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Forschungsinstitut
zur Zukunft der Arbeit
Institute for the Study
of Labor
On the Robustness of Minimum Wage Effects:
Geographically-Disparate Trends and
Job Growth Equations
IZA DP No. 8420
August 2014
John T. Addison
McKinley L. Blackburn
Chad D. Cotti
Geographically-Disparate Trends and
Job Growth Equations

John T. Addison
University of South Carolina,
Durham University and IZA
McKinley L. Blackburn
University of South Carolina
Chad D. Cotti
University of Wisconsin-Oshkosh
Discussion Paper No. 8420
August 2014
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IZA Discussion Paper No. 8420
August 2014
ABSTRACT
Geographically-Disparate Trends and Job Growth Equations

Just as the standard two-way fixed effects model for estimating
the impact of minimum
wages on employment has been sharply criticized for its neglect
of spatial heterogeneity so,
too, have the latest models been attacked for their uncritical use
of state- or county-specific
linear trends (and other spatial counterfactuals). Further
attenuation of the effects of policy is
also alleged to obtain in such circumstances where the true
effect of minimum wages is upon
employment growth rather than levels. This paper investigates
whether such considerations
call into question our earlier findings of statistically
insignificant employment effects for an
archetypal low-wage sector. We report that a continued focus on
employment levels is
indicated and that while experimentation with nonlinear trends
may be productive their use is
unlikely to dislodge the finding of considerably reduced
negative employment effects.
JEL Classification: J23, J38
Keywords: minimum wages, employment, employment change,
spatial controls
Corresponding author:
John T. Addison
Darla Moore School of Business
University of South Carolina
1014 Greene Street
Columbia, SC 29208
USA

E-mail: [email protected]
mailto:[email protected]
3
I. Introduction
In the present paper we seek to establish the extent to which our
findings in Addison, Blackburn, and
Cotti (2012) survive certain criticisms that have been made of
attempts to control for spatial heterogeneity
in minimum wage research in an important new review of the
literature by Neumark, Salas, and Wascher
(2013). In the process, and as a secondary exercise, we also
address a potentially more radical critique
having a basis in the notion that minimum wage effects are
more easily detected in employment growth
than in employment levels, such that conventional controls for
spatial heterogeneity may attenuate
estimates of how the minimum wage affects the level of
employment (Meer and West, 2013). The wider
backdrop to the present analysis is a recent meta-analysis of 27
modern minimum wage studies by
Wolfson and Belman (2014), controlling for many aspects of the
studies, that concludes that minimum

wages have no economically nor statistically meaningful
disemployment effects.1
Using a large sample of county-level employment data,
Addison, Blackburn, and Cotti (2012)
estimated the effect of minimum wages on employment in the
restaurant-and-bar sector. In addition to
time and county fixed effects, our model included a county-
specific effect allowed to follow a linear trend
over time (along with county-level controls) in a framework that
allowed us to assess the consistency of
the estimates with a competitive-model explanation of
employment and earnings determination. In
general, we concluded that minimum wages did not reduce
employment in a sector that contains the
highest percentage of workers at or below the relevant minimum
wage in the United States and in which a
little over 40 percent of workers worked for the minimum wage
plus two dollars or less. That said, our
estimates could be considered largely consistent with a
competitive model in which the elasticity of
demand for labor is very small. Of course in a debate on
minimum wages in which the respective sides do
not take prisoners, “largely consistent” is unlikely to win one
supporters from either side of the divide.

1 See also an earlier meta-analysis by Doucouliagos and Stanley
(2009) that, having taken publication bias
into account, suggests a not dissimilar conclusion in pointing to
an elasticity of -0.01.
4
However, our purpose here is to determine what we can learn
from recent criticisms, much of which we
regard as constructive and productive of research progress.
II. Two Basic Approaches, Then and Now
As is well known, research on minimum wages has gone through
several stages. But we will begin with
the new minimum wage research of the early 1990s (For a
thorough review of the earlier literature, see
Neumark and Wascher, 2007, 2008.) This research focused on
state data because of the advantages of
using simultaneous panels rather than an aggregate time series.
One approach exploited geographical
variation in the setting of minimum wages in an industry case
study approach, whereas the second used a

standard state- panel analysis in which state effects were held
constant. Both approaches sought valid
counterfactual control groups for what would have transpired
absent increases in the minimum wage, and
each reported generally divergent findings. The case studies
pointed to a lack of job loss – even gains –
and the two-way state panel approach suggested the opposite for
long panels of data (with minimum wage
elasticities in the range -0.1 to -0.3). Case studies of a
particular change in the minimum wage in a
particular industry typically used only a short time horizon
(raising obvious concerns about missing lags
in disemployment effects), and in covering individual cases
raised problems of inference and external
validity. For their part, the state panel studies did not allow for
heterogeneous trends in states that
increased minimum wages; for example, states experiencing
greater increases in minimum wages might
have systematically different labor market characteristics
unrelated to their minimum wage policies.
They also largely did not recognize the importance of within-
state error correlation in constructing
standard errors, thereby tending to overstate the precision of
their minimum-wage elasticities (and making

it more likely to find significant effects with limited data).
Enter the new new minimum wage research. This has taken two
forms. The first, and that focused
upon here, uses geographic-specific linear trend variables as a
means of controlling for heterogeneity in
the underlying long-term growth prospects of low-wage
employment (as well as other trends in teen
5
employment). Such geographic-specific linear trends are often
supplemented with time-varying effects for
more aggregated census regions or divisions, again allowing for
spatial heterogeneity in differential
employment patterns including region- or division-specific
economic shocks. The second innovation has
been to execute the case study approach using larger panels.
This approach uses a research design based
on cross-border pairs in a specification that (initially) included
county-pair/period interactions so as to
control for shocks common to both counties, thereby identifying
the effect of minimum wages from
differences in employment changes in paired counties on either

side of a state border.
These two approaches were (mostly) to yield results at odds
with the standard state panel
exercises, providing little or no evidence of job loss in sectors
or for groups most likely to be impacted by
minimum wage increases. Thus, Allegretto, Dube, and Reich
(2011), using Current Population Survey
(CPS) data on teens between 1990 and 2009 obtained minimum
wage effects consistent with the standard
state panel model before sweeping out the variation across
census divisions and allowing for state-specific
trends, only to report essentially zero employment (and indeed
hours) elasticities after their inclusion.2
Other interesting results from their study were (a) an absence of
anticipation effects with the inclusion of
the two spatial controls, and (b) a seeming lack of employment
effects over the business cycle.
Our own analysis used Quarterly Census of Employment and
Wages (QCEW) administrative data
for 1990-2005 for the restaurant-and-bar sector, and evinced a
very similar pattern of results: negative and
statistically significant coefficient estimates for the log
minimum wage in employment regressions
containing fixed county and time fixed effects that declined

sharply in absolute magnitude and became
statistically insignificant with the incorporation of county-
specific trends. As we noted (Addison,
Blackburn, and Cotti, 2012: 424), “…employment in the
restaurant-and-bar sector tends to exhibit a
downward trend in states that have increased their minimum
wages relative to states that have not, biasing
2 Similar results for employment are reported by Dube, Lester,
and Reich (2010) using the Quarterly
Census of Employment and Wages.
6
the fixed effect … estimates … towards finding a negative
employment effect of minimum wages.”3
Recognizing the potential case study bias of the restaurant
sector, we should note that we had earlier
obtained very similar minimum wage impacts in other low-wage
sectors in the retail sector at county level
(Addison, Blackburn, and Cotti, 2009).
A second approach to relaxing the parallel trend assumption of
the standard panel regression

model is presented in the study by Dube, Lester, and Reich
(2010). Using the QCEW, the authors
consider all adjacent counties straddling state borders for which
data are available between 1990 and
2006. Of these 504 counties, some 337 in 288 pairs recorded
some difference in minimum wages. The
impact of minimum wages is obtained from differences in
employment changes in these paired counties,
using unique dummy variables for each pair interacted with time
period. No evidence of employment
losses – up to four years after a minimum wage increase – is
reported for the two sectors (restaurants and
retail) examined in the study.4
III. The Critique of Using State- and County-Specific Linear
Trends
The most extensive critique of the extension/application of the
state panel approach is by Neumark, Salas,
and Wascher [NSW] (2013). A major part of their criticism has
to do with the choice of sample period,
raised by other findings from this new phase of research in
which significantly negative minimum wage
effects do not always vanish with the incorporation of state-
specific trends (see Neumark and Wascher,

2011). In particular, NSW criticize the analysis of Allegretto,
Dube, and Reich (2011) noting that there
were recessions at the start (1990-91) and end of their sample
period. If recessions do not have an
aggregate influence that is common across periods, the longer-
term estimated trend could be biased.
Specifically NSW (2013: 10) observe: “This in turn could lead
to misclassification of periods in which
3 We also reported a similar pattern when state-level trends
were substituted for county-level trends.
4 A similar finding for teenagers using the Quarterly Workforce
Indicators dataset is reported in Dube,
Lester, and Reich (2012).
7
teen employment was high or low relative to the predicted
values net of the minimum wage, and hence
influence the estimated minimum wage effect for reasons having
nothing to do with the longer-run trends
for which the specification is trying to control.” By way of
illustration, NSW present results for
California for a model with state-specific trends. The model is
estimated initially for the period 1994-

