The benefits of preventing smoking onset are well known. Existing reviews clearly demonstrate that increasing the prices of tobacco products reduces smoking prevalence and cigarette consumption. However, only a small number of studies included in existing reviews have examined smoking onset (the transition between never smoking and smoking). Moreover, existing reviews provide limited quality assessment of the data and methods utilised. This paper systematically searches for and critically reviews studies that examine the impact of tobacco prices or taxes on smoking onset. Most studies reviewed have important methodological limitations, including recall bias; a general failure to apply diagnostic tests, to discuss the choice of estimators and distributional assumptions and to conduct sensitivity analysis; and a reliance on empirical approaches that are methodologically weak. On the whole, existing studies do not provide strong evidence that tobacco prices or taxes affect smoking onset.
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Decades of research have clearly demonstrated that the single most effective method to reduce smoking prevalence and cigarette consumption is to increase tobacco prices.1–8
Existing reviews,1–8 however, have important methodological limitations and have weaker generalisability to low- and middle-income countries: they provide limited quality assessment of the data and methods used by the studies and include a relatively small number of studies conducted in low-income and middle-income countries (one exception is Rice et al,7 who attempted to assess the quality of studies). Moreover, as only a small number of studies examine the decision to initiate smoking (the transition between never smoking and smoking), they do not provide definitive evidence regarding the impact of tobacco prices on smoking initiation/onset (as compared to smoking participation, smoking intensity or smoking cessation). Examining factors that influence youth smoking may focus on the decision to initiate smoking or the decision to be a current smoker (ie, participation is conditional on having initiated smoking). The distinctions in these approaches are important. Approaches that model participation do not allow one to distinguish between former smokers who have quit smoking and those who have never smoked. The addictive nature of nicotine plays a critical role in the decision to continue smoking.9 In contrast, the role of addiction in the decision to initiate smoking is of lesser importance. Differences between participation and smoking onset elasticities vary with age—younger individuals are substantially more likely to initiate smoking than older individuals.10
Determining the impact of tobacco prices on smoking onset in low-income and middle-income countries is of particular importance, given how young their populations are and given that many low-income and middle-income countries are experiencing a rise in non-communicable diseases associated with tobacco use.11 With this in mind, to the extent possible, special attention is given to studies conducted in low-income and middle-income countries.
Criteria for considering studies for this review
Types of study
I consider all studies that examine the relationship between the prices of or taxes on tobacco products and smoking initiation or onset.
I include all studies, regardless of date of publication or data collection.
Geographic location and coverage
I include all studies, regardless of the geographic coverage (eg, state, province, municipality).
I include all studies that meet the inclusion criteria, regardless of the language of publication.
Types of ‘outcome’ measures
I include only studies that examine initiation or onset. That is, I only include studies that examine the transition between never smoking and smoking. I exclude any of the following: participation, consumption, cessation, substitution, escalation or persistence.
Search methods for identification of studies
I searched the computerised bibliographic database MEDLINE via PubMed and EconLit. Unpublished literature was also searched via Google and Google Scholar. Four specialty journals were hand-searched (Health Economics, Journal of Health Economics, Nicotine & Tobacco Research and Tobacco Control) and the references from recent reviews were examined.1–8 Searches were last conducted on 21 February 2012. The following search strategy was employed:
MEDLINE: (price*[Title/Abstract] OR ‘Taxes’[MeSH] OR tax*[Title/Abstract]) AND (smok*[Title/Abstract] OR tobacco*[Title/Abstract] OR ‘Tobacco’[MeSH] OR ‘Smoking’[MeSH]);
EconLit: (TI(tobacco* or smok* or cigar*) or AB(tobacco* or smok* or cigar*)) and (TI(tax* or price*) or AB(tax* or price*)).
The review process had four stages:
Studies identified in the electronic and hand-search were pre-screened for relevance.
Relevant studies were assessed for inclusion.
Data were extracted using a standardised form.
The extracted data were analysed and synthesised in user-friendly tables.
