A Universal Basic Income and Work Incentives: What Does the Empirical Evidence Tell Us?

In Part 1 of this series, I outlined some basic economic theory regarding a universal basic income (UBI) and work incentives. By a UBI, I mean an income support policy that provides a set monthly benefit to every citizen. A UBI, as I define it, would to everyone, regardless of income, wealth, or employment status. In that respect it differs from means-tested income support policies (MTIS), such as current US welfare system programs or a negative income tax (NIT), which reduce benefits as the recipient’s income increases.

The fear that a UBI would undermine work incentives is among the most important sources of resistance to the idea. In Part 1, I argued, on theoretical grounds, that replacing the existing welfare system with a UBI would tend to increase average work effort. This part will look at several sources of evidence that support the theory, beginning with the famous income maintenance experiments (IMEs) of the 1970s and 1980s.

What we can learn from the IMEs and what we can’t learn

The income maintenance experiments in question followed a method known as randomized field trials. Each of the experiments enrolled from several hundred to several thousand households and divided them into two groups. They assigned one group to an experimental income support policy while a control group continued to be covered by existing welfare programs, including Aid for Families with Dependent Children (AFDC), food stamps, and others. IMEs testing various policies took place in New Jersey, Iowa, North Carolina, Indiana, Colorado, and Washington. They covered both urban and rural areas; both single parent and two-parent households; and various ethnic groups.



UBI critics have pointed to the IMEs as a key source of evidence about the work incentive effects of a UBI. As Pascal-Emmanuel Gobry puts it: 

Science, properly understood, is the testing of hypotheses through rigorous experimentation. This is not what most published social science studies do.  . . There is, however, one way to gain relatively reliable social-scientific evidence: randomized field trials. . . The UBI is one of the very few, if not the only, domains of social science policy where we have exactly that: extensive, long-term, repeated RFTs, which are the gold standard of evidence in social science.

It is important, then, to understand exactly what these experiments can and can’t tell us. Let’s begin with a key negative: We can learn nothing directly from the IMEs about the effects of a UBI because they did not test such a policy.

Instead, the IMEs tested several variants of a negative income tax. An NIT and a UBI are not the same thing. As explained in Part 1, an NIT is means-tested. All versions of the NITs tested in the IMEs incorporated substantial benefit reduction rates, ranging from 30 to 80 percent. In contrast, a UBI has no benefit reductions. It would be fair to say, then, that the IMEs offer no direct evidence about the effects of a UBI, any more than a clinical trial of the effects of vitamin C on heart attacks would offer evidence about the protective effects of aspirin.

The confusion between a UBI and an NIT is partly a matter of terminology. In a recent essay for Cato Unbound, Matt Zwolinski employs another term, Basic Income Guarantee (BIG), to refer to a broader family of income support programs that have the common feature of guaranteeing a minimum level of income to everyone. A UBI, as I have defined it, is the most "universal" member of the BIG family in the sense that everyone gets the full payment regardless of income, wealth, or work status with no benefit reductions. In addition, BIGs, as Zwolinski defines them, also include NIT policies such as Milton Friedman’s early version, the NIT variants tested in the IMEs, and related programs like a plan advanced by Charles Murray . All of these policies include provisions that reduce the basic benefit by a fraction of a dollar for each dollar earned, beyond some defined amount.

Critics have not always been careful to distinguish between a UBI and an NIT, nor have they consistently recognized that the two have different incentive effects. For example, Manzi, in responding to Zwolinski’s arguments for a BIG, simply recycles a set of arguments that he used in an earlier National Review article about a negative income tax. In doing so, he claims that the IMEs of the 1970s and 1980s showed “every tested variant of a BIG to have pernicious effects” on work incentives. That contention is literally true, inasmuch as all the “tested variants” were one or another formulation of a negative income tax. What Manzi fails to note is that none of the IMEs tested a true UBI.

Let’s turn now to the positives—to what we can hope to learn from the IMEs. The first thing would be something about the incentive effects of a negative income tax.

As Gobry, Manzi, and other critics point out, the raw data from the IMEs show that almost all experimental groups reduced their average work efforts compared to their controls. Gary Burtless of the Brookings Institution summarizes the data in Table 2 of a paper that he prepared for a 1986 conference sponsored by the Boston Fed. The table shows that husbands reduced their work by an average of 119 hours per year, wives by an average of 93 hours, and single female heads of households by an average of 133 hours per year. Only two subgroups, black husbands in New Jersey and black wives in Gary, Indiana, increased their work compared to their control groups.