2007 thereby excluding the 1990-1991 recession and the Great
Recession. They plot the actual residuals
for this period and then the prediction errors for the two
recessionary intervals. It is found that (teenager)
employment was much higher than would have been predicted
by the model for the first recession but
considerably smaller for the second. When the recessionary
intervals are included both separately and
jointly the estimates of state-specific trends over the non-
recessionary period are strongly influenced by
their inclusion.
Given this potential for bias, NSW recommend the use of
higher-order trends in panel data
models. Alternatively, they also suggest the exclusion of sub-
periods of steep recessions in estimating
state-level trends while retaining the whole sample to estimate
minimum wage effects, or the use of a
Hodrick-Prescott filter to detrend the data. They then follow
their own advice in estimating a model of
teen employment, 1990-2011(Q2), using CPS data, first with a
simple state-specific linear trend and then
with a variety of higher-order trends and alternative detrending
methods. Apart from the linear trend

specifications, they report near universally negative and
significant effects of minimum wages on teen
employment.
As a practical matter, NSW spend more time critiquing the
border-county approach. Since we,
too, have expressed reservations over this estimation strategy
(see in particular Addison, Blackburn, and
Cotti, 2009) this is not the place to dwell on this methodology
other than in the related context of NSW’s
criticism of the use of census division-time period interactions
in Allegretto, Dube, and Reich (2011). The
justification for this control is again one of spatial
heterogeneity: employment rates for low-wage groups
vary by census division and may do so differentially over time.
Accordingly, the inclusion of division-
specific time effects eliminates between-division variation,
including division-specific economic shocks,
8
and along with state (linear) trends offers a more complete
control for spatial heterogeneity in differential
employment patterns. Saturation concerns, inter al., led NSW
to recommend the use of a synthetic

control approach to the estimation of treatment effects.
Interestingly, the synthetic control estimator
methodology suggested by Abadie, Diamond, and Hainmueller
(2010) has come to be regarded by all
analysts as an important complement to approaches seeking to
avoid confounding effects of
heterogeneous patterns in low-wage employment that are
coupled with the selectivity of states that have
introduced wage minima. At issue are the results of
incorporating synthetic controls for minimum wage
effects and the overlap between synthetic and local controls
(see, in addition to NSW, Allegretto, Dube,
Reich, and Zipperer, 2013; Dube and Zipperer, 2013; Sabia,
Burkhauser, and Hansen, 2012).
This brings us to the second major criticism of the use of state-
specific trends, linear or otherwise.
In a recent paper, Meer and West (2013) have argued that it is
inherently more likely for the effects of
minimum wage hikes to be reflected in employment dynamics
than in employment levels. They also
argue that the inclusion of state-specific time trends in these
circumstances as a control will attenuate
estimates of the effect of minimum wages on employment
levels. The theoretical reasoning is obtained

from a Diamond-type worker search and matching framework in
which transitions to a new employment
steady state may be slow.5 The practical reasons are two-fold.
First, staggered minimum wage increases
may mean that an increase in the counterfactual’s minimum
wage may quickly erode the gap opened up
by a particular wage hike. This might suggest that there is no
consistent control group in the long run. In
any event, in such staggered circumstances, there is a limited
time interval in which to identify the impact
of minimum wages on employment levels, which problem will
be compounded if minimum wages
initially operate on flows and hence do not affect employment
in a discrete manner. Second of all, and
more important, if the true effect of policy is to change the
slope for an outcome variable rather than its
5 Interestingly, the Meer-West model rests on a similar search-
theoretic reasoning to that employed by
protagonists of the argument that minimum wages will not
adversely impact employment because of
improved matching in the labor market, although they
themselves accept that negative effects will win out
because of a differentially reduced rate of job growth.

9
level then the mechanics of the state-specific time trend
approach can introduce biases. Specifically, any
confounding pre-treatment variation (e.g. any pre-treatment
deviation in employment growth correlated
with the treatment) that appropriately calls for the inclusion of a
state-specific time trend will attenuate
the treatment effect where the actual treatment effect acts upon
the trend itself. Meer and West use both a
stylized model and a Monte Carlo simulation – in both of which
scenarios the minimum wage is related to
the job growth rate but where there is no discrete change in the
level of employment – to illustrate the
attenuation problem.
Meer and West implement a state panel difference-in-
differences specification in which variables
reflecting employment dynamics – the job growth rate, and (its
components) the logs of job creation and
destruction – as well as employment levels themselves are
regressed on the log of state employment, the
share of the state population aged 15 to 59 years, and the log of
annual real gross state product per capita

in specifications controlling for state fixed effects, region-
specific time effects, and state-specific linear
trends. Three data sets are used in the inquiry – Business
Dynamics Statistics, the QCEW, and the
Quarterly Workforce Indicators – together covering the period
1975-2012. Across all three datasets, it is
reported that job growth is strongly reduced by increases in the
minimum wage – the main stimulus being
reduced job creation rather than destruction. On the other hand,
employment levels appear unrelated to
minimum wages in the quarterly data across all specifications,
and for annual data any statistically
significant negative policy coefficient does not survive the
incorporation of state-specific time trends –
even if differential employment growth rates ultimately (after
five years) translate into a large decrease in
overall employment. This pattern of results is consistent with
Meer and West’s expectations that
geographic-specific trends in employment-level regressions can
mask the effects of minimum-wage
changes.

10
IV. Response
In Addison, Blackburn, and Cotti [ABC] (2012) we estimated
employment and earnings equations for the
restaurant-and-bar sector using the QCEW for the period 1990-
2005. Our sample comprised a balanced
panel of 1,825 counties, providing some 116,800 quarterly
observations. Our basic empirical model
regressed the log of employment (and earnings) on the log of
the minimum wages, and a vector of supply
and demand factors (viz. population, total employment, total
average weekly earnings, the unemployment
rate and the enrolment rate), while controlling for fixed county
and fixed time effects. With these data, the
standard panel regressions provided statistically significant
positive minimum wage coefficients in the
earnings equation and statistically significant negative
minimum wage coefficients in the employment
equation. Familiarly, with the addition of county-specific trends
the significance of the earnings result
was unaffected but the coefficient for the minimum wage
though still negative was now very small and

statistically insignificant.
(Table 1 near here)
Although we considered potential shifts in the regression
model’s employment trend more
directly – by incorporating a new variable that allowed the trend
to shift when a county’s minimum wage
was above the federal minimum wage – we did not consider at
that time any other modifications,
including those suggested by NSW. In response, Table 1 now
re-estimates the ABC employment equation
implementing the first procedure suggested by NSW, namely to
allow the state-specific (here county-
specific) trends to be of a higher order than linear. Specifically,
second-, third-, fourth-, and fifth-order
polynomials are considered in Table 1, preceded by
specifications that first exclude county-specific trends
and then include them in a linear form.6 The use of higher-order
trends in two instances serves to render
the small estimated minimum wage effect statistically
significant. Interestingly, the coefficient estimates
for the other regressors are little changed by polynomial
detrending with the exception of findings for the

6 These latter results differ very slightly from those reported in
ABC, as we now exclude the enrolment
rate as a control (whose inclusion has been criticized as it may
itself be a function of the minimum wage).
11
unemployment rate variable in the last two columns of the table
(the signs of which are now perverse).
Overall, however, the results of this first exercise are decidedly
mixed and the suggested minimum wage
elasticities quite modest.
(Table 2 near here)
Table 2 takes up NSW’s other suggestions. The first column of
the table provides summary
results for the minimum wage argument when the county-
specific trend is estimated using only the data
for an interval that nets out the recession years at the beginning
of the sample period, and then uses these
trend estimates to detrend the data for the full sample period.
Use of this revised single trend estimate is
inconsequential in our case: the coefficient estimate changes
from negative and insignificant to positive
and insignificant. The next two columns of the table show

results for alternative detrending of the data.
Calculating the trend in each variable as a linear spline between
business cycle peaks (as in NSW, from
1990Q3 to 2001Q1) also yields a small positive and statistically
insignificant minimum wage coefficient.
Passing each data series by county through a Hodrick-Prescott
filter does yield a marginally significant
negative coefficient estimate for the minimum wage regressor,
but the estimated effect remains small (an
elasticity of -0.04).
(Table 3 near here)
In the above exercises we use the same interval (1990-2005) as
in ABC so as to determine the
sensitivity of the (minimum wage) results reported there to
alternative representations of county-specific
trends suggested by NSW. Next, we extend the QCEW sample
period as far as we can – namely up to
2012 – recalling that the period examined by NSW is very
similar (1990-2011Q2) albeit using a different
sample and dataset (teens from the CPS). Table 3 replicates the
procedures earlier employed in Tables 1
and 2. The sample size increases to 146,749 observations,
though with a reduced balanced panel of 1,595

counties. What difference does allowing for a longer sample
period make? Perhaps the first observation
to be made is that running the standard two-way county panel
model with just fixed effects for county and
12
time now provide no evidence of minimum wages impacting
employment, whereas a small negative but
marginally statistically significant coefficient estimate is
obtained using a simple linear trend. Second, use
of higher-order county-specific trends yields just one
marginally significant minimum wage elasticity. All
such coefficients are now less negative than for the linear trend
and vis-à-vis their counterparts in Table 1.
It is worth noting that this failure to support minimum-wage
effects is not due to an increased imprecision
of the estimates induced by the additional trend controls, as the
standard errors are actually smaller with
the higher-order trend polynomials. Third, turning to the lower
panel of the table, we see that neither
method that uses subperiods of the 1990-2012 period to estimate
the county-specific linear trend yields
statistically significant results. Finally, use of the Hodrick-

