The Effect of Graphic Warning Labels on Cigarette Packages in OECD/EU Countries Ashok Kaul †§ Manuel Schieler † * Christian Agethen † October 30, 2018 Abstract This paper investigates the effect of Graphic Warning Labels (GWLs) on cigarette consumption in OECD/EU countries from 2002 to 2015. We analyze a comprehensive cross-country panel data set and employ fixed effects difference-in-differences regressions, as well as synthetic control methods to evaluate the policy. The average treatment effect obtained from the difference- in-differences approach suggests that GWLs significantly reduce cigarette consumption. Our main result is that GWLs indeed significantly reduced cigarette consumption, but only in the first few years after the introduction as our synthetic control analysis shows. We find the average treatment effect to peak in the second year and then to decline continuously, leading to statistically insignificant results beyond the third year. The estimated effect size is similar, but smaller, when we include illicit in addition to legal cigarette consumption, indicating a potential substitution effect. Finally, our results indicate a modest anticipation effect one year prior to implementation. JEL classifications: I120; I180; L660; M380 Keywords: Graphic Warning Labels; Smoking Behavior; Tobacco Control Policies; Policy Evalu- ation * Corresponding author: [email protected]. † Saarland University, Department of Economics, Campus Bldg. C3.1, Saarbr¨ ucken D-66123, Germany. § University of Zurich, Department of Economics, Z¨ urichbergstrasse 14, Zurich CH-8032, Switzerland. This research did not receive any specific grant from funding agencies in the public, commercial, or not-for- profit sectors. The authors are grateful for the valuable remarks from participants of the 2018 EEA-ESEM conference in Cologne. 1
Transcript
The Effect of Graphic Warning Labels on CigarettePackages in OECD/EU Countries
Ashok Kaul † § Manuel Schieler † * Christian Agethen †
October 30, 2018
Abstract
This paper investigates the effect of Graphic Warning Labels (GWLs) on cigarette consumption
in OECD/EU countries from 2002 to 2015. We analyze a comprehensive cross-country panel
data set and employ fixed effects difference-in-differences regressions, as well as synthetic control
methods to evaluate the policy. The average treatment effect obtained from the difference-
in-differences approach suggests that GWLs significantly reduce cigarette consumption. Our
main result is that GWLs indeed significantly reduced cigarette consumption, but only in
the first few years after the introduction as our synthetic control analysis shows. We find the
average treatment effect to peak in the second year and then to decline continuously, leading to
statistically insignificant results beyond the third year. The estimated effect size is similar, but
smaller, when we include illicit in addition to legal cigarette consumption, indicating a potential
substitution effect. Finally, our results indicate a modest anticipation effect one year prior to
∗ Corresponding author: [email protected].† Saarland University, Department of Economics, Campus Bldg. C3.1, Saarbrucken D-66123, Germany.§ University of Zurich, Department of Economics, Zurichbergstrasse 14, Zurich CH-8032, Switzerland.This research did not receive any specific grant from funding agencies in the public, commercial, or not-for-profit sectors. The authors are grateful for the valuable remarks from participants of the 2018 EEA-ESEMconference in Cologne.
Do Graphic Warning Labels (GWLs) on cigarette packages curb cigarette smoking? The need
for researchers to answer this question is indisputable, given that GWLs have experienced
a rapid rise from only one country implementing them in 2001 to as many as 105 in 2017
(Canadian Cancer Society, 2016). Among tobacco control policies, tax increases, smoking
bans, and media campaigns have been found to reduce smoking prevalence and cigarette
consumption in a large body of literature.1 The literature on GWLs is, however, ambiguous.
Since 2001, as the first country to implement the policy, Canada was at the center of
previous studies. Huang et al. (2014), Azagba and Sharaf (2013), as well as Hammond et al.
(2004) analyze smoking behavior in Canada and find GWLs not only to decrease cigarette
consumption and smoking prevalence, but also to increase attempts at quitting. Supportive
evidence is provided by Borland et al. (2009) and Hammond et al. (2007), who extend the
scope of the analysis to Australia and the United Kingdom. By contrast, a regulatory impact
analysis by the U.S. Food and Drug Admission does not find a significant reduction in smoking
prevalence due to GWLs in Canada. Gospodinov and Irvine (2004) do find a reduction in
cigarette consumption, but argue that this finding might be driven by other tobacco control
policies (i.e., tax increases) and a secular decline in smoking.
