7
Synthesis of Key Studies Examining the Effect of Smoking Bans on Acute Coronary Events

In this chapter, the committee synthesizes the information yielded by the key studies and discusses the overall weight of evidence from them, their uncertainties, the extent to which the uncertainties affect interpretation of their results, and the conclusions that can be drawn from them.

LIMITATIONS AND SOURCES OF UNCERTAINTY IN KEY STUDIES

Some elements of design and uncertainty in the key studies pose challenges in the interpretation of the studies that are relevant to the effect of smoking bans on acute coronary events: the inherently nonexperimental design of the studies, the hypotheses tested in the studies, the lack of closed study populations, the use of less-than-perfect comparison groups, the need to disentangle the effects of a smoking ban itself from concurrent activities that could affect smoking behavior, exposure assessment, outcome, the time from cessation of exposure to secondhand smoke to changes in disease rates, the biologic plausibility of an effect, analytic issues, and the potential for publication bias. Those are all discussed in this section. When reviewing the key studies, the committee kept in mind the characteristics that would make an ideal study to evaluate the effect of an intervention, a smoking ban, on an outcome, acute coronary events. This was a useful framework but a caveat is needed. The committee looked at the study designs and analyses with the advantage of hindsight; such hindsight is helpful in considering how to design a more rigorous evaluation but does not imply that the study authors should have or could have designed an observational study that addressed all of those elements nor that all of those



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7 Synthesis of Key Studies Examining the Effect of Smoking Bans on Acute Coronary Events In this chapter, the committee synthesizes the information yielded by the key studies and discusses the overall weight of evidence from them, their uncertainties, the extent to which the uncertainties affect interpretation of their results, and the conclusions that can be drawn from them. LIMITATIONS AND SOuRCES OF uNCERTAINTy IN kEy STuDIES Some elements of design and uncertainty in the key studies pose chal- lenges in the interpretation of the studies that are relevant to the effect of smoking bans on acute coronary events: the inherently nonexperimental design of the studies, the hypotheses tested in the studies, the lack of closed study populations, the use of less-than-perfect comparison groups, the need to disentangle the effects of a smoking ban itself from concurrent ac- tivities that could affect smoking behavior, exposure assessment, outcome, the time from cessation of exposure to secondhand smoke to changes in disease rates, the biologic plausibility of an effect, analytic issues, and the potential for publication bias. Those are all discussed in this section. When reviewing the key studies, the committee kept in mind the characteristics that would make an ideal study to evaluate the effect of an intervention, a smoking ban, on an outcome, acute coronary events. This was a useful framework but a caveat is needed. The committee looked at the study designs and analyses with the advantage of hindsight; such hindsight is helpful in considering how to design a more rigorous evaluation but does not imply that the study authors should have or could have designed an observational study that addressed all of those elements nor that all of those 

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 SECONDHAND SMOKE EXPOSURE elements would have been under the control of the researchers. Those char- acteristics are summarized in Table 7-1. The table includes a description of the characteristics of studies and some of the ideals and challenges related to them. Researchers must weigh the benefits of those ideals across all the characteristics because a study that meets all the ideals typically will not be feasible to conduct. For example, it would be difficult to conduct a study with a large sample that requires autopsies for all cases. Furthermore, jour- nals often have page limitations that preclude the publication of detailed analyses, such as sensitivity analyses, which ideally would be included in studies like those discussed here. Although the 11 studies discussed here are observational studies and have limitations inherent to observational studies, it is important that the studies took advantage of natural experiments to directly evaluate the ef- fects of an intervention (a smoking ban and concomitant activities) on a health outcome of interest (acute coronary events). As discussed in Assess- ing the Health Impact of Air Quality Regulations: Concepts and Methods TABLE 7-1 Characteristics and Challenges in Study Designa Characteristics Ideal Research Challenges to Consider • Study population Stable population When using “natural” intervention, • Active surveillance such as smoking ban, it is difficult • Large sample to control many aspects of • Adequate baseline data on population • Population cannot be secondhand-smoke exposure • Individual-level data held constant, because of (such as, smoking status, immigration and emigration • Active surveillance is sometimes secondhand-smoke exposure, preexisting risk possible but would increase factors) costs • Sample size is limited by population covered by smoking ban • If prospective, an observational study can have baseline and individual-level data on secondhand-smoke exposure and risk factors, but is much more expensive to conduct and requires more complex human- subjects use approval • Hospital records are not always a reliable source of data on smoking status