The search of electronic bibliographic databases yielded 2732 potential articles (MEDLINE: 1998; EconLit: 734), 336 of which (MEDLINE: 166; EconLit: 248) were selected for further investigation. A further 12 studies were identified via Google and Google Scholar. No additional studies were identified through hand-searches. The review of abstracts (and, when necessary, full articles) yielded a total of 27 studies,10 ,14–40 a substantially larger number than reviewed in any other single study or review. Nearly all studies, however, were conducted using data from the USA and to a lesser extent data from other high-income Organisation for Economic Co-operation and Development countries (Australia, Canada, France, Great Britain, Ireland, Spain and Sweden). Only one study27 used data from a low-income country (until the late 2000s, Vietnam was categorised as a low-income economy by the World Bank. It is now categorized as a lower-middle-income economy).⇓⇓⇓
Tables 1–3 present a synthesised overview of each study included in this review. Studies are presented in chronological order, based on year of publication. The following study characteristics are presented: (1) authors, year of publication, country, journal; (2) methods (statistical analyses, number of time periods modelled); (3) data (type, population, source, sample size); (4) a description of the price/tax measure and, where applicable, how the price/tax measure was adjusted for inflation; (5) covariates; (6) testing for mis-specification; (7) sensitivity analyses; (8) results and (9) whether the sources of support were clearly acknowledged. It is important to note that the descriptions provided represent the reviewer's interpretation and are not necessarily the interpretations provided by the authors. I return to this point later. The appendix presents a glossary of technical terms to facilitate the technical discussion in the following sections.
On the whole, most studies have important limitations, some serious enough that considerable caution is needed when interpreting results. The limitations can be categorised into two broad groups: data and measurement issues; and methodological issues.
Data and measurement issues
Measures of price and of smoking onset can suffer from a variety of measurement issues. Both are examined in turn. First, Tauras et al18 pointed out that when one uses retrospective data, the current location may not match the location at the time of decision. Studies that use a price indicator measured at subnational level (eg, state or province) and that experience high levels of within-country migration or that use long time series will be disproportionally affected. Second, Forster and Jones16 pointed out that their results may be sensitive to their choice of deflators. This issue is likely to be more relevant to studies that use prices measured at province or state level. Such studies, however, typically use national price indices to deflate province-level and state-level prices. One exception is Zhang et al,31 who used consumer price index all-items measured at province level.i Sensitivity analyses using alternative measures of inflation appear to be warranted. Third, prices collected at different points in time may not be comparable. For example, Laxminarayan and Deolalikar27 used cigarette price data for 1992/1993 and 1997/1998 that are not comparable, as they are for different brands that are not in the same price category. Fourth, when one uses longitudinal data, current prices may not match those at the time of decision. With one exception,24 the longitudinal data used have not been collected on an annual basis. Hence most authors resolve to regress smoking onset that occurred over a 2-year period on contemporaneous prices.ii
Taurus and Chaloupka41 stressed that recall bias—imperfect recall by respondents—when using retrospective data can introduce substantial measurement errors. This is especially problematic when respondents are asked to recall the exact year or age at which they initiated smoking when such events occurred decades earlier. How smoking onset is defined varies widely across studies. Little distinction is made between experimentation, occasional smoking, current smoking or daily smoking. Emery et al42 argue that previous studies have not had adequate measures of smoking experience to examine whether prices may affect teens’ smoking decisions. Here again, sensitivity analysis seems particularly warranted. Tauras et al18 and Cawley et al24 present results for such sensitivity analysis. Models with alternative measures of smoking onset are compared and their findings suggest large differences in effect sizes.
The limited number of covariates that are exogenously determined before or when individuals initiated smoking, particularly when using retrospective data, is an additional concern. For example, several studies include individuals’ highest educational attainment, an indicator that is generally not exogenously determined before or when individuals initiate smoking.
As first highlighted by Forster and Jones,16 there is a general failure to apply diagnostic tests to assess the fit of the empirical models of smoking onset. Similarly, the choice of estimators and distributional assumptions are seldom discussed. For example, standard duration models (continuous and discrete) rest on the assumption that each individual will eventually fail (ie, die or, in this case, start smoking). Such an assumption is reasonable when mortality is the outcome under study but can be problematic when smoking onset is the outcome being modeled, as a large proportion of the population never starts smoking. López Nicolás,21 and Kidd and Hopkins26 compared split population models (ie, models that treat the probability of eventual smoking onset as an additional parameter to estimate) and non-split models and found vastly different effects. Similarly, how the issue of duration is incorporated into discrete time model is seldom discussed. This can be important, as ignoring time dependency in the baseline hazard produces a model that is more or less equivalent to an exponential model (ie, the hazard probability is flat with respect to time).43 Another example is the failure to examine the parallel regression assumption that is implicit in ordinal regression models. The parallel regression assumption requires that the separate equations for each category differ only in their intercepts (ie, the slopes are assumed to be the same when going from each category to the next).44
Tauras et al18 and Cawley et al24 submitted that there is not enough variation in cigarette prices within the USA to employ fixed effects (FE). Including FE disallows any of the average unit-to-unit variations in regressors from being used to estimate the parameters of the model. In the USA's case, it amounts to examining only if intra-state changes in smoking onset are associated with intra-state changes in prices. In addition, variables that change slowly will tend to have relatively large SEs. Using ordinary least squares, Cawley et al24 regressed cigarette prices on state and time FE, and found a coefficient of determination of 0.99. This can be of consequence. For example, the main result of DeCicca et al19 (that taxes are not associated with smoking onset) is dependent on the inclusion of state FE.
