Detecting Effects of Living Wage Laws DAVID NEUMARK and SCOTT ADAMS* We estimate the effects of living wage laws on wages of low-wage workers, focusing on the timing of policy, spurious associations, and the type of living wage law passed in a city. Our estimates point to sizable positive wage effects in cities with broad living wage laws that cover employers receiving business assistance from the city. We also explore disemployment effects of living wage laws and find evidence consistent with tradeoffs between wages and employment.
BEGINNING WITH THE PASSAGE OF BALTIMORE’S LIVING WAGE DECEMBER 1994, many cities in the United States have implemented living wages. When this research was completed, there were approximately 70 living wage ordinances in effect in the United States (most in cities, but some applied to counties or school boards) and numerous campaigns for more under way. Living wage ordinances typically mandate that businesses under contract with the city, or in some cases, receiving assistance from the city must pay their workers a wage sufficient to financially support a family. One common feature of living wage ordinances is a wage requirement that is much higher than the traditional minimum wages set by state and federal legislation. For example, by the end of 2000, the living wage in Baltimore, the first city to pass a living wage law, was $7.90. In some cities, such as San Jose and San Antonio, the living wage could exceed $10 (and in Santa Cruz, the living wage is currently $11, or $12 without health benefits). Many living wage ordinances explicitly peg a wage to the level needed for a family to reach the federal poverty line, indicating that the overriding goal of living wage ordinances is to alleviate poverty in the jurisdictions in
ORDINANCE IN
* The authors’ affiliations are, respectively, the Public Policy Institute of California, the Department of Economics, Michigan State University, and the National Bureau of Economic Research; and the Department of Economics, University of Wisconsin–Milwaukee. E-mail:
[email protected] and
[email protected]. We are grateful to Eli Berman, John DiNardo, David Levine, seminar participants at Harvard University, the Kansas City Fed, the University of Illinois, the University of Missouri, PPIC, Rand, UC-Berkeley, UC-Santa Cruz, the University of Washington, and anonymous referees for helpful suggestions. This research was supported in part by the Michigan Applied Public Policy Research Funds, the Broad Graduate School of Management, and PPIC. Any opinions expressed are those of the authors alone and do not necessarily reflect any position of the Public Policy Institute of California. I R, Vol. 42, No. 4 (October 2003). © 2003 Regents of the University of California Published by Blackwell Publishing, Inc., 350 Main Street, Malden, MA 02148, USA, and 9600 Garsington Road, Oxford, OX4 2DQ, UK.
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which they apply. Our longer-term research agenda is concerned with the success of living wages in achieving this goal.1 In the article we address a critical first step in research on living wages. In particular, we attempt to establish whether “first order” effects of living wages are observed, in the form of increased wages of low-wage workers. We also go beyond an analysis of wage effects to examine the most obvious tradeoff that may occur if there are wage increases, specifically employment reductions. There are two potential reasons why first-order effects of living wages on wages may not be observed. First, there is no existing research documenting the extent of compliance with living wage laws [in contrast to minimum wage laws (Ashenfelter and Smith 1979)], and it is conceivable that they are largely ignored or not enforced. This consideration would suggest that a failure to find wage effects should push researchers and policymakers to focus on the implementation and enforcement of living wage laws. In contrast, if an impact of living wage laws on the wages of low-wage workers is detected, this would provide evidence that living wage laws are effective and may have broader effects than might be suggested by their frequent limitation to coverage of city contractors. Second, because living wage laws appear to be targeted on a very narrow group of workers, it may be impossible to detect living wage effects using the standard datasets—most prominently the Current Population Survey (CPS)—that labor economists and other researchers use to study policies with geographic variation, such as the minimum wage, but also welfare or other income-support programs, antidiscrimination legislation, and unemployment insurance, to name some prominent examples. This consideration would suggest that a failure to find wage effects implies that such datasets are not useful in evaluating the effects of living wage laws. Instead, researchers would have to rely on ex ante calculations or simulations—as has been done in a set of city-specific consulting reports and other studies designed explicitly to study workers and firms affected by living wage laws. This would be unfortunate because the CPS provides a large-scale dataset covering essentially all metropolitan areas in the Unites states, permitting generalizations to be drawn, providing “control group” cities where living wages have not been implemented, and readily allowing comparisons with other policies in effect at the same or different times.
1
The figures in this paragraph and cited elsewhere in this article applied at the time this research was completed.
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Living Wage Laws Existing Laws. Living wage laws differ in two important ways from minimum wage laws. First, they specify coverage that is not universal. Summary information on living wage laws is reported in Table 1 for the 21 cities with such laws that are sufficiently large to study with the CPS in our sample period. Column 1 provides information on who is covered by the living wage law. While coverage varies by city, laws tend to apply to some or all of the following groups: contractors or subcontractors (most commonly), employers receiving business assistance from the city, and city employees (least commonly). The living wage laws covering employers receiving business assistance, which figure prominently in the ensuing analysis, are sometimes vague and somewhat heterogeneous. For some cities, the provision is relatively general. For example, the ordinance in Minneapolis refers to employers receiving economic development assistance, whereas in Los Angeles and Oakland the ordinances refer to financial assistance generally, which presumably could entail grants, tax abatements, etc. For others, more specific criteria are provided. For example, San Antonio’s living wage law covers businesses receiving tax breaks, and Hartford’s law covers commercial development projects receiving more than $100,000 in city subsidies or financing. Second, living wages often are high relative to the wage floors set by federal or state minimum wages. The wage levels associated with living wage laws are reported for these same cities in column 2 of Table 1. In many cases (e.g., Hartford and Minneapolis), these wages are pegged to the poverty level for a family of a specified size. In addition, the required wage is sometimes higher if health insurance is not provided.2 Table 2 provides descriptive information comparing the levels of living wages with minimum wages and the wages of relatively low-wage workers, highlighting the wide gaps in most cities between legislated living wages and minimun wages and sometimes also between living wages and wages at the low end of the labor market. All the living wages except Buffalo’s exceeded the federal minimum wage ($5.15) by at least 30 percent in 2000, and the median living wage ($8.19) was 59 percent higher.3 In Hartford and San Jose, living wages exceeded the federal minimum by at least 82 percent and the higher state minimum wages effective in these cities by more than 52 percent. Looking 2
In the empirical analysis reported in this article, we always use the lower wage with health insurance (if there is one), but the qualitative conclusions were not sensitive to using the alternative higher wage. 3 Of course, had the real value of the minimum wage been preserved over the 1980s and 1990s, this comparison between living wages and minimum wages would appear less pronounced.
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TABLE 1 I L W La
Baltimore
Construction and service contracts > $5000
Boston
Contractors > $100,000; subcontractors > $25,000 Contractors and subcontractors > $50,000 (> 10 employees) Contractors and subcontractors
Buffalo
Chicago Dayton Denver Detroit
Durham Hartford
Jersey City Los Angeles
Milwaukee
City employees Contractors and subcontractors > $2000 Contractors, subcontractors, and financial assistance recipients > $50,000 Contractors, city employees Contractors > $50,000; commercial development projects receiving subsidies > $100,000 Contractors Service contractors > $25,000; assistance > $100,000 or $1 million lump sum Contractors and subcontractors > $5000
Wage Provisions (2) Passed in December 1994 but wage requirements were as follows: July 1995 (6.10), July 1996 (6.60), July 1997 (7.10), July 1998 (7.70), July 1999 (7.90) 100% of poverty level: September 1998 (8.23), July 1999 (8.35), July 2000 (8.53) 6.22 with health benefits; 7.22 without: January 2000 (6.22)
Niedt et al. (1999): 1494 –5976 (0.51–2.05%)
July 1998 (7.60)
Tolley et al. (1999): 9807 (1.01%)
7.00 with health benefits; 8.50 without: April 1998 (7.00) 100% of poverty level (assuming 2080 annual hours): March 2000 (8.20) 100% of poverty level with health benefits, 125% without: December 1998 (8.23), March 1999 (8.35), March 2000 (8.53) January 1998 (7.55) 110% of poverty level with health benefits: October 1999 (9.19), March 2000 (9.38)
7.50 with health benefits: June 1996 (7.50) Indexed annually for inflation. Initial wage set to 7.25 with health benefits, 8.64 without: April 1997 (7.25), June 1998 (7.37), June 1999 (7.49), June 2000 (7.69) Poverty level for family of three (assuming 2080 annual hours): December 1995 (6.05), March 1996 (6.24), March 1997 (6.41), March 1998 (6.56), March 1999 (6.67), March 2000 (6.80)
Reynolds (1999): 2300 (0.40%)
Pollin and Luce (1998): 7626 (0.76%)
D N S A
City
Coverage Specified in Legislation (1)
Other Estimates of Affected Workers and Share of Workers in Bottom Quartile (3)
City Minneapolis
Oakland
Omaha
Portland
Coverage Specified in Legislation (1) Assistance > $25,000 as of December 1998; > 100,000 initially Contractors > $25,000; assistance > $100,000
City employees, contractors > $75,000; assistance > $75,000 Custodial, security, and parking attendant contracts Contractors and businesses receiving tax breaks
San Antonio
Businesses receiving tax breaks Service contractors > $25,000 ($50,000 for non-profits); airport leaseholders; home healthcare workers Service contractors > $20,000; assistance > $100,000 (excludes trainees and workers under 18); city employees Contractors
San Francisco
San Jose
Tucson a
July 1996 (7.00), July 1998 (7.50), July 1999 (8.00; starting in this year, the living wage is 9.00 if health benefits are not included) 130% of poverty level for family of three (assuming 2080 annual hours) with benefits, plus 1.39 per hours for health insurance: August 2000 (8.84) 9.27 to 70% of service employees in new jobs, 10.13 to 70% of durable workers: August 1998 (9.27) August 2000 (9.00), plus 1.25 per hour for health insurance, rising to 10.00 in 12–18 months: August 2000 (9.00) 9.50 with health benefits; 10.75 without. Reset each February to the new poverty level for a family of three and adjusted upward for higher San Jose cost of livingcurrently a 45.2% premium: December 1998 (9.50), March 1999 (9.68), March 2000 (9.92) 8.00 with health benefits; 9.00 without: September 1999 (8.00)
Reich et al. (1999): 4800 (1.99%) Alunan et al. (1999): 4766 (1.97%) Williams (1998): 600 (0.25%)
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The table covers those cities with living wages that are included in the wage analyses. When provisions (in column 2) refer to the “poverty level”, this is for a family of four and assumes 2000 hours worked unless otherwise noted. Much of the information for this column was obtained through correspondence with city governments. Some data, however, were obtained through information made publicly available by the Employment Policies Institute (www.epionline.org) and the Association of Community Organizations for Reform Now (www.acorn.org). The consistency of information provided by these two organizations and the city governments gives us confidence in the accuracy and completeness of the above table. In column (3), the numbers of workers directly affected by the laws (as reported in the specified study) are reported. In parentheses, we calculate these as percentages of the workforce in the bottom quartile of the wage distribution. To get the percentages, we divided the numbers of affected workers estimated in these reports by the average monthly number of workers in 2000 in the bottom quartile of the city’s wage distribution, using CPS sampling weights.
