Manuscript: BMJ Low cigarette consumption and risk of coronary heart disease and stroke: a meta-analysis of 56 cohort studies

Transcription

1 CANCER RESEARCH UK & UCL CANCER TRIALS CENTRE UCL CANCER INSTITUTE Cancer Research UK & UCL Cancer Trials Centre University College London 90 Tottenham Court Road London W1T 4TJ website: Telephone; Director: Professor J A Ledermann Dr Wim Weber BMJ 10 August 2017 Dear Dr Weber Manuscript: BMJ Low cigarette consumption and risk of coronary heart disease and stroke: a meta-analysis of 56 cohort studies Thank you very much for the opportunity to revise our paper. Sorry for the slight delay in this, but the statistical analyst works elsewhere now, and we wanted to revise the text carefully to incorporate the very helpful comments and suggestions made by the reviewers (which included switching the focus to the withinstudy analyses, providing additional supporting analyses/references, and raising several features relevant to the topic). Below we address the queries raised during the review process. As far as we can tell, this is the first ever systematic review (with meta-analyses) examining light smoking and cardiovascular disease (and separating coronary heart disease and stroke). We hope that you agree with the external expert reviews that this represents an important body of work that can be used for public health policy and education. The topic is very relevant as many smokers are cutting down rather than quitting. Please let me know if you have any queries. Yours sincerely, Professor Allan Hackshaw, Deputy Director 1

2 Below are the original review comments, and our responses are in blue text under each one. We wondered about adjustment of possible confounding issues in the included studies: Smoking isn t only an independent risk factor, but could be a marker for other cardiovascular risk factors like physical inactivity, unhealthy diet and overweight or obesity. Confounding in relation to smoking and cardiovascular disease (apart from age) is not considered to be a major issue because whilst there are differences in risk factors between smokers and non-smokers, such differences are small (Law & Wald, 2003; Progress in Cardiovascular Diseases). Furthermore, heavy smokers are more likely to have adverse cardiovascular risk factors (such as obesity, poorer diet) than light smokers, because the latter, by definition, choose to have a somewhat healthier lifestyle (the comparison of habits and characteristics between smokers and non-smokers is not of relevance here, where, for example smokers have a lower BMI than non-smokers). This is expanded upon in the 4 th paragraph of the Discussion, with supporting references. Adjusting for these factors can therefore only attenuate differences in cardiovascular risk between light and heavy smokers, not dilute them (which is the main reason one wishes to allow for confounders). Hence, our estimates of excess risk for 1 or 5 per day could be even larger. You wanted to see the effect of a 1 cig consumption compared to a 20 cig consumption. This is an example where availability of individual patient data (IPD) would have helped immensely, because without the IPD you are forced to use the categories of cig consumption reported in the articles themselves, and use category summaries (e.g. median age in each category) in the modelling, rather than individual cig consumption and individual age values. This loses power, potentially considerably, and in particular loses the information wanted to examine the trends at individual level. E.g. see Appendix Table 1 first study. The first category is 1 to 7 cigs per day, and you are then making inferences about 1 cig per day from this model, even though it was not reported directly. Of course, obtaining IPD is not easy, and hence why the approach is used here based on published results. But I wonder whether existing IPD collaborations, like the emerging risk factors collaboration, would already have this information? There are few publically available datasets of cardiovascular disease and smoking, and the aim was to be comprehensive and not restrictive to only a few studies (which would not qualify as a systematic review). Furthermore, cigarette consumption in many cohort studies is actually recorded in categories (e.g. 1-5, 6-10 etc per day), not a specific number. Hence, the assumed gain in power by having a more sensitive measure of exposure is probably not as high as expected, because the raw data for modelling risk would not go down to whole number of cigarettes per subject. Also, relative risk (RR) estimates of 1 per day (or 5) are meant to give an approximate idea of 'light smoking', since smokers will vary their consumption between say 1 and 5 (rather than smoking exactly 1 per day, every day); hence summary estimates from studies should suffice. Under Study limitations in the Discussion, we also provide results from one of the largest cohort studies that used their raw data and a more sophisticated regression model, and show that their results for light smoking are close to ours; representing good validation of our approach. The individual studies in Appendix Table 1, also show clear and direct evidence (without any modelling) that the risk in light smokers is high in relation to heavier smokers, with estimates consistent with ours; again, further validation of our analyses. Whilst using IPD has clear advantages, there are many instances where summary data are used, are sufficiently reliable and have changed practice. Please note that the BMJ published the same type of meta-analysis in 2016 as ours, i.e. using only reported summary data from cohort studies (Aune et al, BMI and all-cause mortality; vol 353). In the Discussion ( Study limitations ) we discuss not having IPD. 2