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 SYNTHESIS OF KEY STUDIES TABLE 7-1 Continued Characteristics Ideal Research Challenges to Consider • Occurs at clearly defined • Investigators have no control Smoking-ban intervention time over terms or timing of • No other activities occur smoking-ban legislation, at same time that could implementation, or enforcement affect smoking rates or secondhand-smoke exposure • Need for exposure • If study is prospective, Exposure assessment assessment depends on study design can include air hypothesis tested monitoring or biomonitoring • Exposure data not needed before and after implementation to test effect of smoking of smoking ban, but increases ban costs and biomonitoring • Exposure data needed to requires more complex human- test effect of secondhand- subjects approval smoke exposure • Both morbidity and • Access to data is sometimes Outcome mortality data analyzed inadequate • Confirmation of acute • It is often not practical to coronary event: have autopsies conducted on • Mortality data all cases unless sample is very confirmed by autopsy or small • Conducting an independent independent review of medical records review of mortality data or • Acute MI data clinically confirming morbidity independently confirmed data with standardized criteria clinically with is possible but would increase standardized criteria costs and require more complex human-subjects approval • In absence of independent review, data are only as good as what is recorded • Time between • Period between implementation Time between implementation and implementation and effect is and effect is difficult to effect clear establish because intervention does not occur at clearly defined time (because of other activities concurrent with ban); effect may increase over time because, for example, there are gradual changes in smoking behavior Continued

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 SECONDHAND SMOKE EXPOSURE TABLE 7-1 Continued Characteristics Ideal Research Challenges to Consider • Both comparison population • Use of external control Comparison group (external control) and same population depends on population before and availability of comparable after implementation of population intervention are used • Effect being tested is • Identifying research designs that Biologic plausibility biologically plausible can address biologic plausibility • In hypothesis-generating studies, biologic plausibility is not always known before study is designed Experimental design • Experimental designs • It would not be possible are typically best able to ethically to test effect of demonstrate cause–effect secondhand smoke on acute relationship MIs experimentally • Hypothesis being tested is • Studies are designed to test Hypothesis clarification clearly stated specific hypothesis; users of • Tested hypothesis matches study results should consider question being asked in study hypothesis when interpreting results determining what questions study can answer • Appropriate statistical • Statistical analysis is generally Statistical Design analysis, determined under control of researchers a priori, controls for designing study, but appropriate confounders options could be limited by • Statistical models can be characteristics of available data • If appropriate data are used to control for potential confounders and trends available, choice of model and • Statistical modeling includes assumptions are under control description of modeling of researchers assumptions and sensitivity analysis of impact of model choice and assumptions on modeling results • Negative results are less • Both researchers and journal Publication bias apt to be published than editors should overcome their positive findings preference for publishing positive findings a A study typically cannot attain the ideal for all characteristics, so researchers must weigh the importance of each characteristic and the availability of data when determining study design.

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 SYNTHESIS OF KEY STUDIES for Accountability Research (HEI Accountability Working Group, 2003) in the context of air-pollution regulations, studies of interventions constitute a definitive approach to determining whether regulations have health benefits. French and Heagerty (2008) also discuss the advantages and limitations of longitudinal data for assessing the impact of policy changes. Nonexperimental Design The key studies discussed in this report are of necessity nonexperimen- tal; they are observational or surveillance studies that looked at the effects of a smoking ban on hospital outcomes. Such studies do not typically have a great deal of information on the individual level, including exposures and in some instances smoking status. The results of ecologic smoking-ban studies can, however, support identification of associations and findings of causality (Rubin, 2008). Hypothesis The majority of the key studies reviewed in this chapter were natural experiments in that there was an intervention (a smoking ban) that would lead to a reduction in secondhand-smoke exposure (with either direct evi- dence from a given ban or indirect evidence from bans in other locales that exposure decreased). The studies took advantage of the intervention to test the hypothesis that a reduction in secondhand-smoke exposure leads to a reduced incidence of acute coronary events. Because of a lack of informa- tion on smoking status, most of the studies did not directly address the question of whether a decrease in secondhand smoke decreases the risk of coronary events, but as discussed above, the data do indicate that second- hand-smoke exposure decreased after implementation of the bans studied; therefore, even the studies that did not have information on smoking status provide supportive evidence of the effects of secondhand smoke. As discussed previously, only two studies (Pell et al., 2008; Seo and Torabi, 2007) had information on the smoking status of cases; therefore, only those two directly addressed the question of the effect of secondhand- smoke exposure on nonsmokers rather than the question of the effect of a smoking ban. In both of these studies a decrease in coronary events was observed among nonsmokers after implementation of the smoking ban. It is important to consider the hypothesis tested in a study when inter- preting a study. A number of different hypotheses related to secondhand- smoke exposure could be tested in a study; each would be best evaluated with a different study design, and each would be related to different ques- tions that were asked of this committee. A cohort study could test the hy- pothesis that long-term exposure to secondhand smoke increases the risk of