Detecting Effects of Living Wage Laws
St. Louis
Wage Provisions (2) 100% of poverty level with health benefits, 110% without: April 1997 (8.03), March 1998 (8.23), March 1999 (8.35), March 2000 (8.53) Initially set to 8.00 with health benefits and 9.25 without, upwardly adjusted by prior December 31 to December 31 change in the Bay Area CPI: April 1998 (8.00), April 1999 (8.15), April 2000 (8.35) 8.19 with health benefits; 8.50 without: May 2000 (8.19)
Other Estimates of Affected Workers and Share of Workers in Bottom Quartile (3)
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D N S A TABLE 2
L W, M W, 10 C W D, 2000a Living Wage (1)
Minimum Wage (2)
10th Centile (3)
All living wage cities, overall Baltimore Boston Buffalo Chicago Dayton Denver Detroit Durham Hartford Jersey City Los Angeles Milwaukee Minneapolis Oakland Omaha Portland St. Louis San Antonio San Francisco San Jose Tucson
— 7.90 8.53 6.22 7.60 7.00 8.20 8.53 7.55 9.38 7.50 7.69 6.80 8.53 8.35 8.19 8.00 8.84 9.27 9.00 9.92 8.00
— 5.15 6.00 5.15 5.15 5.15 5.15 5.15 5.15 6.15 5.15 5.75 5.15 5.15 5.75 5.15 6.50 5.15 5.15 5.75 5.75 5.15
6.67 6.92 8.00 6.00 6.73 6.25 7.50 7.00 7.50 7.75 6.25 5.75 7.25 8.00 8.00 7.00 7.00 6.50 6.00 7.50 8.00 6.00
Non-living-wage cities, overall Northeast Midwest South West
— — — — —
— — — — —
6.50 6.50 6.75 6.25 6.50
a
Estimates in column (3) are weighted, and computed over all months of 2000. The latest living wages and minimum wages in 2000 are shown, using the lower living wage (with health insurance).
above the minimum wage, the living wage exceeded the 10th centile in nearly every city, although the 10th centile wage was within $1 of the living wage in over half of them. A better comparison that is free of the effects of living wages on the wage distribution is provided by the figures in the bottom five rows of the table, which report characteristics of the wage distribution for cities without living wage laws. Living wages often are high compared with the 10th centile overall and in each of the four regions. Another relevant comparison is between living wages and the poverty line for a family of a given size. As Table 1 showed, in many cities the living
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wage is pegged to the poverty line. For example, Boston’s living wage is set so that an individual working 2000 hours earns 100 percent of the poverty line for a family of four, or a wage of $8.53 (in 2000), whereas Milwaukee’s is based on the poverty line for a family of three, or a wage of $6.80. Thus almost all the living wages would be enough for a family of three with a full-time worker to escape poverty, and a number also would be sufficient for a family of four, although the probability of full-time, full-year work may be relatively low for some of the affected workers. We cannot identify workers who work for city contractors or those who work for employers receiving business assistance from the city. However, we can compare living wages with wages for state and local government workers, some of whom are covered by living wage laws in Durham, Dayton, and San Jose. Here it seems sensible to do the comparison only with nonliving-wage cities because the wages of state and local government workers in cities with living wage laws are likely to be directly affected. In these cities, a government worker at the 10th centile earned an hourly wage of $8.00 in the South, $8.08 in the Midwest, and $8.65 in the West. Thus, for two of the three cities (Dayton and San Jose), the living wage exceeds the comparison wage at the 10th centile for state and local government workers. One difficulty in studying living wage laws using standard householdbased datasets is that we do not know precisely which workers are covered. Several consulting reports have undertaken the ambitious effort of estimating how many workers would receive wage increases as a result of living wage laws. Column 3 of Table 1 reports figures based on these reports for some of the cities whose living wage laws we analyze. These reports were ex ante studies trying to predict the effects of proposed living wages. The employment levels in column 3 are estimates of the number of workers directly affected by living wage laws, based on both coverage and whether workers’ wages were below the proposed living wage. They are based on a variety of methods, including direct information on city contracts, back-ofthe-envelope calculations, and surveys of employers. We also have attempted to translate these into percentages. The consulting reports did not estimate coverage in any particular part of the wage distribution but rather overall. In the reported percentages in column 3 we have assumed, as seems reasonable, that the affected workers are in the lowest quartile. To get percentages, we divided the number of affected workers estimated in these reports by the average monthly number of workers from 1996 through 2000 in the bottom quartile of the city’s wage distribution using CPS sampling weights. The estimated shares tend to be around 1 to at most 2 percent. While the estimates in column 3 probably represent the best current information on workers directly affected by living wage ordinances, there are
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a number of reasons to suspect that these coverage estimates are a lower bound on the percentage of workers who actually will be affected. First, the estimates focus on employees of city contractors, not the potentially broader coverage by living wage laws that also extend to employers receiving business assistance from the city. Second, they also generally ignore spillover effects on other low-wage workers not directly covered by the laws but who nonetheless might see wage increases and higher-wage workers whose wages might increase in response to a living wage law. Thus, while the direct coverage estimates from the existing consulting reports suggest skepticism regarding detecting effects of living wage laws in the CPS data, these other potential channels of influence imply that the effects could be more widespread, possibly substantially. Prior Research. While living wage laws are a recent phenomenon, there is a large body of research on the effects of minimum wage laws. Although there has been some controversy surrounding the effects of minimum wage laws, the consensus among economists is still that minimum wage laws reduce employment. As evidence of this, results of a survey published in the Journal of Economic Literature indicated that the median “best estimate” of the minimum wage elasticity for teenagers was –0.1, whereas the corresponding mean estimate was –0.21 (Fuchs, Krueger, and Poterba 1998). Of course, minimum wage laws also raise wages of low-wage workers, leading to the more important but relatively understudied policy questions of whether minimum wage laws help low-wage workers or low-income families. 4 Whatever one’s view of the research on minimum wages, however, its applicability to living wages may be quite limited. In particular, although standard economic theory predicts some reduction in employment among lower-skill workers in response to a living wage law, there are at least four unique features of living wage laws that are likely to weaken their effects relative to standard minimum wage laws. First, although living wage laws are likely to raise the costs of goods and services provided to cities, demand curves for these goods and services may be quite inelastic either because the city finds it possible to raise taxes to cover higher costs (thus largely allowing contractors to pass through the increased labor costs) or because some services have to be purchased in quantities that may be largely insensitive to price. Second, because living wage laws specify wage levels that must be paid without reference to skill levels of workers, employers who do some work covered by these laws and some work that is not covered may
4
See Neumark, Schweitzer, and Wascher (1998, forthcoming).
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reallocate their higher-skill and higher-wage labor to the former and their lower-skill and lower-wage labor to the latter in order to comply, entailing some inefficiencies but moderating any wage-increasing effects of living wage laws. Third, even under broad definitions of coverage by living wage ordinances, only a fraction of the workforce is likely to be covered, in contrast to the near-universal coverage of minimum wage laws. Finally, given the high levels of wages mandated by living wage laws and the potentially low levels of business assistance in some cities that might make an employer subject to living wage laws, one might wonder whether some assistance recipients would cut their dependence on business assistance in order to avoid paying the higher living wages.5 Because of these differences, independent study of living wage laws is required to assess their empirical effects. However, because living wage laws are such a new phenomenon, little empirical research has been conducted on their effects. Most important, no one has attempted a systematic empirical evaluation of the actual effects of living wage laws on low-wage workers and their families. The best-known work on living wage laws is the book by Pollin and Luce (1998), which argues that living wage laws will deliver a higher standard of living to lowincome families. While the primary purpose of this book was to advocate living wage laws as a viable poverty-fighting tool, it is often cited in the debate over living wages. In particular, calculations similar to those used in the book—which is based on Pollin and Luce’s evaluation of Los Angeles’ living wage proposal—have been used in consulting reports evaluating living wage proposals in other cities, including New Orleans, Miami–Dade County, and Detroit, among other cities. Not surprisingly, since they are based on the same assumptions used by Pollin and Luce, these studies reach similar conclusions.6 From the perspective of this article, the fundamental problem with Pollin and Luce’s analysis and the analyses used in the subsequent city-specific consulting reports is that the calculations are hypothetical, based on ex ante calculations rather than on data from before and after the passage of living wage ordinances. For example, Pollin and Luce do not attempt to estimate
5 To the extent that some of these affected recipients are nonprofit organizations providing services to needy individuals and families, living wage laws may have an adverse consequence other than reducing employment. 6 For example, in a report on Detroit’s living wage law, Reynolds (1999) argues that the costs to employers operating under a city contract would increase by only 5 to 9 percent of the cost of the contract. For those receiving financial assistance as part of the Empowerment Zones Program or the industrial facilities tax exemption, the added costs would be under 1 percent of the firm’s annual budget. Reynolds asserts that while the costs are small, there will be a financial benefit accrued by about 2300 Detroit workers who will each see annual income gains for their families of between $1300 and $4400.