Monarrez-Espino et al. (2014) review a wide array of studies which are concerned with
the effects of GWLs, and conclude that the literature so far has failed to provide conclusive
evidence for (or against) an effect of the policy. In particular, they describe previous studies
as heterogeneous (for example, in their design, definitions, and methodology) and often to be
methodologically unsound. Contrary to potential effects on actual smoking behavior, cognitive
effects of GWLs (i.e., quit intentions, health awareness, perceptions, and so forth) appear to
be relatively well-documented and more commonly analyzed in the literature (Noar et al.,
2016).
The growing body of literature on this topic reveals several issues that leave the question
1A comprehensive general overview is provided by Chaloupka and Warner (2000), and a more recent summaryby Wilson et al. (2012). Gallet and List (2003) and Evans et al. (1999) analyze tax increases, Wildmanand Hollingsworth (2013) and Anger et al. (2011) study smoking bans, and Blecher (2008) and Saffer andChaloupka (2000) consider advertising bans.
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about the effectiveness of GWLs essentially unanswered. First, there is no consensus on the
measure of effectiveness. While the majority of studies focus on cognitive effects or intentions,
only a few are concerned with actual smoking behavior, measured as smoking prevalence or
cigarette consumption. Second, studies employing convincing empirical strategies for estimat-
ing the effect of GWLs are scarce. From a policy evaluation perspective, the vast majority of
studies fails to make use of pre- and post-treatment observations, as well as appropriate control
units to their full extent, if at all. Third, the scope of previous studies is mostly limited to one
or—at the most—very few countries that have implemented GWLs. Thus, drawing general
conclusions on the effectiveness of GWLs is questionable, due to heterogeneous tobacco control
policies in these few countries and other confounding factors influencing smoking behavior.
This present paper therefore aims to provide an analysis that alleviates these concerns.
Our measure of effectiveness is cigarette consumption, which can capture both consequences
of effective tobacco control policies. First, a lower prevalence due to quitting and second,
a lower number of cigarettes smoked per smoker due to reduced consumption. To account
for potential substitution effects between the legal and the illicit cigarette markets, we use
cigarette consumption as legal cigarette consumption per capita (legal cigarette consumption),
and as the sum of legal cigarette consumption and non-duty-paid cigarettes per capita (total
cigarette consumption). We analyze a cross-country panel data set of 36 OECD/EU countries
from 2002 to 2015, in terms of introductions of GWLs in about half of these countries at
different points in time. Methodologically, we use two strategies to investigate this tobacco
control policy. First, we use a similar fixed effects difference-in-differences approach as does
Blecher (2008), who analyzes the effect of advertising bans on smoking behavior. Second, as
our main tool of analysis, we use synthetic control methods for multiple treated countries, as
in Cavallo et al. (2013) to construct more accurate control units for each country introduc-
ing GWLs. By construction, the latter approach facilitates an investigation of the treatment
effect’s development over time, as the estimates are period-specific.
In the fixed effects regression, the estimated treatment effect suggests that GWLs lead
to a significant average decline over the post-treatment period of up to 9.1% for legal and
8.7% for total cigarette consumption. Applying synthetic control methods, the estimated effect
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peaks two years after the implementation, with a significant reduction (relative to the control
group) of 12.5% percent for legal and 11.3% for total cigarette consumption, respectively. From
the second year onwards, we find the effect to decline continuously, leading to statistically
insignificant results beyond the third year. This result can be interpreted as a fade-out of the
treatment’s effect. Incidentally, we also find suggestive evidence of a small anticipation effect
one year prior to the policy’s implementation.
The remainder of this paper is structured as follows. Section 2 describes the data set and
our estimation strategy. Section 3 presents the empirical results of the fixed effects difference-
in-differences regressions and synthetic control methods, as well as sensitivity analyses. Section
4 concludes with a brief summary and discussion of our main findings.
