by Carl V Phillips
Many of you will have already seen or heard about a paper by Farsalinos et al., in which they review some case series data from China and observe that for hospitalized COVID-19 patients, the recorded smoking prevalence is far lower than would be expected given the population prevalence. The US CDC also released data a couple of days ago that shows the same pattern. If the data is representative and accurate (but note that there are compelling reasons to question whether either of those is true), this strongly suggests that smoking is hugely protective against COVID-19 inflection and/or the resulting disease progressing to the point that hospitalization is required.
We are not talking at the level of “well I guess smokers get a bit of compensation this year for all the health costs of smoking.” This is at the level of “everyone should take up smoking for a few months until the pandemic abates.” The protective effect implied by the data is absolutely huge.
As you might guess, the usual suspects are doing everything they can to hide and deny this. Indeed, even those reporting the statistics are doing that. My biggest criticism of the Farsalinos et al. paper is that they misinterpret what their results imply, failing to report this and erroneously suggesting their results suggest there is no association.
It is certainly true that it is an extraordinary claim that requires better evidence than we have. As already noted, the quality of both the Chinese and US data is suspect. Still, to assume that something is not true, and that evidence that suggests it is true must therefore be wrong, merely because it would be unfortunate if it were true (in one’s personal view of How The World Should Be), is not exactly scientific thinking.
What really floors me is the fact that people do not want this to be true. We are desperately trying to slow the spread and reduce the severity of a disease we cannot cure or vaccinate against. We are suffering enormous costs in order to do that. How great would it be if everyone could reduce their risk of getting a serious case of the disease by 80% by smoking a few packs?
Needless to say, for anyone other than sociopathic monomaniacs, it would be great. Alas, I doubt it is really true. Still, that is what the statistics suggest.
As for those statistics, well…
The above link is to a working paper version of the paper. I cannot emphasize strongly enough that it is great that the authors posted their paper immediately, and sought comments on it, rather than engaging in the usual horrible health research practice of just sending it to a journal where it is kept secret up until the day that it is etched in stone with all of its flaws. [Update: I have now posted a review attached to the posted paper. It mostly just points the reader back to this post.] I strongly commend the authors for this. After doing that, they submitted it to a journal, and I was asked to review it. (No secrets are being disclosed here. This journal is one of the good ones that does not keep reviewers and reviews secret, and as already noted, the authors did the right thing and already made the paper public.)
The paper is important and timely, the authors have made clear they want public comments, and I think the review is educational. Thus I am posting the review here. Note that the current version of the paper at the link is v.13 (which might change again by the time you read this), while I think the version I reviewed is v.10 (at least it is not the current version, which just went up). If you care, the working paper server lets you look at previous versions, though it probably does not matter much which version you read. You can probably make sense of the review having just read the abstract or heard about the paper, though reading it is not much of a burden (ten minutes or so – it is short).
As I try to remind my readers when I post a review, please keep in mind that my reviews might be what you imagine journal reviews always look like. In reality, the typical review in public health is 1/10th as long, does not even try to review the technical content and instead is based mostly on whether the reviewer likes the conclusions, misses most of the glaring errors in the paper, and offers advice that would probably make the paper worse rather than better. (For a whole lot more on that, see our paper on that topic.)
My review:
This is not an everyday paper. If it were a typical paper, one that used the same methods for some relatively unexciting question, this review would have a tone of “well, ok, but you need to do X and you should not do Y, and there are some other little problems that need to be explicitly dealt with, but sure whatever, it is just the little thing that it is.” That is not an option with this paper.
To summarize my observations before continuing: The result of this analysis is, if true, enormously important. But there is so much uncertainty about the data and so much fundamental material missing from the analysis that we cannot conclude anything based on what is presented. The authors need to do a lot more analysis if they are going to present these results. If they think they can stand by the true implications of what they are reporting, they should do that and present their arguments. If they do not think they can do that, they need to report that fact, as so not report their results as they do, and to definitely not present conclusions that are not supported by their analysis as they do now. (There are also some specific issues that I address.)
The authors are presenting us with evidence that says — if accepted as even roughly valid at the level they are presenting it — that smoking is HUGELY protective against COVID-19 colonization and/or the resulting disease progressing to hospitalization. The magnitude is sufficient that it would not be a joke to recommend people take up smoking until the pandemic subsides (contrary to the authors’ obligatory and dutiful recitation of the “generalized advice to quit smoking”). That is an extraordinary claim (at least in practical terms, whether it is biologically extraordinary or not), and thus demands a more complete analysis than appears in the paper.
To respond immediately to the pre-positioned retort to these observations: It is not acceptable to hide behind the rhetoric of “but we never say that!” (I suppose technically it is not really rhetoric in the paper, but rather the rhetorical equivalent of empty space in art, but it is a bright beacon even in the form of its omission.) The authors assert that their results merely suggest that smoking does not have detrimental effects on COVID-19 outcomes. But this would be like Hill, Doll, et co. reporting their classic results with the conclusion “there is no evidence that smoking protects against lung cancer.” Either this paper — with its results as presented — shows that smoking is protective against COVID-19 with near certainty, or it does not show anything at all because it is massively flawed to some unknown degree. People are already saying this paper provides evidence of a protective effect. They are right if we assume the analysis is even roughly legitimate.
This is especially true in light of the just-reported U.S. CDC statistics that show a similar strong protective association. (Specific review comment: The authors need to cite that report and discuss it in their paper.) It is reasonable to be of the opinion that both of these sets of statistics are misleading for reasons discussed here. But the triangulation certainly should shift posteriors at least somewhat toward believing toward believing the implications of the present paper are really true.
The authors cannot hide from this. Trying to do so is disingenuous.
Had the results really amounted to “we explored the hypothesis that smokers are at higher risk and found data that actually points slightly in the other direction”, then they could have written the easy paper that they did. It is sometimes possible to legitimately say (and by ‘say’ I mean actually say it, explicitly), “our results point somewhat toward causation in a particular direction, but we recognize this would be an extraordinary claim” along with some combination of “the support our statistics offer for such an affirmative claim is modest” and/or “we identify sources of possible error that would plausibly be of the magnitude to create the observed departure from the null” and then land on “but while we cannot claim causation in the direction suggested by our statistics, those statistics make it difficult to believe there is substantial net causation in the other direction.”