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whether there are disemployment effects or hours reductions from living wage laws, nor do they even assume any such effects. It is no surprise, of course, that a calculation based on raising wages of low-wage workers while assuming no employment or hours reductions will look beneficial to lowwage workers.7 There have been attempts to predict the loss of jobs that will result from living wage laws. For example, Tolley, Bernstein, and Lesage (1999) projected that over 1300 jobs would be lost in Chicago from the city’s living wage ordinance.8 As noted earlier, however, living wage laws are quite different from minimum wage laws, and there is little reason to be confident that empirical estimates of the effects of minimum wage laws provide valuable guidance for predicting the effects of living wage laws. Moreover, as with the studies based on Pollin and Luce’s analysis, this work fails to study what has actually happened in a locality or localities where living wage laws were adopted and is again an ex ante study based in large part on conjectures regarding the effects of a living wage law. Since Pollin and Luce’s work grew out of an evaluation of a living wage proposal for Los Angeles and many of the city-specific consulting reports similarly evaluated proposed living wage laws in other cities, there was, of course, no way to measure the observed impact, so this is not a criticism of their approach per se. However, policy recommendations in the absence of such “before and after” evidence are unwarranted or at least very risky. Furthermore, given the accumulating experience of cities with living wage laws, there is no longer any reason to rely on such ex ante evaluations for assessing their policy effects (unless the living wage law is highly unusual, such as the proposed but ultimately defeated Santa Monica living wage), and the present study instead estimates the consequences of living wage laws directly. There have been a few city-specific studies that have begun to implement before-and-after analyses. In particular, Sander and Lokey (1998) study the 7
Pollin and Luce cite only Card and Krueger’s (1994) work specifically in concluding that living wage laws have no employment effects and also state that “Numerous other studies, examining the detailed changes in specific labor markets throughout the country due to an increase in the minimum wage, have produced results similar to those in Card and Krueger’s analysis of New Jersey and Pennsylvania” (Pollin and Luce 1998:41). However, given recent evidence contradicting Card and Krueger’s findings (most directly, Neumark and Wascher 2000), the possibility that workers will face reduced employment prospects or hours reductions as a result of living wage ordinances cannot be dismissed. 8 They also estimated that the cost to the city would be near $20 million per year, including enforcement costs of $4.2 million. The latter figure comes from the Office of Management and the Budget. Some figures reported for Los Angeles and Baltimore suggest enforcement costs well under $1 million (Reynolds 1999), whereas Sander and Lokey (1998) estimate costs in Los Angeles of about $1 million annually.
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early stages of Los Angeles’ living wage law, and Reynolds (2000) examines the impact of the Detroit living wage law on nonprofits. While both provide valuable information, though, they are essentially case studies, precluding generalizations and missing a control group with which to compare experiences to try to gauge the independent effects of living wage laws. Using a different strategy, Pollin and Brenner (2000) report evidence of expected disemployment effects on the part of employers in response to a proposed hybrid living wage/minimum wage law in Santa Monica, although they downplay the importance of this evidence.
Data The data used come from the CPS Outgoing Rotation Group (ORG) files extending from January 1996 through December 2000. The ORG files include approximately 13,000 households per month. In these files, residents of standard metropolitan statistical areas (SMSAs), encompassing all large and medium-sized cities in the United States, can be identified. Since January 1996, the design of the CPS has resulted in the large and medium-sized metropolitan areas in the sample being self-representing. Data on residents of these metropolitan areas are extracted for the empirical analysis, and living wages are assigned to these residents based on major city in the metropolitan area (e.g., Los Angeles in the Los Angeles–Long Beach metropolitan area). This assignment of living wages poses a couple of limitations. First, assignment of people to a metropolitan area based on where they live, rather than where they work, is appropriate to the extent that we are interested— as a policy matter—in how a living wage law affects residents of a city. However, classifying people based on where they work might better reveal direct effects of living wage laws, especially insofar as employees of firms covered by living wage laws working in the city. Second, the correspondence between cities and metropolitan areas is imperfect. In many cases, the metropolitan area will include some suburban areas, but because suburban residents may work in the city, and because employers covered by living wage laws do not necessarily hire only city residents, this is not necessarily inappropriate.9 An additional complication is posed by small municipalities within a metropolitan area that have their own living wage laws (such as West Hollywood or Berkeley). Because residents of (and workers in) these smaller municipalities cannot be identified, this potentially introduces some 9
For expositional ease, the text often refers to cities rather than metropolitan areas.
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measurement error into the prevailing living wage, although it is likely to be relatively minor because of the small share of the workforce covered by these living wage laws relative to the laws of the larger municipalities. Moreover, these living wage laws at least sometimes echo those of the larger city in the metropolitan area (e.g., West Hollywood and Los Angeles implemented the same living wage law in 1997, although in different months).
Evidence on Living Wage Effects on Wages Empirical Approach. To begin our study of living wage effects, we estimate a wage equation for various ranges of the wage distribution in cities. Specifically, we look separately at workers falling at or below the 10th centile, between the 10th and 25th centiles, between the 25th and 50th centiles, and between the 50th and 75th centiles of their city’s wage distribution in a particular month. As an alternative to using the city’s actual wage distribution, we also use an imputed wage distribution. 10 Because the log of an individual’s wage is our dependent variable, using an imputed wage distribution avoids potential problems associated with conditioning the sample on whether an individual’s wage falls within a certain centile range. On the other hand, imputed wages would be expected to identify less accurately those workers likely to be affected by a living wage law because, for example, some low-skill workers earn high wages. For this reason, we view the estimates based on the actual wage distribution as more likely to reveal the effects of living wage laws and focus more on these estimates. 11 In either case, this approach asks whether the average wages of the lowest-wage workers in an SMSA are higher following the implementation of living wage laws (or increases in living wages); it provides indirect evidence in the sense that it does not measure actual wage changes for workers affected by living wage laws. 10
We do this in a simple manner, estimating a standard log wage regression with year and month controls and using predicted log wages from the estimated regression to construct imputed wage distributions for the SMSA-month cell. Of course, the market wages faced by those who choose not to work may be lower than those faced by observationally equivalent individuals who choose to work; this is the standard sample selection problem (Heckman 1979). To assess the consequences of this in a simple manner, the estimates were recalculated reducing the imputed wages of the nonworkers by 5 and 10 percent. The results reported below (for both wages and employment) were qualitatively similar. 11 In the lowest centile range, the biases are likely in similar directions. Using the actual wage distribution, some fraction of workers whose wages are raised by a living wage law may be lifted above the 10th centile, biasing downward any positive effect of the living wage. On the other hand, using the imputed wage distribution probably results in the inclusion in this lower range of more unaffected workers, also biasing any positive effects downward.