Forster and Jones16 ,23 estimated pooled models and models split by gender, and discriminated between them by using likelihood ratio tests. Their results suggested that models should be analysed separately for men and women. Of interest are the results of Kidd and Hopkins,26 and Cawley et al.24 Both found that the effects of prices on smoking onset are substantially different across genders. Several studies included price as time-invariant covariates when using duration models. For example, Douglas and Hariharan10 included measures of prices when the respondents were 18 years old and the change in price between the ages of 15 and 18 years, Grignon and Pierrard25 included prices when the respondents were 14 and 18 years old, Malhotra and Boudarbat36 included prices when the respondents were 15 years old, and Glied20 explored the effect of taxes when the respondents were 14 years old on ‘late’ initiation (defined as initiation that occurred after the age of 16 years). Treating price as a time-variant variable is conceptually more intuitive, as the decision whether or not to start smoking is an ongoing decision, made on the basis of current information.14 Several studies10 ,24 ,28 ,32 ,39 that use duration analysis techniques include a measure of age as an explanatory variable in the duration component of the model. This can be problematic, as age is, by construction, related to age of initiation.iii
Additional limitations include possible correlations between taxes and tobacco control measures or antismoking sentimentiv and, for studies that use longitudinal data, the minimal number of panels available.
Synthesis of results
Despite the relatively large number of studies identified, the considerable heterogeneity in their methodological approaches and the limitations described above greatly limit the ability to make conclusive statements about the impact of tobacco prices on smoking onset. Additionally, several studies use the same data, so the number of independent estimates is substantially smaller than the number of studies. If one considers studies that use a split population duration approach with retrospective data and treat price as a time-variantv covariate, the evidence is fairly limited. Douglas and Hariharan10 (using data from the USA, 1954–1987), Forster and Jones16 ,23 (using data from Great Britain, 1920–1984) and Madden22 (using data from a survey of Irish women, 1960–1998) found small effect sizes that were not statistically significant; López Nicolás21 (using Spanish data, 1957–1990), and Kidd and Hopkins26 (using data from Australia, 1963–1990) found statistically significant but relatively small effect sizes: a 10% increase in prices would delay starting by about 1–1.5 months. Grignon,33 using retrospective data from France, found statistically significant and moderately large effect sizes: a 10% increase in prices would delay starting by about 3–6 months, depending on the specifications.vi
Studies that use a binary approach (eg, probit, logit or linear probability models) provide mixed evidence. DeCicca et al,19 ,37 using longitudinal data from the USA, found large and statistically significant effect sizes for some specifications; for other specifications, small and not statistically significant effect sizes were found. Zhang et al,31 using longitudinal Canadian data, found large and statistically significant effect sizes (the elasticity of initiation with respect to cigarette prices was −3.36), while Cawley et al,29 using USA longitudinal data, found large and statistically significant effect sizes, but for boys only (the elasticity of initiation with respect to cigarette prices was −1.2). Liu,38 using retrospective data from nine large repeated-cross-sectional surveys conducted between 1992 and 2003 in the USA, found large and statistically significant effect sizes for some specifications, and small, wrongly signed and not statistically significant effect sizes for other specifications.
As mentioned earlier, only one study used data from a low-income country. Laxminarayan and Deolalikar,27 using longitudinal data from Vietnam, examined the association between the odds of initiating cigarette smoking and waterpipe tobacco smoking between 1992/1993 and 1997/1998 and changes in the prices of the two tobacco products. They found that changes in the price of cigarettes are significantly and negatively associated with the decision to initiate cigarette smoking (the elasticity of cigarette smoking initiation with respect to cigarette prices was −1.18). With respect to the impact of waterpipe tobacco prices on waterpipe smoking initiation, they found large effect sizes (the elasticity of waterpipe smoking initiation with respect to waterpipe tobacco prices was −1.56) that were, however, not statistically significant. An important limitation of Laxminarayan and Deolalikar's study is that the cigarette price data for 1992/1993 and 1997/1998 are not comparable, as they are for different brands that are not in the same price category. Additionally, waterpipe tobacco prices were not measured in 1997/1998 and had to be imputed.