That is not possible here. Authors cannot choose to declare that their results are not what they are just because they are uncomfortable stating the implications of those results.
The association in the protective direction is not modest, and there is no exploration of the magnitude of errors that might have been skewing things in that direction. There is no attempt to quantify the sources of error, and indeed they are not even effectively identified. If the claim is that there are errors that are sufficient to adjust the observed hugely protective association down to merely “it appears there is no causation in the other direction”, then those errors are sufficiently large and uncertain that nothing whatsoever can be learned from what appears in the paper. Either the potential errors must be explored and quantified rather precisely or the data should be declared to be suspect to such an unknown degree that these numbers should not be reported at all. There is no legitimate way to do something in between. What appears in the paper — effectively “we make the unsupported assumption that the errors in the data perfectly cancel out the magnitude of the huge association we report, and thus we interpret our findings as supporting a null relationship” — is illegitimate.
I expect it is frustrating for the authors that this rare opportunity to produce a stunning result — to be part of what would be, if true(!), the biggest discovery about smoking and health in decades — demands so much more work. But here they are. If this were a jaw-dropping bench discovery, the researchers would work their lab 24/7 to recheck every last detail, replicate, test, etc. There is no such recipe here, but something equivalent needs to be done.
For what it is worth, my quick assessment upon first seeing these results was that the quality of the data is so hopeless that nothing at all can be made of it, and thus this report can only mislead. But that was not a strong prior and I accepted that I might be wrong. Indeed, I was actively excited by the possibility that I was wrong, at both the “scientific curiosity” level and the “this could have huge practical implications” level. After carefully reading what appears now, as well as available commentary about it, my prior did not really move. The authors need to try to convince themselves that their quantitative results are informative and, if they succeed, then try to convince the reader. If they cannot find a reason to be convinced that the data is valid, then they should morph this paper into a report about why they think no one should repeat this quantitative analysis because it is misleading. It is a major epistemic error and arguably a logical fallacy to declare, in effect, that the results support the null hypothesis because they are based on data that is not solid enough to support some other conclusion.
The authors need to have someone on their team who can research Chinese language documents and someone who is familiar with Chinese medical records. Perhaps they do already, but that individual has not contributed what is needed here. For cranking out a typical workaday pub that dredged up an uninteresting association, just downloading the ten papers that happen to be in English and happen to be easy to find, pretending that these represent all available knowledge, is weak methodology but not necessarily a fatal problem. But this very non-boring paper is about a phenomenon that is only a few months old (i.e., an even smaller portion of human knowledge appears in academic journal articles than is typical) and relies on data coming out of a country that …well, let’s say has more than its share of controversy about the validity of research papers, to say nothing of its official statistics. It is not adequate to just take the English-language journal articles and treat them as if they were the available data about Chinese COVID-19 hospitalization.
Someone needs to dig into other reports that may have been written in Chinese, original versions of the papers that form the dataset, etc. They need to see if there is any public discussion about statistics like this and what similar statistics are available in some form. They need to see if there is a samizdat questioning the validity of the internationally reported results. They need to see what Chinese commentators said about this association (surely, if it really exists, someone noticed it and wrote something). They need to review what Western China watchers have said about the Chinese COVID-19 data (it seems safe to assume that the English-language publications did not go out without the approval of the Chinese government).
It is not beyond imagination that the data used here is fabricated. It is definitely plausible that it was intentionally cherrypicked (at the level of deciding what would be reported, not by the present authors) in support of some goal. This should be acknowledged and addressed to the extent possible.
Similarly, someone needs to assess whether the Chinese medical records data is valid. Those of us familiar with US data, upon seeing the aforementioned US CDC report, immediately started thinking, “hmm, ad hoc medical records are known to often fail to collect information on covariates that are unlikely to affect treatment decisions, and sometimes the record keeping methods then just default those to the negative” and also “given all the talk about triage and rationing treatment, it is easy to imagine smokers — who are aware of the medical discrimination they face even under normal circumstance — hiding their smoking status upon interview to try to avoid being denied treatment”. What are the chances that these, or something else like that, happened in China? The authors need to try to figure this out.
The overarching point here is that there is only one potential source of error (if we assume that the data is not intentional disinformation) that really matters here: exposure misclassification. The authors need to make this clear to the reader rather than having a single sentence about it buried in a paragraph in the Discussion. Someone “quitting” smoking because of disease onset and self-identifying as a former smoker is one aspect of this, so it is good the authors make some attempt to address this. But it seems likely to be a pretty trivial contribution to the misclassification compared to mere faulty recording, and thus odd that the authors devote outsized attention to it while basically ignoring the major sources of exposure misclassification.
The Discussion alludes to confounding by SES, but any such effects are likely to be pretty trivial. The authors should run some numbers to demonstrate this (to themselves, and then communicate to the reader). Merely making the qualitative observation “such confounding might exist” is not good enough.
Similarly, the authors allude to unknown age distributions of the sample. One big problem with this is that they do not even report the statistic that this would affect, the EV of smoking prevalence for each sample (which they need to report — see below). The deeper problem is that it does not seem like it could really matter, given the prevalence distribution they report; this is a red herring. The authors should run some numbers (they demonstrate that they have the inputs they need) to show themselves that any effects of this would be trivial, and then report this fact to the reader.
Other commentators have proposed a few other sources of error in these results. None of them seem worth much attention when compared to the major issue. E.g., smokers disproportionately lacking access to healthcare in this population, which seems unlikely to be true to a sufficient degree to matter. But if the authors believe this or any other source of uncertainty is worth even mentioning, then they should run some plausible numbers to inform themselves about how much it could possibly matter and report what they found. Unquantified hand-waving mentions of potential bias are always bad methodology, and this problem really matters in the present paper.