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 SECONDHAND SMOKE EXPOSURE coronary events. A natural experiment (or quasiexperimental design) could be used to test the hypothesis that a long-term reduction in secondhand- smoke exposure leads to a reduced incidence of events, and a case-crossover design with a detailed examination of the temporal relationships between exposure and incidence of events would be ideal to test the hypothesis that secondhand-smoke exposure triggers acute coronary events in at-risk people (personal communication, J. Kaufman, University of Seattle, Washington, January 30, 2009). Each type of study would answer different questions that are in the charge to this committee. Study Populations The key studies reviewed by the committee look at different popula- tions, or portions of populations, have different information available, and have different sample sizes, some of which are small. The differences in the populations limit the ability to quantitatively compare the changes in risk across the studies and, in some cases, limit the confidence in those studies. The studies, however, are retrospective in nature (with the exception of Scotland) and the populations are designated on the basis of the smoking ban coverage and availability of data. The population should be large enough to minimize problems of non- uniformity over short periods, and the baseline exposure to secondhand smoke should be large enough for the study to have the power to detect changes of public-health relevance. In addition, information on the popu- lation, such as smoking status and other risk factors for acute coronary events or cardiovascular disease that could be confounders in the study, should be available. Ideally, the study population will have been under active surveillance or enrolled in a prospective cohort study, so that the data collected before and after implementation of the ban will be directly comparable; and the population will be closed, that is, it will not change over the period of study. Inevitably, the studies that examined the effect of smoking bans were not closed populations; people were free to immigrate to or emigrate from the region studied and to move back and forth between areas with and without bans. The extent of migration in the communities studied most likely varied from study to study. However, as mentioned in Chapter 1, migration would be expected to decrease the effects of smoking bans on acute coronary events in studies unless smokers were selectively moving out of areas with bans and into areas without bans. Although none of the studies discussed the potential for migration extensively, there is no reason to believe that most of the locations would have a large amount of migration of smokers at the time of the ban and over the relatively short period of observation. One exception might be some geographic areas in New York state that are

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 SYNTHESIS OF KEY STUDIES next to other states. For example, smokers in the New York City area might have lived, worked, or socialized in New Jersey (where a comprehensive statewide smoking ban was not put into effect until April 15, 2006) so that they could smoke. Other areas of the state that are farther from state bor- ders (that is, farther from states that might not have had a smoking ban), however, have been much less likely to be affected by such migration. Simi- larly, people in locations that are more isolated (such as Helena, Montana, or Pueblo, Colorado) or in which bans are widely implemented (such as the entire country of Italy or Scotland) are less likely to have moved because of smoking bans. Thus, although migration in the populations studied is possible, the committee does not believe that migration biased the results of the studies substantially. Comparison Groups The key studies used two types of controls. Some compared acute car- diovascular events in a given population before and during smoking bans (internal control group). Such a study cannot evaluate the effects of other changes over time, and this is a concern especially because in many of the areas under study both rates of smoking and rates of acute cardiovascular disease were going down. There was an exception; one study was able to assess what happened when a ban was lifted. Other studies, instead or in addition, selected a comparison or control population (external control group) from an area that did not implement a ban, but otherwise was similar to the population where the intervention occurred. Such a study can to some extent control for larger trends (secular trends), but the comparison populations could differ from study popula- tions in several ways that might be relevant to the risk of exposure to sec- ondhand smoke and to the incidence of acute cardiovascular events. This would be observed in the pre-ban comparison and would add uncertainty to the results. A before–after comparison is useful if data on individuals are collected. If, instead, grouped population data are used in a before–after comparison, one would need to be assured that there is little mobility. Moreover, if there are other communitywide changes related to tobacco, such as a concur- rent antitobacco advertising campaign, a before–after design will be less able to assess the effect of the ban independently of the other changes; a comparison with an external comparison group (not subject to a ban) may be of value so that concurrent changes can be accounted for. However, the fact that multiple studies that used internal or external control groups have found associations between smoking bans and a decrease in acute MI provides stronger evidence that the association is real and not an artifact related to the control population used.

