When California announced it would push the minimum wage for fast-food workers at large chains to $20 an hour in April 2024, the prediction from many corners was straightforward: jobs would vanish. The new floor sat far above what most low-wage workers earned, and franchise operators warned of layoffs and shuttered locations. So what actually happened to fast-food employment in the year and a half after the law took effect?
A new NBER working paper takes up that question. The answer it offers is that pay rose substantially, while the number of jobs barely moved.
A demanding test for a high wage floor
The law in question, Assembly Bill 1228, applies only to fast-food chains with 60 or more locations nationwide. Independent restaurants and full-service establishments stayed under California’s general $16 minimum. That partial coverage is part of what makes the case so interesting. Customers can shift their spending toward uncovered competitors, and employers have reasons to reshuffle operations between covered and uncovered categories. If a high minimum wage were going to destroy jobs anywhere, a setup like this would seem to give it room to do so.
The size of the increase also stands out. Economists often measure a minimum wage’s reach using something called the Kaitz ratio, which compares the wage floor to the typical (median) wage in the area. At $20, the covered fast-food wage reached roughly 77 percent of California’s median hourly wage. That is the highest such ratio for fast-food workers anywhere in the country, and well above the 42 to 62 percent range seen in recent statewide minimum wage hikes.
Arindrajit Dube, an economist at the University of Massachusetts, Amherst, set out to measure the policy’s effect on wages and jobs. Two earlier studies of the same law had reached somewhat different conclusions, and Dube’s paper tries to understand why, while bringing in a data source the earlier work did not use.
Two ways of counting jobs
Dube draws on two government datasets, both built from unemployment-insurance records that cover nearly all private employment. The first, the Quarterly Census of Employment and Wages, counts every worker who received pay during the period containing the 12th of each month. The second, the Quarterly Workforce Indicators, counts workers present at the same employer in two consecutive quarters, giving a point-in-time snapshot of jobs. The detailed fast-food files needed from the second source were released only in early 2026, which is why prior studies had not used them.
The distinction matters more than it might sound. If a single position is filled by two different people during the same pay period, the first method counts both. That means when worker turnover falls, the first dataset’s headcount can shrink mechanically even if the true number of jobs is unchanged. The second dataset is largely immune to that quirk. As we will see, this difference becomes central to reading the results.
To estimate the policy’s effect, Dube compares California to up to 20 states that kept their fast-food minimum at the federal floor of $7.25. The basic tool is a difference-in-differences design, which tracks how an outcome changes in the treated state relative to comparison states over the same period. The headline number researchers use to summarize results is the own-wage elasticity of employment, which asks: for every 1 percent that wages rise, by what percent does employment change? An elasticity of zero means jobs held steady; a value of negative one would mean employment fell as fast as wages rose.
The trend problem and a workaround
Dube identifies a wrinkle that complicates the simple comparison. California’s fast-food employment did not follow a smooth path in the decade before the law. It lagged the comparison states in the mid-2010s, gradually caught up through 2019, rebounded sharply after the pandemic, and leveled off near parity by 2023. With only one treated state, this bumpy history feeds directly into the estimate, since there is no pool of treated states whose idiosyncrasies cancel out.
To address this, Dube applies synthetic difference-in-differences, a method that builds a custom comparison group by weighting control states to closely mirror California’s pre-policy trajectory. The resulting synthetic California, drawn mostly from Idaho, Utah, Pennsylvania, Texas, and Georgia, tracks the real state’s path through 2015 to 2023 and shows no clear break after the law took effect.
What the numbers showed
Across all the approaches, the wage effect was large and consistent: pay in covered fast-food jobs rose by roughly 7 percent, an increase that held up across every specification Dube ran.
The employment picture was far more muted. The conventional difference-in-differences produced an own-wage elasticity of negative 0.19, meaning a modest job decline. The synthetic-control version shrank that to negative 0.04, statistically indistinguishable from zero. The point-in-time jobs data leaned even more positive, with 12 of 16 specifications showing flat or slightly higher employment. Pulling together all 32 estimates, the elasticity ranged from negative 0.29 to positive 0.26.
To put that in context, Dube computes the same measure for 26 statewide minimum wage increases since 2010 and finds a median elasticity of negative 0.02. California’s law, despite its much larger reach, landed comfortably inside that range. As Dube writes, the $20 minimum was “set at a level many predicted would produce large job losses,” yet “raised pay for low-wage workers with modest to no employment costs.” Because wages rose much more than any employment dip, total earnings for fast-food workers as a group increased.
Why turnover may explain the differences
One of the paper’s distinct findings comes from worker flows. The rate at which fast-food workers separated from their jobs fell sharply in California, dropping somewhere between 13 and 25 log points. Dube interprets this as evidence for a monopsony model of the labor market, in which employers hold some power to set wages below what a fully competitive market would pay. In that setting, raising wages reduces the rate at which workers quit, which lowers hiring and training costs and softens any need to cut staff.
This drop in turnover also helps reconcile why the two datasets gave somewhat different employment numbers. Because the first dataset double-counts positions filled by more than one worker in a pay period, a fall in turnover deflates its headcount even when actual jobs are steady. Dube’s calculations suggest this single mechanical channel can account for most of the gap between the two measures. He treats the point-in-time jobs figure as the more reliable one in this case.
The effects also concentrated where the law was designed to bite. Wage increases ran 10.4 to 11.8 percent at the largest firms covered by AB 1228, but only 1.1 to 2.4 percent at the smallest firms, which are mostly exempt. The drop in separations followed the same pattern. Dube argues this alignment between the law’s footprint and its statutory coverage suggests the estimates capture the policy itself rather than some broader California-specific shift, and points to limited wage spillovers onto uncovered businesses.
Reading the results carefully
A few caveats are worth keeping in mind. This is a working paper that has not yet been peer-reviewed. It examines one policy in one state, and the partial coverage and unusually high wage floor make it a specific case rather than a universal verdict on minimum wages. The author also notes that earnings calculations describe the group of workers as a whole; any individuals who did lose hours or jobs are worse off even if the total wage bill rose.
Dube’s broader takeaway is methodological as well as substantive. With a single treated state and a bumpy pre-policy history, the choice of comparison group can swing the headline number, which is why he favors synthetic-control methods that match California’s trajectory directly. On that basis, he concludes that “the sectoral standard in California appears to have worked largely as intended.”