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We restrict our sample to workers with an hourly wage greater than $1 and less than or equal to $100 and to those between the ages of 16 and 70 inclusive. To improve accuracy, we also restrict our analysis to SMSAmonth cells with 25 or more observations.12 Pooling data across months, we estimate the following regression for each centile range: ln(wicmy ) = α + X icmyβ + ω ln(w mincmy ) + γ max[ln(w livcmy ), ln(w mincmy )] + δYYy + δ M M m + δCCc + εicmy
(1)
where w is the hourly wage,13 X is a vector of demographic control variables,14 w min is the higher of the federal or state minimum wage, w liv is the higher of the living wage or the minimum wage, and the equation is estimated separately for each specific centile range.15 It is essential to control for minimum wages because some cities with living wage laws are in states with high minimum wages, and we want to estimate the independent effects of living wage laws. The subscripts i, c, m, and y denote individual, city, month, and year. Y, M, and C are vectors of year, month, and city dummy variables, and ε is a random error term.16 The living wage variable that multiplies γ is specified as the maximum of the (log of the) living wage and the minimum wage. 17 In our sample period,
12 The numbers of observations per city vary as expected. The sample size for Los Angeles, for example, is 17,370 workers. Some of the smaller cities in the sample fail to meet the requirement of 25 observations in some months and are not in the sample for every month from 1996 to 2000. An example of such a city is Tucson (674 total observations). The results of the article are qualitatively similar if the sample is restricted to only the larger cities with enough observations to make the sample cut in every month. 13 We use the hourly wage if individuals report it in the CPS. Otherwise, we divide the weekly wage by the hours the individual reports that he or she usually works in a week. The CPS frequently allocates values for missing information by assigning to a record values from an individual that matches the respondent in terms of demographic characteristics. We delete such allocated records from our sample. 14 The demographic controls include education, age, marital status, race, and gender. We limit our list of controls to basic individual characteristics because job-related controls such as union status or part-time work may themselves be affected by living wage ordinances. However, we verified that including such variables yielded similar results and did not change the conclusions of the article. 15 In the few cases of SMSAs that straddle states with different minimum wages (Davenport– Quad Cities, Philadelphia, Portland, and Providence), we use a weighted average of the minimum wages in the two states, weighted by the shares of the SMSA population in each state. 16 The city dummy variables capture wage differences across cities that are time-invariant. The year dummy variables capture changes in wages over time that are common across states. This ensures that we are always comparing relative changes and obviates the need for inflation adjustment. 17 The analysis ignores county living wages, which in our sample period were on the books in 14 counties (in California, Florida, Illinois, New Jersey, Oregon, Pennsylvania, Texas, and Wisconsin). In many cases the counties covered are small, and in general, county living wage laws have not attracted a great deal of attention, perhaps because the number of workers covered may be quite low. In the analysis in this article, county living wage laws are only relevant if they cover workers in cities included in the data set but classified as not having living wage laws. The only county living wage law that clearly covers
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living wages—when they exist—always exceed minimum wages, so this variable imposes the minimum wage as the wage floor for cities that never pass living wage laws or, for those that do, for the period prior to implementing living wages. If living wages boost the wages of low-wage workers, we would expect to find positive estimates of γ when we are looking at workers in the relatively low ranges of the wage distribution. Finally, we also estimate specifications in which we lag w min and w liv by 6 or 12 months (using the same lag for living wages and minimum wages) to allow for a slower adaptive response to changes in minimum and living wages. Basic Results. The results for Equation (1) are reported in columns 1 to 4 of Table 3; all coefficient estimates and standard errors are multiplied by 100. The table reveals no contemporaneous effects of living wages for any of the centile ranges. Six months after a living wage increase, no significant effects are detected, although the estimated coefficients are all positive and larger than in the contemporaneous specification. At a lag of 1 year, however, we find positive and significant effects for the 0th to 10th centile range, with an elasticity of 0.07 when we use the actual wage distribution and 0.05 when we use the imputed wage distribution.18 A lagged effect is not unreasonable because implementation of living wage laws may be a rather drawnout process, and cities often only apply the wage floor when contracts are renewed (as happens, for example, in Baltimore and San Jose). As we might expect, there is never any strong evidence of wage effects in the higher centile ranges.19 In general, then, these data appear to detect wage-increasing effects of living wage ordinances for the lowest-wage workers, and the
a city included in those we study is in Miami–Dade County. In general, this problem should bias any estimated effects of city living wage laws toward zero because the control group actually may include some individuals subject to living wages. Thus the effects of living wage laws that are reported in this article may be slightly understated. 18 The sample sizes are different for the imputed and actual wage distributions because ties in actual wages at the 10th centile of the wage distribution are much more prevalent than ties in imputed wages, and we include observations tied with the upper bound of each range. This bunching of observations at the 10th centile is most likely due to rounding by the CPS respondents. For example, a large number of individuals report hourly wages of $5.50 (many more than report $5.49 or $5.51), which is equal to the 10th centile of the wage distribution in many cities. The same is true for $5.00 and $6.00. When using the imputed wage distribution, ties like this are less likely. 19 The lack of an effect at the higher end of the wage distribution is consistent with there being no spillover effects into the high end of the wage distribution. In general, however, because we cannot identify who in the lower ranges of the wage distribution is receiving a wage increase directly from the law and who is indirectly receiving an increase through a spillover effect, it is not possible to draw firm conclusions regarding spillover effects.
TABLE 3 E L W L W, A C W L W La All Living Wage Laws Living Wage Laws for Different Centile Ranges
× Potentially Covered Workers
× Contractor Only Living Wage
× Business Assistance Living Wage
25 –50 (3)
50 –75 (4)
≤ 10 (5)
10 –25 (6)
≤ 10 (7)
10 –25 (8)
≤ 10 (9)
10 –25 (10)
≤ 10 (11)
10 –25 (12)
A. Using Actual Wage Distribution Living wage −0.53 0.27 (2.23) (1.62) Living wage 6 1.91 0.84 months ago (2.25) (1.70) Living wage 12 6.95 0.93 months ago (2.40) (1.78)
0.95 (1.65) 2.22 (1.76) − 0.01 (1.85)
−0.03 (1.63) 0.34 (1.79) −1.08 (1.92)
− 4.81 (2.95) − 4.41 (3.05) 0.61 (3.49)
−1.06 (1.81) −1.15 (1.91) −1.28 (2.07)
2.05 (2.54) 5.60 (2.57) 10.61 (2.72)
1.27 (1.79) 2.03 (1.89) 2.26 (2.00)
−3.82 (3.40) − 4.96 (3.63) 0.50 (4.02)
−2.81 (2.27) −2.32 (2.36) −1.92 (2.49)
1.44 (2.78) 5.74 (2.67) 10.54 (2.78)
2.21 (2.11) 2.73 (2.22) 2.72 (2.31)
Sample size
42,912
71,135
72,737
34,196
42,638
34,196
42,638
34,435
42,912
34,435
42,912
B. Using Imputed Wage Distribution Living wage 0.27 −0.24 (2.20) (2.42) Living wage 6 2.51 −0.44 months ago (2.22) (2.42) Living wage 12 4.65 0.92 months ago (2.26) (2.51)
0.30 (1.99) 1.50 (2.12) − 0.42 (2.29)
1.06 (1.93) 2.24 (2.04) 0.95 (2.11)
−2.08 (3.15) 2.40 (3.11) 4.95 (3.13)
−1.90 (3.00) −1.85 (3.09) − 0.99 (3.22)
2.31 (2.42) 3.41 (2.52) 6.26 (2.61)
0.27 (2.79) 0.67 (2.81) 2.71 (3.00)
−0.65 (3.49) 4.32 (3.47) 4.65 (3.53)
−3.69 (3.46) −6.46 (3.56) − 6.76 (3.72)
0.84 (2.64) 1.46 (2.78) 4.64 (2.77)
1.89 (3.13) 3.07 (3.07) 5.53 (3.17)
Sample size
72,316
73,574
31,052
43,164
31,052
43,164
31,282
43,414
31,282
43,414
a
34,435
31,282
43,414
/ 545
See notes to Table 1. The control group is urban workers in cities without living wages. Each entry is an estimate from a separate specification for log wage. Standard errors are reported in parentheses. All estimates are multiplied by 100. For an SMSA’s data to be included in the sample for a particular month, there must be at least 25 observations in that SMSA-month cell. Observations for which allocated information is required to construct the wage variable in the CPS are dropped. For columns (5) to (8), observations for which allocated information is required to construct the covered and uncovered dummy variables are also dropped. The log wage equation controls for year, month, SMSA, education, age, marital status, race, gender, and the minimum wage at the same lag as the living wage variable. The estimates with an 18-month lag are similar to those with a 12-month lag. Reported standard errors are robust to non-independence (and heteroscedasticity) within city-month cells.
Detecting Effects of Living Wage Laws
10 –25 (2)
Centile
≤ 10 (1)
× Uncovered Workers
All Living Wage Laws
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D N S A
results are similar whether we use the actual or imputed wage distribution to construct the centile ranges.20 A couple of issues arise in considering the validity of the evidence based on the research design embodied in Equation (1). First, the equation uses a difference-in-differences strategy to identify the effects of living wages. In this framework, the effect of living wages—the treatment—is identified from how changes over time in cities implementing (or raising) living wages differ from changes over the same time period in cities without (or not raising) living wages. The difference-in-differences strategy is predicated on the assumption that absent the living wage, and aside from differences captured in the other control variables, the cities that pass living wage laws (the treatment group) are comparable with those that do not pass such laws (the control group). While fixed differences between cities are handled by the differencein-differences approach, potentially more troublesome is a difference in the time pattern of changes stemming, for example, from a different prior trend in a dependent variable in the treatment and control groups. 21 Because the specification assumes only fixed city and time effects, with the latter assumed to be the same across all observations, such a difference in the time pattern would tend to be incorrectly attributed to the effects of living wages. To test whether different time trends in the treatment and control groups may bias the estimates, the sample was restricted to include the control group cities and only the pre–living wage observations on the treatment group cities. Specifications were then estimated, adding—in addition to the control variables each one includes—a time trend and an interaction between this time trend and a dummy variable for cities later implementing living wages.22 The estimated coefficient of the time-trend interaction provides 20 In column 1 of Table 3 (as well as in the other columns), three separate specifications are reported—one with contemporaneous living wage and minimum wage variables, one with 6-month lags, and one with 12-month lags. As column 1 shows, the effect of living wages appears in the 12-month lag specification. On the other hand, it turns out that a positive effect of the minimum wage appears in the contemporaneous specification—i.e., minimum wages boost wages at the bottom of the wage distribution, but this effect is dissipated over time. This raises the possibility that in the 12-month lag specification the omission of the contemporaneous minimum wage biases the estimated living wage effect. However, the results were very similar if the contemporaneous, 6-month, and 12-month lags of the living wage and minimum wage variables were included simultaneously or if the contemporaneous minimum wage variable was added to the specification with the 12-month lags. One might expect the different lags of the same policy variable to be highly collinear, but conditional on city, year, and month fixed effects they are not. 21 As an example that receives more attention later, quite a few living wage laws (especially business assistance laws) arise in California. If California was experiencing faster wage growth (and in particular faster growth in wages of low-wage workers), this might lead to a spurious inference that living wage laws boosted wages of low-wage workers. 22 The living wage variable was dropped because all observations are taken prior to the introduction of a living wage.
