Arindrajit Dube

August 20, 2021

In Coombs et al. (2021), we use bank transaction level data from Earnin to track job finding rates of those previously unemployed and receiving UI benefits for 19 states where pandemic UI expired in June versus 23 states which decided to retain the federal benefits through September. We found that while around 1.1 million UI recipients (causally) lost benefits from the early withdrawal, around 145 thousand (around 1 out of 8) of these individuals found jobs. In that study, we found that the loss in benefits led to sharp (20 percent) drop in spending among beneficiaries.

Here I supplement the analysis by looking at month job-finding rate from a public data source, the Current Population Survey (CPS). I compare the same set of 19 Withdrawal and 23 Retain states as in Coombs et al. I plot the monthly job finding rate, controlling for 5-part education categories, gender, detailed race, Hispanic origin, marital status, 6-part age categories, and 16-part unemployment duration categories.

I find that the controlling for these factors, the job finding rates had evolved broadly similarly in Withdrawal and Retain states during late 2020. Following the withdrawal, the job finding rate increased by around 6 percent point in Withdrawal states as compared to Retain states between June and July—a roughly 25 percent increase in the job finding rate. According to the CPS, there were around 2.7 million unemployed individuals in the Withdrawal states in June. This suggests that if the only impact of the policy were through job finding of the previously unemployed, then the expiration led to an added 160,000 (0.06 x 2.7million) additional jobs in Withdrawal states in July—jobs that would otherwise have likely been added a few months later. These estimates are noisy due to sample size limitations in the CPS, but qualitatively similar to what we found using data from Earnin. Note that in reality some of these found jobs may have displaced job finding by those who were not previously in the labor force. Moreover, the reduced demand due to lower consumption may have also affected the number of people losing jobs. For these reasons, the CPS based estimate here (like the Earnin data based estimate) is likely an upper bound of the aggregate employment impact.

Update (August 23, 2021):

Did these modest job gains among those who were initially unemployed come at the expense of job finding among those who were initially outside of the labor force? The extent there are congestion effect, an increase in labor supply due to expiration of unemployment benefits will tend to partly crowd out others’ ability to find jobs. The consequence is that aggregate employment changes will be less than what is implied by increased job finding among the unemployed.

When we look at job finding rates among those who were not in the labor force (NILF), we find a mirror image of the picture above that looked at those who were unemployed. Namely, the flows between NILF and employment fell in relative terms in the Withdrawal states as compared to the Retain states following the end of pandemic UI in the former states. There was a a roughly 1.5 percentage point fall in the job finding rate in the Withdrawal states in relative terms between June and July, driven by an absolute increase in Retain states. Note that since the number of individuals who were not in the labor force was much larger than the number of individuals who were unemployed (around 6 times as large), the resulting reduction in fob finding from NILF seem to more than erase the jobs gains from increased job finding among unemployed.

As one example of who might be those being recruited from outside the initial labor force, we can look at teens. Here we find an especially stark picture. In June, teen job finding rates were 0.11 in Retain states while 0.1 in Withdrawal states. But in July, the former jumped to 0.15 while the latter fell to 0.075. The resulting gap in the teen job finding rate between the two groups of states was much larger than at any point over the analysis period.

The take-away is that the modest increases in employment suggested by job finding among those who were unemployed is unlikely to show up as aggregate job numbers due to substantial reduction in flows into employment from those who were initially not in the labor force.

by Arindrajit Dube

July 18, 2021

So far, 25 states have ended their participation in all or most of the pandemic unemployment insurance (UI) programs: 22 of these states ended them in June, and 3 in July. All of these 25 states have ended the $300/week benefit boost (Pandemic Unemployment Compensation, or PUC). But 21 out of these 25 states have also ended their participation in the Pandemic Emergency Unemployment Compensation (PEUC) that allow workers to collect unemployment benefits past the roughly 26 weeks that most states offer; and in the Pandemic Unemployment Assistance (PUA) program that offers benefits to those who are ineligible to receive standard UI due to insufficient earnings, being freelancers or gig workers, or other reasons. This is relevant because around 3/4 of workers receiving UI right now are receiving it through PEUC and PUA. So ending these programs will mechanically throw the majority of people receiving benefits off UI rolls , which is distinct from any debate about behavioral response to the $300/week PUC which has animated much of the discussion when it comes to the topic. Proponents of cutting off pandemic UI argue that jobs are plentiful, so if pushed out of UI rolls, unemployed workers will quickly find jobs. And as the argument goes, this is especially true in the 25 states cutting off UI, since unemployment rates are lower there than in states keeping the pandemic UI for now.

