone map is used. With the 2020 commuting zones in place of the 1990 ones, the same-zone large-gap estimate is 0.071 (s.e. 0.087). One limit remains. The critique's broader samples also pair counties that share a commuting zone without touching. We ran touching pairs only, so this tests the critique on the paper's own pairs, not on its full sample.

Dube, Reich, Bhatt and Sosinskiy (forthcoming, Journal of Political Economy Microeconomics) reply to the critique with data that stop in 2019. That is before most of the large gaps opened, so neither side of the exchange had tested the large-gap era.

Taylor and West (2023, NBER working paper) run border pairs on limited-service restaurants and find urban losses (−0.040) against rural gains. Our metro and nonmetro large-gap splits are both near zero, though ours are descriptive and theirs are the paper's focus. Our metro estimate, −0.029 (s.e. 0.050), is close in size to their urban −0.040 (s.e. 0.013), but much less precise, and it covers all restaurants, not only limited-service ones. Our living page for Cengiz, Dube, Lindner and Zipperer (2019) reaches a similar conclusion through 2024 from different identifying variation. That design counts jobs missing below a new minimum against jobs appearing just above it, rather than comparing neighbors across a state line. The extension does not test hours, worker composition, prices or profits, and it keeps the paper's restaurant focus. A zero employment elasticity is compatible with adjustment on any of those margins.

These are the judgment calls and data limits behind our numbers, so you can decide how much weight each result deserves.

The extension studies pulled fresh public data on October 14, 2026. In full: