First, Separate the Worker From the Job
In the U.S. nonprofit labor market, the first question is not whether the average wage is high or low. It is whether the average is being produced by the people and jobs concentrated in the sector, by the pay attached to nonprofit employment, or by both. This chapter focuses on that sorting problem. The practical payoff is a more honest comparison: readers can see why nonprofit workers may have higher raw wages than for-profit workers while a comparable-worker estimate points to a penalty, without treating either number as a mistake.
A sector is a sorting machine
A labor market does not place workers into sectors at random. People enter particular industries and occupations, and employers choose from the workers available to them. The resulting sector average is therefore a mixture of worker attributes, job requirements, hours, and locations. If the mixture differs between nonprofit and for-profit employers, comparing the two averages answers a descriptive question about the sectors as they exist, not yet a causal question about what nonprofit status does to pay.
The BLS evidence makes the mixture visible. Compared with for-profit workers, nonprofit workers are more educated and older, more likely to be women and White, and more likely to work in professional occupations. Their employment is concentrated in service industries, including hospitals, educational and social services, other professional services, and religious organizations. Nonprofit workers also work fewer usual weekly hours on average. None of these facts says that one group is intrinsically more valuable than the other. They say that the two sectors draw from different parts of the labor market and organize work differently.
Education and age illustrate how the arithmetic works. In the BLS comparison for 2018–22, nonprofit workers averaged 15.5 years of schooling and 43.7 years of age, compared with 13.8 years and 40.7 years for for-profit workers. A workforce with more formal education and experience may have a higher average wage even if each worker would receive less in a comparable nonprofit job. The reverse is also possible: a sector concentrated in lower-paid occupations or shorter-hour jobs may have a lower average even when the employers in that sector pay competitively for a given role. The average alone cannot tell us which process is operating.
Industry concentration adds another layer. Hospitals, schools, religious organizations, social-service providers, and professional organizations do not simply offer interchangeable versions of the same job. They operate under different funding arrangements and face different demands for credentials, service quality, and coverage. A nonprofit worker classified within a hospital is part of a different labor market from a nonprofit worker in an arts organization. Even within one occupation, the employer's market and the organization's mission can change the resources available for pay.
This matters for the for-profit comparison because “similar worker” and “similar job” are separate ideas. Two workers may look alike in age and schooling while doing work in industries with different revenue models. Conversely, two organizations may compete for similar skills while employing workers with different backgrounds. The BLS analysis addresses this problem by controlling for both worker characteristics and broad job context, but the control variables do not make every nonprofit and for-profit job equivalent. They make a narrower comparison more plausible.
The public sector is a useful reminder of the same point. Nonprofit workers resemble public-sector workers more than for-profit workers in several dimensions of education, age, occupation, and industry. A three-way comparison can therefore reveal that a nonprofit wage is high relative to one benchmark and low relative to another. The relevant question is not which sector wins a ranking; it is which comparison matches the decision or claim being made. A worker considering a hospital job may reasonably compare nonprofit and for-profit hospitals. A national average that combines hospitals, religious organizations, schools, and arts institutions answers a broader but less specific question.
Sorting also includes choices that are difficult to see in a standard dataset. Workers may value mission, stability, location, schedule, advancement, or the kind of service an organization provides. Employers may value credentials, experience, or a particular form of commitment. The supplied evidence does not establish how much each motive contributes to the pay difference. It does establish why worker selection must be treated as a mechanism to investigate rather than a convenient conclusion. Calling a difference “selection” should mean that the composition of workers and jobs differs—not that nonprofit workers are simply less capable or that their lower pay is automatically voluntary.
The diagram's final arrow is as important as its first. Adjustment can make a comparison more informative without making it complete. It can account for characteristics that are measured consistently, but it cannot automatically observe every skill, preference, career decision, or employer practice. The goal is not to remove all complexity from the labor market. It is to identify which part of the initial difference is plausibly associated with the composition we can observe and which part remains for a more demanding analysis.
What adjustment changes—and what it leaves behind
The BLS article offers a clear example of why the distinction matters. Before controlling for worker characteristics, nonprofit workers earned 5 to 13 percent more than for-profit workers in average hourly wages over 1994–2022. After adjustment, the estimated nonprofit differential became a 4 to 7 percent penalty. The raw premium did not disappear because the authors decided that nonprofit work should look worse. It changed because the adjusted comparison asks a different question: among workers with similar measured characteristics and job contexts, is nonprofit employment associated with a different hourly wage?
The controls cover education, gender, union membership, potential experience and its interactions, race or ethnic status, region, metropolitan population size, hours-worked category, detailed occupation, and broad industry. Together, they make the comparison more disciplined than a simple sector average. They also show why “adjusted” should never be treated as a magic word. The estimate is conditional on the characteristics included, the way categories are defined, and the population retained in the sample. A control can reduce one source of compositional difference while leaving another untouched.
There is a further interpretive choice hidden inside that list. Controlling for occupation and industry asks a within-job-context question: among workers placed in similar occupational and industry categories, how does the nonprofit wage compare? That is useful when the aim is to distinguish sector pay from the fact that nonprofits employ different kinds of workers. But it also means that the analysis is not measuring the total effect of the nonprofit sector's employment mix. If nonprofit status is associated with a particular distribution of occupations or industries, holding that distribution constant deliberately sets that part of the sector's difference aside. The estimate becomes narrower and more comparable, not automatically more complete.