So what has been the impact so far on the labor market? How have the policy changes impacted the number of people receiving UI benefits? And have these policy changes boosted jobs in those states so far? Here I use recent data from the Household Pulse Survey (HPS) collected by the Census Bureau to assess the short term impacts of the June expiration. Specifically, the HPS asks whether the respondent received UI in the last 7 days, which allows us to assess the impact of the policy expiration on recipiency. In addition, the HPS also asks whether the respondent is currently working, which allows us to evaluate the employment impacts. The most recent data goes through July 5, 2021. For more information on the HPS, see here.

I group states by their dates of expiration: 4 states ended the programs on June 12, then 8 more states ended them on June 19, and finally 10 additional states ended participation on June 26. The figure below plots the share of population between 18 and 65 years of age that were receiving UI over time by the four groups of states.

We see that in the 12 states where pandemic UI expired on June 12 (grey) or 19 (green), the share of population receiving UI fell sharply between early June and early July, with a drop of around 2.2 percentage points. The difference-in-differences estimate using the non-expiring states as a control group is 2.3 pp (standard error of 0.6 pp).This amounts to a roughly 60 percent reduction in the UI rolls in these states. UI receipt in states with a June 26 expiration (red) fell only modestly as of early July, but that probably reflects some delay between when the programs end and when people receive their last checks. Finally, the share of population receiving UI remained largely unchanged in states where pandemic UI did not expire in June (blue).

What happened to those who stopped receiving UI in June? Did they transition into work as those advocating ending these programs had predicted? The next two figures plot the employment to population (EPOP) rates of 18-65 year olds by the same cohorts of states. The first figure plots over the same time horizon as the unemployment receipts and focuses around the June expiration events. Between early June and early July, the EPOP rates in the states seeing large drops in UI receipt (i.e., 12th and 19th June cohorts in grey and green) saw no uptick in employment. Recall that around 2.2 percent of all 18-65 year olds stopped receiving unemployment benefits between early June and July in these 12 states. At the same time, EPOP in these states declined by around 1.4 percentage points over the same period (while it rose by 0.2 percentage points in states that did not end pandemic UI in June). The difference-in-difference estimate was -1.7 pp (std error of 1.3pp): the 95 percent confidence intervals rule out EPOP rises of 1 pp or more, which is substantially smaller than the 2.2 pp drop in UI receipt. Certainly there was no immediate boost to employment during the 2-3 weeks following the expiration of the pandemic UI benefits.

The second figure zooms out to provide more information about how employment in these four groups of states have evolved over the pandemic. Generally speaking, the early ending states (especially June 12 and 19 cohorts) had higher EPOP rates during 2020, but those gaps had narrowed by early 2021. While a more refined analysis that more closely controls for the evolution of EPOP by expiration groups can be useful, at least over the past few months prior to the expiration, the EPOP in these groups of states seem to have been close in terms of levels and trends.

Did the reduction in UI generosity–both from to individuals losing access to UI programs outright, and for those receiving claims but losing the $300 PUC–lead to greater financial hardship? The HPS asks respondents if in the last 7 days, it’s even difficult to pay for usual household expenses. I define people as stating they are experiencing difficulty with paying for expenses if they say it has been either “somewhat difficult” or “very difficult” in response to this question. The figure below shows an increase in respondents reporting difficulty in paying for expenses following the expiration in the states expiring in June. The difference in difference estimate for the June 12 and 19 cohorts is around 3.7 pp (standard error = 1.9 pp) and this is statistically significant at conventional levels. The fact that more people report hardships than losing UI benefits eligibility makes sense, as even those who remain eligible experience a sizable $300/week cut in benefit level. The overall effect sizes is consistent with how many people lose UI benefits either through eligibility or level of benefits.

Overall, the mid-June expirations of pandemic UI seem to have sharply reduced the share of population receiving any unemployment benefits. But this doesn’t seem to have translated into most of these individuals having jobs in the first 2-3 weeks following expiration. However, there is evidence that the reduced UI benefits increased self-reported hardship in paying for regular expenses. Of course, this evidence is still early, and more data is needed to paint a fuller picture.

(Co-authored with Ben Zipperer. Posted at Washington Center for Equitable Growth)

Puerto Rico today faces a serious debt crisis, recently defaulting on a bond payment. The proximate cause is a slowdown in economic growth since the mid-2000s, which has reduced tax revenues, and a declining labor market, where employment growth has been mostly in the red since 2007.

