Why Understanding Smoking Bans is Important for Estimating Their Effects: California’s
Restaurant Smoking Bans and Restaurant Sales
Robert K. Fleck
Department of Agricultural Economics and Economics
Montana State University
Bozeman, MT 59717
phone: (406) 994-5603
e-mail: rfleck@montana.edu
F. Andrew Hanssen
Department of Agricultural Economics and Economics
Montana State University
Bozeman, MT 59717
phone: (406) 994-5616
e-mail: ahanssen@montana.edu
January 15, 2007
Abstract: A large literature has sought to determine whether smoking bans help or hinder restaurants. Much
of the literature improperly specifies its econometric equations, and thus mistakenly infers causality.
Examining the relationship between restaurant smoking bans and restaurant revenues in 267 California
communities, we reach two main conclusions. First, California’s municipal restaurant smoking bans are
endogenous in a critical way – restaurant sales growth (or something correlated with restaurant sales growth)
appears to cause restaurant bans, not vice versa. Consequently, failure to control properly for trends can
produce spurious “evidence” of causation. Second, ban heterogeneity (e.g., state vs. local) can be exploited to
sort out – or rule out – causal effects. In other words, pooling data and treating smoking bans implemented at
different levels as homogenous (as many studies do) ignores an important source of information, and is likely
to lead to erroneous conclusions. Our analysis holds lessons for the many studies that have examined the
arguably more important question of how smoking bans affect smoking rates.
We thank Joe Fitz and the California State Board of Equalization for sending us taxable sales data. We are also grateful
to Len Casey and the American Nonsmokers’ Rights Foundation for generously sharing their data on smoking bans. For
helpful comments, we thank Rosalie Pacula, Wally Thurman, and participants at the 2006 Western Economic Association
Conference. The Department of Agricultural Economics and Economics at Montana State University provided the
financial support for this research.
I. Introduction
A voluminous literature has sought to quantify the effect of smoking bans, typically on the quantity of smoking,
but also on the performance of affected businesses.1 Various time periods have been explored, types of bans
1For
reviews of studies on smoking bans and smoking behavior, see Chaloupka and Warner (1999, 37-38), Evans et al.
(1999, 731-2), and Tauras (2006, 334). For a review of studies on restaurant bans and restaurant performance, see Scollo and Lal
(2005).
considered, locales examined, and specifications employed. Nonetheless, the majority of studies share two common
failings. First, smoking bans of a given type (e.g., a restaurant ban) are treated as homogenous, when in fact, such bans
have been enacted at various jurisdictional levels (municipality, county, or state), at various times, in various orders,
and in various combinations (with other types of smoking bans, and with similar bans at other jurisdictional levels).
Second, empirical specifications do not adequately control for preexisting trends in the dependent variable. As a result,
many studies arrive at fundamentally wrong conclusions.
We illustrate these points in an investigation of how California’s restaurant smoking bans have affected
restaurant sales. We analyze the effect of smoking bans on restaurant sales for two reasons. First, the issue plays a role
in the policy debate – more than 150 studies (many published in refereed journals and others in consulting reports
undertaken for municipalities) have explored whether smoking bans help or hinder restaurants (see Scollo and Lal
2005). Yet few of these studies properly account for the effects of pre-existing trends (or changes in trends), for the
closely related question of ban endogeneity, or for ban heterogeneity. Second, restaurant sales data are very rich: wellmeasured, available by municipality, by quarter, and over an extended period. Therefore, we can identify effects that
would be obscured by cruder data (e.g., periodic survey responses), enabling us to draw lessons applicable to studies of
the effect of other types of smoking bans (e.g., workplace bans) in other dimensions (e.g., smoking prevalence).
We investigate 267 California municipalities for which the California State Board of Equalization provides
quarterly taxable restaurant sales.2 We begin by employing “naive” specifications (which treat bans as homogenous and
control simplistically for trends) representative of those typically estimated in the literature. The results of our naive
specifications indicate that smoking bans have a large negative effect on restaurant revenues. However, when we
examine municipal and state bans separately, we find a positive association between municipal bans and restaurant
sales, and a negative association between the state ban and restaurant sales. Finally, when we control properly for
preexisting trends in the dependent variable, we find no substantial evidence of any causal relationship running from
either municipal bans or the state ban to restaurant sales.
2The Board of Equalization currently reports such data for the 272 cities with the highest total taxable sales.
Our sample
size is smaller because a full set of data (including taxable sales for restaurants, as well as the Census variables we use) is available
for only 267 California cities.
2
Thus, we reach two main conclusions. The first is that California’s municipal restaurant smoking bans are
endogenous in critical way – restaurant sales growth (or something correlated with restaurant sales growth) appears to
cause restaurant bans, not vice versa. The second is that because communities are heterogenous, one must analyze the
effect of a ban taking into account the level at which the ban was enacted. Pooling data and treating “smoking bans” as
homogenous (as many studies do) is inappropriate – cities that impose bans on themselves are likely to differ
systematically from cities that have bans forced on them by a higher jurisdiction (county or state). Relatedly, analyzing
and/or instrumenting for smoking bans using state-level data (again, as many studies do) may fail to capture the relevant
variation when the bans have force at a lower level of jurisdiction (e.g., a municipal ban).
Our analysis, although focused on restaurant bans and restaurant sales, has implications for the more extensive
literature on how smoking bans influence smoking behavior. Most importantly, it demonstrates the crucial nature of
identifying and controlling for trends in the dependent variable (whether restaurant revenue, as in our data set, or
smoking rates). Although a number of smoking ban studies explicitly acknowledge (and attempt to deal with) the
possibility of endogeneity (e.g., Warner 1981; Chaloupka and Saffer 1992; Evans et al. 1999; Tauras 2006), their
equations may be nonetheless improperly specified in the absence of appropriate controls for differentials in trends
across the relevant units of observation. Furthermore, we find that demographic variables which might plausibly affect
demand for restaurant meals and inspire smoking bans (e.g., income, education), do not explain the differential in
restaurant sales trends, suggesting that more research into the causes of smoking bans is necessary to identify their true
effects.
More broadly, our conclusions are related to the general point that treating policy changes as natural
experiments when using panel data can produce misleading results (e.g., Besley and Case 2000; Heckman and Vytlacil
2001; Bertrand et al 2004).3 In particular, our analysis demonstrates that in a panel setting, simple methods of
addressing serial correlation (e.g., first order autocorrelation corrections, linear trends, time period dummies) are
insufficient to identify the true effects of smoking bans.