The same logic applies to education, experience, and hours. If nonprofit workers have more schooling or experience, the raw average includes the value of that composition. Once those variables are held constant, the adjusted estimate asks what difference remains among workers with similar measured credentials and histories. If nonprofit workers work fewer hours, an hourly wage comparison removes the direct effect of hours on annual earnings but does not answer whether a worker's total yearly income, schedule, or employment continuity is better. No adjustment is neutral about the question; every variable tells us which part of the original comparison we are trying to isolate.
This is not a technical objection to the BLS analysis. It is the reason the result is useful. The article does not pretend that one regression can answer every compensation question. It gives a carefully defined comparison that can be set beside the raw average and the Census worker–firm analysis. A reader who wants to know why the nonprofit sector has a higher or lower overall wage bill needs composition. A reader who wants to know whether comparable nonprofit workers earn differently needs adjustment. A reader who wants to separate persistent worker characteristics from employer effects needs a design that uses worker mobility. These are successive questions, not competing definitions of truth.
The outcome itself matters. The BLS analysis constructs an hourly wage from usual weekly earnings and usual weekly hours, while the Census analysis uses annual administrative earnings in a defined full-time, main-employer worker-year sample. An hourly wage and annual earnings are related, but they are not the same measure. Hours, employment continuity, and the choice of main employer can matter. So can the way each data system identifies nonprofit status. When two studies use different outcomes and populations, a different estimate is not automatically evidence that one study has failed.
The BLS authors also address problems that can distort a wage comparison before the regression begins. Survey earnings are topcoded, so high values are recorded at a ceiling rather than at the worker's actual amount. The analysis estimates the upper tail rather than treating the ceiling as the true mean. Earnings nonresponse creates another issue: the Census Bureau imputes earnings for some respondents, but the matching process does not use nonprofit status, industry, location, and other wage determinants in the same way. Because those imputations can pull sector differences toward zero, the adjusted analysis drops observations identified as having allocated earnings. It also removes the extreme bottom and top 0.5 percent of hourly wages to limit the influence of outliers.
These choices improve the measurement, but they narrow the claim. The article notes that allocation flags are not available for the 1994–95 CPS files, so those years have a different limitation. More broadly, a survey regression with observed controls is not the same design as a worker–firm model that follows people across employers. The BLS result can show a persistent association after a substantial set of measured differences is held constant. It cannot by itself show that the same worker would receive exactly the estimated amount after moving from a for-profit to a nonprofit firm, nor can it separate a nonprofit firm effect from every unmeasured worker trait.
That distinction helps explain what remains inside the adjusted penalty. Unobserved skills may differ across jobs. Workers may select occupations or employers for reasons not captured in schooling, age, or experience. Organizations may offer nonwage features that the hourly wage measure does not express. Funding, bargaining conditions, service demands, and mission-related utility may influence the wage-setting process. These are possibilities supported by the sources' mechanisms and limitations, not a completed list of causes measured by the BLS regression. The estimate says that the measured composition does not account for the entire raw difference; it does not identify one remaining explanation.
Imagine two workers with the same recorded education, age, occupation, and region. One works for a nonprofit hospital and the other for a for-profit hospital. An adjusted estimate treats this as a more informative comparison than two national averages, but it still does not guarantee that the workers have identical skills, negotiate in the same way, or receive the same nonwage benefits. Nor does it show what would happen if one of them changed employers. A change in pay after a move could reflect the employer, a new role, a new location, a break in employment, or a worker's reason for moving. That is why the question of comparable workers eventually leads to the stronger question of how worker and firm effects can be separated through observed mobility.
This thought experiment also clarifies why a sector estimate should not be used as a shortcut in a career decision. A worker may weigh mission, schedule, stability, advancement, and local alternatives differently from the average worker in the dataset. An organization may have a funding constraint that is not shared by a large nonprofit hospital or university. An analyst may need an occupation-specific comparison rather than a national nonprofit benchmark. The evidence supports asking which trade-off is present; it does not imply that a lower wage is acceptable for everyone who values the mission, or that a higher wage proves better management.
A useful comparison therefore has four parts. It names the population—wage-and-salary workers, full-time worker-years, or another defined group. It names the outcome—hourly wage, annual earnings, or a different compensation measure. It states the comparator and the period. Finally, it explains what adjustment means: observed characteristics in a CPS regression are not the same as worker and firm effects identified through job mobility. Without those four pieces, “nonprofit pay gap” compresses too much information into too few words.
This is also why the adjusted result should not be used to judge an individual worker. A sector estimate describes an average conditional relationship in a particular dataset. It does not tell us what a nurse, teacher, social worker, administrator, or clergy member should earn at a particular organization. Nor does it establish that a lower wage is fair because a mission exists. For a real compensation decision, the relevant comparison may need to be within the same occupation and industry, with local labor conditions, hours, benefits, advancement, and organizational resources considered separately. The sources support that direction of reasoning; they do not supply a universal salary schedule.
The central lesson is thus more precise than “control for everything.” First identify how workers and jobs are sorted into the nonprofit and for-profit averages. Then ask what measured differences can be held constant and what remains uncertain. The BLS reversal—from a raw premium to an adjusted penalty—shows that composition is not a side note. Once it is separated, the residual difference becomes a question about nonprofit institutions, labor supply, and employer-side pay rather than a shorthand judgment about the people who work there. That is the point at which economic theory can do useful work: it can explain why mission and organizational form might change the price of labor in opposite directions.