There are many explanations for the economic downturn and the resulting fiscal crisis, but some commentators have incorrectly blamed the island’s high minimum wage. To be sure, the federal minimum wage—which has applied to Puerto Rico since 1983—is much more binding there than it is on the mainland. Because hourly wages are substantially lower in Puerto Rico compared to the U.S. mainland, the federal minimum wage policy affects more of the workforce there. In 2014, for example, the federal minimum wage stood at 77 percent of the median hourly wage in Puerto Rico, compared to 42 percent in the United States. For comparability with existing estimates, if we consider wages of full time workers only, these figures are approximately 70 percent in Puerto Rico and 38 percent in the United States, respectively. Finally, the minimum wage stands at 56 percent of the wage earned by production workers in manufacturing, compared to 38 percent in the United States. Clearly, the Puerto Rico’s minimum wage exceeds the cautious rule-of-thumb of 50 percent of median wage of full-time workers suggested by one of us in previous work.

But does that make it a probable culprit for the island’s current debt and economic troubles? The short answer is: not very likely …

Continue reading here.

In a very helpful blog post, Paul Krugman tries to make sense of Wal-Mart’s recent statement that it is already reaping some gains from raising wages via reduced turnover costs. Krugman’s main point is as follows. If worker productivity is a function of the wage (through improved morale, lower turnover, etc.), and Wal-Mart was initially maximizing profits, then a small change in wages will leave profits largely unchanged.

As Krugman points out, this is logic of the “envelope theorem.” What I want to clarify in this post is that the logic behind this argument is more general than the particular efficiency wage model Krugman works through.  Any time firms are choosing wages to balance various concerns—as opposed to simply accepting a “market wage” as a constraint—the logic of the envelope theorem applies.  What’s more, two types of empirically relevant models of the labor market—monopsonistic competition and efficiency wages—look pretty similar in this regard, and can be thought of as special cases of a more general model.

Krugman discusses the efficiency wage case, where worker productivity is a function of the wage, . Krugman mentions monopsony in passing, but doesn’t analyze it explicitly: this is the idea that higher wages allows firms to employ more workers. In presence of search frictions, a higher wage allows a firm to more easily recruit and retain its workers. Such frictions, therefore, give employers some wage setting power. In the textbook monopsony model, the quantity of labor employed becomes a function of the offered wage.

Of course, both efficiency wage and the monopsony channels may matter. Conversely, neither may be relevant. So overall, we have four cases.

1. Competitive case: 

2. Pure efficiency wage: 

3. Pure monopsony case: 

4. General case:

In the competitive case, wages are fixed by the market, and worker productivity is unaffected by the wage; so the firm just chooses employment . In the pure efficiency wage case, productivity is affected by wage, but labor supply isn’t; in the monopsony case, the opposite is true. In the general case, both productivity and labor supply depend on wages. So the firm chooses a wage, and this determines both its labor supply and the productivity of the workers it employs. Both the ease of recruitment and the increased morale provide “offsets” to the increase in costs due to the wage change.

Now, at the wage where profits are maximized, by definition, the following condition holds:

To understand this condition, say Wal-Mart was maximizing profits initially and chose its wage at   Now, say due to “exogenous” social pressures, it raises wages slightly. A shift like that will not affect profits. Why? Because the gains (ease of recruitment/retention affecting , improved worker morale affecting , whatever else) will be exactly balanced agains the wage costs. This is the envelope theorem in action, and it is a feature of any model where firms choose wages, not just the ones I lay out here.

Now, this logic applies exactly only “on the margin” … meaning for small changes in wages around . In reality, Wal-Mart recently raised its bottom wages amounting to something like 5 percent of its wage bill. But what if, as Krugman hypothesizes, Wal-Mart were to raise wages by 20 percent or 40 percent? Does this logic hold exactly? No, because we are outside of the zone of “small changes;” I would therefore qualify Krugman’s argument about offsets here. The extent to which the offsets are sizable will now depend on the quantitative importance of the monopsonisitc and efficiency wage channels … i.e., the shape of the and functions when we move away from . But what is true is that the labor supply effect and the morale effect lead to a smaller profit loss than is true in the competitive case.

Of course, we have been imagining Wal-Mart just raised its wages “exogenously.” But in truth, Wal-Mart changed wages because it probably faced some pressures—market, social or both. These costs will affect its profit function changing its profit-maxizing wage .  But the logic of labor supply and morale effects implies that there will be some offsetting gains accruing to Wal-Mart from raising its wages. The fact that the company reported savings from lower turnover is consistent with the theory, and with academic evidence from wage increases by other major retailers, as well as from the fast food sector after minimum wage hikes.

Recently, Ken Jacobs, Ian Perry and Jenifer MacGillvary from UC Berkeley Center for Labor Research and Education released a detailed report showing that the majority of public assistance payments—such as EITC, food stamps (SNAP), child care subsidies, TANF, Medicaid–go to working families.  Working, per se, turns out not to be a guarantee against reliance on such assistance. When wages are low (or workers have insufficient hours) families often qualify for tax-payer funded safety net programs. Across states, the working family share of pubic assistance ranged from 43% in Alaska to 66% in Texas.