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0 SECONDHAND SMOKE EXPOSURE Smoking Bans In the 11 key reports reviewed by the committee, the effects of the in- terventions and the effects of events that occurred concurrently with them cannot be separately identified. Some of the studies attempted to quantify or catalog other activities that took place at the time of a smoking ban, but because the relative effects of the different activities on smoking behavior and exposures are unknown and because the activities were not indepen- dent, the committee could not attribute changes in the incidence of acute myocardial infarction (MI) to a particular aspect of a ban. The committee’s conclusions are therefore based on whatever changes occurred at the time of the smoking bans and not on legislation itself. The bans themselves were of varied scope (for example, they covered different types of sites or venues), enforcement of bans has varied, and other interventions often occurred concurrently, such as smoking-cessation and education efforts. As can be seen in Table 6-1, however, most of the bans covered workplaces, including private offices, restaurants, and bars. That could have an effect on the changes in secondhand-smoke exposure in that people could spend about 8 hours or more each day at work compared with typically many fewer hours in restaurants or bars. In the studies reviewed in Chapter 6 there is an attempt to define clearly the specific time at which an intervention occurred. As discussed in Chapter 5, however, smoking bans typically do not occur in a vacuum, so the results of the studies need to be interpreted in the context of all activi- ties that occurred before, after, and at the time of a legislated ban—such as public debate on the law, educational campaigns, voluntary bans in households, and increased support for smoking cessation—and not just in terms of the regulation that was implemented. For example, voluntary bans or other smoking restrictions might precede a legislated ban. The fact that other activities occurred at the same time need not weaken a study, but it can limit the conclusions that can be drawn with respect to what caused observed effects. That is, decreases in adverse health effects that occur with the implementation of a ban cannot necessarily be attributed to the specific legislation; other activities, such as voluntary bans in households or out- reach programs, could underlie the effects. Exposure Assessment To address its charge, the committee must consider the effects of smok- ing bans and the effects of decreases in secondhand-smoke exposure. To do that, the committee assessed the studies to determine whether changes related to the bans are a result of changes in secondhand-smoke exposure. Ideally, in assessing the impact of a change in exposure to secondhand

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 SYNTHESIS OF KEY STUDIES smoke, the size of the change in exposure would be measured to determine whether there is a dose–response relationship. Most of the key intervention studies raise two issues with regard to exposure assessment: a lack of infor- mation on the smoking status of the people with reported cases of acute MI and a lack of information on changes in secondhand-smoke exposure. After a smoking ban is implemented, many smokers quit or decrease the number of cigarettes they smoke, and in the absence of data on smoking status it is difficult to separate a decrease in the number of cases of acute MI due to decreased exposure of nonsmokers to secondhand smoke from a decrease in the number of cases of acute MI due to decreased smoking by smokers. Two of the publications have information on the smoking status of people who had acute MI and analyzed the effects on nonsmok- ers. Seo and Torabi (2007) limited their study to acute MI patients who were nonsmokers, so observed decreases in acute MI are due to decreases in secondhand-smoke exposure. Pell et al. (2008) measured serum cotinine in nonsmokers, so they could draw conclusions about changes in second- hand-smoke exposure at the time of implementation of the ban rather than having to study the effect of the implementation of a smoking ban itself. The relationship between smoking bans and decreases in air concentra- tions of secondhand smoke depends on the concentration of secondhand smoke in the air before the ban, the extent of the ban, and how well the ban is enforced and complied with. None of the key publications, however, contains information on the duration or pattern of exposure of individuals to secondhand smoke. That is, there is no information on how long or how often individuals were exposed before or after implementation of the smok- ing bans. For example, it is not known whether individuals were exposed to high concentrations sporadically for short periods or to low concentrations more consistently or both. Without that information, the committee could not determine whether acute exposures were triggering acute coronary events, chronic exposures were causing continuing damage that eventually resulted in acute coronary events, or a combination of chronic damage and acute exposure led to acute coronary events. Although many of the key publications do not contain air-monitoring or biomarker data to assess the changes in secondhand smoke after ban implementation, other publications on the implementation of smoking bans, either in the regions examined in the key studies or in other regions, show that secondhand smoke decreases after implementation of a ban (see Chapter 2), and the committee concluded that generally the implementa- tion of a smoking ban is associated with decreased air concentrations of secondhand smoke. Secondhand smoke reductions in the venues covered by the bans typically ranged from 50 to 90%. In addition, Pell et al. (2008) did measure serum cotinine in all acute MI cases reported and found that exposures decreased after implementation of a smoking ban.

