Voluntary Minimum Wages: The Local Labor Market Effects of National Retailer Policies

Layer 1 — Overview

Research Question

This paper studies the labor market effects of voluntary minimum wages (VMWs) — company-wide, publicly announced wage floors set by large private employers — in the U.S. low-wage retail and service sector from 2014 to 2023. The central questions are: (1) How do VMWs affect wages and employment at the adopting large retailers? (2) Do VMWs generate wage spillovers to other employers in shared local labor markets?

Data and Setting

The authors use anonymized payroll data obtained from a large U.S. credit bureau, covering the wage distributions and employment of over 4,000 firms and approximately 18 million hourly workers (roughly 22–24% of the U.S. hourly workforce) from January 2013 to August 2023. The database is skewed toward retail and service sectors: over a third of covered workers are in retail, and over half in retail and services combined. Critically, the data also include worker flow information — records of individual workers moving between firms — enabling the authors to define shared labor markets via actual employment transitions rather than broad geographic or industry proxies.

The sample of VMW events consists of 20 voluntary minimum wage policies across 5 large retailers (each with over 150,000 employees nationally), restricted to events with no other major wage policy within six months before or after the focal event. Voluntary minimum wage announcements were identified from an inventory maintained by the National Employment Law Project and independently verified through media sources, then matched to anonymized companies using employer size, industry, and observed shifts in the wage distribution.

Identification Strategy

The authors adapt the gap design from the national minimum wage literature. For each company-by-commuting-zone (CZ) cell, the “gap” measures the percent increase in average hourly wages that would be required to bring all workers in the area up to the company’s new voluntary minimum. The gap is averaged over months −6 to −3 before the event (months −3 to −1 serve as a built-in placebo-in-time check). This variation in bite across CZs — arising because the same nominal VMW level implies different wage increases depending on local wage distributions — is combined with a stacked event study across 20 VMW events. Spillover effects are estimated by regressing log average wages at non-policy establishments on the large retailer’s CZ-level gap measure, progressively narrowing the definition of “labor market” from: (i) all non-policy establishments in the same CZ, to (ii) establishments in industries connected to the large retailer by worker flows (15 three-digit NAICS industries), to (iii) specific establishments with documented pre-event worker flows to or from the large retailer (“connected establishments”).

Main Findings

Own effects: For $15 VMW events, moving from a CZ gap of 0 to a gap of 1 is associated with an approximately 88 log point increase in average hourly wages in the six months after adoption. Given that the average establishment-level gap for $15 VMWs is 0.11, the implied average wage increase is approximately 10.45% (the authors’ estimate is 9–10%, consistent with small wage increases even in zero-gap comparison areas). Employment of workers earning under $30 per hour rose by 4.62% after $15 VMW events, 2.01% after major events (affecting ≥30% of workforce), and 1.25% across all 20 events. These employment increases are entirely attributable to reduced separations rather than new hiring: separation rates fell by 0.42, 0.57, and 1.09 percentage points after all, major, and $15 VMW events respectively — equivalent to reductions of 6.57%, 8.73%, and 15.33% relative to pre-period means. Separations specifically to other database companies fell by 0.07–0.19 percentage points (5.63–13.48% relative to base rates). If anything, new hiring fell modestly after VMW adoption. Total monthly base pay and gross compensation both rose after VMWs, indicating increased total take-home pay without compensatory reductions in hours or bonuses. The total employment elasticity with respect to wages ranges from approximately 0.35 to 0.45, while the quit elasticity is 2.20–2.38 (consistent with dynamic monopsony models in which the labor supply elasticity is twice the quit elasticity).

Spillover effects: Across all three definitions of the labor market, the paper estimates precise, economically negligible cross-employer wage spillovers in the six months following VMW events. Cross-employer wage elasticities are statistically indistinguishable from zero across all specifications. Among the most narrowly defined sample — establishments with documented pre-event worker flows to or from the large retailer — the upper bound of the confidence interval rules out spillovers greater than 0.2% of wages. No wage spillovers are detected for new hires at non-policy establishments either. These null results are confirmed over a 12-month post-event horizon for the subsample of events with no other major policy nearby.