Studies that use discrete time hazard models generally provide evidence that prices have a statistically significant impact on smoking onset. These findings, however, should be interpreted with caution, as only one study40 discusses how duration is incorporated. As stressed earlier, ignoring time dependency in the baseline hazard produces a model that is more or less equivalent to an exponential model.43 Moreover, all studies assume that each individual will eventually fail (ie, start smoking). DeCicca et al,19 ,34 using longitudinal data from the USA (1988, 1990, 1992, 2000), found, on the whole, large and statistically significant effect sizes for some specifications and small and not statistically significant effect sizes for other specifications. More specifically, DeCicca et al15 found ethnicity differences: they found that prices have a statistically significant impact on smoking onset for Hispanic people but not for those of white and African-American ethnicity. Tauras et al,18 using longitudinal data from the USA (1991–1999),vii found statistically significant and large effect sizes that were robust to alternative specifications. Cawley et al,24 using longitudinal data from the USA (1997–2000), found statistically significant and large effect sizes that were robust to alternative specifications, but for men and boys only. Kim and Clark,30 using longitudinal data from the USA (1994/1995 and 2001/2002), found some fairly large effect sizes for some specifications that were, however, not statistically significant. Etilé and Jones,40 using retrospective data from France, found large and statistically significant effect size for women only. Kenkel et al,35 using retrospective data from China, found small effect sizes that were not statistically significant. These results, however, were sensitive to alternative specifications. Nonnemaker and Farrelly,39 using retrospective and longitudinal data from the USA, found that taxes and prices were generally statistically significant and had a moderately large impact, with effect sizes being largest for African-American youth.
Lastly, studies that use more traditional duration models generally provide evidence that prices have a statistically significant impact on smoking onset. Coppejans et al,32 using longitudinal USA data (1988, 1990 and 1992) and Cox proportional hazards models, found that cigarette price levels and price volatility were statistically significantly associated with the hazard of starting smoking. Hammar and Martinsson,17 using Swedish retrospective data (1945–2000) and log-logistic and gamma duration models on a subsample of smokers, found large but wrongly signed effect sizes that were not statistically significant. Arzhenovsky,28 using longitudinal data from Russia and Cox proportional hazards models, found that the price of ‘cheap’ brands, but not the price of ‘expensive’ brands, was statistically significantly associated with the hazard of starting smoking.
A number of studies that did not meet the inclusion criteria merit discussion. Hamilton et al46 assessed the effect of the tobacco tax cuts made in 1994 on the smoking habits of Canadians by comparing short-term trends between provinces where taxes were cut and provinces where taxes were not cut. Hamilton et al observed that the rates of starting cigarette smoking were higher in the provinces where taxes had been cut than in those where taxes had not been cut. Auld,47 using cross-sectional and retrospective data from a Canadian youth survey conducted in 1994 and endogenously switching binary response regressions, examined the impact of cigarette prices on ‘early initiation’ (if a respondent had smoked at least one whole cigarette for 7 consecutive days and was 14 years old or younger when he/she first began to do so) and ‘late initiation’ (if a respondent aged 15–19 years (in 1994) reported having smoked on at least 21 days in the last month). Auld found that prices had a statistically significant impact on early initiation but no impact on late initiation. Farrelly et al48 evaluated the effectiveness of the National Truth Campaign, a prominent USA national youth smoking prevention campaign. Using a longitudinal survey of adolescents aged 12–17 years who were interviewed annually from 1997 to 2004 and a discrete time hazard model, Farrelly et al examined whether variable levels of exposure to antismoking messages over time and across 210 media markets affected smoking initiation. The authors included a time-varying measure of price at state level in their model but did not report its impact. Sen and Wirjanto,49 using a small subsample from a longitudinal survey conducted in South-Western Ontario, Canada, in the early 1990s, found that changes in taxes had fairly large impacts on the initiation and persistence of youth smoking. This study was excluded because it is not possible to disentangle the impact of tax changes on initiation and persistence. Finally, a number of studies examined the impact of price on smoking transitions, uptake or escalation and generally concluded that prices can prevent transitions to higher thresholds of smoking uptake.42 ,50–53
The review points to a number of lessons. First, the extent of the evidence base has been and still is unappreciated (eg, Cawley et al29 and Sen and Wirjanto49). Second, the distinction between smoking initiation/onset (ie, the transition from never smoking to smoking) and smoking participation or smoking uptake is sometimes blurry. Studies that do not examine smoking onset are, at times, cited as evidence that prices have a significant impact on smoking onset (eg, Zhang et al31 and Rice et al7). Third, the interpretation of a study's results may differ between the authors’ own interpretations and the interpretations of the reader (as they may differ between readers). For example, on the one hand, one reader might find that the body of work of DeCicca et al15 ,19 ,34 ,37 provides evidence that prices do not affect smoking onset. On the other hand, if one dismisses the FE specifications, the same body of work can provide evidence that prices do, in fact, impact smoking onset. The interpretation of effect sizes can be even cloudier. A particular concern is the frequent comparison of the elasticities obtained from duration models that are often not comparable across studies, as different ‘time origins’ are used. For example, Forster and Jones,16 and López Nicolás21 assumed that individuals are first exposed to the risk of starting at the age of 0 years; Etilé and Jones,40 Kidd and Hopkins,26 and Madden22 at the age of 10 years; and Douglas14 at the age of 11 years.