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 SECONDHAND SMOKE EXPOSURE There is information on compliance and enforcement of the eight smok- ing bans examined in the 11 key studies. Available data indicate compliance or a decrease in markers of secondhand smoke after the implementation of smoking bans in general but not for the specific study populations in the key publications in Italy (Gallus et al., 2006; Gorini et al., 2005; Valente et al., 2007), New York state (CDC, 2004, 2007; RTI International, 2004), and Scotland (Haw and Gruer, 2007; Menzies et al., 2006; Pell et al., 2008; Semple et al., 2007a, 2007b). Although no data on air sampling could be found for Helena, Montana; Pueblo, Colorado; and Saskatoon, Canada, data indicated a high degree of compliance with the smoking bans in those locations (Bartecchi et al., 2006; Lemstra et al., 2008; Sargent et al., 2004). There is no information on compliance, enforcement, or air monitoring for secondhand-smoke markers in Monroe County, Indiana. In contrast, air monitoring in Bowling Green, Ohio (Akbar-Khanzadeh et al., 2004) indi- cated that the magnitude of the decrease in secondhand-smoke markers in air was related to characteristics of the smoking restrictions. The concentra- tion of secondhand-smoke–related compounds was lower in nonsmoking restaurants than in restaurants that permitted smoking in separate rooms. On the basis of those data, the committee concludes that, with the exception of some establishments in Bowling Green, Ohio, the smoking bans evaluated in the key studies appear to have resulted in a large decrease in potential exposure to secondhand smoke. Decreases in acute MIs were seen in the two studies that evaluated effects only in nonsmokers (Pell et al., 2008; Seo and Torabi, 2007). Given those two facts, decreases in sec- ondhand-smoke exposure likely contribute to the decreases in acute MIs after implementation of smoking bans seen in the studies that looked at the overall population (smokers and nonsmokers). The portion of the decrease in acute MIs that can be attributed specifically to changes in secondhand- smoke concentration, however, cannot be determined on the basis of the available data. Outcomes The key studies varied on the outcomes they examined. Some assessed changes in morbidity, others mortality, and others both. Morbidity and mortality from acute coronary events should be used as outcomes in con- sidering the effect of a smoking ban. For mortality, ideally there would be autopsy confirmation of all deaths that might be due to acute coronary events; however, the larger the study, the less feasible that is. Short of that, medical records and other information could be reviewed independently to confirm the cause of death (not only for those coded as acute coronary events but for those not so coded but possibly acute coronary events none- theless). For morbidity, there should be independent clinical confirmation,