Even worse, these authors, as well as other commentators, have reported observations about detrimental effects of smoking as if they attenuate the implications of the observed association. But the exact opposite is true. (Other commentators have also mentioned the face-touching risk that might be associated with smoking, which has the same implications.) In the Discussion, the authors allude to other diseases that are caused by smoking and that are believed to increase the risk or severity of COVID-19 infection. But they then continue on to a backward interpretation of the implications of this. Assuming that smoking has detrimental effects regarding COVID-19 infection via these pathways, then this would mean that (once again, if the data is legitimate) smoking per se is even more protective against COVID-19.
That is, the reported data shows a protective net effect. If valid, it shows whatever beneficial effects smoking causes minus the detrimental effects from diseases that were caused by the previous decades of smoking. This would further recommend that people take up smoking for a few months right now, for the time where the benefits are available but not long enough to cause any substantial risk of disease. It should be clear from what appears here that I am not leaping to that conclusion. But this is the top-line implication of the observations about detrimental pathways from smoking to COVID-19 infection, as reported in the paper and elsewhere. Those observations clearly do not attenuate the observed association as claimed by the authors and other commentators. (It would really be more complicated than that. Perhaps only past decades of smoking, not current smoking, is protective. But the point is that the authors and others seem to be searching for reasons to downplay the benefit the reported results imply exists, and in so doing, they are making claims that are exactly opposite of what the claims about detrimental pathways suggests.)
The authors go on to get this even more specifically wrong when they say that the posited detrimental pathways from smoking to COVID-19 outcomes means that nothing can be said about the effects of smoking on hospitalization risk. The (net) effects of smoking on hospitalization risk are exactly what their data measure (as usual, assuming it is valid). Note that the authors phrase this claim as “no recommendation can be made”; these are technically defensible weasel words because the results are so uncertain — because of possible misclassification — that it is arguable that no recommendations can be made based on this dataset. But this has nothing to do with the immediate context of the claim, that there may be detrimental pathways.
To reiterate, until the potentially fatal source of error — exposure misclassification — is addressed, there is little point in even mentioning the others. But at least if they are going to be mentioned, their implications should not be misstated.
One interesting observation from other commentators is that we should expect a much larger representation of females in the sample if smoking were protective, given that most males in this population smoke and almost no females do. The versions of this observation I have seen are facile (it requires various “all else equal” assumptions that should be stated, among other things). But it has rough validity and important implications. If the analysis is accepted at face value, this would mean the conclusion would have to be something like, “smoking is protective for the men in this population (the exposure is too rare to judge whether it is protective for the women also); also apparently women in this population are at much lower risk compared to international statistics, so much so that the protective effect for men is not enough to make up all of this difference.” Needless to say that is, once again, a huge “if”. The seemingly better conclusion from observing the surprisingly low representation of females in the sample is “since we seem to need a very convoluted story to explain what was observed, this is further reason to believe that the input data is so flawed as to be uninformative.” An alternative version is “we really have no idea what the reported data represents because we have to come up with seriously wild stories to explain it.”
Specific issues (most of which are moot should the authors choose the option of reporting that no sense can be made of this data):
Whichever of the above potential systematic biases are important, it should be apparent to the authors that random sampling is not the (or even a) major contributor to the uncertainty in the results. Thus, the habitual bold reporting of random error confidence intervals is even worse for this analysis than it normally is in epidemiology. Naive readers (i.e., about 99% of readers) look at those and interpret them as a measure of uncertainty — all of it — which is clearly misleading here. It is even worse when authors make the mistake of averaging results together to produce an aggregate (see below). The authors need to make an explicit statement, early and boldly, not as a subtle implication of vague observations in the Discussion, that these CIs are really not informative (except for the fact that they argue against pooling the data — see below). Even better would be to suppress reporting them at all (at least not in the one table that everyone is going to look at) because they can only serve to mislead.
The authors should not average together the various datasets they are using. This is not nearly as bad as for the typical junk science “meta-analysis” of observational studies, in which the exposure measures, outcome measures, and populations obviously vary wildly. There is potentially sufficient homogeneity of exposure, outcome, population, and methodology here to justify it, unlike most of the time such averaging is done. But there is still too much heterogeneity (and even more inadequate reporting to even judge if there is heterogeneity) in those papers, which the present authors just gloss over. The association observed in the largest block of data (the first paper in the table), when compared to any or all of the next few larger ones, appears to be statistically incompatible with the assumption that these are measures of the same phenomenon. That assumption is the justification for averaging, and if the assumption cannot be justified then averaging should not be done.
[BLOG UPDATE: Wow, I really understated just how bad a methodology the averaging together was. I did not study the source material when I wrote the review. I have done so now. Many of the papers did not count up “hospitalized COVID-19 patients” as the paper claims; some restrict the population to those with particular conditions while for others it is not clear everyone was hospitalized. Far worse still, a few of the papers did not report “current smokers” status as the paper claims, but combined former and current smokers or only counted heavy smokers. For many of the others, it is unclear who was counted in the smoking column. Yet the authors just averaged these all together pretending they were the same measure. No no no no no!]
In their main table, the authors need to calculate and report the expected value of the number of smokers in each row, based on population prevalences (i.e., the EV if the smoking data were from a stratified random sample of the population) using stratification by whatever covariates are available from the original paper. This can at least consider the gender breakdown of each sample, and age distributions and any other available demographics should be used. This is the null-effect baseline the reader needs to compare to the main reported statistic, and it is missing. The reader can roughly calculate this based on what is reported in the text (though only for the gender distribution, not any other covariates), but should not have to do it themselves.
I would, however, advise against taking the typical next step of calculating and reporting the resulting relative risk. Omitting this is (and thus would continue to be) a departure from standard practice; almost every paper in the epidemiology literature reports the equivalent statistic and calls it their main result. But in this case, any reader who is not expert enough to instantly calculate that in their head should probably not be distracted by the captivating bright-line number (this is often true of other epidemiology literature also). Should the authors not heed this advice and choose to report relative risk, they should definitely not follow the typical bad practice of reporting an OR; ORs are a misleading statistic when comparing proportions. It should be reported as a proportion (risk) ratio or, better still, difference.
Regarding the confluence of the two previous observations, at least one previous commentator has recommended that the authors pool the data and compare the result to the EV for the Chinese population as a whole. I would argue that this is misguided for two reasons: First, as noted, the pooling should not be done at all. Second, even if it is, the EVs should be based on as much information data from each of the reports as possible, and thus calculated individually.