Mechanism: The reason for negligible spillovers is that VMWs reduced labor market churn rather than expanding the large retailer’s total employment. Hiring away from large retailers by connected non-policy firms falls after VMW adoption — consistent with fewer separations to recruit from — but overall hiring by non-policy firms does not decline, as these firms substitute toward other hiring sources. This substitutability across new hire sources in a thick market is the proximate explanation for the absence of wage pressure on competitor firms.

Scope Conditions

Results pertain to large national retailers (>150,000 employees) operating in U.S. commuting zones during 2014–2023. The database covers only employers large enough to participate in credit bureau income verification; smaller employers (representing over 75% of U.S. hourly workers by the BLS comparison) are not observed, and the authors caution that spillover effects on smaller firms cannot be assessed. The authors also explicitly note that their null local spillover results do not rule out national-level strategic wage-setting dynamics — the rapid sequential adoption of VMWs across major retailers may reflect national-level competition rather than local market competition.

Layer 2 — Q&A

Q1: What exactly are “voluntary minimum wages” and how do they differ from statutory minimum wages?

Voluntary minimum wages (VMWs) are company-wide, publicly announced wage floors set unilaterally by private employers, typically well above the applicable statutory (federal, state, or local) minimum. Unlike statutory minimums, which bind all employers in a jurisdiction, VMWs apply only to the announcing company across all of its geographic operations in the U.S. The paper studies VMWs adopted by retailers with over 150,000 workers, which include wage floors at levels such as $9, $10, $12, and $15 per hour. $15 VMWs were adopted at a time when few states or localities had yet reached that threshold, meaning the policy bit into the company wage distribution far more deeply than prevailing statutory floors.

Q2: How were VMW events identified and matched to anonymized firms in the payroll database?

VMW events were identified from a database maintained by the National Employment Law Project and verified through an independent review of business news articles. These publicly reported announcements were then matched to the anonymized companies in the credit bureau payroll database using employer size, industry, and the timing of observed shifts in the firms’ wage distributions. An additional three events were identified directly from data: months where the share of workers earning below a given wage level dropped by at least 15 percentage points (for non-$15 events) or 10 percentage points (for $15 events) while the share at exactly that wage bin jumped by at least 10–20 percentage points. The final sample of 20 events was restricted to those with no other major wage policy in the six months before or after.

Q3: How does the gap design work and why does it improve on the fraction-affected approach?

The gap for a given company, commuting zone, and time period is defined as the total wage increase needed to bring all sub-$30 workers up to the company minimum, divided by total wage costs — formally a labor-share-weighted average shortfall from the new minimum across wage bins. The gap leverages more cross-sectional variation in treatment intensity than the simple fraction of workers below the minimum: for a $15 VMW, an area where all workers earn $10 has a gap of 0.50 while an area where all earn $12 has a gap of 0.25. The gap is averaged over months −6 to −3 before the event. The period months −3 to −1 then serve as a placebo window: genuine VMW effects should appear only after the policy’s adoption month, not during the period immediately after the gap is measured. If instead the regression picks up mean reversion in noisy wage data, spurious effects would appear in months −3 to −1 rather than at event time 0.

Q4: What is the magnitude of the wage effect on the large retailers themselves?

For $15 VMW events, the stacked event study estimates that moving from a gap of 0 to a gap of 1 is associated with an approximately 88 log point increase in average hourly wages beginning exactly in the month of policy adoption. Given the average establishment-level gap of 0.11 for $15 VMWs, this implies the average establishment raised wages by approximately 9–10% (the authors compute 10.45% from the average gap, consistent with a slight dampening because zero-gap CZs experienced marginally higher wages too). Wage increases are confirmed persistent at 12 months in robustness checks. For all 20 VMW events pooled, effects are somewhat smaller commensurate with the lower average bite.

Q5: How did VMWs affect total employment and its components at the large retailers?