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a test for differential time trends in the treatment and control groups for the dependent variable in question. For the specifications just presented, as well as all the others reported in this article, this estimated coefficient was small and not significantly different from zero, which bolsters the validity of the research design. This was taken one step further. In particular, for each set of results reported in this article, specifications were estimated including the entire sample period, retaining the differential time trends for the treatment and control groups. Even though in these cases it is more difficult to separate the effects of the living wage law and the time trend for the treatment group—because living wages invariably grow over the sample period—the estimated effects of living wages on the wage and employment outcomes considered generally were similar to those reported in the tables that follow, sometimes a bit stronger and sometimes a bit weaker, but leading to the same qualitative conclusions. Second, the choice of a cutoff at the 10th centile is somewhat arbitrary. It was chosen because comparisons between wages of workers at the 50th and 10th centiles often are used in studies of wage inequality and also because living wages, while generally above the 10th centile, often are relatively close to it. If we assume that living wage compliance is perfect and that there are no effects on wages of other workers, however, then the fact that many living wages exceed the 10th centile suggests that many workers whose wages are increased as a result of living wage laws will be dropped from the sample using the 10th centile of the actual wage distribution as a cutoff. In such a case, the conclusion that living wage laws increase wages of those in the bottom decile of the wage distribution would still be warranted based on the regression results because the positive effects would arise from living wages shifting some workers above the 10th centile, thereby raising the average wage of those below the 10th centile.23 However, these assumptions are unlikely to hold. Workers may not be paid the living wage on all their
23 Indeed, even if all affected workers have their wages increased to a point above the 10th centile, the average wage of those at or below the 10th centile increases; as low-wage workers are “cleared out” from below the 10th centile, the 10th centile increases, and the bottom tenth of the wage distribution is therefore made up of higher-wage workers on average. To see this in a simple example, suppose that there are initially 50 workers, with 5 earning a wage of $5, 20 earning $6, and 25 earning $7, so the 10th centile (the wage of the fifth worker from the bottom when workers are ranked by wages) is $5. Now let one worker’s wage go from $5 to $7. In this case, the 10th centile rises to $6 because the bottom tenth of the wage distribution now includes 4 workers earning $5 and 1 worker earning $6, and the average wage of workers at or below the 10th centile rises from $5 to $5.20. (Furthermore, the average wage increase in the bottom tenth of the wage distribution can exceed the average increase in the 10th to 25th centile range, as it does in this example.)
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hours of work, compliance may be incomplete,24 and there may be spillover effects, so wage effects may be quite likely to show up below the legislated living wage. In addition, we have to remember that the centile (10th or otherwise) is only an estimate and may be quite imprecise for smaller cities. Nonetheless, to explore the sensitivity of the estimated wage effects for the lowest-wage group to the cutoff used, the specifications also were estimated using as cutoffs the 15th and 20th centiles. To give some perspective on the living wage relative to these centiles, in nine of the cities in Table 2, the 15th centile exceeds the living wage, and in six more it is within $1 (of a total of 21 cities). In 14 of the cities, the 20th centile wage exceeds the living wage and is within $1 in five more. The estimated 12-month lagged effects for these specifications—corresponding to the estimate of 6.95 in Table 3—were 3.62 (standard error of 2.10) using the 15th centile and 3.77 (1.86) using the 20th. Thus, through the 20th centile, the estimated wage effect remains positive and statistically significant at the 5 or 10 percent level, with the point estimate somewhat smaller than that obtained using the 10th centile cutoff. Assessing the Magnitudes. Returning to Table 3, the estimated wage effects for low-wage workers, indicating an elasticity of 0.05 to 0.07 in the lowest decile, are arguably surprisingly large. Since we would expect a maximum wage elasticity of 1 for affected workers, the largest effects we should expect are approximately equal to the proportion of workers who are likely to be affected by the living wage. If we use the estimates of this proportion reported in column 3 of Table 1, even assuming that all the affected workers are in the lowest decile of the wage distribution (so that the percentages would be multiplied by 25/10), for most of the studies we would not get very close to 5 percent of the workforce. To see this, take the coverage estimate to be about 2.5 percent (the approximate 1 percent figure in the table multiplied by 25/10). Next, assume that this 2.5 percent of the workforce gets a raise equal to the living wage increase, which is an exaggeration because this assumes that all the affected workers were previously at the minimum wage (in the case of a new living wage) rather than above the minimum wage but below the living wage. Under these assumptions, the estimated effect would be only 2.5 (or an elasticity of 0.025), which is about one-half or less of the estimated effect in the 12-month lag specifications in column 1 of Table 3. 24
Imperfect compliance may include paying wages below the living wage. As evidence of this, when we closely examined wage distributions in cities that had implemented living wage laws, we generally failed to find spikes at the living wage. A possibility for future research is to adapt nonparametric estimation of wage distributions to identify where in the wage distribution living wage laws induce changes [as is done for the minimum wage and family income distributions in Neumark, Schweitzer, and Wascher (1998)].
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Note also that an effect of this size would be about equal to the estimated standard error of the corresponding regression coefficient, making it unlikely that it would be possible to detect an effect on wages of living wage laws that cover and affect only contractors. These considerations raise two distinct possibilities that require empirical investigation. First, the baseline estimates may be badly biased, reflecting some influence other than living wages and hence yielding implausibly large estimated effects. Second, the basis for evaluating the plausibility of the estimated living wage effects may be flawed. These issues are taken up next. Are We Actually Estimating Effects for Covered Workers? Our first step in assessing whether we are detecting actual living wage effects rather than some spurious influences is to estimate separate wage effects for workers more likely and less likely to be covered by living wage ordinances. If the estimated effects are no different for workers more likely and less likely to be covered by living wage laws, we would be inclined to conclude that we are estimating a spurious relationship with living wages. This analysis requires, however, some means of distinguishing workers in the CPS who are more likely to be covered by living wage laws or, more specifically, workers who are potentially covered. We do this by using the limited information we have on workers and the scope of city ordinances. Specifically, if the law refers to specific workers (e.g., custodial, security, and parking attendants in Portland or city employees in a few cities), we try to use the same classification in the CPS. When the living wage law refers generally to contractors, we use workers in construction and in the following service industries: transportation (excluding U.S. Postal Service workers); communications, utilities, and sanitary services; custodial; protective service; parking; and certain professional and social services. This is based on a study of Baltimore’s living wage law (Niedt et al. 1999) that looked at the types of workers and firms under city contracts. Finally, for workers in cities where businesses receiving financial assistance from the city are covered, virtually any nongovernment worker potentially can work for a company that is subject to the legislation. Therefore, we characterize all private-sector workers in the lowest quartile as being potentially covered. To better gauge the implications of these classification methods, we calculated the percentage of potentially covered workers in the bottom quartile of the wage distribution in the cities in our wage analysis. The resulting percentages are quite small (in the range of 3 to 6 percent) for cities with very narrow coverage, on the order of 15 to 20 percent for cities with laws covering contractors but not those receiving business assistance, and typically over 80 percent for living wage laws with business assistance provisions. These
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D N S A
high percentages emphasize that we identify workers who are potentially covered. While the upper bounds provided by the potential coverage classification surely overstate actual coverage substantially, most likely many-fold, our classification may still provide a useful (although noisy) contrast with workers who are not covered by living wage laws, which is all it is intended to do. Given our crude distinction between those workers who are potentially covered by living wage laws and those who are not, we introduce interactions between dummy variables indicating potentially covered and uncovered workers (Cov and Uncov) and the living wage variable and estimate25 ln(wicmy ) = α + X icmyβ + ω ln(w mincmy ) + γ max[ln(w livcmy ) × Covicmy , ln(w mincmy )] + γ ′max[ln(w livcmy ) × Uncovicmy , ln(w mincmy )] + δYYy + δM M m + δCCc + εicmy (2) If we find that the estimate of γ indicates positive living wage effects while the estimate of γ′ does not, our confidence that we are detecting actual effects of living wage laws would be bolstered. Note that when we estimate this specification, the vector X is expanded to include dummy variables representing the worker subgroups that are covered by living wage laws. Since our estimated definition of coverage differs somewhat by city, we added separate dummy variables for each group to pick up wage differences between them and to ensure that the interactions are not simply reflecting differences in levels (i.e., main effects). The estimates are reported in columns 5 through 8 of Table 3. In both panels (but more so in the top one), the results indicate that the positive wage effects of living wages show up only for workers who are potentially covered by living wage laws, based on our potential coverage classification. The estimated effect of living wage laws at a lag of 12 months is statistically significant for these potentially covered workers but not for uncovered workers. Using the actual wage distribution, there is also a statistically significant positive impact in the 6-month lag specification. Thus the results are consistent with those workers more likely to be covered by living wage ordinances receiving the bulk of the wage gains, indicating that the living wage effects that we detect are concentrated among workers who are potentially affected by living wage laws, which in turn makes it less plausible that we are picking up spurious effects associated with these laws. Are Living Wage Laws Broader than Is Commonly Thought? The potential coverage classification used in the preceding estimates includes all private25
The interactions with Cov and Uncov appear inside the max operator so that when these variables are zero, the wage floor is specified as the minimum wage rather than zero.