Prescott filter does again lead to a small but
marginally significant coefficient for the minimum wage,
although on this occasion it is to all intents and
purposes identical to that for the simple county linear-trend
specification.
We next consider the second criticism of the now common
practice of including geographic-
specific trends, namely that their inclusion in the model serves
to attenuate the measured effect of the
minimum wage on employment by virtue of the true effect of
policy being upon the rate of job growth.
This seems to be essentially an argument that minimum wage
effects may have lagged responses – Meer
and West’s (2013) findings support their intuition that this is
because minimum wages largely serve to
lower the rate of job creation in the following time periods. A
similar motivation would seem to lie
behind Sabia’s (2009: 88) argument that state-specific trends in
an employment model may “[reduce]
potentially important identifying variation.” We can see two
reasons why an empirical researcher might
consider omitting a statistically-significant set of independent
variables (in this case, geographic-specific
trends) from a model estimating minimum-wage effects. One is

that a significant collinearity problem is
induced, but at least in our results this does not seem to be a
concern – as consistent estimates of standard
errors for the minimum-wage elasticities are generally not
increased by the inclusion of county-specific
trends. The other concern is that minimum wage changes cause
the other independent variables to
change, so that controlling for the effects of those variables
masks the “total effect” of minimum wages.
13
This is Meer and West’s argument: minimum wages may be
causing a fall in the trend in employment
growth in areas raising the minimum wage, so that controlling
for these underlying trends is
inappropriate. While worth considering, we do not see this as a
relevant argument in the current analysis
– as we report in ABC, the downward trends in employment in
states raising their minimum wages seem
to be actually lessened after minimum-wage increases, rather
than become more severely negative as
Meer and West’s argument would imply.

(Table 4 near here)
As noted earlier, Meer and West do find a significantly negative
minimum wage impact on job
growth in models that allow for state-specific trends in the job-
growth rate. Our own sense is that the
particular specification that Meer and West estimate is
somewhat hard to defend, as it implies a single
minimum-wage increase will have a permanent effect on job
growth. Nonetheless, these kinds of
specifications where job-growth rates are a function of levels of
variables are not uncommon, and likely
able to pick up lagged effects in a parsimonious way relative to
the less restrictive dynamic specifications
one sees in the autoregression literature.7 So, as an attempt to
explore the importance of Meer and West’s
concerns in our data, we estimated similar models with our
1990-2012 data on restaurants and bars from
the QCEW. We preface our findings in Table 4 by recalling that
Meer and West did use the QCEW in
some of their regressions, but their aggregation remained at the
state (rather than the county) level, while
they also chose to look at the broader-based accommodation and
food sector rather than the more low-
wage restaurant-and-bar sub-sector. Further, we will also use

the more standard growth rate measure –
the change in log employment – than the alternative job growth
rate used by Meer and West, although our
results are robust to using the latter measure. The first two
columns of Table 4 present results in which
employment growth is regressed on the levels of variables (also
incorporating county-specific trends). In
7 Simple lag structures have been incorporated in several
studies in the recent minimum-wage literature
(e.g. via inclusion of a simple lagged minimum wage as an
additional control), although our sense is that
these embellishments are generally inconsequential in terms of
conclusions of the studies.
14
contrast with Meer and West, however, our estimate of the job-
growth regression provides tiny and
statistically insignificant minimum wage coefficients.
Our own preference for addressing the concerns raised by Meer
and West is to consider models
that explain long-run changes in employment as a function of
similar long-run changes in the independent
variables. For example, consider a state that raises its minimum

wage one time in the panel. An empirical
model based on 4-year changes would then have that minimum-
wage change showing up as potential
employment change factor for each of the quarters in the
corresponding 4-year period. With lagged
effects we would expect at least some of those quarters in the
following 4 years to have reduced
employment, leading to a nonzero coefficient on the minimum-
wage change variable. The more typical
short-run quarterly differenced models would, on the other
hand, miss these lagged impacts. As noted in
ABC, one advantage of the differenced models is that they also
difference out any static geographic-
specific effects, and the inclusion of geographic dummies is
equivalent to controlling for geographic-
specific linear trends.
In ABC, we estimated such differenced models, but only
considered one-quarter and four-quarter
differences (in the latter case requiring any lagged effects to
show up within a year). These estimations
were similar to our non-differenced results in finding little
supporting evidence of minimum-wage
employment effects. Here, we consider the robustness of this
finding to expanding the sample period to

2012, and considering even longer differences to allow for more
significant lagged effects. As the longest
difference we consider is 6 years, we maintain a consistent
sample across these additional specifications
by starting our estimation with observations beginning in 1996
rather than 1990. The second column of
Table 4 reestimates the Meer-West growth-rate specification
with this restricted time period, leading to a
similar conclusion as with the full sample period. The next four
columns report estimates from fully-
differenced equations with differences measured over 1, 4, 16,
and 24 quarters. In all of these cases, the
estimated minimum-wage elasticities are small and statistically
insignificant. In our focus of study, then,
lagged minimum-wage effects do not seem to be of a concern.
15
Dube (2013) has also directly questioned Meer and West’s
employment growth equation. That is
to say, he regresses employment change on levels of variables
for two of the three datasets used by Meer
and West (viz. the BDS and the QCEW). He broadly replicates

the Meer/West result on aggregate, but
claims that disaggregation – using the QCEW – only supports
the employment growth result in
manufacturing not in retail or accommodation and food
services, although as a practical matter he
annualizes the quarterly data used by Meer and West while
using a more parsimonious specification that
excludes state-specific time trends and business cycle controls.
That said, Dube’s final specification using
a border matching approach including county pair specific year
effects fails to reveal any significant
association between net employment growth and the log of the
minimum wage.
V. Conclusions
The debate on the impact of minimum wages is ongoing.
Although a new consensus has not emerged, a
glance at the conclusions of two main evaluations of the debate
(viz. NSW and Allegretto, Dube, Reich,
and Zipperer, 2013) and more particularly what they see as the
components of a viable research agenda
point in not necessarily dissimilar directions. We refer to the
search for specifications that provide the
most reliable counterfactuals and the potential benefits of a

synthetic control approach in this regard.
Our focus has been to take seriously a number of criticisms that
have been leveled against the use
of state/county-specific trends since in the past criticism has
proven constructive. A pertinent example is
the common-sense suggestion that an environment of deep
recession might well produce clearer evidence
of disemployment that has been reported in much of the modern
minimum wage literature. In Addison,
Blackburn, and Cotti (2013) we focused on two high-risk groups
over the years 2005-2010 and while the
evidence for a general disemployment effect was not uniform
our estimates did suggest that the presence
of negative minimum wage effects in states hardest hit by the
recession. In the present treatment, we have
taken seriously two sets of other criticisms of the state-specific
trends approach while continuing to focus
16
on a high-risk group – here employees in the restaurant-and-bar
sector – but without being tied to looking
at region-specific time effects in conjunction with state-specific
trends. Our results, however, do not serve

to dislodge the persistent finding of considerably low (and
possibly zero) minimum-wage elasticities in
the restaurant-and-bar sector. In one sense however that
particular battle may have already been won, as
David Neumark and his colleagues now admit that “similar
analyses of restaurant employment in the
QCEW are a bit more mixed” (NSW, 2013: 46). We think it
will be difficult to overturn this finding, but
this conclusion should not be used to argue that minimum wage
effects are ‘always and everywhere’ of
this magnitude or for that matter as offering support of the
conclusion that there are “no detectable
employment losses from the kind of minimum wage increases
we have seen in the United States” (Dube,
Lester, and Reich, 2010: 962).
Also our findings might again stimulate research into concerns
having to do with the effects of
minimum wages on hours (reduction), non-wage benefits, and
training as well as along some other
margins of adjustment as suggested by Hirsch, Kaufman, and
Zelenka (2011). And although we did not
on this occasion find any great support for the argument that
state-specific time trends serve to attenuate

the measured effects on employment levels, the notion that
minimum wages might have an effect on
employment dynamics (including firm births) merits further
exploration, building on the work of Portugal
and Cardoso (2006).
17
References
Abadie, Alberto, Alexis Diamond, and Jens Hainmueller. 2010.
“Synthetic Control Methods for
Comparative Case Studies: Estimating the Effect of California’s
Tobacco Control Program.” Journal of
the American Statistical Association (490): 493-505.
Addison, John T., McKinley L. Blackburn, and Chad D. Cotti.
2009. “Do Minimum Wages Raise
Employment? Evidence from the U.S. Retail-Trade Sector.”
Labour Economics 16(4): 397-408.

2012.” The Effect of Minimum Wages on
Labour Market Outcomes: County-Level Estimates from the
Restaurant-and-Bar Sector.” British Journal
of Industrial Relations 50(3): 412-435.
2013. “Minimum Wage Increases in a
Recessionary Environment.” Labour Economics 23: 30-39.
Allegretto, Sylvia A., Arindrajit Dube, and Michael Reich.
2011. “Do Minimum Wages Really Reduce
Teen Employment? Accounting for Heterogeneity and
Selectivity in State Panel Data.” Industrial
Relations 50(2): 205-240.
Allegretto, Sylvia A., Arindrajit Dube, Michael Reich, and Ben
Zipperer. 2013. “Credible Research
Designs for Minimum Wage Studies.” IZA Discussion Paper
No. 7638. Bonn: Institute for the Study of
Labor, September.
Dourcouliagos, Hristos and Stanley, T.D. 2009. “Publication
Selection Bias in Minimum Wage Research?
A Meta-Regression Analysis.” British Journal of Industrial
Relations 47(2): 406-428.
Dube, Arindrajit. 2013. “Minimum Wages and Aggregate Job
Growth: Causal Effect or Statistical
Artifact? IZA Discussion Paper No. 7674. Bonn: Institute for
the Study of Labor, October
Dube, Arindrajit, T. William Lester, and Michael Reich. 2010.
“Minimum Wage Effects Across State
Borders: Estimates Using Contiguous Counties.” Review of
Economics and Statistics 92(4): 945-964.

“Minimum Wage Shocks, Employment
Flows, and Labor Market Frictions.” Mimeographed. Berkeley:
Institute for Research on Labor and
Employment.
Dube, Arindrajit and Ben Zipperer. 2103. “Pooled Synthetic
Control Estimates for Recurring Treatments:
An Application to Minimum Wage Case Studies.” Unpublished
Paper, University of Massachusetts
Amherst.
Hirsch, Barry T., Bruce E. Kaufman, and Tetyana Zelenska.
2011. “Minimum Wage Channels of
Adjustment.” IZA Discussion Paper No. 6232. Bonn: Institute
for the Study of Labor, November.
Meer, Jonathan and Jeremy West. 2013. “Effects of the
Minimum Wage on Employment Dynamics.”
NBER Working Paper 19262. Cambridge, MA: National Bureau
of Economic Research.
Neumark, David and William Wascher. 2007. “Minimum Wages
and Employment.” Foundations in
Microeconomics 3(1): 1-182.
Neumark, David and William Wascher. 2008. Minimum Wages.
Cambridge, MA: Cambridge University
Press.
18

Neumark, David and William Wascher. 2011. “Does a Higher
Minimum Wage Enhance the Effectiveness
of the Earned Income Tax Credit?” Industrial and Labor
Relations Review 64(4): 712-746.
Neumark, David, J.M. Ian Salas, and William Wascher. 2013.
“Revisiting the Minimum Wage and
Employment Debate: Throwing out the Baby with the
Bathwater?” Unpublished Paper, University of
California, Irvine, May (forthcoming in Industrial and Labor
Relations Review).
Portugal, Pedro, and Ana Rute Cardoso. 2006. “Disentangling
the Minimum Wage Puzzle: An Analysis
of Worker Accessions and Separations.” Journal of the
European Economic Association 4(5): 988-1013.
Sabia, Joseph J. 2009. “The Effects of Minimum Wage
Increases on Retail Employment and Hours: New
Evidence from Monthly CPS Data.” Journal of Labor Research
30(1): 75-97.
Sabia, Joseph J., Richard V. Burkhauser, and Benjamin Hansen.
2012. “Are the Effects of Minimunm
Wage Increases Always Small? New Evidence from New York
State.” Industrial and Labor Relations
Review 65(2): 350-376.
Wolfson, Paul and Dale Belman. 2014. What Does the Minimum
Wage Do? Kalamazoo, MI: W.E.
Upjohn Institute for Employment Research.

19
Table 1
Employment Equations for the Restaurant-and-Bar Sector,
1990-2005, Polynomial
Detrending
Order of Polynomial for County-Specific Trends
No Trends 1st 2nd 3rd 4th 5th
Log(Minimum
Wage)
-0.101**
(0.039)
-0.006
(0.033)
-0.051***
(0.014)
-0.041
(0.027)
-0.062*
(0.033)

-0.046
(0.033)
Log(Average
Wage)
-0.139***
(0.048)
-0.129***
(0.036)
-0.116***
(0.032)
-0.097**
(0.038)
-0.089**
(0.040)
-0.079**
(0.043)
Log(Total
Employment)
0.596***
(0.053)
0.770***
(0.061)
0.776***
(0.081)

0.824***
(0.097)
0.849***
(0.109)
0.869***
(0.120)
Unemployment
Rate
-0.001
(0.002)
0.001
(0.002)
0.001
(0.001)
0.002
(0.001)
0.003*
(0.002)
0.004**
(0.002)
Log(Population) 0.327***
(0.101)
0.289***
(0.066)

0.247*
(0.136)
0.241*
(0.133)
0.226*
(0.125)
0.326**
(0.150)
Notes: The dependent variable is the log of employment. The
standard errors in parentheses are
corrected to allow intra-cluster correlation in errors for all
observations within a state. All
regressions included fixed-effects for county and quarter.
Regressions are weighted by the
average population in the respective county. The sample size in
all regressions is 116,800, for a
balanced panel of 1,825 counties.
***,**,* denote statistical significance at the 0.01, 0.05 and
0.10 levels, respectively.
20
Table 2
Employment Equations for the Restaurant-and-Bar Sector,

1990-2005, Alternative
Detrending Methods
Post-1993 Trends Peak-to-Peak
Trends
H-P Filter Trends
Log(Minimum Wage) 0.001
(0.062)
0.027
(0.071)
-0.042*
(0.023)
Notes: See Notes to Table 1. All equations include the same
controls as in Table 1. Standard
errors are block bootstrapped by state using 500 replications.
Post-1993 Trends detrends all
observations based on county-specific trends estimated over the
1994-2005 period. Peak-to-
Peak Trends detrends all data based on county-specific trends
estimated over 1990-Q3 to 2001-
Q1. H-P Filter Trends are the filtered series from a county-
specific application of a Hodrick-
Prescott filter (smoothing parameter=1600) applied individually
to each data series.
21

Table 3
Employment Equations for the Restaurant-and-Bar Sector 1990-
2012, Various Detrending
Methods
Order of Polynomial
No
Trends
1st 2nd 3rd 4th 5th
Log(Minimum
Wage)
-0.000
(0.035)
-0.040*
(0.021)
-0.024
(0.018)
-0.035*
(0.019)
-0.023
(0.014)
-0.010
(0.014)
Post-1993
Trends

Peak-to-
Peak
Trends
H-P Filter
Trends
Log(Minimum
Wage)
-0.038
(0.028)
0.058
(0.072)
-0.041*
(0.021)
Notes: All specifications include the same controls (and
approaches to calculating standard
errors) as in Tables 1 and 2. Sample size is 146,740 in all
equations, for a balanced panel of
1,595 counties.
22

Table 4
Differenced Employment Equations for the Restaurant-and-Bar
Sector, 1990/1996-2012
Time Period 1990-
2012
1996-2012
Difference
Length
1
quarter
1
quarter
1 quarter 1 year 4 years 6 years
Log(Minimum
Wage)
-0.007
(0.009)
-0.004
(0.010)
-0.005
(0.010)
-0.010
(0.008)
-0.014
(0.017)

0.008
(0.025)
Specification of
MW and other
RHS vars.
Levels Levels Differenced Differenced Differenced Differenced
Notes: See Notes to Table 1. All specifications include the
same controls as in Table 1, along
with region/quarter fixed effects. The first two columns of
results are based on specifications
that also detrend the data at the county level. In the “levels”
equation, the dependent variable is
first-differenced but all right-hand-side variables are measured
in levels. In the differenced
equation, all variables are differenced over the same stated
period. Sample size is 145,145 in the
first column, and 108,460 in the other columns.
Are the Effects of Minimum Wage Increases Always Small?
A Re-Analysis of Sabia, Burkhauser, and Hansen

Saul D. Hoffman
Department of Economics
University of Delaware
May 23, 2014
Abstract: In a recent article, Sabia, Burkhauser, and Hansen
report very large negative
employment effects of the 2004-2006 increase in the NY state
minimum wage on young, less-
educated workers. I re-examine their estimates using data from
the full CPS, rather than the
smaller CPS-MORG files they use, and find no evidence of a
negative employment impact. In
this case, the full CPS, which is the source of U.S. official labor
market statistics, is certainly the
more appropriate and reliable data. Furthermore, when I repeat
their analysis using three
states and the District of Columbia that also had a substantial
increase in the state minimum
wage in the same time period, I find evidence of a small
positive employment effect. Together,
the two findings are consistent with other more recent research
that reports very weak or zero
disemployment effects of the minimum wage.
Key Words: Minimum Wage
JEL Codes: J08, J21, J38
In a recent important contribution to the minimum wage

literature, Sabia, Burkhauser,
and Hansen (2012) ask “Are the Effects of Minimum Wage
Increases Always Small?” Using
evidence from the 2004-2006 increase in the New York state
minimum wage from $5.15 to
$6.75, they answer emphatically “no.” They find that
employment for less-educated workers
under age 30 fell by 20%, which yields an employment
elasticity of approximately -0.7, far
larger than estimates found in most of the more recent empirical
minimum wage literature.
Indeed, they conclude that “these findings provide plausible
evidence that large state minimum
wage increases can have substantial adverse labor demand
effects for younger, less-
experienced, less-educated individuals that are well outside the
consensus range of –0.1 to –0.3
found in the literature” (p. 372). This result has been cited by
some conservative think tanks
and on-line commentators as important evidence against an
increase in the federal or state
minimum wages.1 This result also figures prominently in other
analyses of the redistributive
and anti-poverty impact of the minimum wage by the same