3Also
see Heckman’s (2000) more general discussion of the difficulties involved in efforts to infer causality. Heckman,
Flyer, and Loughlin (2006) review the public health literature on the effects of cigarette advertising on youth smoking, and explain
why the methods used in that literature fail to identify causal effects.
3
II. The Debate Over the Effects of Smoking Bans on Restaurants
Many studies have investigated the influence of smoking bans on restaurants. The most complete overview of
this literature is provided by Scollo and Lal (2005), who review 151 studies, about forty of which were published in
peer-reviewed journals.4 The reviewed studies analyze a variety of “performance” measures: taxable sales (by far the
most common), employment levels, number of establishments, number of permit applications, number of bankruptcies,
unemployment insurance claims, self-reported patron intentions, and proprietor predictions. While the evidence is
somewhat mixed, the majority of studies find bans to have either no effect or a positive effect on restaurant
performance. Indeed, some notable studies find that smoking bans improve restaurant performance measures
substantially.5
That an improvement in restaurant performance should follow a smoking ban may appear, at first blush,
puzzling – why would forcing restaurants to do something that they could do voluntarily increase their revenues and/or
reduce their costs? In fact, few of these studies offer any economic theory to support their empirical analyses, but rather
simply assert that more non-smoking customers (or fewer smoking customers) will patronize a non-smoking restaurant,
or that a non-smoking restaurant’s expenses will be lower, ceteris paribus.6 While either outcome is possible, neither
requires coordinated action, so the contribution of a law is not clear.
Nonetheless, a positive relationship between restaurant performance and smoking bans may indeed be
consistent with rational profit maximizing behavior by restaurant owners. For example, there may be a prisoners’
dilemma-style problem among restaurants that renders unilateral action unprofitable but coordinated action profitable.7
4The majority of the peer-reviewed articles appeared in medical and health journals, such as the Journal of the American
Medical Association, or the American Journal of Public Health.
5See,
e.g., Glantz (2000), Alamar and Glantz (2004), and Cowling and Bond (2005). Glantz (2000) and Cowling and
Bond (2005) focus on California.
6The
restaurant will need to fumigate less frequently, for example, and will have fewer burns in carpets or curtains to
mend (e.g., Alamar and Glantz 2004, 520-521).
7For
example, if smokers have a very inelastic demand for dining out, but a strong willingness to travel within a city to
smoke while they eat, a unilateral smoking ban may lose a restaurant more in smokers than it gains in nonsmokers, yet a
coordinated ban may increase the number of nonsmoker patrons without substantially reducing the number of smoker patrons.
Cowling and Bond (2005, 1280) describe a similar idea in the context of a free-rider problem.
4
Alternatively, rather than smoking bans increasing revenue, the direction of causality may run from revenues to bans.8
Or perhaps a third factor explains both restaurant sales growth and smoking bans. In short, the effect of restaurant
smoking bans on restaurant performance remains an open – and empirical – question.
We will analyze the effect of California’s comprehensive restaurant smoking bans on restaurant sales.9
California is an excellent candidate for empirical analysis because it has been a pioneer in the establishment of
comprehensive private-place smoking bans, and because its pattern of passage of smoking bans provides
econometrically useful variation in ban coverage and jurisdiction.10 Because California enacted smoking bans at
several jurisdictional levels (state, county, municipality), a given California community may be covered by more than
one ban. For example, 16 California cities put municipal bans in place before California’s statewide ban took effect in
1995, and another 19 did so afterwards (see on-line appendix B).11 Another reason to engage in econometric
investigation is that casual perusal of the raw data (see on-line appendix B) reveals that some of the cities passing bans
in the 1990s grew extremely rapidly in wealth and/or population during the 1990s – for example, Mountain View,
Santa Clara, and San Jose during the Silicon Valley boom. Properly accounting for these and other factors that
influence restaurant revenue growth is essential to determining a ban’s effects.
III. Data
Our data set is an unbalanced quarterly panel covering 267 California cities for the years 1980-2004. We
8For instance, if restaurants are a zero profit industry, restaurant owners will have less reason to lobby against a ban when
market demand (and hence aggregate restaurant sales) is increasing – entry allows no more than a normal rate of return regardless
of a ban.
9Our
empirical analysis includes only comprehensive bans. We thus do not count laws that merely require separate
smoking sections, or that have exemptions based on the size of the firm. Furthermore, a comprehensive restaurant ban need not
imply a ban for bars that serve food.
10The first seventeen comprehensive workplace smoking bans, the first sixteen comprehensive restaurant smoking bans,
and the first seven comprehensive bar smoking bans passed in the United States were enacted by California communities. As late
as January 1, 2000, 84 of the nation’s 110 workplace bans, 32 of the nation’s 62 restaurant bans, and 20 of the nation’s 43 bar bans
were in effect in California. An implication is that results of national studies of smoking bans during the 1990s will be heavily
weighted towards California. The ANRF is the source for our data on comprehensive private-place smoking bans – see Section
III.
11The
online appendices referred to in this article may be found at . . .
5
include an observation in our econometric analysis if and only if all variables are available for that city and quarter. See
on-line Appendix A for a list of data sources, variable definitions, and descriptive statistics.
Our dependent variable will be Restaurant Revenue, the log of real taxable sales at eating and drinking
establishments. The California State Board of Equalization publishes taxable sales data quarterly, and we were able to
obtain quarterly eating and drinking establishment data for the years 1980-2004. Because the Board of Equalization
reports data for cities with substantial taxable sales, the sample includes all of California’s large cities (i.e., none with a
population above 125,000 in 1990 is omitted), but also includes some small-population cities with large amounts of
taxable sales (business districts, industrial parks).12
Our data on smoking bans come from the ANRF’s (2006b) database on “100% Smokefree Ordinances” for
cities, counties, and states. The organization classifies bans as “100% Smokefree” if they are “comprehensive”; i.e., the
bans prohibit smoking completely rather than (for instance) simply requiring a nonsmoking section. On-line appendix B
lists the California municipalities (and counties) classified by the ANRF as having passed comprehensive restaurant
smoking bans, and the date the bans are said to have taken effect.13 The appendix also lists the date California passed a
statewide restaurant smoking ban. For each municipality for each quarter, we define the variable City Ban to equal to 1
if a comprehensive municipal restaurant smoking ban is in effect, and 0 otherwise (and between 0 and 1 for the quarter
in which the ban first took effect).14 We define the variable State Ban to equal 1 for all municipalities when the state
ban is in effect (i.e., from the first quarter of 1995 onwards) and 0 otherwise. We define the variable Both Bans to
equal 1 if a municipality’s restaurants are subject to both a city and state ban (i.e., it takes on the value of 0 for all
communities prior to 1995, and 1 after 1995 for communities that also have municipal bans in place). Finally, we
define the variable Any Ban to equal 1 if a municipality had a local ban in effect (City Ban = 1) and/or California’s state
ban was in effect (State Ban = 1).