Those results concerning the effects of an NIT should come as no surprise to anyone who has read Part 1 of this series. In Figure 2 of Part 1, we saw that “sweetening” an existing means-tested welfare scheme by increasing the minimum income guarantee and reducing the benefit reduction rate would produce ambiguous results. Some participants would increase their work efforts and others would cut back. The greater the increase in the minimum income guarantee, the more likely a reduction in average work effort, because of the income effect. The greater the decrease in the benefit reduction rate, the more likely an increase in work effort, because of the substitution effect. Also, an increase in either parameter would increase the number of people eligible for the program, thereby potentially reducing the work effort of people who previously had incomes just above the new cutoff level.

Interpretation of the raw data on work responses is complicated by fact that the NIT plans faced by the experimental groups included variations in both the minimum income guarantee and the benefit reduction rate. Furthermore, the tested NITs were not always “sweeter” in both respects compared to the welfare policies available to their respective control groups. Some experimental groups received minimum income guarantees of as much as 135 percent of the poverty level, well above what they would have received from AFDC and food stamps, while others received as little as 50 percent of the poverty level. Some experimental groups faced benefit reduction rates of up to 80 percent, which would have been higher than the benefit reduction rates faced by at least some households in the control groups. Other experimental groups faced benefit reduction rates of as little as 30 percent, which would have been lower than those faced by the control groups. Still, according to analysis of the data presented in Burtless’ Table 4, the effects of changes in each parameter, taken separately, appear to be broadly consistent with the theoretical model presented in Part 1 of this series:

• For both intact families and single heads of household, groups facing a 75 percent benefit reduction rate under the NIT exhibited greater average labor withdrawal than those facing a 50 percent rate.
• For both intact families and single heads of households, groups with higher guaranteed minimums had a greater reduction in work hours.
• Husband-wife families showed a greater reduction in work than single parent families, which is what we would be expect if the control groups of the single parent families were more likely to be on welfare plans with high benefit reduction rates.

Unfortunately, these findings are clouded by methodological flaws in the IMEs. An overview of the findings of the Boston Fed conference points to numerous problems with design, execution and analysis, including inadequate theoretical models, poor formulation of objectives, and unsatisfactory management and administration. These methodological problems cast doubt on whether evidence from the IMEs really meets the “gold standard” characterization.

The most important problem was apparently widespread underreporting of work effort by participants in the experimental groups. To quote Burtless,

Several analysts have found evidence that at least part of the employment and earnings reduction reported in the experiments was spurious. Recipients of negative income tax payments had a clear incentive to underreport their employment and earnings, because to do so permitted them to receive a larger payment than the one to which they were legally entitled. Wage earners enrolled in the control group did not face this kind of misreporting incentive.

Burtless goes on discuss studies that use other data sources, including IRS records, to correct the reporting bias. In the Gary experiment, underreporting appears to have accounted for all of the negative work response. In the Seattle-Denver experiment, underreporting did not greatly change the work response of heads of households, but the reported reduction in hours disappeared for secondary workers.

 In an invited response to Burtless’ paper, Orley Ashenfelter of Princeton University notes that a failure to address the problem of underreporting in advance represented a serious design flaw of the IMEs:

Only an experiment fully informed at the design stage about the possibility for income underreporting, and that tested for its effect, would shed any light on this critical issue. Sadly, the design of none of these experiments was so informed.

By ignoring the evidence of underreporting, critics like Manzi and Gobry overstate the case not only against a UBI, but also against an NIT. As if that were not enough, they compound the overstatement by implying that the observed work reductions represented withdrawals from the labor force. For example, Gobry maintains that as a result of a BIG in any form,

millions of people who could work won't, just listing away in socially destructive idleness, with the consequences of this lost productivity reverberating throughout the society in lower growth and, probably, lower employment, in a UBI-enabled vicious cycle.

Instead, according to research cited by Dylan Matthews in a recent post on Vox, even among participants in the IMEs who reduced their hours worked, full withdrawal from the labor force was a relative rarity. Instead, the reduction in hours worked more often took the form of longer periods of job search between spells of employment. For some that might mean loafing, but for others, it could well mean a more thorough search process resulting in a better job match. In the case of young secondary workers in families receiving NIT benefits, reduction in work often meant more time spent in school. As one participant in the Boston Fed conference reported, the probability of graduation from high school was 25 to 30 percent higher in families receiving the NIT than in the control group.