3 Your analysis approach is 2-stage, wherein the first stage you obtain a regression equation in each study separately. But this has to be obtained by fitting a log-linear model through the RRs being reported for the available categories presented in the publication. This is why you restrict to at least 3 categories. Correct. We are concerned about the regression model used in the first stage. The weighting given to each category is based on the standard error of the RR. However, usually weights are based on variances, and variances of the log RR, not the RR itself. Please note that the log is actually used, because this is the scale of measurement. We did not state it because it is so well known, but have done so now. Secondly, the RRs for each category are correlated with each other, as they are being compared to a common reference group (never smokers). But it does not seem that the correlation is being accounted for when fitting the regression model. A better approach for doing this is given by Greenland (Greenland S, Longnecker MP. Methods for trend estimation from summarized dose-response data, with applications to meta-analysis. American Journal of Epidemiology 1992; 135: ). Without evidence to the contrary, we fear that the whole modelling approach may need to be re-done according to this method. The recommended method (Greendland & Longecker 1992) requires frequency counts in each cigarette by disease/no disease grouping, and assumes that crude and adjusted RRs are similar. However, many studies in our review did not report frequency counts, and for cardiovascular disease, RRs must be adjusted for by at least age (a clear risk factor). Not being able to use this method is a potential limitation, which we have now discussed this ( Study limitations ), but the consequence (mainly having wider 95% CIs) would not change the conclusions. Please also note that our main interest is not in describing the whole dose-response range, but rather the comparison between the lowest and higher consumption category. Even if the first stage was done adequately, the second stage is also not in line with recent guidelines. You use Revman to fit a random effects model to pool the RR for 1 cig per day versus non-smokers. Then separately you pool the results for 5 and 20 per day. But, as mentioned before, the results for 1, 5 and 20 per day are correlated within a study, and therefore a multivariate meta-analysis is required, to account for this correlation. However, this is ignored. Again, see the Greenland paper and other tutorials on multivariate meta-analysis. Further, the analysis uses the Dersimonian and Laird estimation method, but this produces CIs that are too narrow and other approaches are preferable. See Cornell for a nice tutorial We focussed on meta-analyses for 1,5 and 20 cigarettes per day (CPD) separately because this is easy to present graphically for the general readership, and shows the variability between studies. But we did indeed provide results based on the within-study analyses in the text (made clear at the end of the Methods), and the results were very similar (as stated in the Results). We have reorganised the paper to switch the main focus onto the within-study results. In addition, we now also combine the regression models for each study (using a meta-regression analysis within SAS Proc Mixed), and then use the pooled regression model across all studies to estimate the relative risk for 1 CPD (and 5 and 20 CPD). This different approach (which also uses within-study analyses) produces consistent RRs as with pooling the RR for 1 CPD across all studies (same for 5 and 20 CPD). The method by Dersimonian & Laird is, and has often been, used, see for example the BMJ 2016 meta-analysis of obesity (Aune et al), and many other articles. There is ongoing debate about the application of methods like these (including correspondence in the BMJ in 2011; 342:d549). Please 3