Although the ANRF provides the best data available, there are two important caveats the reader should keep in
12We
find that the results we present are not sensitive to the exclusion of these smaller cities; see Section IV.
13The
county bans apply only to unincorporated sections of the relevant counties.
14For
example, if a ban was in place for half of its initial quarter, the value of City Ban is set equal to one-half.
6
mind. First, because we rely upon the ANRF classifications, our estimated effects capture differences between cities
coded by the ANRF as having “100% Smokefree” ordinances and other cities, with “other” including anything the
ANRF does not classify as “100% Smokefree” (which could be a weak ban or no ban at all).15 As a result, there may be
unobserved strength-of-ban differences among cities classified as having “100% Smokefree” bans, as well as among
cities classified as not having “100% Smokefree” bans.16 Second, there are policies related to smoking that we cannot
observe, most notably the degree to which smoking bans are actually enforced. That said, the main finding of this paper
– namely that failing to control properly for trends can generate spurious results in line with those reported in the
previous literature – clearly matters regardless of the degree to which the ANRF data actually measure the relevant
variation in antismoking policy with perfect accuracy.
Because restaurant revenues are likely to be influenced by an enormous variety of city-specific factors, and
because all of the comprehensive restaurant smoking bans came into effect partway through our sample period, we
include city fixed effects.17 To control for general trends in the economy (and in dining out), as well as year-to-year and
seasonal fluctuations, we employ either (i) a linear trend with quarterly seasonal dummies or (ii) a full set of time
dummies for the 100 quarters in our sample.
Even with city fixed effects and quarterly time period dummies included, there remains the need to control for
trends and fluctuations that are not common to the entire set of cities in the sample. For this reason, we use the variable
15Furthermore,
the nature of collecting smoking ban data from city governments (as the ANRF does) introduces the
potential for mis-classifications. Indeed, as Rosalie Pacula pointed out to us, this is apparent from the fact that the ANRF has
revised its classifications over time as it has obtained more accurate information on the nature of the bans in place. Hence, the
estimated effects of the smoking ban variables we use are most accurately interpreted as reflecting a comparison between cities
reported as having “100% Smokefree” ordinances and all other cities in the data set.
16An econometric analysis of smoking bans for the entire U.S. would require careful attention to the fact that some weak
state-level smoking bans preempt stronger local bans and, hence, actually reduce the restrictions on smoking in some localities
(e.g., American Medical Association 2003; Centers for Disease Control 2006). For California, the state-level law did have some
preemptive clauses for 1995-1997, according to the Centers for Disease Control’s (2006) interpretation of the law. Recall,
however, that the state-level ban in place during those years is a “100% Smokefree Ordinance” (i.e., a strong ban) as coded by the
ANRF (2006b). This suggests that, if the preemption of local laws had any effect, the effect likely would have been minor. In
principle, we could test this empirically if we had data on the strength of local “100% Smokefree” ordinances passed before the
state ban, but in practice we cannot (given the dichotomous coding of smoking bans).
17The literature on the determinants of state-level bans suggests a variety of potential causal factors, including cigarette
consumption, income, political leanings, and tobacco production (e.g., Hersch, Del Rossi, and Viscusi 2004; Gallet, Hoover, and
Lee 2006). Also see Shipan and Volden (forthcoming), who focus on the diffusion of antismoking policies from cities to states
(i.e., the effect that the passage of city-level bans in a state has on the likelihood of that state passing a state-level ban).
7
Other Taxable Sales, defined as taxable sales from all sources other than eating and drinking establishments.18 Because
Other Taxable Sales is available quarterly, the variable allows us to control for fluctuations and trends in economic
growth specific to each city in the data set. We also use a group of city-specific trend controls consisting of
demographic variables interacted with a linear time trend. The demographic variables are population, education (the
percent of the population that has a high school degree or higher, the percent of the population that has a bachelor’s
degree or higher), median household income, median home value, and the median residential rent paid.19 We include
education because human capital may be related to both growth in restaurant revenue (highly educated people had more
rapid increases in income over the sample period) and to smoking bans (highly educated people smoke less and may be
more likely to lobby to prevent others from smoking). Median household income serves a similar purpose. We include
home values to control for wealth-related factors not captured by education and income; home values may also proxy
for opportunity costs related to the use of restaurant property. Median residential rent serves a similar purpose. We
employ specifications including 1990 Census measures only, and including 2000 Census measures as well (thus
allowing us to examine how trends in restaurant growth vary with inter-temporal changes in the Census variables).20
IV. Results
Naive Specifications
The objective of our empirical analysis is to illustrate the manner in which many studies of the effect of
smoking bans have gone wrong. We will therefore begin by estimating what we refer to as “naive” specifications –
18In robustness tests, we controlled for seven separate components of Other Taxable Sales, by adding six variables (each a
category of Other Table Sales) to a regression that already included Other Taxable Sales. The six categories were: apparel stores;
food stores; building materials and farm implements; auto dealers and auto supplies (excludes service stations); service stations;
non-restaurant retail stores. Data for each of these six categories were available for most of the cities in the California State Board
of Equalization’s data set, though adding the six categories forced us to drop 1458 observations because of missing data. (We
used the same data sources and units of measurement as we do for Other Taxable Sales.)
19All
demographic variables are in logged form (as is the dependent variable).
20Other potentially useful variables are not available at the city level. For example, the prevalence of smoking among the
population may influence the likelihood of adopting a ban and the effect of a ban on restaurants. Also, the effects of a ban on firmlevel revenue may differ between restaurants of different types – perhaps with positive effects for some and negative effects for
others. But data on smoking prevalence and revenue by restaurant type (e.g., take-out versus full dining room with liquor) are
available only at more highly aggregated levels.
8
naive in the sense that municipal and state bans are assumed identical in their effects (and can thus be pooled).21 These
“naive” regressions provide a baseline for comparison with the previous literature, and with the specifications we will
estimate subsequently.