Structural evidence

So far, we have discussed evidence in the form of direct observation of labor force participation and hours worked. Another approach is to use so-called structural models to estimate elasticities of work effort in response to changes in income and net wages, that is, wages after benefit reductions and taxes. The income elasticity of work supplied tells us the percentage by which hours worked change in response to a one percent change in income, assuming that the net wage does not change. The substitution elasticity tells us the percentage by which hours worked change in response to a one percent change in wages.

Elasticities are important because, as we pointed out in Part 1, theoretical conclusions about work effort are subject to the caveat that, other things being equal, the effects of a change in the minimum income guarantee or benefit reduction rate of a policy would depend on the strength of the income and substitution effects.

The IMEs themselves are one source of data for making structural estimates of elasticities. Burtless summarizes several such estimates in Table 3 of his paper. Estimates of the income elasticity of work effort for women in IMEs ranged from -.07 to -.15, averaging about -.12. The range of substitution elasticities for women was from .11 to .24, averaging .17. For men, the income elasticities ranged from -.075 to -.11, averaging about -.09, and the substitution elasticities were tightly grouped around .085.

There is also a large literature estimating work responses based on nonexperimental wage and income data drawn from surveys of work behavior, tax records, and other sources. A recent working paper by Robert McLellan and Shannon Mok of the Congressional Budget Office summarizes the findings. Generally, the income and substitution elasticities are of the same order of magnitude as those estimated from IME data. For men and unmarried women, substitution elasticities tend to fall into a range from 0.1 to 0.3 and income elasticities from 0 to –0.1. For unmarried women, the substitution elasticity ranges from 0.2 to 0.4 and the income elasticity from 0 to -0.1.

Some studies also estimate an elasticity of participation, that is, the change in the percentage of a given population that would participate in the labor force in response to a change in the net wage. The CBO working paper considers a participation elasticity of 0.25 to be typical. That would mean that we could expect the participation rate to increase by about 2.5 percent for each 10 percent increase in the wage. For example, changing from welfare with a benefit reduction rate of 50 percent to an UBI with no benefit reduction would increase the net wage by 100 percent. If the elasticity of participation were .25, we would expect a 25 percent increase in the participation rate. For example, if 60 percent of welfare recipients worked before, we would expect 75 percent to work after introduction of the UBI.

Other studies estimated elasticities for upper and lower income groups. One study found that the participation elasticity for the bottom 10 percent of the income distribution was twice as high as that for the middle of the distribution. Another study found that the participation elasticity for single mothers was 0.4, higher than the estimation of .25 for the whole population. Still another study found that for low-income groups, the elasticity of labor supply with respect to unearned income (which would include UBI benefits) was only -.04 for women and -.01 for men.

One final type of type of study is worth mentioning: Some economists have taken advantage of “natural experiments” to investigate how people react to large increases in windfall income. For example, a study of Massachusetts lottery winners found that people did not typically retire to a life of idleness even after receiving very large prizes. On average, each $1,000 of prize money caused people to reduce their earnings by only about $110. Another study estimated the effects of inheritances on the work effort of Michigan residents. By and large, inheritance caused only small changes in work effort. Neither of these studies lends any support to the notion that a UBI grant of a few thousand dollars a year would cause massive defections from the labor force.

For readers who are not be used to thinking in terms of elasticities, it may be helpful translate the estimates we have cited into some hypothetial examples. The examples assume that we start with a welfare sysem that guarantees $10,000 for a family of two that has no earned income, and has a benefit reduction rate of 50 percent. We then replace that with a UBI that has a basic benefit of $4,000 per family member and no benefit reduction. For simplicity, all of the examples assume that there are no other income or payroll taxes, and all use elasticities at the midpoint of the ranges reported in the CBO working paper.