2 Data
We analyze a cross-country panel data set covering 36 member countries of the OECD/EU
from 2002 to 2015. Observations are annual and the panel is balanced, providing us with a
total of N = 504 country-year observations. Our measures of smoking behavior are per capita
legal cigarette consumption and total cigarette consumption. The former is defined as retail
sales volumes in sticks of duty-paid, machine manufactured cigarettes, whereas the latter
includes non-duty-paid (illicitly traded) cigarettes in addition.2 Using both variables takes
the possibility into consideration, that a potential reduction in legal cigarette consumption
following the implementation of GWLs is attributable to smokers switching to illicitly traded
cigarettes without GWLs. Both indicators are sourced from Euromonitor.3
Our data set further includes real prices for legal cigarette consumption (provided by
Euromonitor),4 population data (15 years and older) and real GDP (both from the World
2The literature makes a criticism concerning Euromonitor’s data on illicitly traded cigarettes. Most notably,Blecher et al. (2013) argue that there are “striking inconsistencies between country-specific estimates for thesame years published in different editions of [Euromonitor’s reports].” Thus, we use data from one editionexclusively, that is, the most recent edition. Note that we do not take a stance on the quality of the data,but rather employ this variable as an extension to legal cigarette consumption. Moreover, we are not awareof any other data source that provides more reliable cross-country estimates.
3See http://www.euromonitor.com/, last accessed on October 30, 2018.4Real prices are calculated from the retail value (including taxes) as provided by Euromonitor.
the treatment group consists of 14 countries, whereas the 18 remaining countries (i.e., where
GWLs were not in effect by 2015) enter our analysis as potential controls.
3 Estimation Strategy
Our approach to estimating the average treatment effect of GWLs is twofold. In the first part,
we employ fixed effects difference-in-differences regressions, which is arguably the standard
approach to analyzing policy effects in a setting such as ours. We begin by setting up the
difference-in-differences model similarly to Blecher (2008), who investigates the impact of
advertising bans on tobacco consumption, using aggregate level data. In the second part, we
apply synthetic control methods as a natural extension to the difference-in-differences model.
Our twofold approach is essentially comparable to Kreif et al. (2016), who also conduct both
a difference-in-differences analysis and extend it with a synthetic control analysis.
3.1 Difference-in-Differences Regression
In our difference-in-differences regression model, we employ a two-way error component speci-
fication where the error term is decomposed into uit = αi +λt + εit. This decomposition allows
to control for unobserved confounders that vary (i) over country i, but are constant over the
years t (i.e., country fixed effects αi) and (ii) over the years t, but are constant across coun-
tries i (i.e., time fixed effects λt).7 The remainder εit is white noise. In addition, we estimate
a one-way error component specification (uit = αi + εit) that adopts a common linear time
trend rather than time fixed effects λt. For each specification, we estimate Equation 1 with the
dependent variable Cit being per capita (i) legal cigarette consumption and (ii) total cigarette
consumption.
Cit = β1Pit + β2Yit + β3Dit + uit (1)
rate of change for both legal cigarette consumption and total cigarette consumption from one year to anotherexceeds ±30%, without an external event such as a substantial price change explaining this development.
7Baltagi et al. (2000) provide examples of αi and λt in the context of modeling cigarette demand.
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Explanatory variables are real prices for legal cigarette consumption (Pit), real GDP per capita
(Yit), and a binary treatment dummy (Dit). Estimated coefficients can be interpreted as (semi-)
elasticities, since all variables (except for Dit) enter the regression model in logarithms.
At its core, the unbiasedness of the estimated treatment effect (i.e., β3) in difference-in-
differences models relies on the parallel trends (or parallel paths) assumption. That is, in the
absence of the treatment, the dependent variable would have developed similarly in both the
control and the treatment group.
In the context of health economics, this assumption is often violated, for example, due to
confounding treatments (Kreif et al., 2016). Especially with an increasing number of countries
and time periods, confounding policies become more likely to appear, and often impossible to
sort out (Craig et al., 2017).
3.2 Synthetic Control Method
The second part of our estimation strategy consists of an approach that relaxes the assumption
of parallel trends, namely the synthetic control method for comparative case studies (Kreif et
al., 2016). This method allows unobserved confounders to vary over both countries and time,
while assigning unequal weights to countries in the control group (Doudchenko and Imbens,
2017). In addition, the method estimates period-specific treatment effects, which allows us to
investigate the effect of GWLs over time. Because of these features, synthetic control methods
facilitate the construction of more appropriate control groups and render the method “arguably
the most important innovation in the policy evaluation literature in the last 15 years” (Athey
and Imbens, 2017).