So is this a problem? That depends on who you ask. Moreover, there are different reasons for considering this to be a problem.  Here I lay out three such reasons, and assess their relevance. Continue reading →

In January 2014, a funny thing seems to have happened. Parts (though not all) of the econoblogosphere forgot why time series econometrics fell out of favor in the early 1990s when it comes to analyzing minimum wage policies.  Besides the fact that there is a lot more variation in minimum wages than just the federal (or average) minimum wage in the U.S., the timing of the minimum wage increases is very uneven. For example, U.S. minimum wage increases tend to occur more frequently during the late phases of the business cycle (see Figure 4).

Now this timing issue makes trouble even for state panel studies, but it really wreaks havoc on time series analysis. By not having a control group, time series evidence has to rely solely on changes in trends around the time of minimum wage increases, as this blog post by Kevin Erdmann most recently tries to do. In 6 out of the 7 episodes of minimum wages that he considers, employment trends slow down (or fall outright) following the minimum wage increases. In other words, the red post-MW trend lines have a smaller slope than the black pre-MW slopes.

It looks quite remarkable. Linking to this picture, Tyler Cowen quotes Erdmann: “Is there any other issue where the data conforms so strongly to basic economic intuition, and yet is widely written off as a coincidence?”

Well, here’s a reason why this evidence should be written off as a coincidence. Below, I overlay Erdmann’s graph with the NBER business cycle dates in light green. Why am I looking at this?  Because if the post-MW period includes a recession and the pre-MW period does not, that will misattribute the recessionary job losses to minimum wages.

I hand drew the recessions in, and I’m not known for my fine motor skills. But I think you get the gist from the picture above. In 5 of the 6 events, the “post periods” used to fit the post-MW red trend line appear to include a downturn. (In other words, the red trend lines and green shadings overlap.) Now, we know very well that teen employment falls during a downturn. This tends to make the red post-MW trends smaller, providing a very simple explanation for why in 5 out of the 6 cases, the teen employment trend slowed down. And the 6th increase (in September 1961)  happened right after the recession officially ended in February, so one could make an argument that the business cycle can help explain that one too.

Oh, and that 1 episode where the trend line actually rose after the minimum wage increase – which doesn’t fit the job loss explanation?  That would be the minimum wage increase in the late 1990s boom, where the post-MW period does not appear to include a recession. In other words, business cycles can explain the pattern of employment trend changes in at least 6 out of the 7 episodes, and maybe even partly in the 7th.

Look – whether minimum wages cause teen employment to fall remains controversial. I think the clearest U.S. evidence comes from comparing across border counties with different minimum wages, using regional controls, or using synthetic control groups. All of these suggest the impact on teen employment is fairly small for the kind of minimum wage increases we have seen in this country. But whatever your position is on this question, you should probably steer clear of simple time series evidence that economists on both sides of the debate have wisely moved away from.

In a recent post, Tyler Cowen discusses my recent paper on minimum wages and poverty. Cowen acknowledges that “[my] paper, econometrically speaking, is a clear advance over [a 2010 paper by] Sabia and Burkhauser.”  However, he is more persuaded by “facts” such as simulation results from Sabia and Burkhuaser’s paper that claims “[o]nly 11.3% of workers who will gain from an increase in the federal minimum wage to $9.50 per hour live in poor households.”

Cowen concludes that my paper “pays little heed to integrating econometric results with common sense facts and observations about the economy.”

I’m pleased that Cowen thinks my paper represents a clear econometric advance. But I strongly disagree that the econometrics are at odds with common sense facts. Simulation studies are not facts, and when we interpret the relationship between wages and poverty properly, the econometric results appear eminently sensible.

Let’s start with the econometrics. First, both the weight of the existing studies, and my own econometric evidence that Cowen considers an advance, suggest that minimum wages have a modest impact on reducing poverty. I find minimum wage elasticities for the poverty rate ranging between -0.12 and -0.37.  This range of estimates is based on 16 different models, and the list includes just about every specification (or close to it) used in the literature. That includes specifications in Burkhauser and Sabia (2007), Sabia (2008), Sabia and Burkhauser (2010), and  Neumark and Wascher (2011)—except that I use more data.