The methods reporting is inadequate. The authors report what they personally did. But everything hinges on the upstream data collection and recording methods. The authors mention a few random bits of this, but they need to systematically report to the extent they can figure it out (from the paper and any background published elsewhere) how each dataset was collected. To the extent that important upstream methodology choices are not known (not reported in the original papers and not found via further research), this needs to be noted specifically and explicitly.
Due to the inadequate methods reporting, it is not clear if it is possible to stratify any of the input datasets by gender/sex (nor is it even clear whether the reporting was for gender or for sex, though this is a relatively inconsequential point). If it is possible, it should be done. Ideally, the entire main analysis would be restricted to men, given the small exposure prevalence for women at the population level. To the extent that it is possible to stratify any of the data subsets, the stratified results should be reported and analyzed.
“This preliminary analysis, assuming that the reported data are accurate, does not support the argument that current smoking is a risk factor….” Even apart from the core problem with this paper (claiming that a strong association supports a null conclusion) this statement is semantically wrong. “Risk factor” does not mean “increases risk”.
Later in the Discussion, the authors observe that they are only reporting data from hospitalized cases, and then assert that therefore “no conclusions can be drawn” about less severe cases. This is clearly wrong. It would only be true if someone has no beliefs about the relationship between factors that affect the risk of severe cases and factors that affect the risk of less severe cases. It is unimaginable that this is true. Perhaps the authors want to say that they prefer to not try to extrapolate, without erroneously suggesting it is impossible. One way to do that is to not mention the point at all.
The last two sentences, about e-cigarettes, are a non sequitur. If the authors wish to offer a bit of discussion about how smoking is a cocktail of exposures (lung irritants, lung toxins, drug delivery of nicotine and other chemicals, etc.) and then note that we only have data about smoking and thus no idea which of these are causing the observed effects from smoking, that would be worthwhile. (Of course, that only makes sense if the conclusion is reached that the data suggest something is being caused.) But there should not be a context-free mention of another exposure that has a subset of the properties of the smoking exposure (plus some different properties).
A possible way out of this
Having thought about this for a day, I can see a way that the authors can salvage this to produce a legitimate analysis that still serves their (commendable) political goals. It is fairly apparent that the political goal here is to push back against the attempts to twist and cherrypick other data in order to use COVID-19 as an excuse to further their attacks on smoking and smokers. This is a valid and admirable goal. And this data, whatever its biases and errors, can be deployed in support of this mission.
[Aside: Assuming I am right about the mission of this project, the authors’ claims that they have no conflicts of interest is a lie. (Note that [this journal’s] COI policy wisely does not limit its definition of COIs to financial interests, as some journals make the mistake of doing.) If the goal of an analysis is to make a particular point that one personally wishes to make, this is among the biggest conflicts of interest that an author can ever have. It needs to be noted as a COI.]
To use this data to get a legitimate analysis that fulfills the goal, the authors can do the following:
- Fix the specific problems noted above (in some cases by just leaving something out).
- Change the core narrative theme to some paraphrase of this: “There are a lot of claims going around that smoking increases risks from COVID-19. These are generally based on cherrypicking and unsupported guesses. They ignore the data that points in the opposite direction like that out of the US and out of China, the latter of which we present here. Anyone wishing to claim that smoking increases risks needs to acknowledge and respond to these statistics that suggest the effects are hugely in the opposite direction.”
- Strip out all the ornaments that add no knowledge and that suggest that the Chinese data that is being used is valid enough to calculate them. That includes the random error statistics (CIs) and the pooled analysis. Including these does far more harm than good.
- Report the results (smoking prevalence vs. EV of smoking prevalence) honestly. Openly state what it shows if taken as accurate and unbiased: that smoking is hugely protective.
- Address what this implies if true. Do not play the game of asserting what one is “supposed to” always say about smoking. This was submitted to a journal run by harm reductionists not anti-smoking fanatics; take advantage of that. Honestly report that if taken at face value, these results would suggest that taking up smoking for a few months would cause a net health benefit.
(If the authors are not willing to report the obvious implications of their results, then they have no business reporting those results at all.)
- Only after having said that, if so desired (this is optional), go on to say that “we think this is probably not really the case because the data is so unreliable”. Note the phrasing there — personal and subjective. It is not ok to hide this subjective assessment in faux-objective weasel words. It is a subject assessment by a few people, not a result of the analysis. Of course, add any concrete observations that further research reveals, about there being other data that was not reported, that the case series reports were specifically criticized by someone, that the Chinese government is biasing external reporting, etc.
- Note boldly and clearly that the data quality is so uncertain that it is difficult to have much faith in its implications, or to be confident of any other conclusions that follow from it. Reiterate at that point that, nevertheless, those who would claim that smoking increases COVID-19 risk still need to deal with this elephant in the room to make their claims. Note that this does not excuse the authors from trying to figure out as much as they can about the data quality. Saying “here is what we did to try to sort out what this data really means, but just could not figure it out” is different from saying “we did not bother to even try to understand our data, and thus we do not understand it”.
7a. Note the multiple sources of fundamental doubt about this data: Normal misclassification at the recording level. The clearly biased sample (whatever happened to end up in English-language journals, which is only a sliver of the data that exists in China; the low prevalence of females). Possible games by the Chinese authorities to intentionally bias this reporting.
7b. Mention that there are other possible sources of bias (the confounding and such) but they are of such small consequence that they are not even worth addressing given the data quality problems.
- Emphasize that the data inherently captures the net effects of smoking on COVID-19 outcomes, not just protective causal pathways. Thus observations about detrimental pathways are not a reason to dismiss the observed association — they are already baked into it. That is, the authors need to not only fix the error that they made on this point, but explicitly point out that it is an error to think that way (because it appears to be a strangely common mistake to make). Thus, whatever those who desire to indict smoking might have to criticize about these results, noting that there are detrimental causal pathways is not one of them, since they are already part of this. (However, it is legitimate to say “I believe there are such clear detrimental pathways that it seems implausible that the net effect is beneficial, which is one reason to believe this data is biased.”)