We begin this part by establishing the synthetic control method in the version of Abadie
and Gardeazabal (2003) and Abadie et al. (2010) (i.e., only one country receives the treat-
ment). Subsequently, we present an extension and inference technique to cover multiple
treated countries, as in Cavallo et al. (2013). There are t ∈ {1, . . . , T} time periods and
i ∈ {1, . . . , J + 1} countries of which one (e.g., i = 1) receives the treatment (i.e., implements
GWLs) in t = T0 + 1. Thus, J countries remain, where GWLs have not been introduced (i.e.,
the donor pool). We observe T0 pre-treatment and T1 = T − T0 post-treatment periods, while
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1 ≤ T0 < T holds. Following Equation 1, the dependent variable in country i at time t is Cit.
In the actual scenario, CIit is the smoking intensity when GWLs are in effect from t = T0 + 1
on. In the counterfactual scenario, CNit is the smoking intensity if GWLs had not been imple-
mented. The treatment effect for the treated country at time t is then the difference between
both scenarios, i.e. α1t = CI1t − CN
1t . Because only CIit is observable, CN
1t has to be estimated
before α1t can be derived. The synthetic control method does so by searching for a weighted
combination of countries from the donor pool, such that k = M + r pre-treatment predictors
of the treated country are replicated best. In particular, M predictors are linear combinations
of the dependent variable, while other r predictors can be explanatory variables. The (k × 1)
vector X1 contains the predictors of the treated country, whereas the (k × J) matrix X0 con-
tains those of the donor pool. Hence, the countries that constitute the synthetic control group
are weighted such that the difference between X1 and X0 is minimized. The optimization
problem is given by Equation 2:
‖X1 −X0W‖V =
√(X1 −X0W )′ V (X1 −X0W )
W→ min (2)
W is a (J × 1) vector containing the weights of each country in the donor pool.8 Ultimately,
the vector of optimal country weights W ∗(V ) minimizing Equation 2 depends on the predictor
weights stored in V , a (k × k) non-negative diagonal matrix. In practice, there are various
approaches to obtaining V . We follow Abadie et al. (2010) and Abadie and Gardeazabal
(2003)’s recommendation, where V is chosen such that the pre-treatment deviation between
CI1t and CN
1t is minimal, given the k predictors. The measure of deviation is the Root Mean
Squared Prediction Error (RMSPE) of Cit prior to the implementation of GWLs.
So far, there is no consensus among researchers regarding the choice of the k = M + r
predictors.9 Although applications of synthetic control methods typically entail the use of
several lagged outcomes M , a key topic of discussion concerns the number of lags included.
8We follow the original set-up introduced by Abadie et al. (2010) where country weights w2, . . . , wJ+1 arerequired to be non-negative and to sum to one. See Doudchenko and Imbens (2017) for a generalizationallowing country weights to be negative, not summing to one, and allowing for a permanent additive differencebetween the treated unit and the controls—similar to difference-in-differences procedures.
9For a recent discussion on the choice of predictors in the context of specification searching, see Ferman et al.(2018).
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For example, Kreif et al. (2016), Gobillon and Magnac (2016), Bohn et al. (2014), Billmeier and
Nannicini (2013), and Hinrichs (2012) use each pre-treatment observation of the dependent
variable. On the other hand, Abadie et al. (2015), Smith (2015), Kleven et al. (2013), Montalvo
(2011), Abadie et al. (2010), and Abadie and Gardeazabal (2003) use only a selection of
lagged outcomes and linear combinations of the dependent variable (e.g., the mean across pre-
treatment observations in addition to other explanatory variables). As Kaul et al. (2017) show,
using each pre-intervention observation of the dependent variable, together with covariates r
renders all of these covariates irrelevant. Consequently, our modeling choice is reduced to
either using all pre-intervention observations without further covariates, or using a mix of pre-
intervention outcomes and other covariates. Doudchenko and Imbens (2017) reveal substantial
advantages of using many (if not all) lagged outcomes. They recognize that “in terms of
predictive power, the lagged outcomes tend to be substantially more important, and as a
result, the decision on how to treat these other pre-treatment variables need not be a very
important one”.
