Why the Headline Number Flips
The H-1B program’s central wage question is not whether its workers are high earners in the abstract, but how the pay attached to a new, employer-sponsored hire compares with the pay of a suitably defined U.S.-born worker. This chapter focuses on the mechanism behind the apparent reversal from an H-1B raw advantage to an adjusted disadvantage. Understanding that mechanism lets the reader interpret a regression as a structured comparison—and see why its result still cannot speak for every employer or explain every cause.
From broad comparison to conditional estimate
Start with two groups standing in the same labor market but not occupying the same distribution of jobs. H-1B workers in the study are disproportionately young, male, highly educated, and concentrated in high-paying technical occupations and metropolitan areas. The native comparison group is more dispersed across occupations, industries, and places. If those differences are left in the data, a wage comparison mixes the effect of being an H-1B worker with the effect of being more likely to work in software, in a major technology hub, or in a highly paid industry.
The first estimate therefore asks a broad question: what is the average wage difference between the observed H-1B and native samples? In the revised NBER analysis, H-1B workers have a raw advantage of about 4.4 percent in the initial specification. That result is compatible with the Economic Innovation Group’s broader comparison, which reports median H-1B pay of $120,000 in 2024 versus $67,000 for the average native-born worker. Both numbers can be true because neither is yet an apples-to-apples comparison of workers with the same job-related characteristics.
The next step changes the question. A regression adds metropolitan-area controls so that the comparison is no longer driven simply by the fact that H-1B workers cluster in particular labor markets. The apparent advantage disappears. Adding education, age, gender, and occupation controls produces a disadvantage of about 13.6 percent. Adding industry fixed effects produces an adjusted gap of −0.161 log points, described in the paper as roughly 16.1 percent.
The sequence is not a series of increasingly aggressive corrections applied to one fixed fact. Each step defines a different counterfactual. The raw estimate asks what the observed groups earn. A geography-adjusted estimate asks what remains after their locations are made more comparable. A skill-adjusted estimate asks what remains among workers with similar measured education, age, gender, and occupation. The fully specified estimate adds industry differences. The number moves because the question moves.
A simple example makes the logic concrete. Suppose the H-1B sample contains many software developers in San Jose, while the native sample contains more managers, nurses, and accountants spread across the country. The H-1B group may have a higher raw average because of its occupational and geographic mix. If the analysis then compares a software developer with another software developer in the same broad labor market and with similar observable education and age, the relevant difference can point in the other direction. The controls do not prove that the H-1B worker is paid unfairly; they remove selected sources of compositional difference so that a narrower association becomes visible.
The paper also reports a similar pattern in a median-log quantile specification. The unadjusted median advantage is about 7.2 percentage points, but after the covariates it becomes a 15.2-point disadvantage. This matters because the reversal is not created solely by a few extremely high or low earners. At the same time, the dollar and log summaries should not be treated as interchangeable. When two groups have different wage distributions, the arithmetic mean in dollars and the mean of log wages can point in different directions. The unit of measurement is part of the result.
There is a second reason to resist reading the control sequence as a moral ranking of estimates. Geography is not merely scenery around a wage; it can represent access to a labor market, cost of living, and the kinds of employers located there. Occupation is not just a label; it is a coarse description of work that may still contain different responsibilities. Industry can capture pay-setting practices that are not visible in an occupation code, but it can also bundle firms and jobs with very different production processes. The fully specified coefficient is meaningful only relative to the analyst’s decision to treat these dimensions as the relevant sources of comparability.
The construction also works in one direction. The analyst uses the native sample to predict what a worker with the H-1B beneficiary’s observed characteristics would earn, then compares that predicted value with the petition wage. The prediction is not an offer made to that worker by a real alternative employer. It is a model-based counterfactual assembled from the native group. This is why the result can be useful for asking whether observable characteristics explain the pay difference while remaining unable to tell us what an individual employer would actually have paid.
The diagram should be read from left to right as a change in the comparison, not as a machine that discovers a final truth. A control can make two groups more alike along one dimension while leaving important differences untouched. It can also encode a substantive judgment about which differences should be held constant. Holding occupation fixed may be useful when the question concerns pay within broad job categories. It does not show whether the worker would have chosen that occupation without the visa, whether the job differs in quality, or whether an H-1B worker brings skills not recorded in the data.
Consider the kinds of differences that can survive the sequence. Two software developers may have different responsibilities, customer-facing demands, security clearances, or employer-specific skills even if they share a Census occupation code. Two workers in the same metropolitan area may face different commuting patterns or labor-market segments. Age and education are observable, but ambition, negotiation ability, immigration alternatives, and productivity are not captured in the same way. These omissions do not invalidate the comparison. They define the remaining interpretive burden: the coefficient summarizes what is left after the selected variables, not everything that makes one hire different from another.
The location split makes the selection problem visible without solving it. The revised paper finds a larger adjusted disadvantage for beneficiaries receiving visas abroad than for those already in the United States. That pattern might be consistent with different access to information, different educational pathways, different employers, or different unobserved skills. It is evidence that the H-1B population is not uniform; it is not a test that identifies which explanation is correct. A regression can expose a pattern and still leave the mechanism open.