authors (Sabia and Burkhauser
2010).
Their analysis is based on employment data from the Current
Population Survey-Merged
Outgoing Rotation Group (CPS-MORG) files for 2004 and 2006.
They use a variety of difference
methods to compare employment changes in NY to the
corresponding changes in either
neighboring states or a synthetic control group. The analysis is
very capably executed, but it is
ultimately undermined by two factors. First, the data set they
use yields estimates of the
employment rate in NY and the control group states that differ
substantially from the
corresponding official rates derived from the full CPS sample.
The MORG files used by Sabia,
1 See, for example, Hotz-Eakin (2013) in the Huffington Post
and Employment Policies Institute (2012).
1
Burkhauser and Hansen (hereafter SBH) are a subset of the

regular CPS that includes the one-
quarter of the CPS panel that is rotating out of the sample after
either four or eight months in
the survey.2 The full CPS, not the one-quarter MORG
subsample, is the source of official BLS
tabulations of employment and unemployment and it is clearly
the preferred data source. SBH
used the MORG data because, unlike the regular CPS, the
MORG includes information on wage
rates for workers paid by the hour and weekly earnings for other
workers. This is essential
information for computing wage impacts of the minimum wage,
but not for estimating
employment effects. As shown below, the employment rate
effects computed from the full
CPS files for 2004 and 2006 yield a very different picture of the
impact of the minimum wage
increase in NY. While the MORG files are, in principle, an
appropriate data set to use, in
practice their representativeness may fail for relatively small
state-by-age group samples, such
as are used in their analysis.
Second, NY appears to be a somewhat idiosyncratic treatment
state. In natural

experiments like this one, it is always necessary to assume that
the treatment and control
groups are similar except for the treatment itself, here, the
minimum wage increase. If that
were true, then, by extension, states with minimum wage
increases similar to that in NY would
be expected to have relatively similar responses. But that is not
the case. Three other large
states (Illinois, Florida, and New Jersey) and the District of
Columbia had minimum wage
increases at the same time that were quite substantial—an
average increase of $1.03 or 18.7%.
The employment response to the minimum wage increase in
these states is substantially
2 CPS sample members are interviewed for four months
consecutively, leave the survey for eight months, and then
return for another four months. They are part of the ORG files
in both of their final months of interviewing.
2
different from that in NY. Indeed, the employment rate of the
same group analyzed by SBH

increased in these states relative to states that had no increase
in the minimum wage.
In this paper, I re-examine the NY minimum wage experiment
analyzed by SBH using
both the CPS-MORG and the full CPS data for 2004 and 2006.
I also apply the same methods to
examine the impact of the minimum wage increase in the other
states with a sizeable increase.
The next section of the paper briefly reviews the analysis and
findings of SBH and then focuses
on the NY experiment. The following section provides a
parallel analysis of the impact of
minimum wages in the other states that also had substantial
increases during the same time
period.
II. Employment Effects of the NY Minimum Wage Increase
Background. Between 2004 and 2006, the state minimum wage
in New York was
increased in two steps from $5.15 to $6.75, while the federal
minimum was unchanged at
$5.15. Three geographically-proximate states—New
Hampshire, Pennsylvania, and Ohio—had
minimum wage rates of $5.15 throughout the period and are

used by SBH as a control group.3
The use of geographically proximate areas with different
minimum wages was first famously
used in a natural experiment context by Card and Krueger
(1994) following the 1992 increase in
New Jersey’s minimum wage. Similar approaches have been
used subsequently in research by
Dube, Naidu, and Reich (2007), who compared restaurant
employment in San Francisco and
neighboring cities after a local increase in the minimum;
Hoffman and Trace (2009), who
compared Pennsylvania and New Jersey after a federal minimum
wage increase that affected
3 Four other neighboring states (Vermont, Massachusetts,
Connecticut, and New Jersey) either had an increase in
their state minimum or had a constant, but higher minimum.
3
only Pennsylvania; and Dube, Lester, and Reich (2010), who
compared restaurant employment
in adjacent counties that are across state boundaries and are
subject to different minimum

wages.
SBH use primarily difference-in-difference methods, with and
without control for
covariates. As the group potentially most adversely affected by
the minimum wage increase,
they focus on 16-29 year olds without a high school degree.
They also use a difference-in-
difference-in-difference model to compare employment changes
of the target group to the
employment changes for a putatively unaffected group across
the two sets of states. Finally, in
addition to the three neighboring states, SBH also compare NY
to a synthetic control group
using the methods of Abadie, Diamond, and Hainmueller
(2010).
Their analysis uses data from the CPS-MORG files, which are
the merged annual files for
the outgoing rotation groups of the regular CPS. Each month’s
ORG file contains one-quarter of
the full CPS sample who are rotating out of the sample after
four or eight months of interviews.
Thus, the annual MORG file contains three times the sample
size of any single month’s CPS and

one-quarter the sample size of the full annual CPS. Monthly
sample sizes for a sample that
includes just a few states and a restricted age and education
range can be relatively small. For
16-29 year olds with less than a high school degree, the CPS-
MORG annual file includes 989
persons in NY in 2004, 916 in 2006, and 1765 and 1499 for the
control group. Monthly sample
sizes average about 75-80 for NY and 125-150 for the control
group. Sample sizes for subgroups
by age bracket are obviously much smaller.
4
SBH use the MORG files because they first examine whether
the minimum wage
increase affected the distribution of wage rates. Only the
MORG file contains information on
wage rates. For this reason, the annual MORG files are the data
source used in the annual BLS
reports on the characteristics of minimum wage workers (BLS
2013) and are occasionally also
used in analyses of wage inequality (Card and DiNardo 2002).
While they are essential for that

purpose, they are not ideal for the analysis of employment rates,
because of their smaller
sample size. Indeed, for employment analyses, they have no
advantage whatsoever over the
full CPS sample.4 The full CPS sample is always the source for
official tabulations of labor
market outcomes, including employment, labor force
participation, and unemployment. In
many cases, the MORG files may be a suitable substitute for the
full CPS; they are, after all, a
random part of a nationally-representative sample. But with
smaller sample sizes, the
representativeness may not carry through.
Analysis. To re-examine the impact of the NY state increase in
the minimum wage, I
downloaded the MORG files for 2004 and 2006 from the NBER
website and the corresponding
monthly CPS files from the US Census site using Data Ferrett.
Table 1 summarizes the age, race,
and education distribution of the CPS and MORG samples. The
estimates shown utilize sample
weights and thus are population estimates. In terms of these
observable characteristics, the

CPS and MORG files are very similar. Age, race, and the
proportion male are virtually identical
and the education distributions differ only slightly. The only
mean that is statistically different
across the data sets at the 10% level or more is the proportion
with very low education in the
4 This point has been made previously by Addison, Blackburn,
and Cotti (2013), who recommend that researchers
use the MORG files only to examine wage effects and then use
the full CPS to examine employment effects.
5
control states, where the MORG files has a higher proportion.
In both data sets, the NY
samples have a much higher proportion of blacks from the
control state samples, a lower
proportion with 10 years of education and a higher proportion
with twelve years (but no
degree); these differences are statistically significant. The full
annual CPS files provide samples
for the NY and control group states that are about four times as
large as the MORG samples.

In my re-analysis, I focus on the comparison to the
geographically-proximate states
rather than the synthetic comparison group. The results of the
two analyses in SBH are virtually
identical.
In Table 2, I show the re-analysis of the NY v NH/PA/OH
natural experiment separately
by state, year, and data source. For each age group, I show the
MORG results from their Table
3 and my estimates from the full CPS. The huge adverse
employment effect reported by SBH is
easily seen. The employment rate for the less-educated younger
workers in NY plummeted
from .362 to .291 between 2004 and 2006, a 20% decline.
Employment in the control group
states was essentially unchanged, yielding a difference-in-
difference estimate of −0.076 that is
statistically significant at the 5% level. Since the wage
increased 31%, the employment
elasticity is a very sizeable −0.63. My estimates from the
MORG files are identical to theirs,
both for means and sample size, which confirms that their
analysis does not involve any
idiosyncratic coding or sampling whatsoever. There is no

question that the MORG files show a
very substantial adverse employment effect of the minimum
wage increase in NY on this group
of relatively young, less-educated workers.
6
The estimates from the full CPS, presented in the second row,
show a very different
picture, however. The 2004 employment rate for NY is a full 2.6
percentage points lower than
the MORG estimate, while the 2006 CPS estimate for NY is
about 1.6 percentage points higher.
For the control states, the 2004 employment rate from the full
CPS is very close to the MORG
estimate, but the 2006 rate is 1.7 percentage points lower than
in the MORG file. The net effect
of all these adjustments is a DID estimate of the impact of the
NY state minimum wage increase
of less than one percentage point (−0.008) that is statistically
insignificant, compared to the
statistically significant -0.076 estimate from the MORG data.
The two DID estimates are clearly