• Jane is a single mother, on welfare, with one child. She initially works 1,000 hours per year at a wage of $8 per hour. Her $10,000 maximum benefit is subject to a reduction of $4,000 because of her earnings, so her disposable income consists of $8,000 of earned income plus $6,000 of benefits, net of reductions, or $14,000 in total. Another way to look at it would be to say that her net wage is $4.00 per hour, after benefit reductions. Under the UBI, her benefit would be $8,000, not subject to reduction. If she worked the same number of hours, her disposable income would be $16,000 ($8,000 UBI benefit + $8,000 earnings)—a 14 percent increase. With an income elasticity of work effort of -.05, a 14 percent increase in income would cause a .7 percent decrease in desired hours worked, or 7 hours per year. At the same time, by eliminating the 50 percent benefit reduction, the UBI would increase Jane’s net wage from $4.00 per hour to $8 per hour—a 100 percent increase. With an elasticity of substitution of .3, the UBI would induce a 30 percent increase in desired hours worked, or 300 hours per year. Taking the two effects together, total work hours would rise by 293 hours. On balance, then, replacing the current welfare system with a UBI would increase Jane’s net income from $14,000 to $18,344 ($8000 (UBI) + $8 X 1293 hours). Her total income and hours worked would both increase.
• David, a middle-class professional in a traditional marriage to a nonworking spouse, no children, earns $60,000 per year after taxes, a little above the median household income. He works 2,000 hours per year. The UBI does not change his net wage, so it has is no substitution effect, but it raises his disposable income by 13 percent, to $68,000 per year, or 13 percent. Applying an income elasticity of -.05 means that he would reduce his desired hours of work by about .65 percent, or 13 hours per year. However, if, as I have suggested elsewhere, the UBI is financed in part by eliminating middle-class tax loopholes (without changing marginal tax rates), Dave’s income would increase by less than the full $8,000 and he would reduce his annual work by less than 13 hours.
• Bruce, a single 20-something, is not eligible for any welfare programs. He lives on an old boat, gets by without health insurance, and makes enough to meet his basic needs by working 800 hours a year doing odd jobs at $10 per hour. He spends his spare time watching birds and playing the guitar with friends. With the UBI, his income would jump to $16,000 per year, a 100 percent increase. Applying a typical income elasticity of -.05, we would expect him to cut his work back 40 hours per year. However, the -.05 is just an average. Maybe Bruce is not typical. Maybe he would be prefer to continue his $8,000 a year lifestyle, not working at all, and spend 800 more hours a year on birds and music. The UBI would allow him to do so if he chose.

These are hypothetical examples, but they illustrate a key point: The income effect of a UBI, which discourages work, is weak, whereas the substitution effect, which encourages work, is strong. One reason for the relative weakness of the income effect is the simple fact that the absolute value of the income elasticity is less than that of the substitution elasticity—a finding common to nearly every statistical study of work behavior. The other reason is that for most people, a UBI of the kind I have described causes a relatively small percentage increase in income, when we take prior earnings and welfare benefits into account.

Given a weak income effect and a strong substitution effect, there is only one case in which a UBI can cause a large decrease in work effort, let alone complete withdrawal from the labor market. That is to posit a person like Bruce, who initially receives no income support benefits at all, who is not just able to live on a very low income but enjoys doing so, and who has an income elasticity that is far greater that the population average.

Most people can probably think of at least one person they know, or have heard of, who fits the “Bruce” profile. Anecdotal evidence is powerful, and people are quick to extrapolate from a couple of guitar players spotted in their local park to millions of Bruces “listing away in socially destructive idleness.” However, bear in mind that actual data from the IMEs, from econometric studies of labor market behavior, and from “natural experiments” like lotteries and inheritance uniformly indicate that, when it comes to population averages, there just aren’t enough Bruces to outweigh the effects of the tens of millions of Janes and Daves.

The bottom line

In the two parts of this series, if have argued that standard economic theory and available empirical evidence support the idea that a well-designed and properly financed UBI, introduced as a replacement for our current welfare system, would be more likely to increase than to decrease average work effort for the population as a whole.

I have also questioned the conclusions some critics have drawn from the income maintenance experiments of the 1970s and 1980s. In doing so, however, I don’t intend any blanket criticism of the experimental approach. On the contrary, I think that a randomized field trial of a true UBI, conducted along the lines of the IMEs of earlier years, could help resolve some of the outstanding issues. A recent Republican proposal, Expanding Opportunity in America, calls for using some funds now allocated to federal welfare programs to fund state-level experiments with new ideas. The initial draft of the proposal specifically barred experiments with a UBI or any other policy that did not include a work requirement, but we can hope that is not the last word.

Meanwhile, the theoretical analysis and indirect evidence that we do have remains largely supportive of the proposition that a UBI would have a favorable impact on work incentives.