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 SYNTHESIS OF KEY STUDIES through review of medical charts and perhaps other information, that cases meet standardized criteria, such as those recommended by the World Health Organization (WHO) or others that take into consideration electrocardi- ography, biomarkers of cardiac damage, and pain. It is necessary, in the case of both mortality and morbidity, that International Classification of Diseases (ICD) guidelines be followed rigorously in identifying underlying causes of death and morbidity as opposed to merely abstracting the bottom line on the hospital discharge or the death certificate. Surveillance studies rely heavily on the use of a standardized system for classification of diseases, ICD, issued by WHO. Most countries use that system in connection with hospitalizations as well as deaths. The United States, uniquely, uses a modification of the system, the ICD-Clinical Modification (ICD-CM), to classify diagnostic information from medical records and for medical reimbursement. ICD-CM is more detailed, using an additional (fifth) coding digit. The ICD system is revised about every 10 years, and both ICD- and ICD-0 were in use in some countries in the key studies under review.1 Regardless of whether ICD- or ICD-0 is used, physicians and oth- ers typically list all causes of death and list the underlying cause of death last on the death certificate.2 Regardless of the ICD code, that is often done incorrectly; coders using death certificates for gathering statistics are directed in the ICD rules to select the listed underlying cause of death only if it could have given rise to all the other conditions listed as among the causes of death. Otherwise, they are to determine a logical sequence of events that could have led to death and select the underlying cause of the sequence, disregarding “ill-defined conditions.” In that respect, a change between ICD- and ICD-0 is of potential relevance to this review: in ICD- 0, for the first time, the diagnosis “cardiac arrest, unspecified,” I46.9, is regarded as ill-defined. In addition, what was a single code for acute MI in ICD- (410) is expanded in ICD-0 to six codes (I21.0–I21.4 and I21.9) that specify the site of MI. According to an analysis by the National Center for Health Statistics, the switch from ICD- to ICD-0 resulted in small but significant decreases in coding of cause of death as heart diseases in 1 ICD-0 endorsement by WHO in 1990 was followed by implementation at different times by different countries (WHO, 2009). According to the National Center for Health Statistics (National Center for Health Statistics, 2009), in the United States as of January 1, 1999, ICD- 0 has been used to code and classify mortality data from death certificates, and the U.S. De- partment of Health and Human Services has proposed regulations to replace ICD--CM codes with ICD-0-CM codes sets for health-care diagnoses and procedures as of October 1, 2011 (HHS, 2008). ICD-0 codes were in use in the study in Saskatoon (Lemstra et al., 2008). 2 WHO defines the underlying cause of death as the disease or injury that initiated the train of events that led directly to death or the circumstances of the accident or violence that produced the fatal injury.

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0 SECONDHAND SMOKE EXPOSURE fore implementation of a smoking ban and predicted the outcome after implementation. Figures 7-1–7-4 show the observed admissions for acute MI and those predicted without the statewide smoking ban under Scenarios 1–4, respec- tively. Figure 7-5 shows the estimated underlying trend for the whole period when a spline with 3 degrees of freedom was used (Scenarios 2 and 4). Table 7-6 summarizes the point estimates, the 95% CIs, and the p-values of the main effect of the smoking ban and the interaction term between the smoking ban and the linear function of time. The committee estimated these quantities under two regression models defined under Scenarios 1 and 2, which use linear and spline trends, respectively. As can be seen in Table 7-6, the resulting estimate changed from 0.0338 (95% CI, 0.0038–0.057; p = 0.0272) with a linear trend to 0.0503 (95% CI, 0.0110–0.089; p = 0.0122) with a spline trend. The difference in results between Figure 7-1 and Figure 7-2 depends on the assumption of linearity in the trend in rates of acute MI during the entire study period (Scenario 1). If the assumption of linearity is relaxed, the results change substantially because the committee is estimating the trend for the entire study period, that is, using data from before and after 3,800 3,600 3,400 Number of Admissions 3,200 3,000 2,800 2,600 2,400 2,200 Without Statewide Ban Observed Admissions 2,000 99 00 01 02 03 04 05 06 07 Year FIGuRE 7-1 Observed admissions for acute MI and those predicted without state- wide smoking ban on basis of Scenario 1. The dashed vertical line indicates when during 2003 the statewide ban was implemented. 7-1 rev.eps

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 SYNTHESIS OF KEY STUDIES 3,800 3,600 3,400 Number of Admissions 3,200 3,000 2,800 2,600 2,400 2,200 Without Statewide Ban Observed Admissions 2,000 99 00 01 02 03 04 05 06 07 Year FIGuRE 7-2 Observed admissions for acute MI and those predicted without state- wide smoking ban on basis of Scenario 2. The dashed vertical line indicates when during 2003 the statewide ban was implemented. 7-2 rev.eps 3,800 3,600 3,400 Number of Admissions 3,200 3,000 2,800 2,600 2,400 2,200 Predicted Admissions Observed Admissions 2,000 99 00 01 02 03 04 05 06 07 Year FIGuRE 7-3 Observed admissions for acute MI and those predicted on basis of Scenario 3. The dashed vertical line indicates when during 2003 the statewide ban was implemented. 7-3 rev.eps