The first two columns of Table 1 present the results of estimating our naive specifications, using data for the
entire 1980-2004 time period. Both regressions include city fixed effects, a linear time trend, and seasonal dummies,
and correct for first-order autocorrelation; Regression 2 also includes Other Taxable Sales. The variable of interest is
Any Ban, which equals 1 if the municipality was covered by either a state or local ban during that quarter. In both
regressions, the coefficient on Any Ban is negative, statistically significant, and reasonably large (implying a roughly 4
percent reduction in restaurant revenues). These results are consistent with the hypothesis that restaurant smoking bans
reduce restaurant sales.
Is the coefficient on Any Ban picking up something other than just a smoking ban effect? In order to
understand better what the coefficient on Any Ban is capturing, we will replace it with separate variables for state and
municipal bans: City Ban (equal to 1 if the municipality has a city ban in effect), State Ban (equal to 1 during the state
ban period), and Both Bans (equal to 1 if restaurants in the municipality are subject to both a city ban and the state ban).
The results are shown in Regressions 3 and 4 of Table 1. The coefficient on State Ban is negative and
statistically significant in both regressions, and of roughly the same magnitude as the Any Ban coefficient in
Regressions 1 and 2. The coefficients on City Ban are negative, but less than one third the magnitude of those for State
Ban and far from statistical significance. Finally, the coefficients on Both Bans are positive, and of magnitudes that
offset the combined estimated effects of City Ban and State Ban.22 These coefficients would imply that the state-level
ban alone (i.e., not in conjunction with a city-level ban) has a substantial negative effect on restaurant revenues, while
having both a city ban and the state ban is roughly equivalent to having no ban at all. Clearly, this suggest the
21In
fact, there are good reasons to expect that local bans and state bans will differ systematically in terms of their
consequences. Notably, cities that choose to adopt any given policy may do so because those particular cities expect large benefits
and/or small costs resulting from that policy. By contrast, a state-level policy is imposed on all cities in the state – not just those
that would choose on their own to impose the policy.
22Recall that one should sum the coefficients for City Ban, State Ban, and Both Bans to find the estimated effect of having
a city-level ban in place in the years after the state ban took effect. The estimated effect of having both bans in place is -0.00166
Regression 3 and 0.00201 in Regression 4.
9
possibility of specification error.
In brief, it appears from Table 1’s results (if correct – a question we will address shortly) that the local and
state-level smoking bans have different relationships to restaurant revenues, and that the negative coefficient on Any
Ban in Regressions 1-2 reflects primarily the influence of the state ban on restaurants in municipalities that did not pass
city bans.23 Therefore, our next step is to look at municipal and state bans independently.
Municipal Bans
We begin with municipal bans. We will start with specifications identical to those estimated in Regressions 1-2
of Table 1, with the difference that our variable of interest will now be City Ban (municipal bans) instead of Any Ban.
Because our principal goal at this point is to test whether cities with bans are inherently different from cities without
bans, we will estimate specifications that ignore the passage of the state ban. Regressions 1-2 of Table 2 shows the
results. Interestingly, the sign of the City Ban coefficient has flipped from negative (in Table 1) to positive, with point
estimates implying roughly 3 percent higher revenue (t=2.22) for the specification that includes Other Taxable Sales.
Why does the City Ban coefficient change from negative to positive when the state-level ban is ignored? A
possible reason is that the linear time trend (included in all the equations discussed so far) inadequately captures the
difference between early and late years in the sample; this is a critical concern because controlling for the period of the
state-level ban is econometrically identical to controlling for the last ten years of the sample. To account better for
trends and fluctuations common across all cities in the sample, we estimate in Regressions 3-4 of Table 2 the same
specifications as in Regressions 1-2, but replace the linear time trend with a full set of time period dummy variables.24
23By comparing Regression 1 to Regression 2, and by comparing Regression 3 to Regression 4, one can see that although
Other Taxable Sales (coefficients of 0.39 with t>73) adds substantially to the explanatory power of Regressions 2 and 4, the
coefficients on the smoking ban variables do not change dramatically with the addition of Other Taxable Sales. Furthermore, if we
include the six additional controls for categories of taxable sales (described in Section III), we reach the same conclusion. With
the additional controls added to Regressions 2 and 4, the coefficients are -.0275 (t=5.59) for Any Ban, -.0192 (t=0.97) for City
Ban, -.0285 (t=5.74) for State Ban, and .0478 (t=2.46) for Both Bans. Thus, if the smoking ban coefficients in Table 1 are the
result of an omitted variable bias, the omitted variable appears not to be highly correlated with various types of non-restaurant
taxable sales.
24In other words, each of the 100 quarters in our data set has its own dummy variable. Note that with time period
dummies included, the coefficient on City Ban measures the relative (to cities without bans) effect of the ban on revenues. For
example, if restaurant revenues in a city are unchanged following passage of its municipal ban, but fall in other cities that do not
have municipal bans, the coefficient on City Ban will be positive.
10
As Regressions 3 and 4 show, the coefficients on City Ban are larger when time period dummies are included and,
regardless of whether we control for Other Taxable Sales, statistically significant.25 In short, controlling for crosssectional differences and fluctuations over time, municipal bans appear to be associated with between 4 and 5 percent
higher restaurant revenues (relative to restaurants in non-ban cities). These specifications thus yield results similar to
those of a number of previous studies that (as discussed in Section II) find that smoking bans have a positive and
statistically significant effect on restaurant sales.
Of course, correlation is not causation. To investigate the question of causation more thoroughly, we reestimate Regressions 3-4 separately for 1980-1994 (before the statewide ban) and 1995-2004 (after the statewide ban).
The results are shown in Table 3. When the specifications are estimated on 1980-1994 data (Regressions 1-2), the
coefficient on City Ban is negative and statistically insignificant. By contrast, when the specifications are estimated on
1995-2004 data (Regressions 3-4), the coefficient on City Ban is positive, nontrivial in magnitude (implying roughly 2
to 4 percent higher revenue) and statistically significant (t=2.51) in Regression 4 (i.e., when controlling for Other
Taxable Sales). In short, the positive association between municipal restaurant smoking bans and restaurant sales
apparent in the previous regressions (Table 2) appears to depend on including the period following the state ban.