Detecting Effects of Living Wage Laws
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sector workers in cities where the living wage laws cover employers receiving business assistance. Indeed, it is the living wage laws in these latter cities that drive the wage effects. When we excluded from the sample completely those cities with living wage legislation that applies to firms receiving business assistance from the city and then reestimated Equation (2), we found no statistically significant effects of living wages. On the one hand, this suggests that wage effects of narrow living wage laws may not be detectable (or may not exist). On the other hand, it emphasizes that some living wage laws are much broader than simply mandating higher wages for city contractors (and perhaps city employees). Specifically, when living wage laws extend to employers receiving business assistance, their effective coverage may be more extensive than what is suggested by the reports summarized in column 3 of Table 1.26 This may explain the large living wage effects reported earlier. 27 To explore this possibility more directly using all the data, we alter our basic specification to distinguish between the effects of living wage laws that cover contractors only (as well as city employees) and those which cover employers receiving business assistance; the latter are surely broader because nearly every living wage law covering busness assistance recipients also covers contractors.28 We interact dummy variables for the two types of living wage laws (Bus and Con) with out living wage variable as in ln(wicmy ) = α + X icmyβ + ω ln(w mincmy ) + γ max[ln(w livcmy ) × Buscmy , ln(w mincmy )] + γ ′max[ln(w livcmy ) × Concmy , ln(w mincmy )] + δYYy + δM Mm + δCCc + εicmy (3) The results, reported in columns 9 through 12 of Table 3, indicate that the effects of living wage laws on wages are significant only for cities with the broader variety of living wage laws that cover employers receiving business assistance from the city. In the top panel, the estimates are large and statistically significant at a lag of 1 year and imply an elasticity of 0.11 for workers in the lowest decile. In the bottom panel, the magnitudes of the estimated effects are similar for both types of living wage laws but statistically significant (at the 10 percent level) only for the business assistance living
26 Reynolds (1999) presents crude calculations for Detroit suggesting that taking account of only one type of employer covered by business assistance provisions substantially increases the number of affected workers. This issue, as well as other reasons why different types of living wage laws may have different effects, requires more serious study in future research. 27 These also may be exacerbated by the aforementioned positive spillover effects from living wages to wages of other workers. 28 Living wage laws covering city employees only or city employees and contractors only are also included in the contractor-only group. However, this concerns only two relatively small cities (Dayton and Durham), and omitting these cities from the analysis had virtually no impact on the estimates.
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D N S A
wages laws. Thus, as our back-of-the-envelope calculation suggested earlier, we find little evidence of an effect for laws that cover contractors only, although the contrast is less sharp for the lower panel on the imputed wage distribution. Do the Living Wage Effects Reflect Unmeasured State-Level Changes? The difference-in-difference strategy we use to identify the effects of living wage laws is intended to avoid evidence based on a spurious relationship with other changes in cities passing living wage laws by using a control sample of cities that did not pass such laws. The fact that we found no wage effects in higher parts of the wage disribution is evidence against some forms of spurious relationships; that is, one could think of the combined evidence as providing a difference-in-difference-in-differences estimate for low-wage relative to high-wage workers. Nonetheless, state-level policy changes (or state-level changes in economic conditions) affecting lowerincome families may affect labor market outcomes for low-wage workers and may coincide with the passage of living wage laws. Although we did control for state minimum wages in our original analysis, other policies, such as state earned income tax credits (Neumark and Wascher 2001) or welfare reform (Meyer and Rosenbaum 2001)—some parts of which are not so easily measured—may have an impact on low-wage workers. To address the possibility that state-level changes represent confounding influences in our estimates of living wage effects, we augment and alter Equation (3) to use only within-state variation in living wage laws to identify the effects of living wage ordinances on wages. The wage equation now becomes ln(wicmy ) = α + X icmy β + ω ln(w mincmy ) + γ max[ln(w livcmy ) × Buscmy × LWcmy , ln(w mincmy )] + γ ′max[ln(w livcmy ) × Concmy × LWcmy , ln( w mincmy)] (4) + θmax[ln( w livcmy), ln(w mincmy )] + δYYy + δM M m + δCCc + εicmy Equation (4) embodies two changes. First, we assign the living wage to all cities in the state.29 If no city has a living wage law, wliv is set to wmin. For all states except California, at most one city in the state has a living wage law, in which case all cities in the state get assigned that living wage. In California, where multiple cities have living wage laws, a weighted average is used for observations in the state.30 Second, the living wage variables (still interacted with Bus and Con) are interacted with a dummy variable for the city in 29 For this analysis, individuals in SMSAs with living wages that straddle states (Portland and St. Louis) are assumed to be part of the state where the bulk of the SMSA residents live (Oregon and Missouri, respectively). 30 If we simply drop Oakland, San Francisco, and San Jose and apply the Los Angeles living wage to all remaining observations in the state, the results are virtually unaffected.
Detecting Effects of Living Wage Laws
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which the living wage is actually imposed (LWcmy), which is set to 1 for every month in which the city’s living wage law is in effect and 0 otherwise (and always for cities without a living wage). This specification allows θ to pick up any state-level changes correlated with living wage changes, whereas γ and γ′ capture the differential changes in the city in which the living wage is actually implemented.31 The latter are the causal effects we are after and correspond to difference-in-difference-in-differences estimators using other cities in the same state as the control sample.32 We also estimate an expanded version of Equation (4) in which we add rural workers in the same state to the control sample, in which case we also add state dummy variables to the regression. In either case, no longer are the living wage effects inferred from differences in outcomes between all cities that have adopted living wage laws and those which have not. Instead, the effects of living wage laws are identified from the differences in outcomes between cities that have adopted laws and cities (and other areas) in the same state that have not adopted these laws. The results are reported in columns 1 through 4 of Table 4; since we only found effects for the lowest decile of the wage distribution in the preceding analysis, here we restrict our attention to that decile. In the top panel, using the actual wage distribution to identify low-wage workers, the estimated effects on wages are very similar to the corresponding estimates in columns 9 through 12 of Table 3. Specifically, for living wage laws that apply to employers receiving business assistance, the estimated elasticities of wages with respect to living wages are in the 0.10 to 0.11 range and statistically significant, whereas the estimated effects for contractor living wage laws are again smaller and insignificant. However, in the bottom panel, using the imputed wage distribution, the estimated effect of business assistance living wage laws declines slightly (to an elasticity of 0.04 or 0.03), which coupled with increased standard errors renders the estimated effect statistically insignificant. Nonetheless, the point estimates are little changed, suggesting that unmeasured state changes correlated with living wage increases do relatively little to bias the estimated effects of living wages. Another approach to this issue is to consider specific cities (or states) that may be driving the results and whether unique factors in those areas could be generating a spurious relationship with living wages. A reviewer 31 We also estimated a specification that allowed state-level changes to differ depending on whether the living wage effective in the state was of the business assistance type or the contractor type. This resulted in no appreciable changes in the results. 32 On the other hand, this limits slightly the number of cities for which an effect can be identified because Minneapolis and Portland are the only cities in their respective states that are included in our wage sample. For those cities, there is no control group. Thus, for the estimation of the wage effects, the impact of living wages is identified from the remaining cities.
554 /
Urban Workers in Same State as Control Group
× Contractor (1) A. Using Actual Wage Distribution Living wage −3.70 (3.44) Living wage −5.16 6 months ago (3.67) Living wage 0.43 12 months ago (4.08) Sample size
a
See notes to Tables 1 and 3.
× Business Assistance (2)
× Contractor (3)
× Business Assistance (4)
1.72 (3.17) 5.27 (3.12) 10.39 (3.32)
−3.54 (3.37) − 4.76 (3.06) 0.77 (4.00)
1.36 (3.02) 5.65 (2.96) 11.27 (3.12)
34,435
B. Using Imputed Wage Distribution Living wage −0.87 (3.57) Living wage 3.46 6 months ago (3.52) Living wage 4.05 12 months ago (3.61) Sample size
Urban and Rural Workers in Same State as Control Group
31,282
Distinguish Legislated from Mandated Living Wage Increases × Contractor × Legislated × Mandated (5) (6) −1.72 (3.39) −5.25 (3.86) 1.89 (4.22)
−3.54 (3.54) 2.35 (3.53) 3.10 (3.52)
× Mandated (8)
−6.04 (3.36) −1.58 (3.38) 3.98 (3.48)
7.64 (3.12) 12.12 (3.07) 18.59 (3.18)
−0.34 (3.22) −1.68 (3.39) 1.52 (3.22)
1.76 (3.18) 4.10 (3.23) 8.25 (3.61)
34,435 −0.99 (2.98) −0.38 (2.91) 3.92 (3.03)
46,364
× Legislated (7)
−16.07 (9.80) 1.86 (9.20) −5.29 (9.22)
51,179 0.33 (3.04) −0.58 (3.14) 3.44 (3.30)
× Business Assistance
0.02 (3.71) 4.19 (3.71) 4.35 (3.72)
−5.31 (6.24) 7.24 (6.59) 8.38 (8.26) 31,282
D N S A
TABLE 4 E L W L W, A E, W B 10 C W Da
Detecting Effects of Living Wage Laws
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suggested to us that much of the identification of the effects of business assistance living wage laws comes from three California cities (Los Angeles, Oakland, and San Jose) because there are 10 cities with business assistance living wage laws, but 4 of these were enacted in late 1999 or 2000. If other factors were influencing economic conditions (including wages) in California cities, it is conceivable that we are finding spurious evidence of living wage effects. Of course, the preceding analyses (e.g., allowing differential trends and comparing effects in different parts of the wage distribution) should address this concern to a large extent. Nonetheless, we also reexamined the results allowing for different effects of business assistance living wage laws in these three California cities and the other cities. The results indicated that the wage effects of these living wage laws were, if anything, stronger in nonCalifornia cities than in California cities. Specifically, we augmented the specification in columns 9 and 11 of Table 3 to allow interactions of the living wage variables with indicators for California and non-California cities, thus estimating separate effects of business assistance living wage laws on the wages of the lowest-wage workers in these two sets of cities. The estimated 12-month lag coefficients (standard errors) for these laws were 0.088 (0.039) for California cities and 0.117 (0.037) for non-California cities. Combined with the earlier evidence, these latter results should assuage concerns that the results are spuriously driven by other changes in California cities. Does Endogenous Policy Bias the Estimated Living Wage Effects? The final possibility we consider is that city officials time the passage of living wage legislation to coincide with strong economic conditions for lower-wage workers, when a living wage is likely to be relatively less binding but still accomplishes whatever political goals might underlie such policies. This sort of timing could provide an alternative explanation of our large estimated wage effects. To tackle the issue of the timing of the legislation, we use the fact that some cities mandated subsequent increases in the living wage at the time they passed their original ordinance. We separate living wage changes into those which are legislated and those which subsequently result from mandated increases specified earlier. The mandated increases, which are normally part of the original legislation and tie the level of the living wage to federal poverty definitions, are not expected to be as intertwined with economic conditions (at least deliberately) as the legislated increases might be. 33 33
For every city, the initial living wage is treated as legislated. Subsequent increases (if they occurred) are treated as mandated if the living wage is indexed (usually to the poverty line). Thus in Portland and Baltimore increases subsequent to the initial living wage are treated as legislated, whereas those in other cities are treated as mandated.