After $15 VMW events, log total employment of sub-$30 workers rose by 4.62%; after major VMW events (≥30% bite), 2.01%; after all 20 events, 1.25%. The increases are entirely driven by retention gains. Separation rates fell by 1.09 percentage points after $15 VMWs, 0.57 p.p. after major events, and 0.42 p.p. after all events — translating to reductions of 15.33%, 8.73%, and 6.57% relative to pre-period means. Separations to other database companies specifically fell by 0.07–0.19 percentage points (5.63–13.48% relative to the base mean). New hiring — measured as year-on-year log change in hires to control for seasonality — fell after VMW adoption, consistent with a reduced need to replace departing workers.

Q6: What do the labor supply elasticities implied by the VMW results look like?

The total employment elasticity with respect to wages ranges from approximately 0.35 to 0.45 across the three event groupings. Under standard dynamic monopsony models, the labor supply elasticity facing the firm equals twice the quit elasticity in steady state (Manning, 2003). The quit elasticity — derived by dividing the proportional reduction in separations by the log wage increase — ranges from 2.20 to 2.38, consistent with the earlier monopsony-based case study of Ford’s $5 workday (Raff and Summers, 1987) and implying substantial firm-level wage-setting power.

Q7: Did VMWs increase total take-home pay or were wage gains offset by reductions in hours or bonuses?

The paper examines log average monthly base pay and log average gross compensation (which includes bonuses and overtime) as additional outcomes. Both measures rose after $15 VMW events, indicating that the wage floor increase translated into genuine improvements in total take-home pay without compensatory reductions in hours or other non-wage compensation. The monthly gross pay series is an average over calendar year-to-date months, so increases appear gradually rather than as a sharp jump at the adoption month; nevertheless the upward trend is evident and consistent.

Q8: What are the estimated spillover effects on wages at non-policy employers?

Across all three definitions of the labor market — all non-policy establishments in the same CZ, establishments in the 15 connected industries in the same CZ, and establishments with documented pre-event worker flows — the estimated cross-employer wage effects are precise zeros. The stacked event study in the post-period shows coefficients centered on zero with small confidence intervals. The difference-in-differences cross-employer wage elasticity (instrumenting the large retailer’s wage change with the gap) is also indistinguishable from zero. Among the most exposed connected establishments, the point estimate is slightly positive but economically negligible; the upper confidence interval bound rules out spillovers greater than 0.2%. Results are confirmed over a 12-month horizon for the clean-event subsample.

Q9: Could the null spillover result reflect mean reversion bias rather than a true zero?

The authors address this concern explicitly. For the policy-company gap design, they build in a placebo-in-time check by measuring the gap over months −6 to −3 and checking that no wage effects appear in months −3 to −1. For the non-policy spillover analysis, they also examine an alternative treatment variable — the gap between non-policy establishments’ wages and the large retailer’s new VMW — and find evidence of mean reversion: wages begin rising in the pre-period in the direction of this gap measure. They correct for this by detrending post-period estimates using a linear extrapolation of the pre-period trend. After detrending, spillover effects remain indistinguishable from zero.

Q10: Why are spillover effects so limited if the large retailer is drawing fewer workers away from competitors?

The paper’s mechanism analysis shows that while the probability of a non-policy firm hiring a worker from the large retailer falls after a VMW event (consistent with fewer separations to recruit from the large retailer), the overall rate of hiring by non-policy firms does not decline. Non-policy firms substitute toward other hiring sources — primarily other non-policy companies — rather than hiring fewer workers overall. This substitutability across recruiting sources in a thick labor market mutes the competitive pressure on competitor wages: since non-policy firms can replace the reduced flow from VMW companies with workers from other sources without changing total employment, they face no pressure to raise wages.

Q11: How do the results differ when focusing on CZs where the large retailer accounts for a larger employment share?

The authors test whether larger local market presence amplifies spillovers by splitting the sample at the median employment share of the large retailer in the CZ. They find no evidence of positive wage spillovers even in CZs where the large retailer’s employment share is above the median, confirming that neither local market size nor market concentration is a mechanism for spillover transmission in this setting.