4 note that none of the meta-analyses that originate from the Oxford CTSU (Sir Richard Peto) make allowance for heterogeneity/random effects. However, I, and others, often use it to (a) provide wider 95% CI and (b) that many readers are used to seeing some sort of allowance for heterogeneity. Potential for publication bias or small study effects is not examined Please note that the association between smoking and CVD is well established, and because this is causal it must have a dose-response relationship. Therefore, we are not trying to examine a new association for the first time, or one where causality is uncertain, where publication bias would be of relevance. Also, the dose-response data in most studies were certainly not the main purpose of the paper, but rather one of several/many results that readers would expect to see, hence publication bias should be minimal if at all. We attempted to avoid small study effects by only including large studies (>50 CVD events). What if the original study already analyses cig consumption as a continuous variable? E.g. If a study actually gave the effect of a 1-cig increase on CHD risk (i.e. exactly what we want), then did you discard this information in favour of their approx approach based on categories? Correct, these were not included. It is known that heavier smokers inhale less, and the extent of this should be taken into account when correlating with risk. This has been described before, see for example Law et al (BJC 1997, reference 14), which shows how the reported number of cigarettes should be adjusted for cotinine and CoHb. None of those studies that reported a regression coefficient (i.e. for 1-cig increase) made this adjustment. A study was required to have at least 50 events. Given the potential for small study reporting bias in this field, this could be sensible, but the justification is actually not given in the paper. This is now mentioned in the Methods. No CIs given in the text itself. Several are now provided. Study quality was not examined, as noted in the discussion. We have now added a new section in the Results on this. Relative risks given, but we think you mean hazard ratios. It is not clear how many odds ratios were used instead of HRs (see methods), but these are not the same measures. Correct; the majority were hazard ratios, otherwise age-adjusted relative risk based on incidence/mortality rates using person-years. There were no odds ratios (the term was included by mistake). Is the RR of 2.19 for those that smoke 20 per day in line with what we know? It seems low. This is about right. See (new) 5 th paragraph of the Discussion, and reference 85. Different studies adjust for different factors, and so where does that leave us in terms of understanding the overall results? This is usual for systematic reviews of observational studies (including the one on BMI and mortality in the BMJ 2016). We now have a new section discussing confounding (4 th paragraph of Discussion). 4

5 Reviewer: 1 Comments: Relevant for patients: Yes. The article is relevant from the perspective of (future) patients. The research shows that contrary to lung cancer in CHD and stroke the risk of getting CHD or a stroke remains high even when smoking only 1 to 5 cigarettes daily. Many smokers believe there is little or no risk associated with smoking only a few cigarettes on a daily basis. Awareness of the risk of smoking only a few cigarettes is important to stimulate smokers to stop smoking. Cardiovascular specialists, stop smoking specialist and primary care physicians etc. should be made aware of the risks associated with smoking only a few cigarettes daily. This has the potential of keeping more people healthy. Areas of relevance that are missed: Yes. In the study there is a significant difference between the RR in men and women. However nowhere is there any attention given to these differences in RR and the differences of the effects of smoking only a few cigarettes. If I read the results correctly women have a higher risk for both CHD and stroke when smoking than men even at a lower level of smoking and the risks decrease less in women. I feel this is a missed opportunity for a study that explicitly looked at both men and women (which is a positive). There is already a discrepancy in knowledge about CHD and stroke between men and women. This article could be clearer on the differences of the effects of smoking between men and women for CHD and stoke. We now mention the higher risk among women in the Results, Discussion and Key Points, and a supporting reference. Methods used: I don t know enough of the methods used to be able to judge them. What can be improved: I feel that the formulation of the key points (p.12) is confusing. The impression I get is that the key points are formulated in comparison to the deceasing risk of lung cancer without mentioning lung cancer. The key points could be formulated mote clearly. You say that the risk of CHD and stroke is high in relation to smoking 20 a day, which is true especially in comparison to lung cancer and what you had hoped/expected to find. This can be formulated more clearly. The last bullet point is very clear as is the conclusion (p.11). It is important for both men and women to stop smoking completely, but it seems the risk is even higher for women. Maybe you could add that for women it is even more important to stop smoking completely. Then the study becomes more relevant in stop smoking advice. That would increase the relevance of the study in giving guidance and advice on treatment (stop smoking). And would make the paper more relevant to patients and doctors. We have revised the bullet points, and hope they are now clearer. What is missing: From a (future) patients perspective what is missing is pack years. It is hard to place the results in the perspective of how long and how much people have been smoking over time and the effects this has on the results found. Though I can understand this was not included in the study, it would be good to include why in the study limitations (p.9). Pack-years is considered by several experts in tobacco and health as misleading, because it does not differentiate that risk from the first say 10 years of smoking is less than in later years (when risk has accumulated); see Peto Br J Cancer 2012;107:p406. Duration of smoking is generally considered to be an indicator of future risk, but was missing from most studies, and the US General Surgeon s Report (2010) discuss the problems with this measure (reference 87), i.e. it is completely correlated with age, 5