This is why a fully adjusted coefficient is best described as a conditional association. It is evidence that, within this sample and specification, H-1B petition wages are lower than the wages predicted for a constructed U.S.-born baseline with selected characteristics. It is not a direct estimate of the causal effect of visa status. The coefficient could reflect employer bargaining power, unobserved productivity, different job responsibilities within a common occupation, selection into employers, or the way the two datasets measure wages. The controls reduce some uncertainty; they do not make the remaining uncertainty vanish.
To identify one of those mechanisms, the evidence would need to do more than align demographic and job categories. A study of bargaining power would need information about mobility, offers, and the costs of changing sponsors. A productivity explanation would need output or performance measures, not only the wage paid. A compliance investigation would need the employer’s applicable wage determination and payroll records. The merged regression is not defective because it lacks all of this; it is answering a narrower question. The mistake would be to borrow its coefficient as if it had collected evidence for a broader one.
The location split illustrates the point. In the revised paper, the adjusted disadvantage is about 21.9 percent for beneficiaries receiving their visas abroad and 11.8 percent for those already in the United States. Workers already in the country may include former foreign students and may have more information about the U.S. labor market. That difference is consistent with several stories, including different worker populations and different bargaining positions, but it does not select one story on its own.
The average hides different employers
The aggregate coefficient becomes even less suitable as a universal label when the employer dimension is restored. The H-1B petition identifies the firm, so the paper can estimate how the typical H-1B worker at a given firm compares with the constructed native baseline. Those firm estimates vary sharply. Average H-1B salaries range from more than $170,000 at Meta and Apple to about $97,000 at Infosys and Tata Consultancy Services. Google’s adjusted gap is close to zero, while Meta’s is positive. Wipro, HCL, and Tech Mahindra show large negative gaps in the paper’s table.
The exact table illustrates the spread without turning it into a league table. Google’s adjusted log gap is −0.002 and IBM’s is −0.025, while Meta’s is +0.107. Wipro’s is −0.397, HCL’s −0.357, and Tech Mahindra’s −0.371. These figures are useful because they attach the aggregate question to identifiable employer patterns; they are not a claim that a company’s coefficient is the wage difference inside every team or job it operates. The table also includes positive estimates at employers such as Walmart and McKinsey, showing why the program cannot be described by a single direction even within the largest firms.
These contrasts are not simply a list of good and bad companies. A firm coefficient compares the typical H-1B worker associated with that employer with a comparable native worker in the broader high-skill labor market. The paper explicitly cautions that the coefficients do not estimate a within-firm wage effect. They can reflect the firm’s pay practices, the types of workers it recruits, the jobs it sponsors, and the locations in which those jobs exist. A positive coefficient at one employer and a negative coefficient at another can therefore coexist without either one explaining the entire program.
The distinction between “at a firm” and “inside a firm” is important for interpretation. If an employer sponsors unusually specialized workers, the coefficient may reflect that selection. If it sponsors entry-level workers in one occupation and experienced workers in another, a single firm label compresses those differences. The estimate remains relevant to the employer’s observed H-1B hiring pattern, but it cannot tell us whether two employees doing the same work receive different pay. That would require a different design and more detailed within-employer information than the supplied analysis reports.
The concentration pattern makes the aggregate interpretation more subtle. Nearly 75 percent of H-1B hires in the sample are outside the 25 firms with the most petitions. The data identify 46,146 distinct firms with at least one hire over the four-year period; the median firm hired one H-1B, and the 75th-percentile firm hired three. The largest outsourcing firms are visible, but they do not account for every observation.
That is why the paper examines “all other firms,” whose adjusted gap is about −18.7 percent. It also estimates a sizable negative gap among firms that hired only one H-1B worker and among firms that hired at most three. These results argue against a narrow explanation in which the mean is produced only by a handful of large outsourcing pipelines. But they do not justify the opposite overstatement—that every employer pays H-1B workers less than market wages. Sparse observations at many firms make firm-specific estimates uneven, and the constructed native baseline remains the same kind of comparison problem.
Employer heterogeneity also changes the policy stakes. If an average negative coefficient represented one uniform employer practice, a single fee might be evaluated against a relatively simple response. If the coefficient combines technology companies paying premiums, outsourcing firms paying deficits, and thousands of small employers with different hiring patterns, the incidence of a fee will vary. Some firms may be paying for access to a worker whose wage is already high relative to the baseline; others may be benefiting from a lower wage or from skills that the regression does not observe. A policy aimed at the mean can therefore affect firms and workers who sit on opposite sides of it.
The safest interpretation is layered. The raw comparison tells us that H-1B workers are concentrated in jobs and places with high pay. The adjusted comparison tells us that, after selected observable differences are accounted for, petition wages are lower than predicted native wages in the revised NBER specification. The firm results tell us that the association is distributed unevenly across employers. None of those statements alone identifies the underlying cause.
It also matters which population is being averaged. A large negative estimate among “all other firms” can coexist with near-zero or positive estimates at prominent technology companies because the mean gives more weight to the entire observed workforce than to the examples readers are most likely to recognize. Conversely, a few visible outsourcing firms can make the debate feel more settled than the broader distribution warrants. The paper’s findings argue that the aggregate result is not only a story about a handful of firms, but they do not turn the remaining firms into one homogeneous group.
Before treating the adjusted number as an answer to “what H-1B workers are paid,” ask what it has actually held constant and what it has not. The next boundary is especially important: a conditional coefficient is a statistical comparison, while a legal wage rule uses an employer’s actual wage and the prevailing wage for a particular employment. The evidence becomes more useful when those questions remain separate rather than being fused into a single verdict.