Q12: How do these VMW spillover results compare to prior evidence on employer wage-setting spillovers?

The main prior U.S. evidence (Staiger et al., 2010) studied a federally mandated wage increase at Veterans Affairs hospitals and found a cross-establishment wage elasticity of approximately 0.19 for registered nurses at neighboring hospitals. The authors note two key differences: first, the VA policy increased both wages and employment at treated facilities, whereas VMWs primarily reduced separations without increasing hiring, so the supply of workers to competitor firms was not squeezed. Second, the market for low-wage retail and service workers is likely thicker (more potential hires available) than the market for registered nurses, allowing competitors to substitute hiring sources without bidding up wages.

Q13: What do the null local spillover results imply about national-level wage dynamics?

The authors explicitly caution against reading the null local spillover result as implying VMWs have no broader effect on the low-wage labor market. The rapid and successive adoption of VMWs across major retailers during 2021–2022 could reflect national-level strategic wage-setting competition — firms mimicking each other’s announcements in an arms-race dynamic during tight labor markets — rather than local competitive transmission. The paper does not test for national-level strategic interactions and calls for further research on this dimension.

Key Concepts

Voluntary Minimum Wage (VMW): A company-wide, publicly announced wage floor set unilaterally by a private employer, applying across all of the firm’s geographic operations in the U.S., typically well above applicable statutory minimums. Distinct from legally mandated minimum wages in that they bind only the announcing firm and arise from the firm’s own strategic or reputational motivations.

Gap Measure: Borrowed from the national minimum wage literature (Card, 1992; Draca et al., 2011), this is the percent increase in a firm’s average hourly wage that would be required to bring all workers in a given commuting zone up to the company’s new voluntary minimum. Formally the labor-share-weighted average shortfall from the VMW across sub-$30 wage bins. A gap of 0 means no workers fall below the new minimum; a gap of 1 means all workers would need to be raised to the minimum, doubling the average wage. Used as a continuous treatment variable capturing the local bite of the policy.

Stacked Event Study: An empirical design in which a separate 12-month panel (6 months pre- and post-event) is constructed for each of the 20 VMW events, these datasets are stacked, and the effect of the continuous gap treatment is estimated jointly across all events, with event-specific indicators interacting all regressors to allow each event to have its own intercept.

Placebo-in-Time Check: A robustness test built into the gap design by computing the gap over months −6 to −3 and verifying that wage effects do not appear in months −3 to −1 (the period between gap measurement and VMW adoption). Genuine policy effects should materialize at the adoption month; spurious effects driven by mean reversion in noisy wage data would appear in months −3 to −1 because the gap would mechanically predict wage reversion toward the mean in the period immediately following its measurement.

Connected Establishments / Poaching and Feeder Establishments: Specific firm-by-CZ cells identified as sharing a labor market with the large retailer via actual worker flows. “Poaching establishments” hired at least one worker from the large retailer in the 12 months before the VMW event. “Feeder establishments” had at least one worker subsequently hired by the large retailer in the same pre-period. These are the most narrowly defined and most economically relevant labor market competitors for testing spillover effects.

Quit Elasticity / Labor Supply Elasticity (Firm-Level): The quit elasticity is the percent change in the separation rate divided by the percent change in wages induced by the VMW. Under standard dynamic monopsony models (Manning, 2003), in steady state the recruit elasticity equals the quit elasticity, and the firm-level labor supply elasticity equals twice the quit elasticity. The authors estimate quit elasticities of 2.20–2.38, implying labor supply elasticities of 4.40–4.76 to the firm — consistent with meaningful but not extreme monopsony power.

Cross-Employer Wage Elasticity: The percent change in wages at a non-policy employer’s establishment associated with a 1% change in wages at the large retailer in the same commuting zone, instrumented using the large retailer’s gap interacted with the post-event indicator. Estimated to be a precise zero across all market definitions and event groupings in this paper.