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 SECONDHAND SMOKE EXPOSURE 3,800 3,600 3,400 Number of Admissions 3,200 3,000 2,800 2,600 2,400 2,200 Without Statewide Ban Observed Admissions 2,000 99 00 01 02 03 04 05 06 07 Year FIGuRE 7-4 Observed admissions for acute MI and those predicted on basis of Scenario 4. The dashed vertical line indicates when during 2003 the statewide ban was implemented. 7-4 rev.eps 200 Crude Hospitalization Rate (per 100,000) 180 160 140 120 Smooth Function of Time Observed Admission Rate 100 99 00 01 02 03 04 05 06 07 Year FIGuRE 7-5 Crude acute MI hospitalization rate (per 100,000) with smooth func- tion of time using 3 degrees of freedom. The dashed vertical line indicates when during 2003 the statewide ban was implemented. 7-5 rev.eps

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 SYNTHESIS OF KEY STUDIES TABLE 7-6 Summary of Point Estimates, 95% Confidence Intervals, and p-values of Main Effect of Smoking Ban and Interaction Term Between Smoking Ban and Linear Function of Time Estimatea 95% Confidence Interval p-value Acute MI scenario 1 Statewide smoking ban 0.0338 0.0038 0.0537 0.0272 Statewide smoking ban by –0.0077 –0.0094 –0.0059 <0.0001 time interaction Acute MI scenario 2 Estimate of main effect 0.0503 0.0110 0.0896 0.0122 of statewide smoking ban without statewide smoking ban by time interaction Estimate of main effect of 0.0706 0.0288 0.1123 0.0009 statewide smoking ban with statewide smoking ban by time interaction. Statewide smoking ban by –0.0073 –0.0136 –0.009 0.0248 time interaction a Betacoefficient representing change in hospitalization rate over time after implementation of smoking ban. implementation of a ban. Estimates of the trend (both linear and spline) based on only data from before the ban are less sensitive to the parametric specification of the trend. Another important assumption is in the interpre- tation of the results. In fitting a linear trend, the authors of all the studies assumed that any departure in the observed number of hospital admissions from the linear trend after implementation should be attributed entirely to the ban. The committee did not explore which model and assumptions are most appropriate but presents this information to examine the effect of model choice. Given that model choice can affect the results substantially, it is important to discuss the rationale for and the sensitivity of the results to the choice of model in publications, especially for more statistically sophis- ticated analyses. Publication Bias The published studies all showed some statistically significant evidence that smoking bans reduced the risk of cardiovascular disease events. There is a possibility that if an investigation shows no reduction or a small re-

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 SECONDHAND SMOKE EXPOSURE duction that is not statistically significant, the investigators will not be motivated to submit the results for publication or, if they do submit them, journal editors will consider such “negative studies” to be of low priority. Those considerations do not invalidate the published studies, but they sug- gest that a meta-analysis or quantitative estimate based on the published studies might overestimate the effects of smoking bans. The committee tried to identify and seek the results of all studies of the effects of smoking bans on the incidence of cardiovascular disease events. It searched CRISP and ClinicalTrials.gov to determine whether other studies of the effects of smoking bans on acute coronary events had been funded or approved and never published, and it found none. The National Association of City and County Health Officials Web site was also searched to determine whether other studies had been initiated, and the committee requested information from the Centers for Disease Control and Prevention and AHA on other studies that were under way or had been conducted and never published; no such studies were identified. There is still the possibility that studies showing no association were conducted but not published; this would bias the data toward there being an association between secondhand-smoke exposure or smoking bans and acute coronary events. WEIGHT OF EvIDENCE FROM kEy STuDIES The 11 studies reviewed in this chapter show remarkable consistency: all were observational studies that used different analyses and showed decreases in the rate of acute MI after implementation of eight smoking bans. Those decreases ranged from about 6 to 47%, depending on the study and the analysis. That consistency in the direction of change gave the committee confidence that smoking bans result in a real decrease in the rate of acute MIs. Apart from their consistency, most studies drew conclusions that ap- pear to be stronger than the data and analyses warranted. Some researchers have combined the results of the studies with meta-analytic methods to provide a point estimate of the decrease and an associated standard error (Glantz, 2008; Richiardi et al., 2009). The committee concluded that there are too many differences among the studies to have confidence in such a point estimate based on combining results of the different studies. First, the nature of the “treatment”—the smoking ban and collateral programs—is far from clear in specific studies, so there may not be a com- mon intervention to assess. Any form of causal analysis needs to be explicit about the details of the intervention and the fidelity with which it was im- plemented. In addition, some of the studies tested different “treatments” as part of their hypotheses: some looked simply at the effect of smoking bans, others looked more directly at changes in secondhand-smoke exposure.