6 which in itself is a risk factor for CVD. We now mention this in the Discussion, but refer to one of the cohort studies that investigated both measures, and the conclusions do not change. There is a mention of mis-reporting heavy smokers as light smokers. What about mis-porting light smokers as heavy smokers? Other research has shown that reporting the amount smoked is not always accurate. We now mention light smokers who mis-report as heavy smokers, though consider this to be uncommon (it is akin to never-smokers reporting as smokers). Additional Questions: Please enter your name: Dominique Hamerlijnck Reviewer: 2 Comments: Overall Comment: This is a well-done systematic review and meta-analysis. It address an issue of public health and clinical relevance. Specific Comments: 1. Page 3 (2nd sentence) - suggest to include "globally" to "the absolute number of smokers has increased..." 2. Page 3 (4th paragraph, 1st sentence) - "ETS" - ETS is an industry term to be avoided. SHS is preferred (See IARC Monograph 83). Page 4 (top paragraph) - suggest deleting..."which has never been conducted." 5. Page 10- "supporting biological mechanisms" - Would comment on the proposed mechanisms for SHS and discussion of SHS versus active smoking. The 2010 report of the US Surgeon General would be a useful reference here. These have all been incorporated in the revised paper. Additional Questions: Please enter your name: Jonathan Samet 6

7 Reviewer: 3 Comments: This is a well-conducted and well-written review and my comments are meant only to enhance the authors' work. This systematic review addresses the question of whether cigarette smoking at low intensity (i.e. only a few cigarettes a day) confers a coronary hazard and shows that ~40% of the excess coronary risk can be attributed to smoking only 1 cig/day which is an important public health message. My main concerns about the paper regard the reliance on published data and the eligibility criteria. The authors excluded studies that did not report at least 3 smoking categories (not including never smokers). Is it conceivable that those studies that reported two or few categories of smoking intensity may have shown results that may differ from the findings presented here and that the reason that they didn t publish the HR for CHD at low intensity was that there was no increase in risk relative to never smokers? Using only 2 observations (smoking categories) to fit any regression model would probably produce unreliable results so is rarely done. The dose-response data in many of the studies we included were not the main purpose of the paper, but rather results that readers would expect to see in articles on smoking, hence publication bias is unlikely. The (high) increased risk at low intensity is accepted by many groups now (see US Surgeon General s reports). What is important supporting evidence is (i) the direct (non-modelled) results from studies in Appendix Table 1 and (ii) the detailed analysis of CPS II (reference 53) both very consistent with our quantitative estimates. The advantage of our work is that it contains a large number of studies and covers CHD and stroke. Moreover, several cohort studies have publicly available datasets (e.g. ARIC, MESA, CARDIA) and individual-participant data meta-analysis are increasingly more common with authors willing to contribute data, so I m not wholly convinced by the authors statement in the Discussion that we did not have individual-level data for study subjects because many studies are old, and it would have been unfeasible to collect these raw data. We agree there are some such datasets, and now mention this in the Discussion ( Limitations ). But we noticed that some are not very large, and if we only included these studies, we would not be able to refer to our work as a systematic review. Can the authors please provide a list of the excluded cohorts? We had previously published data from the Asia Pacific Cohort Studies Collaboration (>460,000 people) that would seem pertinent to this review: cigarettes per day <10, >20 cigs per day (IJE Huxley et al. APCSC 2005) This study had been flagged, but during the review and selection process had been misunderstood to be a meta-analysis of studies already included because it actually consists of a collection of cohort studies. However, we have checked and there is no overlap, so this study can now be added. We thank the reviewer for spotting this. It made little difference. I d also like to see a test for publication bias as well as quality assessment which are important and standard components of systematic reviews. We are not trying to examine a new association (for the first time), where publication bias would be of relevance, and as stated above, dose-response data is often reported routinely and not the focus (or often even discussed) in the text of the paper. We now provide a new section in the Results on quality assessment. Regional comparison some cultures women report undersmoking relative to men due to the unacceptability potentially underestimating the risks of 1 cig per day in women. We had previously 7