[Update: I left out my conflict of interest statement that I submitted with the review. I know a lot of you are fans of my COI statements, so here it is:
I really despise people who are trying to use the pandemic as an excuse to pursue their attacks on tobacco product users.
Tobacco harm reduction, anti-THR lies, and related topics 
Could this study be duplicated easily? The place to do it would be the UK assuming they have computerized medical charts for large numbers of citizens. By now there must be a substantial number of smokers, vapers, and former smokers who have tested positive for the virus. When the antibody test is easy to get there is that group to include. Whether smoking is protective or not there should be plenty of data available to study already.
It would be easy to do this study, and do it far better than the sloppily collected data we have. Anyone with access to patients — a single busy hospital or whoever — could systematically and carefully collect data on smoking (and whatever else might be of interest). There are problems, of course. There are not exactly a lot of extra resources available to gather data once they get busy with COVID-19 cases. Some of the patients are unable to answer, and close relatives (usually an available good source of such data) are locked out. Still, it would not be all that hard, and potentially incredibly useful if something was found that seemed to dramatically change the risk (as smoking appears to in the paper reviewed here, but with better data we could better believe it). I am really disappointed we have not yet seen some preliminary results of some such surveys.
VERY much in agreement Carl! The analysis of the data by Dr. Farsalinos et al seemed well done, but the presentation of the logical result of those data seemed so unclear as to appear almost deliberately hidden.
I think I would disagree on the presentation of an OR however. Such presentations are simple and clear for laypeople to understand, and without them even people who’ve followed the news on studies and numbers and analyses for years can have difficulty seeing the trees through the forest.
In 1998 Boffetta et al published the World Health Organization’s massive international study of exposure to various levels of secondary tobacco smoke. The study had been long expected to provide the “definitive” answers as to how great a risk was posed to people from such exposures to both adults and children over the years. Instead, any possible effects were so small that the researchers could not find significance in ANY of them… except for one:
The WHO study found A STATISTICALLY SIGNIFICANT 22% *PROTECTION* FROM FUTURE LUNG CANCER among children raised in smoking homes as opposed to those raised in nonsmoking homes. Boffetta presented the numerical findings clearly although his verbal description of those findings made it clear that he did not support the results they pointed to. (Whether he felt that way himself or simply agreed to such a presentation under pressure is not known, but should be noted as a possibility.) Here is the presentation from the WHO’s abstract:
—–
” RESULTS: ETS exposure during childhood was not associated with an increased risk of lung cancer (odds ratio [OR] for ever exposure = 0.78; 95% confidence interval [CI] = 0.64- 0.96).”
—–
Note the verbal misinterpretation of the ONLY socially meaningful statistically significant result of their worldwide research. Compare that to many more “modern” papers that will take ORs with CI ranges that INCLUDE “1.0” and verbally interpret them as having “borderline significance” in attacks on secondary or tertiary smoke exposure.
But at least the WHO’s 1998 data was presented in a clear fashion that ordinary people without a degree in statistics could see and understand for themselves. I believe it would be a positive element if Dr. Farsalinos presented his current findings in that form as well.
As noted, aside from that one minor difference, I applaud your presentation of the conclusions that could or should have been drawn from the findings. While it is understandable that the authors might not want to formally say things that might encourage people to smoke in general, the primacy of the importance of presenting the truth in a way that people can readily see should win out.
While arguments could be made at the moment that Corona may not present as great a threat to individual long term health as smoking might, those arguments are based upon assumptions (e.g. “We’ll have a vaccine.” OR “CV19 won’t mutate for repeated future infections.”, OR “There will be no negative long term health effects that will show up in the future from today’s CC19 infections.” Those assumptions MAY all be true, but at the moment they are indeed simply assumptions. If some or all of them are substantially wrong, it is at least CONCEIVABLE that smoking COULD be found to be “healthier” overall if it offered a significant enough protection from CV19 infection — unlikely perhaps, but possible — and the information should be presented honestly.
Carl, I’m sure you’ll be strongly attacked for your open presentation/interpretation of the findings that Dr. Farsalinos gathered and presented, but I believe it will eventually be seen as a strong contribution toward the truth.
Again, VERY well done!
– MJM
P.S. And I’d be remiss if I didn’t add a pointer to the man who I believe first pointed toward this issue ALMOST TWO MONTHS AGO (!), Frank Davis, a years-long fighter against the fanatic fringe of British Antismokers. See Frank’s blog of Feb. 11th at https://cfrankdavis.wordpress.com/2020/02/11/how-to-prevent-coronavirus-start-smoking/ and follow through his successive entries as he follows and develops the idea in intermittent entries in the seven following weeks!
Thanks.
I will respond to the second paragraph with: Really? Do you really understand what it means when someone tells you there is an OR of .33? Could you recite what that really means? I bet most people could not and I would have to think about it and maybe write it down first. If 50% of the men in the population smoke and 25% of the men who are hospitalized smoke, that is an OR of .33. Does that really work for you intuitively, or would it make more sense to have the prevalence ratio of .5? Better still would be to convert it to absolute risk and calculate the difference, since that is what people really should based their decisions on, though that requires a bit more work and bringing in some more number. ORs are a necessary evil sometimes and sometimes they are actually the best statistic to report, but not for proportion data.
It has actually been known since 2003, since the same was true for SARS. See my sister post that links to the “exhaustive lit search” reddit thread.
Lots of stuff to think and digest. One question: what is your opinion of the role of nicotine on the enzyme ACE2? One observation: it would be a sublime irony and a blow to anti-smoking & anti-nicotine fanaticism if smoking (or perhaps nicotine) turn out to have protective properties, even if they do not offer a high rate of protection (assuming this could be quantified).
I don’t really want to opine on the biochemistry – I am really a just consumer of such information (though, of course, one who can read more critically than most). I have seen this hypothesis, but have not looked closely enough to know how convincing the arguments for it are. I should. I shall.
This has been being discussed since mid-late February here:
https://old.reddit.com/r/COVID19/comments/faluhv/an_exhaustive_lit_search_shows_that_only_585_sars/
It is not only smoking, it is also COPD and asthma. And the same lack of smokers is not seen in studies of other diseases such as influenza (once you account for the presence of children) or heart disease.