The fact that the municipal bans are associated with higher restaurant revenues in the later period (but not in the
earlier period) may reflect the influence of the state ban; however, the results also suggest the possibility that restaurant
sales may simply be trending differently in cities that passed municipal restaurant smoking bans than in other cities. In
order to investigate this possibility, we define two new variables. The first is City Ban*Time, which is the dichotomous
variable City Ban multiplied by a linear time trend (which runs from 1 to 100 over the sample period). City Ban*Time
will capture trend differences between ban and non-ban cities at times when a municipal ban is in effect. The second is
Ever Ban*Time, which is the product of a dummy indicating whether a city ever put into effect a restaurant smoking
ban, multiplied by the linear time trend.26 Ever Ban*Time will capture long-term differences between ban and non-ban
25Again,
this conclusion is robust with respect to including additional retail sales measures. Adding the six additional
variables to Regression 2 yields a coefficient on City Ban of .0185 (t=1.69). Adding the six variables to Regression 4 yields a
coefficient on City Ban of .0389 (t=3.75).
26Ever
Ban is thus equal to 1 for ban-passing municipalities over the entire sample period (i.e., before and after their
municipal bans were put into place).
11
cities – differences that are independent of whether or not the ban is in effect.
The results of including these two additional variables are shown in Table 4. Regression 1 of Table 4 is
estimated for the pre-statewide ban period (1980-1994). The coefficient on Ever Ban*Time is positive, statistically
significant (t = 2.22), and non-trivial in magnitude (.33 percent greater revenue with each passing year, relative to other
cities).27 In other words, restaurant sales growth was more rapid in cities that passed bans whether or not the ban was
in effect. This is consistent with there being systematic pre-ban differences between ban-passing cities and non-banpassing cities.
What about the effect of actually having a ban in place? That effect is captured by two variables: City Ban and
City Ban*Time. The two variables have coefficients with offsetting signs (i.e., one positive, one negative); when the
coefficients are interpreted jointly, the magnitude of the estimated effect is nontrivial (a roughly 3% decrease in
revenue), but the coefficients on the two variables are far from statistical significance (individually and jointly).28 In
short, the equation provides at most very weak evidence that city bans affect restaurant revenue.
We next examine whether the pre-ban trend differences can be accounted for by a basic set of demographic
variables plausibly related to restaurant revenue and smoking bans. Regression 2 includes six new variables, each an
interaction of the linear time trend with a 1990 Census variable (population, high school degrees, bachelor’s degrees,
income, home value, and rent).29 Regression 3 adds six more variables, each an interaction of the linear time trend with
a 2000 Census variable. Thus, Regression 2 allows the growth in restaurant revenue to vary between cities in relation
to the levels of demographic variables, and Regression 3 allows the growth in restaurant revenue to vary between cities
in relation to levels and changes in the demographic variables over the decade of principal interest.
Examining the coefficient estimates from Regressions 2 and 3 of Table 4, it can be seen that the levels and
changes in the demographic variables do not explain the differences in trends between cities that passed bans and cities
27Over
the period of the panel (100 quarters) an exogenous difference in trends of this magnitude could lead to a
substantial overestimation of the effect of smoking bans if a naive estimating framework were employed.
28The
joint effect ranges from -0.034 in 1990 (when the first city ban took effect) to -0.031 in 2005 (the end of our
sample). In an F-test of joint significance, p=.48.
29See
Section III and on-line Appendix A for descriptions of these variables.
12
that did not. In fact, adding the full set of demographic controls (Regression 3) more than doubles the size of the
estimated coefficient on Ever Ban*Time (with t=5.26 on the coefficient in Regression 3). In sum, whatever caused the
differences in trends does not appear to be highly correlated with any of a quite general set of demographic variables.
And having a smoking ban in effect does not appear to have any statistically significant association with restaurant
sales.30
Regressions 4-6 in Table 4 repeat the specifications used in Regressions 1-3, but use data from 1995-2004 to
estimate the equations. As with the earlier period, the results show a substantial and statistically significant greater
growth rate in ban-passing cities, whether or not the bans were in effect.31 Once again, this suggests a systematic
difference in some exogenous influence(s) on restaurant revenue – influences that studies employing naive
specifications would interpret as the causal effect of smoking bans on restaurant revenue.32
As robustness test, we examined the sensitivity of our results the exclusion of cities with small populations.
This is potentially important because the sample consists of municipal data assembled by the California State Board of
Equalization on the basis of the size of the taxable sales, not the size of the municipality. Thus, our sample includes
some small cities that are potentially unrepresentative.33 When we re-estimated our equations excluding cities with
fewer than 20,000 people in 1990, the results were very similar to those shown in Tables 3-6.
30As
an additional test of whether cities that will pass bans in the future differ from cities that will not pass bans in the
future, we re-estimated Regression 3 allowing the coefficient on Ever Ban*Time to differ between early and late passers of city
bans (i.e., cities that passed bans prior to the passage of the state ban and cities that passed bans after the passage of the state ban).
The results are quite striking: The coefficient for early passers is 0.00094 (t=1.71) and the coefficient for late passers is 0.00260
(t=5.69). Thus, the cities that passed bans after the passage of the state ban had rapid restaurant revenue growth prior to the
passage of the state ban. As for the evidence that having a city ban in effect matters, it remains as weak as in Regression 3.
31As
for Regression 3, we re-estimated Regression 6 allowing the coefficient on Ever Ban*Time to differ between early
and late passers of city bans. Again the results are quite striking: The coefficient for early passers is 0.00318 (t=3.89) and the
coefficient for late passers is 0.00282 (t=3.47). Thus, early passers had rapid restaurant revenue growth even after the state ban
was in effect. And so did late-passers, whether or not the city bans had yet been passed. The evidence that actually having a city
ban in effect matters remains as weak as in Regression 6.
32As
a robustness test, we expanded the set of controls in Regressions 3 and 6 by adding the six additional controls for
categories of taxable sales (described in Section III). The results were similar, although the adding the additional controls caused
the estimated coefficients on Ever Ban*Time to decline somewhat in magnitude: 0.00142 (t=4.25) for the 1980-1994 period;
0.00174 (t=3.28) for the 1995-2004 period.
33For example, the City of Industry had only 580 people in 1990, and 777 in 2000, yet averaged over $19 million dollars
per quarter in taxable sales at eating and dining places between 1980 and 2004 (see on-line Appendix A for descriptive statistics
for population and other variables).