8 reported that compared with men who smoke, women who have a 25% excess risk of CHD is this true at low smoking intensities? To do so, one would need to compare the RRs in women and men derived from the same cohort. This was noted by Reviewer 1, and we now provide this in the Results section, including results from within the same cohort, where available. Comparison with former smokers would be informative one would anticipate a lower relative risk relative to 1 cig/day. This would significantly extend the analyses and hence paper, and addresses a different question, i.e. that people who smoke 1 per day have a higher risk than former smokers. Our interest is only in current smokers, and how differences in their habits significantly affect their risk of CVD. Have the authors overstated the case that there is still widespread misunderstanding in the general population that smoking only a few cigs to be less harmful? The Every cigarette kills and One cig takes a minute off your life are well known campaigns. Further, I would argue that higher tobacco taxes and population wide health promotion campaigns are largely responsible for the low smoking rates. E cigs are relatively new China was the country of origin of e-cigs but has one of the highest smoking rates in the world and the use of e-cigs in developed countries is illegal e.g in some States of Australia the use of e-cigs containing nicotine is illegal. We agree. There have indeed been occasional studies on light smoking, media news items that appear after individual studies are published, or governmental reports on smoking that mention this issue. But it is still not common knowledge. For example, the lead author (Hackshaw) delivers a module on cardiovascular epidemiology for an executive level Masters course at the London School of Economics, where ~40 attendees were middle to senior level international cardiologists and cardiology researchers, and when they were shown the findings from the submitted manuscript (in December 2016) none of them were aware of the large effects at low consumption and were most interested. Also, previous reports/studies have focussed on coronary heart disease and we include stroke (rarely reported). We now acknowledge prior campaigns/work in the Introduction (last paragraph), and Policy implications and future research. How did studies reporting more than 3 categories or categories of smoking not 1, 5, 10 dealt with in the analysis? We used all the smoking categories reported by a study publication, now stated in the Methods. The forest plots are difficult to read as the figures have been stretched. Could the data be ordered by weight? In the main paper we have moved most forest plots to the Appendix, and hope that the 4 left behind are clearer now. Ordering by size of effect, we believe, is easier to understand, as there is a clear trend from smallest to largest effect. Can the authors provide confidence intervals around the excess relative risks? These measures are based on ratios which have unusual mathematical properties. Instead we provide the th centile values using the individual observations from Figure 1, as a measure of variability. Additional Questions: Please enter your name: Rachel Huxley 8

9 Reviewer: 4 Comments: The authors are to be commended for their substantial effort at surveying the literature, identifying appropriate research articles, abstracting results and aggregating a vast amount of information on CVD effects associated with consumption of cigarettes. The paper is clear and well written, and the authors analysis strongly endorses the conclusion that very low intensity smokers continue to incur increased CVD risk and that smokers would achieve far greater health benefits from complete smoking cessation than from a reduction of smoking intensity. While results and conclusions are generally supported, the paper suffers from the use of older, less comprehensive statistical methodologies (see 1997 references). A more systematic evaluation of the shapes of the exposure-response relationship for each study and for the meta-analytic combined data would strengthen of their results. I offer several comments in no particular order. General comments: The paper sometimes conflates cigarette smoking exposure and cigarette smoking exposure rate, i.e., consumption or cigarettes/day (CPD). CPD is a metric of intensity and not a metric of actual exposure to cigarette smoke. CPD represents one component (consumption rate) which, together with duration of smoking, enables the creation of a metric proportional to the total cigarettes consumed (i.e., pack-years). This distinction is important, since for example the impact on CVD risk differs depending on whether one smokes 5 CPD for 1 year, 10 years or 50 years. Additionally, health benefits from cessation of smoking will differ under these scenarios. The authors clearly wish to convey an important public health statement regarding risk of CVD among low intensity smokers. However, statements about disease risks at 1 or 5 CPD are necessarily incomplete without linking CPD to smoking duration and thus total exposure (pack-years). The authors have set themselves a difficult task, namely, the estimation of risks at low CPDs under the constraint that risk cannot be accurately characterized solely with CPD. The paper would benefit from a more nuanced discussion of this issue. We used exposure as a general epidemiological term, but have now replaced this word with consumption or CPD throughout to be specific. The issue of smoking duration has been discussed in the US Surgeon General s Report 2010 (reference 87), with the limitation that it is completely correlated with age (and so can be difficult to separate the effects of these 2 risk factors). Also, most studies did not report results by duration, and high profile studies (e.g. the Oxford University Million Women Study, reference 58) still only focus on CPD (and in that article they specifically state why they avoid using pack-years). In the Discussion, we now have a new paragraph devoted to duration (under Limitations ), including results from an individual study that examined this alongside CPD. Methods - Study selection and data extraction: If I am correctly reading Appendix Figure 1, the statement on inclusion/exclusion criteria indicates that the authors excluded six studies for which the RRs of cardiovascular disease decreased with increasing cigarette consumption. First, the text in the Methods section omits this restriction. More importantly, this exclusion is inappropriate. Unless there are good a priori reasons, one cannot simply exclude data because the pattern of risks fails to conform to a desired trend. Under the paradigm that studies represent repeated samplings from a larger universe, a summary of RRs using only positive studies would clearly be biased. This restriction is now added to the Methods. In the Appendix (under Appendix Figure 1) we now make clearer why these studies were excluded. First, a real decreasing trend is implausible because a causal relationship between smoking and cardiovascular disease is well-established which must mean there is an increasing trend. Observed decreasing trends are by chance, and due to, for example, small number 9