statistically different. The lower bound of the 95% confidence
interval for the DID estimate
from the full CPS is -0.035, which is less than half the point
estimate in SBH’s analysis.
A similar pattern is seen in the next two rows, which focus on
the subset of 16-19 year
olds. The employment rates from the MORG files yield a DID
estimate of 6.3 percentage points,
equivalent to an elasticity of −0.79, given the lower baseline
employment rate. Again, the main
factor is a very sharp decline in the employment rate in NY,
while the employment rate in the
control states is essentially unchanged. With the full CPS data,
the 2004 NY employment rate
for this subgroup is 2.7 percentage points lower and the 2006
rate is 1.1 percentage points
higher than in the MORG files. Thus, the estimated decrease in
the NY employment rate is 2.6
percentage points, less than half the decrease in the MORG
data. At the same time, the control
state employment rate change moves in the opposite direction,
from neutral in the MORG data
to a 2.1 percentage point decrease in the CPS data. None of the
four sets of mean differences

are large enough relative to their standard error to be
statistically significant, but the net result
is a DID estimate of less than half a percentage point, rather
than the 6.3 percentage points
7
computed by SBH. Again, the lower bound of the 95%
confidence interval for the DID estimate
from the CPS (−.033) is about half the MORG point estimate
presented by SBH.
The remaining rows of the table show the employment rates for
the other age
subgroups examined by SBH. The general pattern follows what
has been seen in rows (1)-(4).
For 20-24 year olds, SBH find a difference-in-difference
estimate of −12.4 percentage points,
primarily due to an enormous 10.7 percentage point drop in the
NY employment rate,
equivalent to a 19.9% decrease. With the CPS, the difference-
in-difference estimate is about
one-quarter as large (−3.7 percentage points) and is not
statistically significant. The underlying
NY employment rate decline in the CPS is half as large as in the

MORG and it is partly offset by a
two point decline in the control states, rather than the 3.5
percentage point increase in the
MORG data. The employment rates and sample sizes in the
MORG imply that the NY sample
contained 94 employed 20-24 year olds without a high school
degree in 2004 and 63 in 2006. If
the employed numbers had, instead, been 91 and 68—hardly
large changes—the MORG
employment rates would have matched those from the full CPS.
For 25-29 year olds without a high school degree, the MORG
difference-in-difference
estimate of the effect of the minimum wage on employment is
−5.3 percentage points. In the
CPS, the estimate is actually positive (0.011), but not close to
statistical significance. Again, the
very small sample size in the MORG, which ranges from 109 to
158, is potentially an issue.
Finally, in the last rows, which focuses on 20-29 year olds with
at least a high school degree—a
group plausibly largely unaffected by the minimum wage—the
two sets of estimates are very
similar. Note that this is the largest sample size in the MORG
by a very substantial margin.

8
The final column shows difference-in-difference estimates
adjusted via regression for
age, education, race, and gender.5 Again, I report the estimates
from SBH for the MORG file
and my corresponding estimates from the full CPS files. The
procedures I follow are similar to,
although probably not literally identical, to what SBH do.6 In
their estimates, the adjusted DID
effects are very similar to and sometimes slightly greater in
absolute value than the unadjusted
results. Thus, for example, the adjusted DID estimates are
−0.073 for the full sample, −0.072 for
teens, and −0.141 for 20-24 year olds. All of these effects are
statistically significant at the 95%
level. With the CPS data, adjustment for covariates makes the
impacts a bit larger in absolute
value, but still quantitatively small and not statistically
significant. For all young, less-educated
workers, the adjusted DID estimate is −0.018 with a standard
error of −0.0137. The largest

adjusted effect and largest t-statistic is for 20-24 year olds,
where the DID estimate is −0.054
and the t-statistic is 1.5.
Difference-in-difference-in-difference estimates are shown in
Table 3. Here, the
comparison is between across-state employment rate change
differences for an at-risk group
and one essentially unaffected by an increase in the minimum
wage across the two sets of
states. The DIDID allows for further control for otherwise
unmeasured factors that might differ
between the treatment and control states (Hoffman, 2014). As
the unaffected group, SBH use
persons age 20-29 with a high school degree, whose
employment rate changes were shown in
the bottom rows of Table 2. Their estimates are shown in their
Table 4 for models including
covariates or, alternatively, can be computed from the figures
presented in their Table 3
5 Full regression results are available on request.
6 They do not present the estimates or exact details of coding.
7 Treating the point estimate as if it were statistically
significant yields an elasticity of −0.11, which is at the low end
among previous studies that find negative employment effects.
9

without adjustment for covariates. The results are virtually
identical, so to keep the analysis
simple, I focus on the DIDID without covariates.
All of the figures in Table 3 were previously presented in Table
2. The first panel shows
the DID estimate (2006−2004) of −0.008 for the affected group
(age 16-29, not a high school
graduate) from the full CPS. The next panel shows the
corresponding estimate for the
unaffected group (−0.0005). The DIDID estimate from the CPS
is, therefore, −0.0075 with a
standard error about twice as large as that. The estimate from
SBH using the MORG is shown in
the bottom row: it is −0.086 with a t-statistic of 2.6. The
corresponding regression-adjusted
DIDID estimate from their Table 4 is −0.078 with a t-statistic of
1.70. I do not present the DIDID
estimates for the other subgroups shown in Table 2, but it is
obvious that they will be very
similar to the DID estimates in that table, since the control

group DID is itself very small,
implying that correction for other unmeasured effects is not
quantitatively important.
Interpretation. What should we make of the differing CPS and
MORG estimates? As I
have argued above, the CPS data is the source for official BLS
employment estimates. With the
CPS data, for example, any researcher can exactly replicate
national published BLS employment
estimates for teens or any other age group. This includes not
only the annual average (not
seasonally-adjusted) employment and unemployment rate, but
also the underlying monthly
rates and the corresponding number of persons employed and
unemployed. I have done that
10
with the 2004 and 2006 CPS samples for teens.8 All estimates
exactly match the BLS figures
available at http://data.bls.gov/pdq/querytool.jsp?survey=ln.
In contrast, estimates from the MORG do not replicate the
official figures, although at

the national level, the differences in estimates from the two data
sets are relatively small. The
official average teen employment rate in 2004 computed from
the CPS and reported by the
Bureau of Labor Statistics was 36.4%, while in the MORG file,
it is 35.7%, a difference of 0.7
percentage points (about 2%). In 2006, the difference is 0.3
percentage points. The 2004
difference is statistically significant at the 5% level, while the
2006 is not. In both cases, the
differences are quantitatively small.
At the state level, however, where sample sizes are much
smaller, the differences are
often much larger. Consider 2004 when, as noted above, the
difference in the average annual
employment rate for teens at the national level between the two
data sets was 0.7 percentage
points. I calculated the state-level teen employment rates with
both data sets and then
computed the difference. The average absolute value of the state
differences was 1.4
percentage points and the median difference was 1.5 percentage
points. In 15 states, the
difference was greater than two percentage points, with four

states having a difference greater
than three percentage points.
For the analysis sample used by SBH (age 16-29, not high
school graduate), the same
pattern holds. The national employment rates in 2004 are .388
in the CPS data and a virtually
identical .385 in the MORG data. But the average absolute value
of the difference at the state
8 I use this group rather than the sample used by SBH because
national published estimates are available for
comparison. The teen employment data is for 16-19 year olds.
11
level is 1.4 percentage points, and 15 states have a difference of
two percentage points or
more. Unfortunately for the SBH analysis, NY and PA are
conspicuous outliers of opposite signs:
for NY, the MORG employment rate, as seen in Table 2, is 2.6
percentage points higher and in
PA, it is 1.4 percentage points lower (result not shown
separately in Table 2). In OH and NH, the

estimated employment rates differ by just 0.2 percentage points
in the two data sets.
Figures 1 and 2 provide some further insight into the differing
NY employment rate
estimates. The employment rate in the CPS is a weighted
average of the rates for the ORG and
non-ORG parts of the sample and it is easy, therefore, to back
out the employment rate for the
non-ORG sub-sample. The two figures plot the employment rate
by month for the two
subsamples. In 2004 (see Figure 1), the ORG series is clearly
far more variable, which is not
surprising given its smaller sample size. The average month-to-
month change in the
employment rates is 7.5 percentage points, compared to 2.9
points for the non-ORG sample.
The two series are within 1-3 percentage points in five months,
and in another four months,
they differ by four to six percentage points, with the ORG
higher in two and the non-ORG higher
in the other two. But in the remaining three months, they differ
by 10-15 percentage points,
with the ORG estimates always higher, and in each case
followed in the subsequent month by a

change in the ORG rate that eliminates most of the difference
between the estimates. The
three outlier months account for almost all of the 3.5 percentage
point difference in the annual
rates for the two subsamples. In the other nine months, the
simple average difference is less
than one percentage point. The monthly differences are
statistically significant at the 5% level
in two months and for the year as a whole.
12
In 2006 (see Figure 2), the ORG series is again much more
variable from month to
month; the average month-to-month change is again .075,
compared to .042 for the CPS.9
There is no clear pattern in the differences; the ORG rates are
lower in eight months, higher in
three, and close to the non-ORG rate in only one. Again months
where the two rates differ the
most are typically followed by months where the ORG rate
moves toward the more stable non-
ORG rate. This is true for February, April, June, September,
and November. Overall, because