Now, if this range does not include your preferred estimate, that’s fine. But, then you need to acknowledge that you also do not believe empirical results from regressions in the previous papers using one of the 16 models I do estimate. Another possibility is that you like one of the 16 models, but prefer earlier results that showed a weaker connection between the minimum wage and poverty. In that case, you need to explain why you believe a result from a smaller sample of data used to one that uses more data. This is especially important because many of the estimates in the literature are highly imprecise, in part due to use of small samples. You are not allowed to pick econometric results from a specification when you agree with the outcome, but dismiss results from the same specification when the results are not agreeable to you.

So is this type of econometric evidence—of the sort that has become the hallmark of applied micro-economics in the past few decades—out of touch with the “real world?” Instead, should we turn to simulations like those in Sabia and Burkhauser to get closer to reality?  As a believer in the credibility revolution in economics, I’m going to go ahead and say, no. Actually, the type of estimates that I have found both in my own work, and generally from the literature, is what you would expect based on the pattern of wages and family incomes if you also account for the commonsensical—and empirically supported—propositions that: (1) workers above the minimum get some raise too (“spillover effects”), and (2) reported wages in survey data is measured with error which makes the relationship between low wages and low family incomes weaker than it is in reality.  The simulation results like Sabia and Burkhauser do not in fact account for these, and they understate the association between minimum wages and low family incomes.

So let us go through these points more carefully. As I report in my paper, poor workers are  disproportionately low-wage workers. In 2013, 63 percent of workers under the poverty line reported earning less than $10.10/hour, as compared to 22 percent of workers overall. This is broadly consistent with my econometric findings: that minimum wages raise family incomes relatively more at the bottom of the family income distribution.  At the same time, I also explicitly state that the relationship between low wages and low family incomes (e.g., poverty) is indeed imperfect. In 2013, around 18.9 percent of workers who reported earning under $10.10/hour were in families under the poverty line, and around 46.0 percent were below two times the poverty line. So yes, the minimum wage is a “blunt” tool if the only goal were to reduce poverty. (Curious why my estimate of 18.9 percent differs from Sabia and Burkhauser’s estimate of 11.3 percent? Jump to the Postscript at the end.)

But, I also point out in my paper that using the distribution of reported wages to make predictions about minimum wage impact on poverty—like Sabia and Burkhauser do—will almost certainly under-estimate the true effects. To see why, consider the assumptions made by Sabia and Burkhauser in their simulations:

1. They assume that most workers reporting a wage under the old minimum will not get a raise when the minimum wage goes up.
2. They also assume that no one above the new minimum will see a raise.

These assumptions are inconsistent with a large body of evidence. First, there is almost certainly some wage spillover or “ripple effects”, as shown most recently by Autor Manning and Smith (2010)—a paper Cowen says is of “highest academic pedigree.” A minimum wage increase ripples up to the 20^th percentile of the wage, which would simply not happen if there were no spillovers. Interestingly, a recent study by the Hamilton Project uses spillover estimates from a paper by Neumark et al. (2004) to estimate that a total of 35 million workers would get a raise from increasing the minimum wage to $10.10/hour, many more than number of workers directly affected by the policy.

Second, many workers who report earning lower than the current minimum wage are in reality earning at or slightly higher than the minimum wage, and they will also see their wages rise. In general, the more measurement error there is in wages and other sources of incomes, the weaker the relationship between poverty and low wages will appear to be. Measurement errors don’t just “wash out”—they weaken correlations in what economists call an “attenuation bias.” The concern with measurement error in reported wages is also discussed in Autor, Manning and Smith 2010. And while measurement errors may lead to problems inferring exactly why we see spillover effects, they mean the kind of assumptions used by Sabia and Burkhauser will understate the true relationship between minimum wages and poverty.

Third, many of the workers who are truly being paid lower than the statutory minimum in the informal sector will see an increase, a phenomenon is sometimes called the “lighthouse effect.” There are different explanations for this, but consider the following analogy. There are people who drive at 70 miles an hour even when the speed limit is 65; now if the speed limit is lowered to 55, most people who were previously driving at 70 miles an hour will also lower their speed, while continuing to speed a bit. A similar logic applies to cases like the minimum wage where the probability of detection likely varies with the extent of violation.

So to take stock, if you consider the Sabia and Burkhauser simulation results  as “facts” you also are claiming that no worker reporting a wage below the old minimum will get a raise, and no one above the new minimum will get a raise. These are not very good assumptions, and they certainly are not facts.

Of course, you don’t have to make these assumptions. You could allow for spillovers. You could allow for wages to rise below the minimum. You could allow for measurement error in reported wages and other sources of income. But then you are not in a world where tabulating survey data gives you simple facts that are beyond reproach. You need to make additional assumptions to make causal claims. And we have not even begun to talk about behavioral effects—be they on labor demand side, or on labor supply side such worker search effort, etc. (And by the way those do not all go in the same direction.)  So you could add a lot more assumptions and continue with the simulation route, or you could use quasi-experimental approach used in almost all of applied micro-economics to empirically estimate the effect of minimum wages on poverty and other outcomes.  Of course, you would want to subject your identifying assumptions to specification checks and falsification tests to ensure you have reliable control groups; and you would account for possibly confounding policies such as state EITCs. And when you do all of that, and some more, you would probably end up with a paper like this one.

