Article Text


Is it time to abandon youth access programmes?
  1. J R DiFranza1
  1. 1Department of Family Medicine and Community Health, University of Massachusetts Medical School, 55 Lake Avenue, Worcester, MA 01655, USA; difranzj{at}
    1. C M Fichtenberg2,
    2. S A Glantz3
    1. 2Department of Epidemiology, Johns Hopkins School of Public Health, Baltimore, Maryland, USA
    2. 3Center for Tobacco Control Research and Education, University of California, San Francisco, San Francisco, USA
      1. P Ling4,
      2. A Landman4,
      3. S A Glantz4
      1. 4Center for Tobacco Control Research and Education, University of California, San Francisco, San Francisco, USA; glantz{at}

        Statistics from

        In their editorial “It is time to abandon youth access tobacco programmes”, Ling et al1 base their argument on an in press meta-analysis of youth access interventions by Fichtenberg and Glantz.2 These authors conclude that there is no proof that youth access interventions work to reduce youth smoking rates. Sadly, this analysis includes 10 methodological flaws, each one of which individually renders the conclusions scientifically invalid.2 One of the invalid figures from the Fichtenberg analysis has been reprinted in Tobacco Control.1

        Three of the eight studies included in the meta-analysis did not involve any actual enforcement of the law, and the authors of a fourth study concluded that enforcement was inadequate because of a political backlash from merchants.3–7 The inclusion of at least three of these studies is scientifically unjustifiable as it has been established for over a decade that merchant education programmes alone are ineffective at attaining the levels of merchant compliance that can be expected to reduce youth access to tobacco.8,9 Three out of the five studies included in the analysis of the effects of youth access restrictions on past 30 day smoking did not involve enforcement. The authors inappropriately list the Baggot study as including enforcement and fines when in fact the inspection method was so flawed that no merchant was ever caught and none were prosecuted.4

        In the Baggot study, merchant compliance is reported as 100%.4 None of the stores sold to youths aged 13 years or under during enforcement checks, yet 100% of smokers among the community youths surveyed reported that they regularly bought tobacco from stores and only rare subjects reported ever having been turned down. The study's authors correctly concluded that the compliance inspections were an invalid measure of youth access. Yet Fichtenberg and Glantz included this invalid data in the analyses of a threshold effect and it is also included in the figure printed in Tobacco Control.1,2

        It was improper to include a study from England where the legal age is 16 years as the majority of secondary school students would be of legal age to purchase and no impact on youths ages 14–15 would be expected.4

        It was improper to include the study from Australia. In addition to the fact that the study involved no enforcement, 46% of the students in the intervention group actually lived outside the intervention area!5

        The meta-analysis improperly combined studies of different designs including cohort, cross sectional, controlled interventions and non-controlled interventions.

        Combining these studies is also inappropriate because the ages of the youths, and the methods used to test compliance, differed dramatically from study to study. For example, a compliance rate of 82% for a 14 year old is equivalent to a compliance rate of 62% for a 17 year old.10 A compliance rate of 42% for behind the counter sales is equivalent to a compliance rate of 58% for self service sales.11 Differences in the techniques used to measure compliance render all of the computations and conclusions in this paper invalid.

        The authors' basic premise is that the percentage change in merchant compliance should correlate with the percentage change in the prevalence of youth smoking. The use of this measure represents a straw man. In my review of 176 articles concerning youth access, I cannot recall anybody in this field ever suggesting that the change in percentage of merchant compliance is an appropriate measure of youth access. To the contrary, there is wide agreement among experts in this field that absolute levels of merchant compliance above 90%, as measured through realistic compliance checks using youths close to the legal limit, will be necessary to effect a change in the prevalence of youth smoking.12

        In the figure presented in the Tobacco Control editorial,1 intervention communities are being inappropriately compared to control communities from other continents and legal systems. If the authors wanted to compare smoking rates and youth access interventions across communities, a random sample should be used, uniform measures should be employed, and other confounding factors such as socioeconomic status and the cost of tobacco should be controlled for. When this type of analysis has been performed on a community and state level of analysis, reductions in youth smoking have been observed.13,14

        It has been known for centuries that the prevalence of smoking increases during adolescence. This factor must be controlled for in cohort studies by the inclusion of a matched control group. During the period when most of these studies were conducted there was a secular trend of dramatically rising teen smoking rates observed in English speaking countries. Since merchant compliance would also be expected to increase over time in these intervention studies, it would be expected that a positive association between the intervention and smoking prevalence would be seen in both cohort and cross sectional studies if enforcement were completely ineffective. The meta-analysis does not appropriately incorporate control communities for each intervention community. Only three control communities are included for 15 intervention communities across seven studies.