13
The State Ban
In sum, there is little evidence of a causal relationship running from municipal restaurant smoking bans to
restaurant revenues. How about the state ban? To investigate, we limit our sample to cities that never passed municipal
bans (we have already established that ban-passing cities are systematically different from other cities). We include
fixed effects, a linear trend, seasonal dummies, and controls for other taxable sales. Our variable of interest is State
Ban, which takes on the value of 1 for all cities from the first quarter of 1995 onwards. The results are shown in
column 1 of Table 5. The coefficient on State Ban is negative, statistically significant (t=6.78), and substantial
(implying that the state ban is associated with roughly a 4 percent reduction in restaurant sales). This is consistent with
the hypothesis that restaurant revenues in cities without a self-imposed ban were adversely affected by California’s
statewide ban.
But is the relationship causal? We will again investigate the role of pre-ban trends. Because the state ban
affects all municipalities at the same time, we will look directly at coefficients on time period dummies. We define
sixteen year dummies, running from 1989 (the year before California’s first municipal smoking ban) through 2004 (the
end of the sample period). If the negative coefficient on State Ban truly reflects the effect of California’s state
restaurant smoking ban on restaurant revenues, we should find evidence of a break – a deviation from the pre-state-ban
trend – and that break should occur at the time the state ban took effect.
Regression 2 shows the results. Although the ban year (1995) is indeed associated with a negative deviation
from the pre-1989 restaurant revenues trend, so are the preceding six years. And the deviations increase nearly
monotonically from 1989 right through 2004. Thus, the coefficient on State Ban in Regression 1 provides (at best) very
dubious evidence of causality.
That said, the dubious nature of the evidence only becomes apparent when one
examines the pre-ban deviation from the trend.34
What are the general lessons here? First, Tables 1-4 taken as a whole show that municipal ban-passing cities
differ systematically (i.e., even when the ban is not in effect) from other cities in ways that regressions with city fixed
34Repeating
our earlier robustness tests, we added the six additional controls for categories of taxable sales, and we
examined the sensitivity of our results the exclusion of cities with fewer than 20,000 people (1990 Census). In both tests, the
results were similar to those shown in Table 5.
14
effects, time period dummies, and panel controls for other types of retail sales (and even demographic variables) will
not fully capture. Second, the recognition that bans differ in type is essential for efforts to understand the ways in
which systematic differences across units of observation can produce misleading results. Our analysis illustrates the
importance of both points – we find that differences in trends between ban passers and non-ban passers, along with
changes in trends over time, can generate spurious evidence that city-level bans increase restaurant revenue (Tables 2
and 3) and state-level bans decrease restaurant revenue (Table 5).
V. Discussion
Implications for Studies on the Effect of Smoking Bans on Restaurants
One of the best of the many studies relating restaurant bans to restaurant revenues is by Bartosch and Pope
(2002), who examine the effect of municipal bans on taxable restaurant meal receipts in Massachusetts, using a sample
running from 1992 to 1998.35 Bartosch and Pope employ specifications containing various controls, including fixed
effects and time trends. Their variable of interest is a linear trend for the months following the implementation of a
smoking ban. They find the coefficient on that variable to be statistically insignificant, and conclude that smoking bans
therefore did not affect restaurant sales.
The results of our analysis suggest a potential problem with Bartosch and Pope’s specification: It fails to
account for pre-ban trends in restaurant sales. What if restaurant sales in ban-passing cities were trending differently
than in non-ban cities before the bans were passed? For example, if the ban-passing cities were experiencing faster
growth in restaurant revenues before the bans went into effect (as we find for California), and the result of the bans was
to cause revenue growth to fall to the level of that of non-ban cities, Bartosch and Pope’s specification would pick up
the same statistically insignificant coefficient on the post-ban time trend it does. Yet the true effect of restaurant bans
on sales growth would be negative. In short, although Bartosch and Pope’s general conclusion may be correct, their
analysis is insufficient to indicate whether or not Massachusetts’ restaurant smoking bans affect restaurant revenues.
Alamar and Glantz (2004) develop an interesting alternative approach, in which they examine whether
35Some
Massachusetts municipalities enacted comprehensive restaurant smoking bans, some enacted laws simply
requiring separately ventilated smoking rooms, and some enacted no private place antismoking laws at all.
15
restaurant smoking bans affect the market value of restaurants (when restaurants are put up for sale). Alamar and
Glantz find that restaurant smoking bans are positively associated with the market value of restaurants, controlling for
revenue, and conclude that smoking bans therefore make restaurants more valuable.
Yet again, the potential problem is a lack of attention to preexisting trends, this time in property values. If
communities that saw faster growth in property values were also more likely to pass restaurant smoking bans, Alamar
and Glantz’s specification would produce the positive association between bans and restaurant market values that they
find, but there need not be anything causal in the relationship. Particular concern is warranted because the time period
covered, combined with the geographical concentration of smoking bans, renders the need to control for trends in
property values acute. Between 1991 and mid-2002 (the period of the Alamar and Glantz study), the vast majority of
local comprehensive restaurant smoking bans (99 out of 118) were implemented in two states, California and
Massachusetts; furthermore, as discussed, California passed a state ban in 1995 which prohibited smoking at restaurants
in every California community. Both California and Massachusetts saw enormous run-ups in property values over the
same period. Because Alamar and Glantz do not control for trends in property values, it is impossible to tell whether
they are picking up the effect of smoking bans, or simply the fact that communities that enacted restaurant smoking
bans experienced more rapid growth in (or even just higher levels of) property values than did communities that did not
enact bans.
Implications for Studies on the Effect of Smoking Bans on Smoking
A number of studies have investigated the effect of smoking bans on smoking behavior.36 Our analysis
suggests that the results of such studies should be treated with caution. To illustrate, consider Evans et al. (1999),
perhaps the best extant study on the effect of workplace bans on smoking. Evans et al. analyze a longitudinal data set
of responses to 1991 and 1993 NHIS surveys, and conclude that smoking rates are lower in firms that ban smoking
(taking self-selection of workers into account). However, because Evans et al. use longitudinal data, it impossible for
them to establish whether or not firms with workplace smoking bans were experiencing a differential decline in
36The idea is that a ban raises the cost of smoking (by making smoking less convenient) and
thus reduces the quantity of
smoking. For overviews of the literature, see Chaloupka and Warner (1999, 37-38), Evans et al. (1999, 731-2), and Tauras (2006,
334). Also see, e.g., Saffer and Chaloupka (2000) on the effects of advertising bans.