Based on the current review, the evidence is not sufficient to conclude that prices (or taxes) affect smoking onset. It is important to note that this review does not conclude that there is evidence of no effect. Rather, this review concludes that the evidence is too limited to make any conclusive statements about the impact of tobacco prices or taxes on smoking onset. Similarly, this review does not challenge the overwhelming evidence that prices and taxes reduce overall tobacco use and, more specifically, tobacco use among youth.
The conclusion of the current review is at odds with the conclusions of previous reviews. Rice et al7 concluded that ‘[o]verall, the evidence suggests that price is effective in deterring young people from starting to smoke’. (p. viii). The very low number of studies included in the Rice et al review probably explains the conflicting conclusions.viii Chaloupka et al,54 writing on behalf of the International Agency for Research on Cancer (IARC) Handbook Volume 14 Working Group, concluded that there is sufficientix evidence to conclude that ‘[i]ncreases in tobacco excise taxes that increase prices reduce the initiation and uptake of tobacco use among young people, with a greater impact on the transition to regular use’. Explaining the conflicting conclusions of this review and that of IARC is more arduous. This review's emphasis on methodological approaches and the differing search strategies and inclusion criteria (the IARC study evaluated 17 studies, including two49 ,55 which are excluded from this review) may, at least partially, explain the conflicting conclusions. IARC's approach, which emphasises the role of expert opinion, may also explain the conflicting conclusions. Research has highlighted the limitations of expert opinion. For example, there is evidence that experts tend to use non-systematic methods when they review research.56
This review has several limitations. First, although the search strategy was systematic, the review process was not. Screening for relevance, assessment for inclusion, data extraction and interpretation were conducted by a single reviewer. It is better methodology that at least two independent reviewers conduct such tasks.12 ,13 Second, a priori methods of assessment were not used because of the lack of quality assessment tools and the heterogeneity in the methods utilised.12 ,13 Readers are urged to refer to original studies and not to rely uncritically on the descriptive information of the individual studies provided in this review. Third, a number of the studies reviewed failed to provide important methodological information, which rendered quality assessment difficult. As discussed earlier, most studies that used discrete time hazard models failed to discuss how the issue of duration was incorporated into their models. One study even failed to report how discrete time hazard models were estimated (eg, probit, logit, complementary log-log, etc).34
This review highlights a number of data and methodological limitations in existing studies that examined the impact of prices or taxes on smoking onset, and concludes that limitations are pervasive and serious enough that considerable caution is needed when interpreting results. Consequently, future research of higher methodological quality is warranted. The dearth of studies conducted using data from low-income and middle-income countries is an additional concern. The generalisability of studies conducted in high-income economies to low-income and middle-income settings, notably to countries with dramatically different patterns of tobacco use and tobacco control environments, is fairly limited. The contributions of additional studies that use similar USA data and similarly weak methodologies pale in comparison to the potential of methodologically rigorous studies conducted in low-income and middle-income settings.
What this paper adds
Existing reviews clearly demonstrate that increasing the prices of tobacco products reduces smoking prevalence and cigarette consumption.
Only a small number of studies included in existing reviews have examined smoking onset (the transition between never smoking and smoking); moreover, existing reviews provide limited quality assessment of the data and methods used.
This review identifies a substantially larger number of studies than those reviewed in any other single study or review, assesses their data and methods and, on the whole, finds that the evidence is not sufficient to conclude that prices (or taxes) affect smoking onset.