the ORG employment rate is more often lower than the non-
ORG rate, the average annual rate
from the MORG is 1.7 percentage points lower than the CPS
(see Table 2, rows 1 and 2).
The same comparison for the control states also shows far more
variability by month for
the ORG sample than the non-ORG10, but the difference in the
rates is smaller. In 2004, for
example, in eight months the two series are very close, in three
months the non-ORG rate is
higher, and in one month the ORG rate is higher. As previously
seen in Table 2, the annual rates
differed by about three-quarters of a percentage point. In 2006,
the two rates are similar in
eight months, but now the ORG rate is higher in three months
and lower in one. On average,
the months with a positive ORG difference, which are as large
as 9.8 percentage points, yield a
1.7 percentage point higher employment rate.
In both years, the higher variability in the employment rate
from month-to-month in the
MORG than in the CPS is undoubtedly related to its smaller
sample size. Why this translated

into a higher employment rate for NY in 2004 and a lower one
in 2006 is a puzzle, but it is
genuine—and unfortunate for the SBH analysis. It is, I suspect,
simply a small sample problem.
9 Some seasonal variability in the employment is expected for a
population that includes many students.
10 In 2004, the average month-to-month change is .022 for the
CPS and .049 for the MORG. In 2006, the
corresponding averages are .019 and .047.
13
As I noted above, a relatively small change in the number of
persons reported as employed in
the MORG is all that is necessary to yield employment rates
similar to the CPS, especially for the
subgroups with smaller samples. One possibility is fluctuation
in the proportion of the MORG
NY sample that is teenaged. In 2004, this proportion ranges
from under 50% to almost 75%
with an average of 66.6%, while in 2006 it ranges from 63% to
79% with an average of 70%.
Monthly variation in the teen population share explains 55% of
the variation in the difference

between the two sets of monthly employment rates in 2004, but
almost none of the variation
in 2006.
Whatever the explanation, when estimates differ, as they do
here, there is no option
but to accept those from the full CPS, which is four times larger
and indisputably more fully
representative. On that basis, I conclude that the natural
experiment created by the increase in
the minimum wage in NY shows a negligible impact on
employment of persons age 16-29
without a high school degree.
III. How Representative is New York?
If the New York minimum wage natural experiment is to be of
policy importance, it
ought to have some predictive value for other states with
minimum wage increases. As a test,
one can conduct the same kind of natural experiment using other
states to assess the validity of
using NY as a representative case. In fact, such a natural
experiment can readily be done. Over
the same time period, New Jersey, Florida, Illinois and the
District of Columbia increased their

minimum wage substantially, while another seven states
increased their minimum wage by
much smaller amounts.
14
To examine this, I again use the full CPS data for 2004 and
2006. I focus on the three
states plus DC with the largest increases and compare them to
all states that had no increase
over this time period. More refined comparisons could
undoubtedly be made, but the results
of this exercise ought to be suggestive. The minimum wage
increased in these states11 by an
average of $1.03, equivalent to an 18.7% increase.12 For the
same sample restrictions as in SBH
(age 16-29, not a high school graduate), the CPS files include
8,000-9,000 observations for the
four states with an increase in the minimum wage and
approximately 65,000 in the 39 states
with no increase.
Table 4 shows the employment rates in the two groups of states
before and after the

minimum wage increase and the corresponding difference-in-
difference estimate. In 2004, the
employment rate in DC, IL, FL, and NJ was 36.6%, while in
2006, after the increase, the
employment rate increased by 3.4 percentage points to 39.9%.
In the states with no increase,
the employment rate increased 0.6 percentage points. This
yields a difference-in-difference
estimate of 2.74 percentage points that is statistically
significant at the 5% level. Panel B shows
the comparable information for 20-29 year olds with at least a
high school education.
Employment rates in both years are very similar in the two
groups of states, rising by about one
percentage point, presumably for reasons having nothing to do
with any change in the
minimum wage and reflecting, instead, employment changes due
to the overall state of the
economy. The difference-in-difference estimate is a miniscule
−0.0007. Interpreted as an
indicator of the general state of the economy, this estimate
suggests that overall conditions
11 For ease of exposition hereafter, I refer to DC as a state.
12 The increase in the other seven states ranged from $0.25

(Maine) to $0.55 (Wisconsin) with an average increase
of 7.5%.
15
were quite similar in the two sets of states. Finally, Panel C
combines the two sets of estimates
to compute the DIDID estimate of the impact of the minimum
wage increase in DC, FL, IL, and
NJ. The DIDID estimate is 0.0281 and it is statistically
significant at the 5% level or better. Thus,
this natural experiment suggests that the minimum wage
increase in these states had a positive
effect on employment of young, less-educated workers.13
I also computed employment rate changes using the CPS-
MORG sample to see whether
the same sample issues that affected the NY v control state
comparison would arise here.
Sample sizes are about twice as large as the samples for NY and
the control states used by SBH.
In this case, the DID estimates from the MORG files are
essentially identical to those from the

CPS. The employment rate in the MORG is one percentage
point lower than the CPS in both
years for the states with an increase in the minimum wage,
while in the states with no increase
the MORG employment rate is about 0.2-0.3 percentage points
lower than the CPS in both
years.14 Although the employment levels differ, the trend is
identical, resulting in a DID
estimate for the employment change of .0275 with a standard
error of .0154 and t-statistic of
1.79. The DIDID estimate from the MORG is lower than with
the full CPS, because the MORG
files show a more positive employment rate change for 20-29
year olds with at least a high
school degree in the states with a minimum wage increase than
in the states with no increase.
The DIDID estimate is 0.0105 but with a t-statistic barely
greater than one.
13 I also estimated adjusted DID models with the same
covariates used in Table 2. The estimated minimum wage
DID effects for the two samples are .0206 (standard error
=.013) for the age 16-29 year olds and .0070 (standard
error =.009) for the more educated 20-29 year olds. Full
regression results are available on request.
14 The estimated 2004 and 2006 MORG employment rates are
35.6% and 39.1% for the four states with a

substantial minimum wage increase and 39.1% and 39.7% for
the states with no increase.
16
III. Discussion and Conclusion
Sabia, Burkhauser, and Hansen asked “Are the Effects of
Minimum Wage Increases
Always Small?” and answered emphatically “no” for the case of
New York’s increase in the state
minimum wage between 2004 and 2006. The implied
employment elasticities in their paper
are in the range of −0.6 to −0.8, well above the consensus
estimate in the earlier minimum
wage literature of −0.1 to −0.3 (Brown, Gilroy, and Kohen
1983; Neumark and Wascher 2008)
and even further above some more recent estimates that show
essentially no effects. The
employment rate changes they report are so large that any
reasonable policy analyst would
have to question the wisdom of such a policy. They are also so
large that labor economists

might well wonder about their accuracy.
My re-analysis of the SBH natural experiment yields results that
are substantially
different than theirs. I find no evidence of a negative
employment impact for young, less-
educated workers in NY following the minimum wage increase.
The difference in results reflects
the different data sources used, rather than differences in
method. SBH used the CPS-MORG
files, which are a one-quarter subsample of the full CPS, while I
used the full CPS files. In this
case, the MORG files yield incorrect estimates of the
employment rate changes in NY and in the
control states, substantially overstating the apparent impact of
the minimum wage change. A
closer examination reveals very large month-to-month
employment rate changes in the MORG
files, a result that is not terribly surprising in light of the small
monthly sample sizes. For
example, the difference between the annual employment rates in
the two data sets for NY in
2004 is fully accounted for by three outlier months, each of
which is followed by a month that is
17

very close to the CPS estimate. The huge employment decline
for 20-24 year olds in the MORG
data could be eliminated if 4-8 additional sample members
reported a different employment
status.
I also presented evidence from another natural experiment
involving an increase in
state minimum wages in Florida, Illinois, New Jersey, and the
District of Columbia, all of whom
had quite large increases in their minimum wage. I compare
employment rate changes in those
states to changes in the 39 states that had no increase. I find
evidence of a positive
employment effect of 2.74 percentage points or 7.5%.
Interestingly and perhaps reflecting the
larger sample sizes involved or just the laws of sampling
variability, I find very similar results
using the MORG files.
SBH were not inherently wrong in using the MORG files and
their analysis and methods
are appropriate. Rather, they were unlucky. The difference

between employment rates at the
state level from the CPS and MORG is a cautionary tale for
applied labor economists, especially
for analyses using a DID strategy with relatively small samples
and a population mean that is
reasonably low. In that case, a small difference across data sets
in the number of persons
employed can end up yielding very different estimates. It is
true that previous minimum wage
employment analyses have relied on the MORG data, including
Hoffman and Trace (2009) and
Allegretto, Dube, and Reich (2111). It may be prudent to
revisit those studies to see whether
estimates based on the full CPS sample validate the MORG
estimates. As shown in this paper, it
is an empirical issue: for the NY natural experiment the CPS
and MORG estimates were quite
18
different, but for the other states with an increase in the
minimum wage, the two sets of
estimates were quite similar.