10 of events in either the low or high consumption group. Second, and perhaps more importantly, because the trend is decreasing, the RR for smoking 1 CPD will always be higher than for 20 per day, which yields large values of the percentage of excess RR for 1 CPD when expressed as that for 20 CPD. For example, in one such study, Rosengren et al 1992, the observed relative risks are 2.8, 2.8, 3.1 and 2.1 for smoking 1-4, 5-14, and >24 per day (an observed decreasing trend). The modelled relative risks for smoking 1 or 20 per day are 2.89 and 2.79, and because the effect is larger with 1 per day, the percentage of excess risk is 106% ([2.89-1]/[2.79-1]) much higher compared to the average estimate for CHD of 44% among men (Table 1 of the main paper). Including the 6 studies with negative slopes yields a percentage of excess RR of 62% among men (for heart disease), noticeably higher than 44%, and we consider it a potential over-estimate (i.e. the results would be unduly influenced by studies that show spurious and implausible dose-response relationships). We hope that this provides sufficient justification. The text is not entirely clear on this point, but presumably the authors abstracted RRs for all CPD categories in the various studies and not just those results related to the designated categories, 1, 5, and 20 CPD. Please clarify. The extraction of data for all categories is required for a more complete evaluation of RR patterns. This is correct, and we now clarify this in the Methods. Methods - Statistical methods: Instead of modelling risk with consumption for each study (which is non-linear), we modelled the logarithm of risk, using similar methods as before.12,14 This involved fitting a log-linear variance weighted regression model between risk or RR and cigarette consumption. Although this approach makes the relationship more linear (when examined on a log scale), it might still under-estimate the increase in risk at very low consumption levels. - The logic for this methodology approach seems convoluted. From the Abstract, the authors objective is to use the dose-response relationship between cigarette consumption and risk of coronary heart disease and stroke, in order to quantify the risk of cardiovascular disease (CVD) for smoking 1-5 cigarettes/day. Thus, the first step would identify an appropriate dose-response relationship for each study, followed by an examination of the consistency of the dose-response relationship across all studies. For example, if the exposure-response relationships differed substantially among the studies, then a simple summarization of heterogeneous RR patterns across all studies may not be appropriate. The authors believe the CVD and CPD relationships are not linear. However, the authors then need to explain why RR trends for all or most studies will be log-linear. Almost certainly, this will not be the case, i.e., trends across the full range of CPD will not increase exponentially. Consequently, a studyspecific log-linear model, i.e., RR(x_s) = exp(b_s x_s), where x_s is CPD (or perhaps a cotinine-adjusted CPD) for study s, will result in a biased estimate of βs. This in turn means that the weighted summary across studies, exp(b) = Sum_s {w_s * b_s}, will likely also be biased, where w s are the weights. If we had raw data we would indeed have followed the reviewer s suggestion to explore different models. However, in the absence of this, simpler models fitted through summary data should be acceptable (and we raise this in the Discussion). In the abstract we now remove the words dose response as it might be confusing, because our ultimate purpose was not to describe the shape of the whole consumption-risk range but rather compare the lowest consumption with the highest (or about 20 cigarettes per day). We agree that even a log-linear regression might not truly represent the whole dose-response curve, and had already stated this in the original manuscript. But given the limited data values in each study publication, the opportunity for more sophisticated models is restricted. Please note that our focus is actually on comparing the lowest consumption group with the higher one (around 20 CPD), rather than describing the whole dose-response range. We provided support (validation) of our results/estimates using two sources of evidence (observed and non-modelled results from individual studies in Appendix Table 1; and a sensitive analysis of the CPS II study using the type of model recommended above by the reviewer). The CPSII study paper also showed 10