Financial support from the Social Sciences and Humanities Research Council of Canada, and the Centre for Health Economics and Policy Analysis is acknowledged. I thank Jeremiah Hurley, Michael Boyle, Michel Grignon, Joy de Beyer, Jinhu Li, Teh-wei Hu, Noori Akhtar-Danesh, Pete Driezen and members of the polinomics seminar at McMaster University for helpful comments and discussions.
Glossary of technical terms
Duration analysis: analysis in which the dependent variable measures the duration of time that units spend in a state before experiencing some event.43 Duration analysis is also known as survival analysis, event history analysis, failure-time analysis and reliability analysis.43 ,57
Continuous-time duration analysis: duration analysis in which time is measured as a continuous variable (ie, it can take on any non-negative value)58; the exact time of duration is known or assumed to be known.57 ,59
Split population duration model: duration model in which the probability of eventual failure is less than one (ie, the duration model does not assume that all units will eventually fail); also known as a split population survival time model, mixture model or cure model.16 ,60
Cox proportional hazard model: duration model in which the baseline hazard is left unspecified, treated as an unknown function of time; the most commonly used duration model.61–63 The baseline hazard function, which depends on time (but not on covariates), summarises the pattern of duration dependence, assumed to be common to all units.64
Duration (or time) dependency: the extent to which the conditional hazards of the events of interest rise or fall over time.65 The hazard rate is, roughly, an indication of how likely failure is to occur at any given time, provided the unit has survived until that time.66
Duration independence: a hazard rate that is time invariant (ie, the risk of failure does not depend on how long a unit has survived).66
Duration dependence: a hazard rate that is time variant (ie, the risk of failure varies with time).66
Elasticity: a measure of the responsiveness of one variable to a change in the value of another variable. Specifically, the ratio of the percentage change in the former to the percentage change in the latter.67
Price elasticity (of demand): a measure of the responsiveness of the demand for a good or service to a change in its price.67
Fixed effects (FE): generally refers to effects (or coefficients) that are constant if they are identical for all groups in a population.68 Including FE disallows any of the average unit-to-unit variations in the regressors from being used to estimate the parameters of the model.57 ,69 See Gelman (2005) for a discussion of various definitions of fixed effects.68
Multinomial regression model: regression model in which the dependent variable measures a nominal outcome (ie, an unranked categorical outcome).44
Ordinal regression model: regression model in which the dependent variable measures an ordinal outcome (ie, a rank-ordered categorical outcome). Ordered logit and ordered probit models are the most commonly used models for ordinal outcomes in health and social sciences.44
Parallel regression assumption (proportional odds assumption for the ordinal logit model): an assumption implicit in ordinal regression models which requires that the separate equations for each category differ only in their intercepts (ie, the slopes are assumed to be the same when going from one category to the next).44
Retrospective data: longitudinal data obtained using retrospective recall methods (ie, reporting events that happened in the past).70
Heaping: when respondents cannot recall a specific value and provide a ‘prototypical’ response near the actual value, resulting in the over-representation of certain values.70
Longitudinal data: data in which the same units are observed over multiple time periods. For example, data pertaining to individual-level changes over time, observed periodically over a certain duration.71
Competing interests None.
Provenance and peer review Not commissioned; externally peer reviewed.
↵iii Co-linearity between age and elapsed time at risk (ie, duration) makes it difficult to identify their separate effects.
↵iv DeCicca et al19 argued that if taxes are correlated with tobacco control measures such as advertising bans and smoke-free policies, or antismoking sentiment, estimates of the price or tax responsiveness will be inaccurate. This issue is mostly relevant to studies conducted in federated states such as the USA, Canada and India, where taxes and tobacco control measures may differ substantially across states or provinces.
↵v A number of studies used a split population duration approach with retrospective data but included a time invariant measure of price. These studies are described in all three tables.
↵vi Grignon's working paper33 was subsequently published in the Journal of Socio-Economics.44 The price elasticity of smoking onset estimates, however, do not appear in the journal version. Hence the findings discussed refer to Grignon's working paper.
↵vii Eight and 10 graders in 1991, 1992 and 1993 with follow-up surveys at 2-year intervals until 1999.
↵ix IARC evaluates the strength of the evidence using four categories: inadequate/no evidence, limited evidence, strong evidence and sufficient evidence. ‘Sufficient evidence: an association has been observed between the intervention under consideration and a given effect in studies in which chance, bias and confounding can be ruled out with reasonable confidence. The association is highly likely to be causal’.54
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