My findings of employment effects that are either negligible, as
in the case of New York,
or positive, as in the case of DC, FL, IL, and NJ, are largely
consistent with the newer round of
minimum wage employment estimates. Dube, Lester, and Reich
find no negative employment
effects comparing counties across state lines with different
minimum wages and Hoffman finds
no negative effect of the 2009 federal minimum wage increase
in a comparison of individuals in
states where the minimum did increase and those where the
minimum did not increase
because the state minimum already exceeded the new federal
standard. Belman and Wolfson’s
(Belman and Wolfson 2014) meta-analysis review similarly
concludes that minimum wage
effects in the US are very small in magnitude and not
statistically insignificant.
It is important to caution that the findings reported in this
paper reflect the range of
minimum wage increases observed in the data. They support
the idea that modest minimum
wage increases in the 10-20% range phased in over a two-year
period may not be problematic

in terms of employment. But they are not informative about
what the employment
consequences might be for much larger increases. At the current
$7.25 level of the federal
minimum wage, a 20% increase would boost the minimum to
$8.70. The recently proposed
increase to $10.10 amounts to a 39% increase and the often-
discussed $15 per hour minimum
wage is far outside that range.
Finally, SBH find particularly large impacts on 20-24 year olds
without a high school
degree and my estimates from the CPS, although considerably
smaller than theirs and not
19
statistically significant, are also largest for that group. Unlike
teens without a high school
degree, for most of the workers in this age group, their
educational attainment is terminal.
Hoffman and Trace also found larger effects for workers in this
age group. It may well be that
this group merits further attention in minimum wage analyses.

20
Bibliography
Abadie, Alberto, Alexis Diamond, and Jens Hainmueller. 2010.
"Synthetic Control Methods for
Comparative Case Studies of Aggregate Interventions:
Estimating the Effect of California’s
Tobacco Control Program." Journal of the American Statistical
Association 105: 493-505.
2013. "Minimum Wage Increases in
a Recessionary Environment." Labour Economics 23: 30-39.
Allegretto, Sylvia A., Arindrajit Dube, and Michael Reich.
2111. "Do Minimum Wages really
Reduce Teen Employment? Accounting for Heterogeneity and
Selectivity in State Panel
Data." Industrial and Labor Relations Review 50 (2): 205-239.
Belman, Dale and Paul J. Wolfson. 2014. What Does the
Minimum Wage Do? Kalamazoo, MI:
W.E. Upjohn Institute.
Brown, Charles, Curtis Gilroy, and Andrew Kohen. 1983.
"Time-Series Evidence of the Effect of
the Minimum Wage on Youth Employment and Unemployment."
The Journal of Human
Resources 18 (1): 3-31.
Bureau of Labor Statistics. 2013. Characteristics of Minimum

Wage Workers: 2012, U.S.
Department of Labor.
Card, David and John E. DiNardo. 2002. "Skill-Biased
Technological Change and Rising Wage
Inequality: Some Problems and Puzzles." Journal of Labor
Economics 20 (4): 733-783.
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 (4):
772-793.
"Minimum Wage Effects Across
State Borders: Estimates Using Contiguous Counties." Review
of Economics and Statistics
92 (4): 945-964.
Dube, Arindrajit, Suresh Naidu, and Michael Reich. 2007. "The
Economic Effects of a Citywide
Minimum Wage." Industrial and Labor Relations Review 60 (4):
522-543.
Employment Policies Research. 2012. "New Study: Past New
York Wage Hike Caused
Substantial Job Loss," http://www.epionline.org/release/o335/,
accessed May 20, 2014.
Hoffman, Saul D. 2014. "Employment Effects of the 2009
Minimum Wage Increase: New
Evidence from State Comparisons of Workers by Skill Level."
The B.E. Journal of Economic
Analysis and Policy: 1-27.

21
Hoffman, Saul D. and Diane M. Trace. 2009. "NJ and PA Once
Again: What Happened to
Employment When the PA–NJ Minimum Wage Differential
Disappeared?" Eastern
Economic Journal 35 (1): 115-128.
Holtz-Eakin, Douglas. 2013. "The Mythology of the Minimum
Wage." Huffington Post,
November 15, 2013, accessed May 20, 2014.
Neumark, David and WIlliam L. Wascher. 2008. Minimum
Wages. Cambridge, MA: MIT Press.
Sabia, Joseph J. and Richard V. Burkhauser. 2010. "Minimum
Wages and Poverty: Will a $9.50
Federal Minimum Wage Really Help the Working Poor?"
Southern Economic Journal 76 (3):
592-623.
Sabia, Joseph J., Richard V. Burkhauser, and Benjamin Hansen.
2012. "Are the Effects of
Minimum Wage Increases Always Small? New Evidence from a
Case Study of New York
State." Industrial & Labor Relations Review 65 (2): 350-376.
22

Table 1. Sample Characteristics, NY and Control States,
Workers Age 16-29, No High School
Degree, by Data Set
New York Control States
CPS-MORG CPS CPS-MORG CPS
BLACK 0.249 0.246 0.135 0.136
MALE 0.531 0.532 0.522 0.526
AGE 19.199 19.165 18.649 18.626
EDUC <=9 0.272 0.257 0.260 0.244
EDUC = 10 0.285 0.290 0.328 0.333
EDUC = 11 0.339 0.339 0.353 0.361
EDUC=12 (No
Degree)
0.105 0.114 0.060 0.062
Number of
Observations
1905 7436 3265 12986
Note: Control states are New Hampshire, Pennsylvania, and
Ohio. All estimates are population
characteristics using sample weights.

23
Table 2. Employment Rate Effects of NY State Minimum Wage
Increase, 2004-2006
(Standard Error in Parentheses; Sample Size in Brackets)
Group and
Data Source
NY 2004 NY 2006 NH, PA, OH
2004
NH, PA, OH
2006
Diff-in-Diff Adjusted
Diff-in-Diff
16-29, w/o
HS degree
MORG
CPS
0.362
[989]
0.291

[916]
0.409
[1765]
0.414
[1499]
−0.076**
(0.029)
−.073**
(0.028)
0.336
[3854]
0.308
[3582]
0.417
[6909]
0.397
[6077]
−0.008

(0.014)
−0.018
(0.013)
16-19, w/o
HS degree
MORG
CPS
0.260
[685]
0.196
[659]
0.357
[1383]
0.356
[1198]
−0.064**
(0.032)

−0.072**
(0.036)
0.233
[2698]
0.207
[2547]
0.366
[5406]
0.344
[4836]
−0.005
(0.015)
−0.016
(0.014)
20-24, w/o
HS Degree
MORG
CPS

0.537
[176]
0.430
[148]
0.524
[224]
0.560
[170]
−0.124
(0.077)
−0.141**
(0.071)
.515
[686]
0.458
[604]
0.549
[877]

0.528
[720]
−0.037
(0.038)
−0.054
(.036)
25-29, w/o
HS Degree
MORG
CPS
.604
[128]
.620
[109]
.603
[158]
.671
[131]

−0.053
(0.034)
−0.070
(0.051)
0.593
[470]
0.631
[431]
0.599
[626]
0.627
[521]
0.011
(0.043)
−0.006
(.041)
20-29, >= HS
Degree

MORG
CPS
0.694
[2082]
0.700
[1844]
0.759
[3422]
0.754
[3503]
0.010
(0.009)
0.005
(0.005)
0.695
[8197]

0.701
[7323]
0.755
[13612]
0.762
[13791]
−0.001
(0.009)
−0.003
(0.008)
MORG estimates from Sabia, Burkhauser, and Hansen, Table 3.
** Statistically significant at 5% level or better.
* Statistically significant at 10% level or better.
24
Table 3. Difference-in-Difference-in-Difference Estimates of
Employment Rate Effect of
Minimum Wage Increase, NY v NH/OH/PA, 2004-2006

Group NY NH/PA/OH
16-29, w/o HS degree
2004 0.336
[3854]
0.417
[6909]
2006 0.308
[3582]
0.397
[6077]
Difference-in-Difference -0.008
(0.014)
20-29, high school degree
or more
2004 0.695
[8197]
0.755
[13612]
2006 0.701
[7323]
0.762
[13791]

(0.009)
Diff-in-Diff-in-Diff (CPS) -0.0075
(0.017)
Diff-in-Diff-in-Diff (MORG) -0.086**
(0.033)
Source: Current Population Survey, 2004 and 2006. MORG
estimates from Sabia,
Burkhauser, and Hansen, Table 3.
25
Table 4. Employment Rate Effects of State Minimum Wage
Increase, 2004-2006, DC, FL, IL, and
NJ and States with No Increase
Group DC, FL, IL, NJ States with No MW
Increase
A. Age 16-29, w/o HS degree
2004 0.3664
[9014]

0.3945
[66548]
2006 0.3999
[8673]
0.4006
[66534]
Difference 0.0335**
(0.0073)
0.0061**
(.0027)
Difference-in-Difference 0.0274**
(.0078)
Adjusted Difference-in-Difference
B. Age 20-29, at least HS degree
2004 0.7416
[19017]
0.7464
[148336]
2006 0.7520
[18697]
0.7575
[131314]

Difference 0.0104**
(0.0025)
0.0111**
(.0016)
(.0048)
C. Diff-in-Diff-in-Diff 0.0281**
(0.0091)
Source: Current Population Survey, 2004 and 2006.
26
0%
10%
20%
30%
40%

50%
60%
J F M A M J J A S O N D
Em
pl
oy
m
en
t
Ra
te
Month
Fig. 1. Employment Rate by Month, Persons 16-29 without
HS degree, NY, 2004, ORG and Non-ORG CPS Samples
Non-ORG
ORG
27
0%

10%
20%
30%
40%
50%
J F M A M J J A S O N D
Em
pl
oy
m
en
t
Ra
te
Month
Fig. 2. Employment Rate by Month, Persons 16-29 without HS
degree, NY, 2006, ORG and Non-ORG CPS Samples
Non-ORG
ORG
28

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