That’s interesting. That should really be cited when writing about this (not as authority, but just to recognize precedent). Consider it cited here, thanks to the wonder of the comments section. I will recommend it to Farsalinos et al in my next round of comments.
When things are moving this fast, Reddit, blogs, and whatnot are always going to be ahead of journals. It is sad that people who buy into the myths of the journal cartel do not realize this. Of course, there is the challenge that those same source are also somewhat ahead of the journals in producing junk theories. (And, yes, I know what I said there, and I mean it.)
I can care less about being recognized and want nothing to do with the journals. Thanks, though.
Please excuse any formatting errors, I don’t know what works on this site.
Also, it has been recently reported that the symptoms in severe cases are more similar to high altitude sickness rather than ARDS:
* https://www.ncbi.nlm.nih.gov/pmc/articles/PMC7096066/
* https://www.reddit.com/r/COVID19/comments/fu4c36
/frontline_nyc_doctors_think_covid19_should_be/
* https://www.reddit.com/r/COVID19/comments/fugq77/covid19_does_not_lead_to_a_typical_acute/
Smoking is also reported to help for that:
* https://www.ncbi.nlm.nih.gov/pubmed/28947454
Also:
https://www.theguardian.com/books/2007/oct/17/sportandleisure.sport
The last is particularly intriguing because that suggests an acute effect, which is probably different than any chronic effect mediated by ACE2. Then again that was in mountain climbers (basically athletes) rather than elderly sick patients.
I don’t know enough to comment on the effects of smoking on hypoxia, let alone the best clinical care for serious COVID-19. I never tried smoking anything when suffering from altitude hypoxia, so I guess I could be wrong, but it sure feels like about the last thing you would want to do then.
More generically, though, it is impossible to just write off any claimed benefit from smoking/nicotine just because it appears to be a niche theory that few subscribe to. This is because there is such intense resistance to admitting to any benefits (and allowing further research). There is even resistance to accepting the reduction of neurodegenerative disease, for which the evidence is overwhelming.
Yes, obviously there is a great anti-smoking bias here. But either way there are many people saying smoking does help with high altitude sickness which appears to be similar to this illness.
Cocoa is also used in Peru for acute altitude illness so perhaps it is a vasoconstriction effect: http://culturelocker.com/story/2013/Peru-coca.html
I would believe that. Coffee is pretty helpful.
If smokers are at significantly lower risk (than nonsmokers) of becoming infected by the virus, a possible explanation is that something in the tobacco smoke and/or the smoke residue on the hands, lips and/or saliva of smokers may harm or kill the virus.
If that is found to be the case, nonsmokers would benefit from holding and mimicking the smoking of a cigarette (without inhaling the smoke) could provide a similar risk reduction (as smoking cigarettes) for contracting the virus.
The data (which again is quite possibly completely misleading) seems a bit more consistent with the interpretation that it stops progression to serious cases rather than stopping initial infections. That would argue for lung effects or perhaps nicotine. Of course the problem is that if smoking really is protective, there will be so much resistance to doing the useful research to figure out which part of the cocktail of exposures matter, so that it will be too late before it is known.
Asthmatics and COPD patients are also underrepresented though. COPD patients could be attributed to former smokers, but asthmatics?
It is so hard to make sense of this data. We need focused studies (not hard, but need resources — see other comment thread). Could lung diseases really protect against this lung disease? Really? Well, most anything is possible. But bad data collection seems more likely. Or it could be they are at such higher risk that they do not survive to get hospitalized.
Please look through (at least ctrl-f) the exhaustive lit search reddit post. The survivorship bias idea doesn’t work for smokers. See the source on prevalence in the general population which also includes data by age group and the one paper that reported smoking and disease severity by age. Less info is available for asthma/COPD.
“If smokers are at significantly lower risk (than nonsmokers) of becoming infected by the virus, a possible explanation is that something in the tobacco smoke and/or the smoke residue on the hands, lips and/or saliva of smokers may harm or kill the virus.”
Somehow, while almost anything is possible in the universe, I would not list “smoke residue on the hands” as being a serious contender in explaining what appears to be a reduction in a lung disease of 50 to 90% from COVID in smokers. In terms of lips or saliva, I would think that “smoke residue” is likely to be far more concentrated in pipe and cigar smokers and that we would have somewhere picked up the concentration in those populations by this point.
Given the disease focus in the lungs, I’d say at a wild guess that it might be more worthwhile to look at the inhalation of smoke by smokers as the causative element here. And, if I was one of those who in the almost magical power of highly diluted secondary smoke, I’d be looking at gathering data on secondary smoke exposure and COVID.
Can you imagine a world where such research would NOT have already been done if initial populations had shown a 3 to 1 or 10 to 1 ratio of smokers falling ill from COVID when compared to nonsmokers? Or would there have been a near-instantaneous jumping to see blame could also be laid at the doorstep of secondary exposure?
– MJM, who can’t think of anything cute at all to say about the dereliction in research and presentation that’s generally been taking place in this area…
I am a vaper now (I stopped smoking a year ago and started vaping) I will say I fully doubt these numbers, they are out of China. True it would be nice IF nicotine has some protective effect against covid-19, but I doubt it.
Also I would say if you don’t smoke or vape, DO NOT START. True the UK RCP says vaping is 95% safer (read safer not safe) then smoking I still would discourage any one from vaping if they don’t smoke or are not already vapers.
There are similar numbers out of the US.
There is no reason to assume that if(!) the protective effect exists, it is caused by nicotine. I note that in the review.
If the numbers in the paper are valid, they say that someone could improve their health prospects by smoking for the next few months. Personal feelings about the wisdom of smoking do that change that. Perhaps they could get the same benefit from vaping or snusing, if it really were the nicotine, but there is not reason to assume that.
RCP is wrong. There is no conceivable way that vaping is 5% as harmful as smoking.
Pingback: Vaping Digest 6th April – vapers.org.uk
From the fact ex-smokers have similarly low hospitalizations, I’d think this has to do with some long-term change in the airway epithelium (probably by the smoke, not the nicotine).