16
smoking before the bans were implemented. Furthermore, Evans et al. note that in their sample, there was a large
increase between 1991 and 1993 in the fraction of workers employed by firms banning smoking in all work areas (from
61.7 percent in 1991 to 73.4 percent in 1993). Over the same period, the number of U.S. communities with
comprehensive workplace smoking bans increased from six to 34, and 26 of the 28 new bans were enacted in
California. Therefore, Evans et al.’s results may be heavily influenced by California in a manner that their simple
inclusion of state cigarette taxes (the study’s only location-based measure) will not capture. In short, although Evans et
al.’s conclusions may be correct, additional tests are needed before one can confidently infer causality from their
results.37
What Causes a Restaurant Smoking Ban?
The evidence from our analysis is consistent with increases in restaurant sales leading to restaurant smoking
bans, not vice versa. But what is the causal mechanism? There are two principal possibilities: Restaurant sales growth
affects smoking bans directly (i.e., is causal), or a third factor influences both smoking bans and restaurant sales growth.
While a thorough investigation of this issue is beyond the scope of our analysis, we can speculate.
First, it is possible that restaurant sales growth causes restaurant smoking bans directly, by reducing the
incentive of restaurant owners to lobby against bans. Restaurant owners and restaurant associations have typically been
the most vocal opponents of restaurant smoking bans.38 If restaurateuring is a zero profit industry with a perfectly
elastic supply of inputs, fast revenue growth – i.e., rapid increases in market demand – simply leads to entry. Even if a
smoking ban reduces restaurant sales growth somewhat as compared to no ban, an incumbent restaurant owner in a
rapid growth area will be affected (if at all) only in the short run (i.e., during the time it takes the rate of entry to adjust).
If the ban leaves restaurant rents intact, the only long run effect of a ban would be less entry than would have otherwise
37Also note that similar econometric problems may arise when estimating the effects of advertising bans.
If, for example,
cigarette advertising bans tend to be adopted by countries that already have rapidly decreasing cigarette consumption, then
regressions with year dummies and country fixed effects (e.g., Saffer and Chaloupka 2000) may yield erroneous evidence that
advertising bans reduce cigarette consumption. Naturally, the bias would be in the other direction if cigarette advertising bans tend
to be adopted by countries with rapidly increasing cigarette consumption. Whether such a bias exists is an important question for
future research.
38See, for example, the discussion and citations in Bartosch and Pope (2002, ii38).
smoke.org).
17
See also the ANRF website (www.no-
occurred. By contrast, if total restaurant revenues are growing very slowly (or are stagnant or declining) and entry
requires incurring a sunk cost, a restaurant smoking ban that reduces market demand to the point where prices fall will
be opposed by incumbent firms.
Alternatively, rather than there being a direct causal relationship between bans and revenue, an omitted factor
may explain both. Human capital is a plausible candidate – as we suggest in Section III, human capital may affect both
the likelihood of passing a ban (if wealthy, highly educated people are disproportionately opposed to other people
smoking and more effective at lobbying) and the frequency of dining out. We found trend differences between ban and
non-ban cities to be robust to the inclusion of obvious demographic proxies for human capital (e.g., education, income),
but a third factor, imperfectly correlated with these measures, may cause smoking bans. For example, restaurant
smoking bans may be more likely in communities with residents who are health conscious or more engaged in outdoor
sports; alternatively, political variables, such as voter activism or the aggressiveness of antismoking groups may
influence the passage of restaurant smoking bans (see Chaloupka and Saffer 1992; Hersch, Del Rossi, and Viscusi
2004; Shipan and Volden forthcoming). Such factors are likely related to education and income, but a key component
of the relationship may not be captured by the Census variables we employ.39
VI. Conclusion
In this paper, we have investigated the relationship between comprehensive restaurant smoking bans and
restaurant revenues, examining 267 California cities over a twenty-five year period. Our findings provide evidence that
localities passing bans differ exogenously from localities that do not, and that they differ in a manner that confounds
naive econometric attempts to estimate the causal effects of smoking bans. For California, these exogenous differences
remain even after controlling for city fixed effects, time dummies, and demographic factors. If in this respect California
is representative of the country as a whole, then studies based on data sets from other states will have similar problems.
And, of course, if California and other states that led the way in passing bans – notably Utah and Massachusetts – are
not representative (especially in terms of rapid growth in the restaurant industry during the 1990s), then inference using
39For
example, health conscious people may tend to be wealthy, but wealthy people as a whole may not be health
conscious.
18
state-level data will face obstacles similar to those we demonstrate for city-level data. In this light, properly estimating
the effects of smoking bans (on smoking or on restaurant revenues) requires a more thorough understanding of why
some jurisdictions pass bans while others do not.
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20
Table 1: Naive Specifications by Type of Ban, 1980-2004
Any Ban
1
2
3
4
Restaurant
Restaurant
Restaurant
Restaurant
Revenue
Revenue
Revenue
Revenue
1980-2004
1980-2004
1980-2004
1980-2004
-0.0459488
-
-
-0.011898
0.0375595
(7.44)
(7.05)
City Ban
0.0132173
(0.54)
(0.55)
-
-
0.0476426
0.0391737
(7.64)
(7.29)
0.0591985
0.0530823
(2.53)
(2.53)
State Ban
Both Bans
Other Taxable Sales
Time
0.3930517
0.3929712
(73.86)
(73.90)
0.0063177
0.0037068
0.0062685
0.0036693
(39.00)
(31.10)
(38.48)
(30.62)
City Fixed Effects
included
included
included
included
Quarterly Seasonal
included
included
included
included
Correction for
yes
yes
yes
yes
Autocorrelation
ρ = 0.83
ρ = 0.74
ρ = 0.83
ρ = 0.74
R2 (within)
0.1156
0.3238
0.1165
0.3253
obs
24193
24193
24193
24193
Dummies
21
cities
267
267
267
267
quarters
99
99
99
99
t statistics in parentheses.
Dependent variable and independent variables (except smoking ban variables, Time,
and dummies) measured in logs.