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D N S A
Estimating these two separate effects requires that we introduce into Equation (3) interactions of the living wage effects with indicators for whether the living wage in effect in a particular month is the result of a specific act of legislation (Leg) or was mandated in earlier legislation (Man) as in ln(wicmy ) = α + X icmyβ + ω ln(w mincmy ) + γ max[ln(w livcmy ) × Buscmy × Mancmy , ln(w mincmy )] + γ ′max[ln(w livcmy ) × Concmy × Mancmy , ln(w mincmy )] (5) + δ max[ln(w livcmy ) × Buscmy × Legcmy , ln(w mincmy )] + δ′max[ln(w livcmy ) × Concmy × Legcmy , ln(w mincmy )] + δYYy + δM Mm + δCCc + εicmy If the bulk of the effect of living wages laws arises from legislated living wage changes, captured in δ (for business assistance living wages), we would be more inclined to attribute the estimated effects reported earlier to endogeneity. On the other hand, the effects of mandated increases, captured in γ, should be more immune to bias from endogenous policy. Columns 5 through 8 of Table 4 report the results. As before, positive and statistically significant wage effects are detected only for living wages covering employers receiving business assistance. More to the point, the effects of such living wage laws are considerably stronger for mandated than for legislated increases. For the mandated increases, we now find a positive wage effect (with an elasticity of 0.12) that is significant at the 10 percent level in the 6month lag specification when we use the actual wage distribution. The effect is smaller and not significant, however, when we use the imputed wage distribution. In the 12-month lag specification, the estimated wage effects are positive and statistically significant only for the mandated increases, and the latter is much larger, with an elasticity of 0.19 in the top panel and 0.08 in the bottom panel.34 These estimates may be implausibly large, suggesting that these results should be interpreted cautiously. Qualitatively, though, because there are, if anything, stronger effects estimated for mandated increases, this evidence contradicts the endogenous timing hypothesis, under which the positive bias should show up in the estimates of the effects of legislated increases.35
34
One potential problem is that mandated increases at a lag of 12 months may largely reflect legislated increases at a lag of 24 months, given that in many cases an initial living wage is passed, with mandated increases in subsequent years. We attempted to test for this possibility by adding to the specification lags of 24 months in both legislated and mandated increases, but the estimates tended to be uninformative; given the short period over which information on living wages is available, this is not surprising. 35 Alternatively, it suggests that the bias from endogenous policy is in the opposite direction. In any event, the mandated increases provide a more compelling experiment.
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Employment Effects To this point we have been concerned with establishing whether we can detect effects of living wages on the outcome that should be most directly affected, namely, wages. We have established that there appears to be a detectable causal effect of broad living wage laws that cover employers receiving business assistance from the city. Higher wages are clearly one goal of living wage laws. However, the potential gains from higher wages may be offset by reduced employment opportunities. To examine such a tradeoff, we now turn briefly to a parallel analysis of the employment effects of living wage laws using essentially the same framework that we used to study the effects of these laws on wages. We use the same specifications that are used in the analysis of wages, substituting linear probability models for individual employment status. 36 The only difference is that we cannot classify nonworking individuals based on their position in the wage distribution. Instead, we impute wages for everyone and use the imputed wage distribution to classify individuals based on imputed wages. 37 The basic results with no distinction as to the type of living wage law or more refined attempts to address causality are reported in columns 1 through 4 of Table 5. Above the 10th centile, there is no evidence of disemployment effects, which is not surprising given the lack of wage effects. Interestingly, there is some evidence of positive employment effects higher in the imputed wage distribution, consistent with substitution toward higherskill workers. However, focusing attention on those at the bottom of the (imputed) wage distribution, the employment effects mirror the wage effects, with a fairly large estimated negative effect (−5.62) in the 12-month lag specification that is statistically significant. Given an average employment rate of about 0.4 for individuals in this range of the imputed wage distribution, this implies an elasticity of employment with respect to the living wage of –0.14.38 Looking next at the distinction between the contractor-only
36
For a detailed discussion of the linear probability model, see Greene (1997:873–74). We do this using the same method we used to obtain the imputed wage distribution for our wage estimates. If we used actual wages for workers and imputed wages for nonworkers, we would rarely have nonworkers in the extreme percentiles of the wage distribution. For the employment estimates, the impact is identified for three additional cities with living wage laws (Duluth, Madison, and New Haven) because with the inclusion of nonworkers these cities have 25 or more observations for some months both prior to and after the implementation of a living wage; in general, there are many more city-month cells with 25 or more observations when looking at employment. 38 If the estimated employment effect is compared with the estimated wage effect, the evidence indicates an employment elasticity with respect to the “realized” wage increase of −2 [(−5.62/0.40)/−6.95], larger than the −0.5 figure that is taken as a consensus in the labor demand literature (Hamermesh 1993). This suggests that the estimated disemployment effect, insofar as it arises solely due to the 37
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All Living Wage Laws Living Wage Laws for Different Centile Ranges Centile of Imputed Wage Distrilbution
≤ 10 (1)
10–25 (2)
25–50 (3)
50–75 (4)
× Contractor Only Living Wage ≤ 10 (5)
10–25 (6)
× Business Assistance Living Wage ≤ 10 (7)
10–25 (8)
Living wage
−1.77 (2.14)
0.02 (1.81)
2.58 (1.18)
1.79 (1.04)
−3.62 (3.13)
−0.10 (2.67)
−0.49 (2.77)
0.10 (2.30)
Living wage 6 months ago
−3.22 (2.26)
1.16 (1.88)
2.31 (1.24)
1.32 (1.08)
−6.07 (3.37)
0.61 (2.79)
−1.25 (2.91)
1.53 (2.39)
Living wage 12 months ago
−5.62 (2.45)
1.62 (2.02)
1.55 (1.31)
2.44 (1.16)
−5.12 (3.77)
0.95 (3.05)
−5.99 (3.08)
2.10 (2.54)
Sample size
83,326
118,541
197,477
199,703
83,326
118,541
83,326
118,541
a
See notes to Tables 1 and 3. Reported are the estimated effects of the living wage on the employment of individuals in the range of an SMSA’s imputed wage distribution specified at the top of each column. Observations for which allocated information is required to construct the employment variable in the CPS are dropped. Estimates are from linear probability models. Reported standard errors are robust to non-independence (and heteroscedasticity) within city-month cells.
D N S A
TABLE 5 E L W L P E, A C W L W La
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living wage laws and the business assistance laws, in columns 5 through 8, the results partly mirror the wage effects. In particular, in the 12-month lag specification for the lowest-skill individuals, only for living wage laws with business assistance provisions is the estimated disemployment effect (−5.99, or an elasticity of about −0.15) statistically significant; this corresponds exactly to the specification and type of living wage laws for which the evidence indicated that living wage laws boost wages. On the other hand, the point estimate for contractor-only laws, while statistically insignificant at the 10 percent level, is not as different in magnitude as was the estimated wage effect.39 Table 6 also parallels the previous analysis of wage effects by conducting the two experiments meant to assess the causality question, first using urban or urban and rural workers in the same state as the control group and then distinguishing between mandated and legislated increases, looking only at those individuals below the 10th centile of the imputed wage distribution. Mirroring the wage results, many of the estimated disemployment effects are relatively insensitive to the alternative control groups we consider.40 Similarly, the estimated disemployment effects generally are considerably larger for mandated living wage increases. Thus, looking at the individual coefficient estimates in the specifications for which we found that living wage laws boosted wages, the point estimates indicate disemployment effects. However, despite the correspondence of the pattern of positive wage and negative employment effects, these individual coefficient estimates are weak and not statistically significant for some of the specifications. In our view, this does not provide a basis for concluding “average” wage effect of living wages, is larger than would be expected. However, living wages may entail greater increases in projected future labor costs than the wage increase that identifies the typical labor demand elasticity, given their frequent indexation. Also, this elasticity focuses on one narrow category of workers rather than on labor overall, so substitution possibilities may be greater. 39 The hours worked by those in the lower end of the imputed wage distribution also may be an outcome of interest because employers may reduce hours when living wage laws are passed. On the other hand, living wage laws may induce employers to economize on fixed employment costs, including the health benefits that these laws sometimes encourage, leading employers to increase the hours of some current workers and reduce the number of new hires. In looking at hours as an outcome, we found negative but relatively small (elasticity less than – 0.1) and statistically insignificant effects of living wages for those at the lower end of the imputed wage distribution. However, when we restricted the sample to include only those employed (i.e., restricted the sample to those with positive hours), the results suggested positive hours effects for lower-skill workers. Thus, although the estimates did not provide evidence of overall hours reductions, they were consistent with living wage laws leading employers to try to reduce fixed costs of employment. 40 The additional cities with living wages that enter the sample (Duluth, Madison, and New Haven) are in states with other (larger) cities that have living wage laws. Thus, as described earlier following Equation (4) for the analysis of wages, a weighted average of living wages in the state is used for the other workers in the state who are part of the control group.