The ex-smoking exposure data is far more suspect still than the smoking exposure data. I am not inclined to think very hard about what it implies if accurate. That said, yes, if that were really causation then it would have to be some long-term change, and so perhaps my contingent remark about the benefit (*if* the smoking exposure data is right, selection bias is not huge, etc.) of smoking a few packs would be incorrect.
CNN (far from a trusted source on nicotine issues) released a “special edition” here https://edition.cnn.com/2020/04/06/opinions/smoking-vaping-covid-19-coronavirus-maa/index.htm
Besides the expected propaganda (EVALI etc) the piece mentions the following text:
“Smoking has many negative effects on respiratory health, and the possibility of a relationship between smoking (both traditional cigarettes and marijuana) or vaping with Covid-19 were raised by early observations in China. One report, looking at 1,099 laboratory confirmed cases in China, revealed that 12.4% of smokers either died, required ICU admission or needed intubation, compared to 4.7% among never smokers. Another study found that among Chinese patients diagnosed with Covid-19 pneumonia, the odds of disease progression (including death) were an order of magnitude higher among smokers compared to non-smokers. The World Health Organization has noted that cigarette smokers are likely to have more serious illness if infected with Covid-19.”
The reference of the study with 1099 patients is a NEJM article https://www.nejm.org/doi/full/10.1056/NEJMoa2002032 and the reference for other Chinese study is https://journals.lww.com/cmj/Abstract/publishahead/Analysis_of_factors_associated_with_disease.99363.aspx
CNN is voicing the same interpretation of other media outlets (from papers like this one from Vardavas et al https://doi.org/10.18332/tid/119324). In the NEJM study of the 1099 hospitalized patients there were 961 non and former smokes and 138 smokers. Of the whole lot 67 progressed to serious condition, of these 17 (25.8%) were smokers and 50 non and former smokers. This means that more smokers (17/138 = 12.4%) progressed than non and former smokers (50/961 = ~5%). The other Chinese study reported similar outcomes.
However, these reports are hiding the elephant in the room: smokers are still underrepresented in all stages of the CIVID-19 diseases (as highlighed by Farsalinos, Barbouni and Niaura).
Given the lack of data that you mention, is it possible to put forward as a sort of preliminary hypothesis that
(1) smokers have a lesser chance to become hospitalized but (2) once they are hospitalized they have higher chance to progress to serious condition?
It seems that Vardavas et al (and CNN and other media outlets) are emphasizing (2) while dismissing (1). This is a serious source of bias, since (2) is expected because of accumulated harms from smoking but (1) is completely unexpected.
What is your take on this?
Yes, this is exactly whats going on in the data, there is not one shred of evidence for smokers being at higher risk. All the evidence points the other direction. The same was true for SARS and it was covered up or at least dismissed/ignored. There are no missing smokers in Chinese data on pneumonia or heart disease.
Another thing the OP paper mentions I hadn’t thought of is that smokers admitted to the hospital would be going through nicotine withdrawal on top of everything else.
Yes, all valid points. It is really too bad that the original-OP (the paper) is not tight enough to be able to address these and overtly shies away from trying to address them. I hope it is improved to overcome those limitations.
To expand Roberto’s hypothesis, it is plausible that we have (a) smoking protects against either getting colonized or the resulting COVID progressing to hospitalization (could sort the two out with population-representative testing data) + (b) smoking exposure status increases the risk of worst outcomes should hospitalization occur + (c) part or all of b is caused by forced abrupt withdrawal during treatment, perhaps specifically nicotine withdrawal (could partially sort this out with an experiment where some treated patients are given nicotine patches; it would be hard to substitute for other effects of smoking though).
I’m not sure that nicotine patches would be a good idea
Nicotine patches may boost intensive care risk – 2006
“The team examined the intensive care records of 224 smokers, half of which received NRT, mostly via skin patches.
Surprisingly, they found that 18 of the patients on NRT died, compared with just three of the smokers that did not receive nicotine. Also, the average duration of an ICU stay for patients given nicotine was 24.4 hours, about 2 hours longer than their cold-turkey counterparts.
“We have to be aware that we may be doing some harm [by giving patients NRT],” Afessa warns.
He notes that many of the patients in the study had been admitted to the ICU because they had gone into sepsis due to an infection. Sepsis can cause the body to release myocardial depressant factor, a molecule that reduces the pumping power of the heart.
Nicotine may further weaken the hearts of these patients by causing the coronary artery feeding the heart, to narrow, he suggests. This would reduce the amount of oxygen being pumped to other organs in the body. Many of the ICU patients in the trial died of multiple organ failure.”
http://www.newscientist.com/article/dn10380-nicotine-patches-may-boost-intensive-care-risk.html
Nicotine Substitution Does Not Reduce Intensity of Withdrawal Symptoms in Hospitalised Smokers: Presented at ERS
“VIENNA, Austria — September 22, 2009 — Offering nicotine substitution to smokers hospitalised for elective surgery does not have a significant effect on reducing cravings or other nicotine withdrawal symptoms, according to a phase 3 study presented here at the 19th Annual Congress of the European Respiratory Society (ERS).
In addition, no further differences were seen in rates of smoking cessation 1 to 6 months following the study.
“Hospitals have been smoke free by law since 2006 in Belgium, so we saw in-hospital smoking cessation as a teachable moment for patients,” explained Kris Nackaerts, MD, University Hospitals Leuven, Leuven, Belgium, on September 16.”
http://www.docguide.com/nicotine-substitution-does-not-reduce-intensity-withdrawal-symptoms-hospitalised-smokers
I tried to find out where the idea for nicotine patches had come from and it appears to have been be based on Green Tobacco Sickness.
“Scientists know that nicotine replacement therapies, such as patches and chewing gum, increase minor heart symptoms, such as irregular or rapid heartbeat.”
http://www.medicalnewstoday.com/articles/269983.php
“We put the tobacco on our skin and waited to see what would happen,” Jarvik recalled. “Our heart rates increased, adrenaline began pumping, all the things that happen to smokers.” ?
https://www.uclahealth.org/murray-e-jarvik-84-professor-and-nicotine-patch-co-inventor
You can tell that he was a neversmoker
“Green tobacco sickness (GTS) is an illness resulting from dermal exposure to dissolved nicotine from wet tobacco leaves; it is characterized by nausea, vomiting, weakness, and dizziness and sometimes fluctuations in blood pressure or heart rate”
http://www.cdc.gov/mmwr/preview/mmwrhtml/00020119.htm
I was pleased when vaping came about, though I’ve never managed to find out what temperature the liquid vapourises at.