Thus, we employ all pre-treatment observations of cigarette consumption in our synthetic
control approach.10 Aside from potentially higher predictive power and the best possible fit of
the synthetic control unit in terms of RMSPE, this approach also offers a significant computa-
tional advantage. Obtaining V becomes much easier when using all pre-treatment observations,
since vk = 1T
for all k corresponding to lags of the dependent variable (see Kaul et al., 2017).
To extend the synthetic control method to account for the multitude of treatments that
occur over the course of our observational period, we follow Cavallo et al. (2013)’s approach
to calculate the average treatment effect. There are g ∈ {1, . . . , G} countries receiving the
treatment (i.e., implementing GWLs) at—possibly—different points in time t. Thus, as the
number of pre- and post-treatment periods can differ across countries, we need to diverge from
the common time index t. Cavallo et al. (2013) do this by introducing the so-called lead l,
which indicates the lth period posterior to the implementation of GWLs. The synthetic control
method is now applied separately to each of the treated countries in a first step. Accordingly, we
10Using a set of lagged values in addition to prices and GDP, as in our fixed-effects regression, does not affectour results. In line with Doudchenko and Imbens (2017) and according to our expectations, most of theweight is assigned to the lagged values of our outcome variable.
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obtain G lead-specific estimates of the treatment effect α1,l, . . . , αG,l. To ensure comparability
of the estimated effects between countries, we normalize the dependent variable of a treated
country to be equal to 1 in l = 0.11 In a second step, the estimated treatment effects are
averaged over all G countries, resulting in an average lead-specific treatment effect αl given
by Equation 3:
αl =1
G
G∑g=1
αg,l (3)
Ultimately, we follow Cavallo et al. (2013)’s extension to Abadie and Gardeazabal (2003) and
Abadie et al. (2010)’s approach in conducting exact inference techniques which are similar to
permutation tests. In general, for a treated country g, a placebo study is conducted in which
the synthetic control method is applied to each of the J countries from the donor pool. In doing
so, we derive the exact distribution of the estimated placebo effects. This procedure enables us
to assess whether the estimated treatment effects from any of the G treated countries are large,
compared to their placebo counterparts from the J potential control countries. In particular,
let αPL(j)1,l be the estimated placebo effect for a donor country j which received the placebo
treatment at the same time as country 1 received the actual treatment. We assume that we
are doing inference about negative point estimates at each lead. The lead-specific one-sided
p-value for the estimated treatment effect α1,l is then given by Equation 4:
p-valuel = Pr(αPL(j)1,l < α1,l
)=
∑J+1j=2 I
(αPL(j)1,l < α1,l
)J
(4)
As our objective is to conduct inference on the average (rather than the country-specific)
treatment effect αl, we need to consider that calculating the average treatment effect smooths
out some noise. To take this fact into account, Cavallo et al. (2013) suggest the following
procedure: Derive all placebo effects for each treated country g by using the J donor countries.
Now, for each lead l and each possible permutation, compute the average placebo effect. The
resulting placebo averages are indexed by np ∈ {1, . . . , NPL} and the actual treatment effect
11Normalization is required, because the lead-specific estimates depend on the level of Cit at this point. Wenormalize by dividing the dependent variable in both the actual and counterfactual scenarios (i.e., CI
g,t and
CNg,t) by the value of the dependent variable at the time of the treatment (i.e., CI
g,l=0).
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αl is ranked in the distribution of these NPL placebo effects. Hence, the resulting p-value is
given by Equation 5:
p-valuel = Pr(αPLl < αl
)=
∑NPLnp=1 I
(αPL(np)l < αl
)NPL
(5)
4 Empirical Results
In this section we present our estimates on the average and period-specific impact of GWLs
on cigarette consumption using fixed effects difference-in-differences regressions and synthetic
control methods.
