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.
531
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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.
Detecting Effects of Living Wage Laws
/ 533
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.
534 /
TABLE 1
I  L W La
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%)
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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%)
/ 535
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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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
Detecting Effects of Living Wage Laws
/ 537
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
538 /
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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).
Detecting Effects of Living Wage Laws
/ 539
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.
Detecting Effects of Living Wage Laws
/ 541
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.
542 /
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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.
Detecting Effects of Living Wage Laws
/ 543
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
544 /
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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 La
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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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.
Detecting Effects of Living Wage Laws
/ 547
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)].
Detecting Effects of Living Wage Laws
/ 549
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
550 /
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
/ 551
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.
552 /
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
/ 553
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 Da
Detecting Effects of Living Wage Laws
/ 555
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.
556 /
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.
Detecting Effects of Living Wage Laws
/ 557
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
558 /
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 La
Detecting Effects of Living Wage Laws
/ 559
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.
560 /
I W Da
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 
Detecting Effects of Living Wage Laws
/ 561
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.
562 /
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
Detecting Effects of Living Wage Laws
/ 563
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
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