11 there was no low threshold (we now say this in the Discussion), and this can only be reliably examined using raw data down to very low levels of consumption (exposure), which is not possible from the summary data we have available. - The authors do not undertake a systematic analysis of their data. One possible approach would proceed as follows: (i) Using the AIC or other model fit statistic, evaluate the exposure-response for each study under a variety of RR models, e.g., linear, RR(x) = 1 + b*x; log-linear, RR(x) = exp(b*x); power, RR(x) = x^b; linear-exponential, RR(x) = 1 + b*x*exp(g*x); extended log-linear, RR(x) = exp{b1*x + b2*x^2} or RR(x) = exp{b1*x + b2*ln(x)}, etc. (ii) After the identification of an appropriate model, analyze the combined meta-data across studies using an appropriately rich class of models to evaluate the form of the dose-response and to test homogeneity across studies under either fixed and/or random effects assumptions. (iii) Compare the final fitted model with study-specific RRs by CPD categories and with summary RRs by CPD categories to demonstrate consistency between the combined model and the category-specific RRs. (iv) Estimate RRs at various CPD amounts. Note that given a well-fitting RR model for CPD, this final comparison is almost superfluous since the model characterizes RRs across the full range of CPDs. (v) Additionally, it would be useful to formally consider possible threshold values. Although it seems unlikely in these data, a formal evaluation of a threshold would strengthen the conclusion that there is no save level of smoking. For (i) to (v) above: As explained above and now further in the Discussion, a limitation of our study is the ability to examine more sophisticated models (like the ones proposed above), than the simpler log-linear one using summary data based on only several smoking categories. The models proposed above are much better suited to using individual participant data. We are also aware that the BMJ has a general readership, and a paper that has a large mathematical component is likely to detract from the main public health conclusions. We have now added a new figure (Appendix Figure 9) and text in the Results ( Model reliability ) showing several examples of how well the fitted model matched the observed results from individual studies; and hope that this is acceptable. It appears that the tables and figures display only the fitted RR estimates. This makes it difficult for a reader to interpret the accuracy of the authors fitted models. Currently, there is no demonstration that fitted RR models for each study and for all studies combined conform to the category-specific RRs. Currently, readers cannot assess the validity of the results of the modeling. Appendix Table 1 and Figures 2-4 provide some information, but not in relation to the fitted models. Appendix Table 1 shows the observed RRs (without modelling) and also the RRs from our fitted models, specifically for studies reporting low exposure. They match generally well. We have also added a new figure (Appendix Figure 9) and text in the Results ( Model reliability ) showing several examples of how well the fitted model matched the observed results from individual studies. 11

12 Specific comments: Page 4, The non-linear relationship between CHD and low cigarette consumption is not well recognized. : While I appreciate the importance of the emphasis on low smoking intensity, in my view this is an overstatement, unless the authors meant it as a statement about a non-researcher population. Several reports from the mid-2000s have pointed out the non-linearity of the RRs with CPD. For example, the 2014 Report of the US Surgeon General state that The 2006 Surgeon General s report provided evi dence that exposure to secondhand smoke increases the risk of CHD in exposed nonsmokers. In addition, that report provided the first evidence that very low levels of exposure have disproportionate effects on CHD risk and the risk flattens out at higher levels of cigarette consump tion, indicating that the dose-response relationship for smoke exposure and CHD is nonlinear. The reviewer is correct; when we say not well recognized we are mainly referring to non-researchers, but there are many clinicians and health specialists who are also still unaware of this issue. We have now clarified the text. Please see response to similar comment by Reviewer 3. What is the meaning of IV in the various tables, as in Risk Ratio IV, Random, 95% CI? IV is inverse variance now defined. 12