So where does this leave us?   As I said in my paper, policies like cash transfers, food stamps, and EITC are better targeted to help the poor, although even there minimum wages are better thought of as complements and not substitutes. More generally, however, motivations behind minimum wage policies go beyond reducing poverty. The popular support for minimum wages is in part fueled by a desire to raise earnings of low and moderate income families more broadly, and by fairness concerns that seek to limit the extent of wage inequality, or employers’ exercise of market power.  And the evidence suggests is that attaining such goals through increasing minimum wages is also consistent with a modest reduction in poverty, and moderate increases in family incomes at the bottom.  

Postscript. If you were paying close attention, you would have noticed a potential discrepancy. Sabia and Burkhauser argue that 11.3 percent of workers who will gain from an increase in the federal minimum wage to $9.50 per hour live in poor households, and 36.8 percent are under twice the poverty line.  I find that 18.9 percent of workers who will gain from an increase to $10.10 an hour are in families below the poverty line, and 46.0 percent under twice the poverty line. So what is going on here? Two things. First, Sabia and Burkhauser use the “household” as the unit to calculate poverty status, while I use “family.” While neither is clearly superior to the other, you should know that official Census definition of poverty uses the family as the unit. And for whatever reason, Sabia and Burkhuaser use a family based poverty measure when they run regressions, but use households when the do simulations. Second, low wage workers actually appear to be somewhat poorer today than they were in 2008, which is the period Sabia and Burkhauser were analyzing. I will have more to say on this in a future post, but the upshot is that even on this narrow count, it is more accurate to say the 19 (and not 11) percent of workers who report wages below the proposed $10.10/hour are in families that would be officially designated as being poor. And as I explained above, this number is almost certainly too small due to measurement error in both wages and other incomes. Return to the post.

Excerpted from Section 2 of my paper:  Minimum Wages and the Distribution of Family Incomes. Key sections are in bold. Alterations (but not deletions) from the paper are marked in square brackets [ ].

In this [post], I review the key papers on the topic of minimum wages and [poverty] based on U.S. data, and discuss their findings and limitations. My primary goal here is to provide a quantitative summary of the existing evidence, focusing on the [official] poverty rate elasticity as the most commonly estimated distributional statistic. [A poverty rate elasticity with respect to the minimum wage of, say, -0.2 means that a 10 percent increase in the minimum wage reduces the poverty rate by 2 percent. Note that this is different from a 2 percentage point reduction in the poverty rate.]

I begin by describing the process of selecting studies for this review. First, I only consider peer-reviewed publications since the early 1990s, i.e., the beginning of the “new economics of the minimum wage” literature. Second, I only include studies that report estimates for some statistic based on family incomes (such as poverty, quantiles, etc), and not other outcomes such as utilization of public assistance. Third, studies are included only when they empirically estimate the effect of minimum wages, as opposed to simulate such effects. This selection process yields 13 studies, 12 of which are used in my quantitative summary.

As a way to quantify the existing evidence, Table 1 reports the key estimates from the 12 studies for which I could construct an elasticity of the poverty rate with respect to the minimum wage. When the original estimates are not reported as poverty rate elasticities, I use information in the paper to convert them (and standard errors) to that format for comparability. To minimize the impact of subjective judgment, I have used the following guidelines for selecting estimates. (1.) I report estimates for all of the demographic groups studied in each paper; the sole exception is for workers, since minimum wages can affect who is in that group and lead to sample selection problems. (2.) When a study uses multiple econometric specifications, I include all of them in Table 1, except: (a.) the handful of estimates that did not include state and time fixed effects (or equivalent) as controls; (b.) estimates from sub-periods reported in a few of the papers, and (c.) specifications with lagged minimum wages reported in a few of the papers. Overall, these guidelines lead me to report 54 elasticities in Table 1, which represent either all or nearly all of the estimates of minimum wage impact on the poverty rate available in each of the papers.