        In the same analysis, the few control communities are inappropriately included as additional “data points” in the mix. Baseline data rather than outcome data were used for one intervention community. These procedures indicate that the intention of this analysis was not to determine the impact of the interventions as the authors state.

        The Fichtenberg and Glantz article2 is strongly reminiscent of the “scientific” papers secretly commissioned by the now defunct Tobacco Institute. It is sad that the scientific literature continues to be poisoned for political ends. The Tobacco Control editorial1 which was based on this travesty of science also excludes and misinterprets data which contradict the authors' long held biases.15


        Authors' replies

        Since DiFranza's criticism of the editorial by Ling et al1 concentrates mostly on criticism of the paper by Fichtenberg and Glantz, published in Pediatrics,2 we are writing to respond to these criticisms separately. We recognise that this is unusual, since the standard procedure would have been for DiFranza to write to Pediatrics after the paper was published there. DiFranza, however, chose to write to Tobacco Control (based on a preprint we provided him as a courtesy), so we are responding here.

        The premise of youth access programmes is that if merchant compliance reaches a high enough level, it will reduce youth access to cigarettes and, therefore, youth smoking. The goal of our analysis was to see if, based on the available literature, there was a relation between merchant compliance and youth smoking. Whether or not the laws were being enforced at the time and, if so, in what manner, is irrelevant to this analysis. If youth access programmes work because high merchant compliance leads to lower smoking, there should be an association between high merchant compliance rates and low youth smoking rates, regardless of what led to those rates of compliance. If an intervention designed to increase merchant compliance was successful, we should see high compliance rates and low smoking. If the intervention was not successful, because they did not include enforcement as DiFranza suggests, then we should see low compliance and low smoking. Both of these cases would contribute to our test of the hypothesis that increased merchant compliance was associated with reduced smoking. The data to not exhibit such an association (fig 1A of Fichtenberg and Glantz2).

        All youth access programmes measure merchant compliance through undercover sales attempts by underage youth, as was done in the Bagot3 study. If merchant compliance measured in this way is not an accurate reflection of youth access, then none of the studies of youth access that base their effectiveness on merchant compliance are valid. The goal of our analysis was not to determine if compliance is a good measure of youth access, but rather to relate the most commonly used metric for measuring the effectiveness of youth access programmes, namely merchant compliance, to youth smoking rates.

        DiFranza says that we should not include studies from England because the legal age to purchase cigarettes is 16 years. We see no reason why youths aged 14–15 would not be affected by laws limiting purchase of cigarettes to those 16 and older.

        DiFranza objects to including data from Australia, because 46% of the students lived outside the enforcement area.4 As discussed above, whether or not active enforcement was involved is irrelevant to our analysis of the association between merchant compliance with youth access laws and youth smoking prevalence. All that is important is that compliance and smoking was assessed in the same community. In this case the authors point out that for the follow up survey, 46% of students in the intervention community—which was defined based on school location—did not live in the intervention area. They conclude that this would be a problem if these children bought cigarettes closer to home rather than to school. Since there was no residence information from the baseline survey it was not possible to limit the analysis to students living in the intervention area. Nevertheless, we chose to include the study in our analysis despite this limitation. It is important to note that the results of this study were consistent with the others.

        There is no problem with combining studies of different design in a quantitative meta-analysis, as long as all studies are measuring the same end point.5,6 As was reported in the methods section of our paper, the quantitative meta-analysis only included controlled studies.