4.1 Difference-in-Differences Regression
As shown in Table 1, depending on the trend and outcome variable, we find an average
decrease over the post-treatment period of between 8.3% and 9.1% respectively. This effect is
statistically significant at the 5% level throughout the model specifications. Accordingly, the
results suggest that GWLs are on average effective in reducing both per capita legal cigarette
consumption and total cigarette consumption over the post-treatment period. The estimated
effects tend to be smaller—in terms of absolute values—when illicitly traded cigarettes are a
component of the dependent variable (i.e., total cigarette consumption). A possible explanation
of this result is a marginal, but statistically insignificant substitution effect between legal
cigarettes and illicit cigarettes without GWLs. With respect to the time trend, using time fixed
effects in addition to country fixed effects (two-way model), the estimated treatment effect is
larger than using a linear time trend (one-way model). Employing time fixed effects, we find
total cigarette consumption to decline on average by 8.7%, while legal cigarette consumption
even drops by 9.1% due to the introduction of GWLs. Our estimates from one-way models
with a linear time trend are slightly smaller. The estimated treatment effect in these one-way
models amounts to an average reduction of 8.3% for total cigarette consumption, and 8.8%
for legal cigarette consumption. Estimated price elasticities range from −0.47 to −0.42 and
are statistically significant at the 1% level. Price elasticities are higher in the legal market,
∗∗∗ p < 0.01; ∗∗ p < 0.05; ∗ p < 0.10; Standard errors are in parentheses. Note: Thecontrol group consists of 18 countries and the treatment group of 14 (see Figure 1).
which is a common observation, due to positive cross-price elasticities between the legal and
the illicit cigarette markets.12 Estimated income elasticities range from 0.59 to 0.81 and are
statistically significant at the 1% level. The magnitude of both price and income elasticities is
consistent with previous findings from the literature (see Gallet and List (2003) and Chaloupka
and Warner (2000) for an overview).
4.2 Synthetic Control Method
Figures 2 and 3 depict the results of our synthetic control analysis for legal and total cigarette
consumption, from 10 years leading up to the introduction of GWLs to 5 years post implemen-
tation.13 In the year of their implementation, we estimate an average decrease in legal cigarette
consumption of 4.3% due to GWLs. Two years later, legal cigarette consumption in the treated
countries is on average 12.5% lower than their synthetic control. After peaking in the second
12On the example of Canada, Gruber et al. (2003) as well as Galbraith and Kaiserman (1997) have shownthat smokers substitute duty-paid with non-duty paid (i.e., illicitly traded cigarettes) to circumvent priceincreases, which—in turn—antagonizes the estimated price elasticity for legal cigarette consumption.
13For the three treated countries (Mexico, New Zealand, and Norway), we were unable to properly match thepre-treatment path of the outcome variables (i.e., we could not construct valid counterfactual scenarios). Ourresults from the fixed-effects regression analysis are robust to this restriction of the treatment group. Re-estimating our specifications from Table 1 without the three countries shows that changes in the estimatedcoefficients are negligible. Table 2 in the appendix provides the respective estimates.
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year, the estimated impact of GWLs declines and is no longer significant beyond the third
year. This fade-out effect is in line with Borland et al. (2009) and Hammond et al. (2007), who
argue that smokers eventually become desensitized and accustomed to being confronted with
GWLs. Another explanation is based on the addictive nature of cigarette smoking, combined
with naive smoker assessments of their future cigarette consumption, as described in Gruber
(2002). Thus, we find that GWLs have a sizable and statistically significant impact on legal
cigarette consumption, but only in the first three years after their introduction.
Incidentally, we detect a possible anticipation effect prior to the adoption of GWLs for
both outcome variables. One year prior to the implementation, legal cigarette consumption in
countries with GWLs is on average 1.6% lower than it would be in the counterfactual scenario.
This effect is comparatively small, yet statistically significant. Malani and Reif (2015) provide
two possible explanations of such anticipation effects. For one thing, prior media coverage
can cause part of an intervention’s actual effect to appear within the pre-treatment period.