Card and Krueger (1995) consider the short run impact of the 1990 federal minimum wage increase on the poverty rate for those 16 years or older, and regress the change in the state-level poverty rate between 1989 and 1991 on the the proportion earning below the new federal wage in 1989 (“fraction affected”).  Their bivariate specification has an implied minimum wage elasticity for the poverty rate of -0.39, but controls for employment and regional trends reduce the overall elasticity in magnitude to the range (-0.36, -0.08), and the estimates are not statistically significant at the conventional levels. They also find that the 10th percentile of the (unadjusted) family earnings distribution responds positively to the minimum wage increase, with an implied elasticity between 0.28 (bivariate) and 0.20 (with controls); these are statistically significant at conventional levels. A major problem with this analysis is that the estimates are imprecise. This is mainly due to the very short panel structure. For example, the 95 percent confidence interval associated with the poverty rate elasticity in their most saturated model is quite wide: (-0.65, 0.49).

Addison and Blackburn (1999) consider teens, young adults, and junior high dropouts between 1983-1996. Using state-year aggregated data and two-way fixed effects, they find sizable poverty rate elasticities for teens and junior high dropouts in the range of (-0.61, -0.17), with an average of -0.43. They find more modest sized estimates for young adults (an average elasticity of -0.24). Morgan and Kickham (2001) study child poverty using a two-way fixed effects model with data between 1987 and 1996, and find a poverty rate elasticity of -0.39. Stevans and Sessions (2001) consider the overall poverty rate in the 1984-1998 period; their most comparable estimate is from a two-way fixed effects model, and appears to yield an elasticity of -0.28. Gunderson and Ziliak (2004) consider the impact of a variety of social policies on the poverty rate and the squared poverty gap using both post and pre-tax income data between 1981 and 2000. For the population overall, they find a small overall poverty rate elasticity of -0.03, with a range of -0.02 to -0.06 across demographic groups. However, they specifically control for the wage distribution, including the ratio of 80th-to-20th percentile wages. This inclusion of the inequality measures is problematic, as it could block the key channel through which minimum wages would actually reduce poverty, namely raising wages at the lower end of the wage distribution. DeFina (2008) uses state-aggregated data from 1991-2002 and finds that minimum wages reduce child poverty in female-headed families, including those headed by someone without a college degree. The estimated poverty rate elasticities are -0.42 and -0.35, respectively.

Burkhauser and Sabia (2007) examine the effects on state-level poverty rates for 16-64 year olds and single mothers during the 1988-2003 period using specifications with two-way fixed effects. Depending on controls, their estimates of the poverty rate elasticity range between -0.08 and -0.19 for the population overall, and between -0.07 and -0.16 for single mothers. While none of the estimates are statistically significant, the point estimates are all negative, and the confidence intervals are consistent with sizable effects. In a follow-up study, Sabia and Burkhauser (2010) consider the 2003-2007 period and find little effect [of minimum wages on poverty]. This study is limited by a rather short sample period. Since it is an update of their previous paper, it is unfortunate that they do not also report estimates using the full sample (1988-2007) instead of just considering a five year period. While their point estimate is small (-0.05), the 95 percent confidence interval is fairly wide (-0.34, 0.24).

Sabia (2008) uses individual level CPS data from 1992-2005, and a two-way fixed effects specification augmented with state-specific quadratic trends to study the effect on single mothers. He finds statistically insignificant but again mostly negative and often sizable estimates, with a poverty rate elasticity of -0.22 from his main specification; for single mothers without a high school degree, the estimate is larger in magnitude (-0.28) while still not statistically significant. Sabia and Nielsen (2013) use the SIPP between 1996-2007 and find an overall point estimate of -0.31 (without state-specific linear trends) or -0.03 (with trends). However, these are imprecise estimates, as the 95 percent confidence intervals are (-0.93, 0.30) and (-0.27, 0.22), respectively—the former set is consistent with nearly all other estimates in the literature. Their estimates also appear to be sensitive to the inclusion of state-specific trends, but again, the imprecision of the estimates makes it difficult to draw any firm conclusion. Overall, two of the four papers coauthored by Burkhauser and/or Sabia suggest small to modest negative effects, while the other two produce fairly imprecise or fragile estimates. However, the overall evidence from their papers does not actually rule out moderate sized poverty rate elasticities.

Neumark and Wascher have coauthored three papers that are of particular relevance. Neumark and Wascher (2002) consider movements in and out of poverty by forming two-year panels of families with matched March CPS data between 1986 and 1995. Because they do not directly estimate the effect of the policy on poverty rates, Table 1 does not include estimates from this paper. [However, in a related paper], Neumark, Schweitzer and Wascher (2005) also use [the same data] between 1986 and 1995. They estimate the effect of discrete minimum wage [changes] on the distribution of the income-to-needs ratio, and their estimates suggest that an increase in the minimum wage actually increases the fraction of the population in poverty: they report a poverty rate elasticity of +0.39.