        DiFranza objects to combining studies because the ages of the youths, and the methods used to test compliance, differed. While we agree that factors such as age and sex of the youths may impact measured merchant compliance, we did not expect this variability to mask the effect of youth access programmes, if they actually affected youth smoking rates. The small number (five) of controlled studies of youth access programmes which reported youth smoking made it impossible to stratify according to the age of the youths used in the compliance checks.

        DiFranza objected to our evaluation of the change in youth smoking prevalence as a function of change in merchant compliance on the grounds that it is necessary to obtain compliance rates above 90% to have an effect on youth smoking prevalence.7 In addition to the fact that the data show no empirical evidence to support the hypothesis of such a threshold (fig 1A in Fichtenberg and Glantz,2 reproduced as fig 1 in Ling et al1), our basic premise is that if youth access programmes actually reduced youth smoking, higher compliance rates would be associated with lower youth smoking rates. We examined this hypothesis in two ways. First, we compared compliance and smoking rates in all communities for which both variables were measured at the same time. Since this is an ecological analysis which does not take into account trends over time, we then examined the relation between changes in compliance and changes in smoking in case what mattered was whether there was a reduction in sales to youth rather than the absolute level of compliance at one time (fig 1B in Fichtenberg and Glantz2). The data presented in fig 1A show that there is no threshold of effectiveness at 90% compliance. Smoking rates for communities with compliance above 90% vary between 19.4–32.5%, with a mean of 25.9%. In communities with compliance rates below 90%, smoking rates vary between 15.6–37.7% with a mean of 25.7%. There is no evidence of a threshold of effectiveness.

        DiFranza suggested that we control for a wide variety of socioeconomic and demographic factors, because “When this type of analysis has been performed on a community and state level of analysis, reductions in youth smoking have been observed”.8,9 Given the small number of studies available, it was not possible to explore the effects of potential confounders such as other tobacco control policies, price of cigarettes, and socioeconomic status. Nonetheless, in our discussion we report the results of population based studies, including but not limited to, those referred to by DiFranza. Chaloupka and Pacula,9 in the study cited by DiFranza, do indeed find that statewide enactment and enforcement of youth access laws was associated with reduced youth smoking. However, in another analysis10 the same authors found that this effect was restricted to black teens. The study by Siegel et al8 does indeed find that the presence of youth access laws was associated with decreased smoking initiation rates; however, they conclude that this decrease was not mediated by decreased access because youths reported no decrease in perceived access.

        In the first part of our analysis (fig 1A), we compared compliance and smoking in all communities for which there was information. Since we were not trying to assess the effects of interventions but rather to see if there is a relationship between compliance and smoking, we did not make a distinction between control and intervention communities, or between baseline and follow up data. As DiFranza points out, this type of analysis does not take into account temporal trends or other potential confounders. In order to take these into account we performed a quantitative meta-analysis using only controlled studies (n = 5). This analysis yielded a pooled effect of a 1.5% decrease in youth prevalence (95% confidence interval 6% decrease to 3% increase).

        Tutt cited a paper by his group11 that was not included in our meta-analysis because it was not listed in Medline or cited in any of the other papers we located. Adding his results to those we report, however, does not affect the conclusions of our analysis. The correlation between merchant compliance and 30 day teen smoking prevalence including these data is 0.042 (p = 0.799) compared with 0.116 (p = 0.486) reported in fig 1A of our paper.2 Likewise the correlation between change in merchant compliance and change in youth smoking is −0.163 (p = 0.504) compared with 0.294 (p = 0.237) without it. Thus, including the data from Tutt et al11 actually strengthens the conclusions in our paper.

        It is time for enthusiasts of youth access interventions to recognise that while these interventions may have seemed like a good idea, they do not achieve their primary goal of reducing youth smoking. All that happens is that youth obtain their cigarettes from other sources.21


        Both Tutt and DiFranza are missing the larger point of our editorial. Unlike public health forces, the tobacco industry has unlimited resources to push their agenda. We made the point that in a real world of limited public health resources, those resources are better concentrated where they have been shown to be most effective. Youth access is clearly not that area. Tobacco industry documents show that the industry has run rings around public health forces when it comes to youth access, successfully co-opting it to the point that it now serves the industry's purposes.

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