Similarly, enacting the legislation—but not actually implementing it in practice—can induce a
similar effect. In the context of cigarette smoking, both examples can apply, since they enhance
the perception of associated health risks, leading to a (temporary) reduction in cigarette
consumption, even before a smoker is directly confronted with GWLs. After all, smokers
are forward-looking in their smoking decision (Gruber and Koszegi, 2001). Finally, a small
gap between the actual and counterfactual scenario is evident in period −7. Both gaps are
explained by extraordinary and sizable price increases in two treated countries, namely France
(28.2%) and Hungary (7.7%). Since only five other treated countries are used to construct this
data point, the two countries exert a substantial influence. We further investigate this issue
in our sensitivity analysis.
The estimated treatment effects for total cigarette consumption show a similar pattern,
although their magnitude is somewhat smaller. In the year of GWL implementation, we find
total cigarette consumption in the treatment group to be on average 3.1% lower than in the
synthetic counterpart. Again, the effect of GWLs has exerted its full effect two years after the
implementation, with the relative difference between the actual and synthetic dependent vari-
able amounting to −11.3%. Comparing the treatment effects among the dependent variables,
13
Figure 2: Average Effect of GWLs on Legal Cigarette Consumption Per Capita.
we find that the estimates for total cigarette consumption are—in terms of absolute values—
about 1 percentage point per period smaller than for legal cigarette consumption. This result
is consistent with our difference-in-differences estimates and might again be attributable to a
small-scale substitution effect between the legal and illicit markets.
4.3 Sensitivity Analysis
We pursue three approaches in order to check the robustness of our estimates. The first is to
refine our two-way difference-in-differences model to include binary dummy variables for each
pre- and post-treatment period of a treated country, as in Gruber and Kleiner (2012).14 In
doing so, we test for a violation of the parallel trends assumption prior to the treatment im-
plementation and use post-treatment estimates to validate findings from the synthetic control
analysis. Figure 4 in the appendix provides the estimated coefficients and their 95% confi-
dence intervals. For legal cigarette consumption, we only find one of the very first periods to
deviate significantly from a common trend. However, an F-test on the joint significance of the
coefficients rejects the null hypothesis of parallel pre-treatment trends. The size and signifi-
cance of the estimates for the post-treatment period support our findings from the synthetic
14Here, the last pre-treatment period serves as the omitted base group.
14
Figure 3: Average Effect of GWLs on Total Cigarette Consumption Per Capita.
control analysis. Given that the validity of the parallel trends assumption is questionable in
our setting, and is also generally untestable (Kreif et al., 2016), we believe that the synthetic
control method provides the most feasible identification strategy of the parameter of interest.
Our second sensitivity analysis entails conducting a leave-one-out study, which is the standard
approach for testing the sensitivity of synthetic control estimates to a specific country in the
data set.15 The multitude of treatments in our analysis enables performing a leave-one-out
study for the treatment group. In doing so, we test the sensitivity of the average treatment
effect to the inclusion of specific countries implementing GWLs. For example, Cavallo et al.
(2013) find their estimated average treatment effect to be driven by two treated countries
with radical political revolutions following the actual treatment, when analyzing the impact
of catastrophic natural disasters on economic growth. Hence, we iteratively exclude one of the
treated countries from our analysis, re-estimate the average treatment effect on legal cigarette
consumption and rerun the full inference procedure. As a result, we obtain 11 estimates of
the average effect of GWLs, as well as their respective placebo distributions. The results from
this approach are presented in Table 3 in the appendix. Irrespective of which treated coun-
15Abadie et al. (2015) recommend iteratively excluding a country from the synthetic control group, in orderto investigate changes in the country weights.
15
try we exclude, the estimated treatment effect reveals a similar pattern to that in our main
analysis. In particular, the decline in legal cigarette consumption due to GWLs intensifies
and is statistically significant (at least) at the 5% level until the second year after the treat-
ment. The subsequent onset of a fade-out effect is also robust to the exclusion of any specific
country from the treatment group. From the second post-treatment period onwards, we find
the treatment effect to decline and eventually become insignificant in the following years.