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I W Da Urban Workers in Same State as Control Group
× Contractor (1)
× Business Assistance (2)
Living wage
−3.25 (3.17)
Living wage 6 months ago Living wage 12 months ago
Distinguish Legislated from Mandated Living Wage Increases × Contractor
× Business Assistance
× Contractor (3)
× Business Assistance (4)
× Legislated (5)
× Mandated (6)
× Legislated (7)
× Mandated (8)
0.28 (3.00)
− 4.16 (3.09)
1.35 (2.89)
−1.48 (3.19)
−16.32 (7.39)
−2.42 (3.27)
0.85 (3.36)
−5.87 (3.41)
−0.81 (3.17)
−6.18 (3.31)
−0.06 (3.03)
− 4.90 (3.63)
−12.45 (6.93)
−1.14 (3.45)
−1.43 (3.71)
− 4.78 (3.80)
−5.33 (3.35)
−5.07 (3.73)
− 4.53 (3.21)
− 4.05 (4.07)
−10.98 (6.98)
−7.69 (3.91)
−6.33 (3.95)
Sample size a
Urban and Rural Workers in Same State as Control Group
See notes to Tables 1, 3, and 5.
83,326
118,355
83,326
D N S A
TABLE 6 E L W L P E, A E, W B 10 C
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that living wages do not reduce employment of the lowest-skill workers. In any classic statistical test, of course, all that evidence like this establishes is that we cannot reject the null hypothesis of no disemployment effect. However, we believe that the close correspondence between positive estimated wage effects and negative estimated employment effects across the various specifications makes it more plausible that our failure to find strong evidence of disemployment effects is a result of imprecision owing at least in part to small numbers of living wage increases available for analysis.
Conclusions Using standard household-level labor market data, our research points to sizable effects of living wage ordinances that specify relatively broad coverage on the wages of low-wage workers in the cities in which these ordinances are enacted.41 This evidence argues for a detailed analysis of these data to assess whether living wage ordinances ultimately achieve their policy goal of helping poor or low-income families. In the absence of evidence of wage effects, we would have concluded instead either that living wage laws are ineffective or that they cannot be assessed through standard labor market data sources with which researchers have studied other labor market policies that vary geographically. If heterogeneity with respect to coverage of living wage laws is ignored and the estimates of the overall effect of these laws are evaluated in light of existing estimates of coverage based on city contractors, the magnitudes of our estimated wage effects are larger than would be expected based on the apparently limited coverage of living wage laws. Additional analyses of these wage effects indicate that the large effects are not driven by spurious or endogenous relationships stemming from other state-level policy changes or the timing of policy changes to coincide with advantageous economic conditions for low-wage workers. Rather, we find that the effects are driven 41 A recent article by Bertrand, Duflo, and Mullainathan (2001) looks at the impact of serial correlation in the error term (and the data) across observations on the same unit (in this case, cities) on standard difference-in-difference estimators. It finds that, especially in the absence of statistical diagnostic tests, these estimators are likely to lead to biased and often understated standard errors and hence erroneous findings of statistical significance. Unbiased estimates of the standard errors allowing an arbitrary serial correlation pattern in the error can be obtained easily by “clustering” the data by city (rather than, for example, by city and month). However, the resulting standard errors are conservative (if anything, too large) because no structure is imposed on the serial correlation. This estimator was implemented for all the key specifications reported in this article. While the standard errors generally rose somewhat, the changes were not dramatic, and thel significant results reported in this article remained statistically significant at the 5 or 10 percent level.
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D N S A
by cities in which the coverage of living wage laws is considerably broad, namely, cities that impose living wages on employers receiving busines assistance from the city. This leads to two points that should influence our reading of some past research on living wages and shape our future research. First, existing analyses of the likely effects of living wage laws based on narrow coverage and ignoring business assistance provisions may be quite misleading. Second, at least some living wage ordinances—specifically those with business assistance provisions—may operate somewhat more like relatively broad minimum wage laws than like narrow living wage laws centered on city contractors and city employees. While this suggests that conclusions from the minimum wage literature may be somewhat informative about the effects of living wages laws, living wage laws are nonetheless sufficiently different—aside from their much higher mandated wage floors—that independent evaluation of their success in helping low-skill workers or poor families is warranted. Finally, we ask whether there are disemployment effects that offset some of the positive wage effects of some types of living wage laws. While the point estimates are consistent with tradeoffs between wages and employment, the statistical evidence of disemployment effects is relatively weak. However, given that the largest estimated disemployment effects tend to correspond with the same cases in which we find the largest positive wage effects, we regard it as more likely than not that living wages reduce employment of those with low skills. Living wages have only been in existence for a short time, however, and as yet in a limited number of cities. While our difference-in-differences research design identifies the effects of living wages from differences in changes in wages or employment between cities passing and not passing living wage laws, one could still argue that we are identifying the effects of living wages from relatively few episodes. More work will need to be done to evaluate whether the results we have found hold in the larger set of cities that seem likely to adopt living wages over time and whether they hold over the longer term in cities with living wages that continue to maintain or raise them. Aside from providing estimates of the impact of living wage laws that have been implemented to date in cities across the United States, the empirical evidence that we find regarding the positive effects of living wage laws on the wages of low-wage workers indicates that there is a potentially fruitful research agenda on the effects of these laws that can be pursued exploiting cross-city variation in household-level datasets, although we also believe that other research designs and data-collection strategies should be
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exploited. In addition, the evidence of potentially offsetting disemployment effects implies that this research will have to grapple with the question of whether living wage laws, on balance, help low-wage workers and lowincome families. R Alunan, Susan, Lisel Blash, Brian Murphy, Michael Potepan, Hadley Roff, and Odilla Sidime-Brazier. 1999. “The Living Wage in San Francisco: Analysis of Economic Impact, Administrative, and Policy Issues.” Unpublished paper, San Francisco Urban Institute. Ashenfelter, Orley, and Robert S. Smith. 1979. “Compliance with the Minimum Wage Law.” Journal of Political Economy 87(April):333–50. Bertrand, Marianne, Esther Duflo, and Sendhil Mullainathan. 2001. “How Much Should We Trust Differences-in-Differences Estimates?” Unpublished paper, University of Chicago. Card, David, and Alan B. Krueger. 1994. “Minimum Wages and Employment: A Case Study of the Fast-Food Industry in New Jersey and Pennsylvania.” American Economic Review 84(September): 772–93. Employment Policies Institute. 1998. “The Baltimore Study: Omissions, Fabrications, and Flaws.” Unpublished paper, Employment Policies Institute, Washington. Fuchs, Victor R., Alan B. Krueger, and James M. Poterba. 1998. “Economists’ Views About Parameters, Values, and Policies: Survey Results in Labor and Public Economics.” Journal of Economic Literature 36(September):1387– 425. Greene, William H. 1997. Econometric Analysis, 3d ed. Upper Saddle River, NJ: Prentice-Hall. Hamermesh, Daniel S. 1993. Labor Demand. Princeton, NJ: Princeton University Press. Heckman, James. 1979. “Sample Selection Bias as a Specification Error.” Econometrica 47(January): 153–61. Meyer, Bruce D., and Dan T. Rosenbaum. 2001. “Welfare, the Earned Income Tax Credit, and the Labor Supply of Single Mothers.” Quality Journal of Economics 116(August):1063–114. Neumark, David, and William Wascher. 2001. “Using the EITC to Help Poor Families: New Evidence and a Comparison with the Minimum Wage.” National Tax Journal 54(June):281–318. ——— and ———. 2000. “Minimum Wages and Employment: A Case Study of the Fast-Food Industry in New Jersey and Pennsylvania: Comment.” American Economic Review 90(December):1362–96. ———, Mark Schweitzer, and William Wascher. Forthcoming. “Minimum Wage Effects Throughout the Wage Distribution.” Journal of Human Resources. ———, ———, and ———. 1998. “The Effects of Minimum Wages on the Distribution of Family Incomes: A Non-Parametric Analysis.” Working Paper No. 6536, National Bureau of Economic Research, Cambridge, MA. Niedt, Christopher, Greg Ruiters, Dana Wise, and Erica Schoenberger. 1999. “The Effects of the Living Wage in Baltimore.” Working Paper No. 119, Economic Policy Institute, Washington. Pollin, Robert, and Mark Brenner. 2000. “Economic Analysis of Santa Monica Living Wage Proposal.” Unpublished paper, Political Economy Research Institute, University of Massachusetts, Amherst, MA. ——— and Stephanie Luce. 1998. The Living Wage: Building a Fair Economy. New York: The New Press. Reich, Michael, Peter Hall, and Fiona Hsu. 1999. “Living Wages and the San Francisco Economy: The Benefits and the Costs.” Unpublished paper, Center on Pay and Inequality, University of California, Berkeley, CA. Reynolds, David. 2000. “Impact of Detroit’s Living Wage Law on Non-Profit Organizations.” Unpublished paper, Center for Urban Studies and Labor Studies Center, Wayne State University, Detroit, MI. ———. 1999. “The Impact of the Detroit Living Wage Ordinance.” Unpublished paper, Center for Urban Studies and Labor Studies Center, Wayne State University, Detroit, MI.
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Sander, Richard, and Sean Lokey. 1998. “The Los Angeles Living Wage: The First Eighteen Months.” Unpublished paper, UCLA and the Fair Housing Institute. Tolley, George, Peter Bernstein, and Michael D. Lesage. 1999. “Economic Analysis of a Living Wage Ordinance.” Unpublished paper, Employment Policies Institute, Washington. Williams, Regina. 1998. “Analysis of a Living Wage Policy.” Unpublished paper, City Manager’s Published Report, San Jose, CA.