This is the only paper in the literature that I am aware of which finds such a [clear] poverty-increasing impact of the policy for the overall population. [H]owever, there are numerous non-standard aspects of their research design. Their method does not properly account for state and year fixed effects. They “mimic” state and year fixed effects by shrinking all families’ incomes by the proportionate change in the median income in that state (pooled over years) and also by analogously shrinking the median change in that year (pooled over states).  This constitutes an assumption that state and year effects are scale shifts that proportionately shrink the entire family income distribution. In other words, they impose the assumption that various counterfactual quantiles in states are moving proportionately to the median, which is an unattractive assumption, and much more restrictive than the inclusion of state and year dummies in a regression of the poverty rate on minimum wages [which is the standard approach]. Additionally, they use an ad hoc adjustment in the change in densities to account for the fact that some observations have both contemporaneous and lagged increases. These non-standard techniques raise serious questions about the study, especially since it stands out in terms of producing a sizable positive poverty rate elasticity. To my knowledge, no one, including any of the authors, has used this methodology in any previous or subsequent paper.

In contrast, Neumark and Wascher (2011) uses a more conventional approach to study the interactive effects of EITC with minimum wages over the 1997-2006 period. Although their focus is mostly on wage and employment effects, they do provide some evidence of minimum wage effects on the share of 21-44 year olds with incomes below the poverty line and one-half the poverty line.  Like most of the literature, they include state and year fixed effects; they also include demographic and state-level controls similar to this paper. Unfortunately, the authors do not report an overall minimum wage effect, and instead focus on their interaction effects with EITC. However, we can use the regression coefficients along with other information provided in that paper to back out a poverty rate elasticity with respect to the minimum wage using straightforward calculations. For the broadest group that they considered—21-44 year old family heads or individuals—their results suggest a minimum wage elasticity of -0.29 for the proportion with an income under the poverty line, and -0.45 for the proportion with an income less than half the poverty line (“extreme poverty”).  For a group constituting the majority of non-elderly adults (and representing many children as well), the evidence from Neumark and Wascher (2011) suggests that minimum wages have a moderate-sized impact in reducing poverty and extreme poverty. These results seem to be qualitatively different from the findings in Neumark et al. (2005), and much more similar to rest of the literature.

To take stock, the results in this literature are varied and sometimes appear to be inconsistent with each other. But is it possible to filter out some of the noise and actually obtain a signal? First, I note that across these 12 studies, nearly all (48) of the 54 estimates of the poverty rate elasticity are negative in sign. Indeed, only one study by Neumark et al. (2005) suggests that minimum wages actually increase the overall poverty rate. Moreover, this study uses an unconventional methodology that is both different from all other studies, and is also problematic.

Second, if we take an “average of averages” of the poverty rate elasticities for the overall population across the seven studies that provide such an estimate so that (1) each study is weighted equally, and (2) within each study, all specifications reported in Table 2 are weighted equally as well, we obtain an average poverty rate elasticity of -0.07. However, excluding Neumark et al. (2005) [which uses a problematic and unconventional methodology], the “average of averages” of the poverty rate elasticities is -0.15. [Overall] the existing evidence points towards a modest impact on the overall poverty rate.

Besides these seven studies, five additional studies reviewed here provide estimates for subsets of the population. If we take an “average of averages” of the poverty rate elasticities across all 12 studies, while (1) weighting each study equally, and (2) weighting each specification and group within study equally as well, we also obtain an elasticity of -0.15. If we exclude Neumark et al. (2005), the “average of averages” across the 11 studies is -0.20. There are, of course, other ways of aggregating estimates across studies. However, when I consider the set of nearly all available estimates of the effect of minimum wages on poverty, the weight of the evidence suggests that minimum wages tend to have a small to moderate sized impact in reducing poverty. [Below, I also plot histograms of all 54 elasticities—both unweighted, as well as weighted by the inverse of the number of estimates in each of the 12 studies, so that each study is weighted equally.]

While there is a signal in the literature that minimum wages tend to reduce poverty, it is also true that the existing evidence is clouded by serious limitations. These include (1) inadequate assessment of time-varying state-level heterogeneity [i.e., states with high and low minimum wages have very different trajectories on a host of dimensions unrelated to the policy]; (2) limited sample length and/or exclusion of more recent years that have experienced substantially more variation in minimum wages; (3) insufficient attention to serial correlation [which means many of the tests of statistical significance may be incorrect]; (4) use of questionable estimators; and (5) frequent omission of demographic and other covariates. In [my own analysis], I use more and better data along with more robust forms of controls to address these limitations in the existing literature.

My post on minimum wages for the Great Divide series at the New York Times:

http://opinionator.blogs.nytimes.com/2013/11/30/the-minimum-we-can-do/