Lastly, the presence of a potential anticipation effect in the year prior to the implementation
of GWLs is also supported, as the corresponding estimates are significant (at least) at the
5% level throughout. However, for a few of the even earlier pre-treatment periods, we find
the actual and counterfactual scenario to deviate significantly over several runs. In general,
these estimated effects, as well as their respective placebo distributions, need to be interpreted
with caution. As only a few countries contribute observations to the earliest leads, estimates
rely heavily on the exclusion of any further country. For example, the sample size in lead −8
(−9) is insufficient, as we only have data on four (three) countries to estimate the treatment
effect and derive the respective placebo distribution. Nevertheless, a significant decline in legal
cigarette consumption in lead −7 for most runs of this study is striking. The average difference
between the actual and synthetic dependent variable in this lead is driven by extraordinary
price hikes in France (28.2%) and Hungary (7.7%). Accordingly, discarding either one of these
countries renders the lead-specific estimates insignificant and close to zero.
In our third sensitivity analysis, we discard the countries with the fewest pre-treatment
periods (i.e., Australia, Belgium, and Chile) where GWLs had already been introduced in
2006. In doing so, we increase from four to six, the minimum number of periods over which the
synthetic control method mimics the path of a treated country’s dependent variable. A longer
pre-treatment period enables a more accurate representation of the trend and puts less weight
on a single country-year observation. Figures 5 and 6 in the appendix present the estimated
treatment effects and the respective inference for legal and total cigarette consumption. In
general, the results of the sensitivity analyses support our main findings in terms of both size
and significance.
16
5 Conclusion
Our results suggest that GWLs are only temporarily effective in curbing cigarette smoking.
Using difference-in-differences regression models, we find a significant average decrease in legal
cigarette consumption of about 9% over the post-treatment period, due to the intervention.
Employing synthetic control methods, we find the treatment effect—relative to the counter-
factual scenario—to amount to approximately −4% in the year of implementation. This effect
increases to about −12% in the second year after the implementation, but fades out in the
third year and beyond. One possible explanation of this effect is that smokers become desen-
sitized and accustomed to GWLs over time. Another explanation is the occurrence of relapse
after quitting due to GWLs. Identifying the core reasons for this development is certainly a
promising area for further research. We also find evidence of a possible anticipation effect. In
the year prior to policy implementation, we estimate a significant treatment effect of about
−1% for both legal and total cigarette consumption. In general, the findings for both dependent
variables are qualitatively similar, but the measured effect is about 1 percentage point per pe-
riod smaller for total cigarette consumption. This result may hint at a small substitution effect
between the legal and illicit markets for cigarettes. A potential extension of our work, which is
beyond the scope of this present paper, is to evaluate the in- and outflows of illicit cigarettes
between neighboring countries and their relation to tobacco control policies such as GWLs.
The availability and ease of access to illicit cigarettes without GWLs may significantly affect
the demand for both legal and illicit cigarettes. Another useful anchor for future research
would be to extend our analysis beyond the cigarette market. Analyzing potential tobacco
substitutes without GWLs can improve our understanding of differentiated tobacco control
policies and their impact. The rising demand for—so far less strictly regulated—electronic
cigarettes is surely especially relevant in this context.
17
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A Appendix
Difference-in-Differences Regression without New Zealand, Norway, and Mexico
Table 2: Fixed Effects Difference-in-Differences Regression without New Zealand, Norway, and Mexico
Legal Consumption Total ConsumptionPredictor Two-Way One-Way Two-Way One-Way
∗∗∗ p < 0.01; ∗∗ p < 0.05; ∗ p < 0.10; Standard errors are in parentheses. Note:Here, countries that could not be fitted appropriately with Synthetic Controls,i.e. New Zealand, Norway, and Mexico, were excluded. Hence, the control groupconsists of 18 countries and the treatment group of 11 countries (see Figure 1).
Differential Trends in Difference-in-Differences Regression
Figure 4: Pre- and Post-Treatment Trends in Legal and Total Cigarette Consumption Per Capita.
22
Synthetic Control Method without Australia, Belgium and Chile
Figure 5: Average Effect of GWLs on Legal Cigarette Consumption Per Capita (without Australia, Belgium and Chile).
Figure 6: Average Effect of GWLs on Total Cigarette Consumption Per Capita (without Australia, Belgium and Chile).
23
Leave-One-Out Study for the Treatment Group
Table 3: Average Treatment Effects on Legal Cigarette Consumption in a Leave-One-Out Study for the Treatment Group
Leave-One-OutLead AUS BEL CHL GBR CHE TUR FRA ESP DNK HUN IRL