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 SYNTHESIS OF KEY STUDIES Second, the population of interest varied from study to study in both explicit and implicit ways. Some looked at a population as a whole, others focused on smokers and nonsmokers separately. Population differences in responses to the interventions, such as changes in behavior, and differences in preexisting disease could exist. Those differences could be assessed and accounted for differently among studies, but many of the studies were silent on those issues; when they were not, they differed in how the issues are addressed. Third, given the absence of randomization into treatment and nontreat- ment groups, the choice of comparison groups for assessing the effect of an intervention is problematic. The studies under review varied substantially in that regard. Some studies used historical controls, others used longitudinal statistical adjustments with such techniques as time-series analyses and stratification by demographic group. The problem with respect to estimat- ing the magnitude of the overall effect is that the studies at hand did not adopt the same analytic strategy and did not make the ideal adjustments. Fourth, the relative changes in the numbers of acute events appear to vary from study to study, and this poses problems in the examination of the heterogeneous responses to the interventions. There are two ways to try to deal with such heterogeneity: include possible confounding variables as part of the model to remove heterogeneity by adjustment, and consider adding an extra component of variation in the error term for heterogeneity to make the standard errors larger than they would have been if the results had been homogeneous. Several of the studies included adjustment variables to capture effects of demographic groups, seasonality, or both, but each made such adjustments differently. Small numbers of events, as observed in several of the studies, militate against elaborate statistical adjustments for demographic groups or considerations of seasonality, and the adjustments that several of the studies made appear far from optimal. That leaves open the question of whether studies should focus on individual-level rather than group-level assessments and, if so, how they should do that. Finally, the studies varied widely in their measures of acute cardio- vascular events and in the time until differences were observed. In some instances, investigators allowed the time to effect to be determined by the data; in others, they hypothesized different periods. When all those and other factors are taken into account, no simple meta-analytic technique is adequate for assessing the magnitude of the effect of a smoking ban or of the effect of a reduction in exposure to sec- ondhand smoke on acute cardiovascular events. In summary, the studies all appear to have found substantial reductions in acute cardiovascular events after the implementation of smoking bans and in that sense were consistent, but separately and collectively they had statistical shortcomings. The committee concludes that the shortcomings

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 SECONDHAND SMOKE EXPOSURE do not negate the evidence of an association between smoking bans and the incidence of acute MI or, for the relevant studies, secondhand-smoke exposure and the incidence of acute MI. As a consequence of the variabil- ity and the limitations, however, it is difficult to use them to estimate the magnitude of the effect of smoking bans or secondhand-smoke exposure on the incidence of acute MI. CONCLuSIONS • The extent to which the studies assessed possible alternative causes of changes in hospitalizations—health-care availability, use of dif- ferent cardiac medications, new diagnostic criteria, and a decrease in all hospital admissions during a period—should be considered, especially if before–after comparisons are being made in the ab- sence of a comparison area. Given the multiple factors that could affect the rate of acute MIs, however, an assessment of secular trends is preferable. • Results of studies that included self-reported assessments of expo- sure to secondhand smoke cannot necessarily be compared with results of other studies that did the same thing unless the survey instruments (such as interviews) were similar. • All the studies are relevant and informative with respect to the questions posed to the committee, and overall they support an association between smoking bans and a decrease in acute cardio- vascular events. • The magnitude of the effect cannot be determined on the basis of the studies, because of variability among and uncertainties within them. • In most of the studies, the portion of the effect attributable to de- creased smoking by smokers as opposed to decreased exposure of nonsmokers to secondhand smoke cannot be determined. • The studies support, to the extent that it was evaluated, an associa- tion between a reduction in secondhand smoke and a decrease in acute cardiovascular events. The strongest data on that association in nonsmokers come from • Analyses of only nonsmokers (Monroe, Indiana, and Scotland). • Analyses that showed decreases in secondhand smoke after im- plementation of smoking bans. • At the population level, results of the key intervention studies reviewed by the committee are for the most part consistent with a decrease in risk as early as a month following reductions in secondhand-smoke exposure; however, given the variability in the

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