22
Table 2: City Ban Results, 1980-2004
City Ban
1
2
3
4
Restaurant
Restaurant
Restaurant
Restaurant
Revenue
Revenue
Revenue
Revenue
1980-2004
1980-2004
1980-2004
1980-2004
0.0278366
0.0283496
0.0485734
0.044877
(1.64)
(2.22)
(3.12)
(3.71)
Other Taxable Sales
Time
0.3927224
0.3259433
(73.43)
(53.6)
0.0055748
0.0030987
(41.18)
(34.57)
City Fixed Effects
included
included
Quarterly Seasonal Dummies
included
included
Time Period Dummies
Correction for Autocorrelation
included
included
included
included
yes
yes
yes
yes
ρ = 0.83
ρ = 0.75
ρ = 0.82
ρ = 0.74
R2 (within)
0.1129
0.317
0.2227
0.3705
obs
24193
24193
24193
24193
cities
267
267
267
267
quarters
99
99
99
99
t statistics in parentheses.. Dependent variable and independent variables (except
smoking ban variable, Time, and dummies) measured in logs.
Table 3: City Ban Results by Time Period, 1980-1994, 1995-2004
City Ban
Other Taxable Sales
1
2
3
4
Restaurant
Restaurant
Restaurant
Restaurant
Revenue
Revenue
Revenue
Revenue
1980-1994
1980-1994
1995-2004
1995-2004
-0.0003415
-0.0169005
0.0214885
0.0356972
(0.01)
(0.74)
(1.28)
(2.51)
0.3071133
0.4372404
23
(38.44)
(55.14)
City Fixed Effects
included
included
included
included
Time Period Dummies
included
included
included
included
yes
yes
yes
yes
ρ = 0.67
ρ = 0.58
ρ = 0.70
ρ = 0.64
R2 (within)
0.2778
0.3912
0.2551
0.4063
obs
Correction for Autocorrelation
13782
13782
10156
10156
cities
255
255
267
267
quarters
59
59
39
39
t-statistics
in parentheses. Dependent variable and independent variables (except
smoking ban variable and dummies) measured in logs.
Table 4: Differences in Trends Between Ban-Passing and Other Cities
1
2
3
4
5
6
Restaurant Revenue
Restaurant
Restaurant
Restaurant
Restaurant
Restaurant Revenue
1995-2004
1980-1994
City Ban
City Ban*Time
Ever Ban*Time
Other Taxable Sales
Population 1990*Time
High School 1990*Time
College 1990*Time
Income 1990*Time
Rent 1990*Time
Home Value 1990*Time
Revenue
Revenue
Revenue
Revenue
1980-1994
1980-1994
1995-2004
1995-2004
-0.0367351
-0.0088357
-0.0217451
0.0129353
0.002689
0.0181047
(0.72)
(0.17)
(0.43)
(0.36)
(0.08)
(0.51)
0.0000554
0.0001431
0.0000949
-.0000762
0.0000317
-0.0000609
(0.07)
(0.17)
(0.12)
(0.18)
(0.08)
(0.15)
0.0008334
0.0013693
0.0019311
0.0024648
0.0024137
0.0030000
(2.22)
(3.75)
(5.26)
(3.77)
(3.72)
(4.65)
0.3061662
0.2918734
0.2773008
0.4392894
0.3706293
0.3555628
(38.27)
(35.83)
(33.80)
(55.48)
(41.58)
(39.35)
-0.0010565
-0.0077537
0.0000188
-0.0031905
(8.93)
(10.22)
(0.12)
(5.42)
-0.0005624
-0.0081403
0.0019615
0.0092538
(0.49)
(3.21)
(1.54)
(2.71)
-0.0010702
0.0001023
-0.0018802
-0.0086664
(2.17)
(0.11)
(4.48)
(6.91)
0.006443
0.0025431
0.0031126
-0.0007902
(7.13)
(1.25)
(2.73)
(0.31)
0.0005718
0.0032002
0.00079
0.0015791
(0.42)
(1.61)
(0.44)
(0.63)
-0.0027115
0.0015439
-0.0016259
0.0037957
24
(4.65)
(1.89)
Population 2000*Time
High School 2000*Time
College 2000*Time
Income 2000*Time
Rent 2000*Time
Home Value 2000*Time
(2.35)
(3.55)
0.0067531
0.0033159
(9.09)
(5.69)
0.0078655
-0.0087546
(2.71)
(2.57)
-0.0003433
0.0076886
(0.32)
(6.44)
0.0026646
0.0070306
(1.33)
(2.73)
-0.0011769
-0.0053449
(0.62)
(2.16)
-0.0042849
-0.0055881
(5.48)
(5.48)
City Fixed Effects
included
included
included
included
included
included
Time Period Dummies
included
included
included
included
included
included
Correction for Autocorrelation
yes
yes
yes
yes
yes
yes
ρ = 0.58
ρ = 0.60
ρ = 0.54
ρ = 0.64
ρ = 0.63
ρ = 0.61
R2 (within)
0.3915
0.41
0.4271
0.4097
0.4302
0.4547
obs
13782
13782
13782
10156
10156
10156
cities
255
255
255
267
267
267
quarters
59
59
59
39
39
39
t statistics in parentheses.
Dependent variable and independent variables (except smoking ban variables, Time, and dummies) measured in logs.
Table 5: Effects of the State-Level Ban in Cities Without Municipal Bans
State Ban
1
2
Restaurant Revenue
Restaurant Revenue
1980-2004
1980-2004
-0.0378087
(6.78)
Other Taxable Sales
Dummy 1989
0.4104262
0.4012202
(73.82)
(71.79)
-0.0354792
(5.53)
Dummy 1990
-0.0769534
(9.02)
Dummy 1991
-0.0899179
(8.89)
Dummy 1992
-0.123288
25
(10.74)
Dummy 1993
-0.1531029
(12.01)
Dummy 1994
-0.1903584
(13.64)
Dummy 1995
-0.2192906
(14.44)
Dummy 1996
-0.2404854
(14.67)
Dummy 1997
-0.261195
(14.86)
Dummy 1998
-0.2632027
(13.99)
Dummy 1999
-0.2735062
(13.67)
Dummy 2000
-0.2952737
(13.92)
Dummy 2001
-0.3019641
(13.43)
Dummy 2002
-0.293944
(12.37)
Dummy 2003
-0.3019628
(12.07)
Dummy 2004
-0.3122987
(11.88)
Time
0.0034722
0.0072216
(28.04)
(21.21)
City Fixed Effects
included
included
Quarterly Seasonal Dummies
included
included
Correction for Autocorrelation
yes
yes
ρ = 0.74
ρ = 0.72
R2 (within)
0.3348
0.3557
obs
21420
21420
cities
238
238
quarters
99
99
26