Oh, and I wrote a reply to Roberto’s original comment in this thread previously but it is not posted so apparently I failed to hit “send” (grrr), so I will try to duplicate the basic content it here….
I agree that is a very valid hypothesis, and should be examined with good data.
The data CNN uses is just as suspect as the data used in the present paper, for similar reasons. I have stopped being surprised, having seen it so many times throughout my career in social sciences, by the attitude “b-b-b-b-but what do you mean I have to look at and carefully consider the source and validity of the data? it’s just THE DATA, not something you have to think about!” But while not surprised, I remain baffled by it. How can anyone — even a news reporter — think like that?
The reason that they stand more chance of serious p[rogression ios because, in the hopspital they arem not permitted to smoke so they are losing their barrier
Looking away from nicotine entirely might help
Nitric Oxide Can Help Treat Pneumonia, Researchers Say
1993
“A group of Medical School researchers has discovered a bizarre twist on the harmful effects of car exhaust and cigarette smoke: nitric oxide, a component of both pollutants, can help treat a deadly type of pneumonia.
“Instructor in Anaesthesia Dr. Jesse D. Roberts, Jr., a member of Zapol’s research group, said the discovery also explains why mountain climbers short of breath often claim that smoking cigarettes makes them stronger. The seeming paradox may be due to the presence of nitric oxide in cigarette smoke”
“And nitric oxide may only be the tip of the iceberg. The idea behind the treatment, that pollutants that are toxic in high doses are actually essential chemicals in the human body, may open a whole new world of safe drugs for other diseases.
Carbon monoxide, another toxic gas present in automobile exhaust, has also been shown to be a chemical messenger between cells, Brain said. “It’s remarkable that it’s escaped everyone’s notice for so long,” he said.”
“According to Zapol, it all reduces to one simple thing. “Good things hide in pollutants and cigarettes,” he said”
https://web.archive.org/web/20051029212635/http://www.thecrimson.com/article.aspx?ref=222612
As you will know, Nitric oxide as a vasodilator and carbon monoxide as an antinflammatory have only relatively lately been found to be made by the human body as part of the immune system and might explain the missing smokers.
I really don’t want to get into speculating about the relative plausibility of biological pathways here. But it is useful to have a list of them, just to defuse sloppy thinking like “well if smoking helps then vaping must be even better because it is like smoking but without the harms from smoking.”
The discoveries of endogneous NO and CO are not recent but date to last century.
Ironic that Dr Joe Brain of Harvard made this comment about CO in 1993:
“It’s remarkable that it’s escaped everyone’s notice for so long,” he said.
Remarkable indeed given key role he played in designing and overseeing the largest lo fest most expensive CO study ever conducted in USA, a study that USA EPA commissioned from HEI in 1983 to support its 1971 standard.
The HEI srudy found that CO exposure helps some men with angina and heart disease exercise longer after expsoure to CO than fresh air — the first to find this– but covered this up to give EPA results it wanted to defend keeping CO NAAQS standard unchanged.
Brain led the most recent EPA CASAC CO NAAQS review panel in 2011 and wrote EPA Adminstrator Jackson that the panel supported keeping the standard unchanged based on that one study (Allred et al).
For public story of this fraud, see newspaper article here:
https://dailycaller.com/2017/08/07/exclusive-researcher-claims-to-have-evidence-one-of-epas-most-successful-clean-air-rules-is-based-on-fabricated-data/
Thank you for your reply.
As a keen gardener from an early age with an interest in the nightshade vegetables , tobacco research seemed so untrustworthy and single minded I gave up on it and looked elsewhere.
I have posted a few I thought pertinent on Frank Davis’ blog over the last few days, but here are a couple I haven’t.
‘Surprise benefit from carbon monoxide’
2008
“Scientists believe that carbon monoxide may be of benefit to patients with serious lung conditions such as asthma and chronic obstructive pulmonary disease (COPD).
New research has revealed that that people with COPD who were given a small amount of the gas showed signs of improvement in their condition.
Researchers at the University Medical Centre in Groningen, the Netherlands, found that the gas appeared to ease the inflammation of lung tissues when given in low doses over a four-day period.
However, it has been stressed that carbon monoxide, a toxic gas found in car exhaust is still dangerous, and it is very difficult to gauge a safe dose for patients.
The research was published in New Scientist magazine
https: //web.archive.org/web/20080320231756/http://www.irishhealth.com/?level=4&id=13267
Anti-inflammatory effects of inhaled carbon monoxide in patients with COPD: a pilot study
2007
https://erj.ersjournals.com/content/30/6/1131
The evolution of carbon monoxide into medicine.
2009
“The discovery that carbon monoxide (CO)-a highly publicized toxic gas molecule-can have powerful benefits and curative effects not only changed how we view CO, but has, with tremendous contradiction, resulted in clinical trials of CO for the treatment of various pathologies. There is sound preclinical evidence that, at a low concentration, CO has benefits in numerous and diverse diseases in rodents, large animals, and humans. CO especially has potential benefits in inflammatory disorders. As CO moves ahead in the clinic, we continue to advance our understanding of how it functions, especially as the number of potential clinical applications expands. CO’s mechanisms of action at the cellular level depend on the disease and the experimental focus, but the one constant is that CO reestablishes homeostasis.”
https://www.ncbi.nlm.nih.gov/pubmed/19558742
It seems to me in peruading people to give up smoking and offering only nicotine as a substitute which apparently remains unchanged when passed through fire unlike most things, they may have been throwing the baby out with the bath water.
For Example
Nicotine: does it have a role in the treatment of ulcerative colitis?
“Ulcerative colitis is a chronic inflammatory disease state of unknown etiology. Its progression is erratic, with patients experiencing periods of exacerbations and remissions. Current therapeutic options have yielded less than satisfactory results.
With the discovery of the potential relationship between nonsmoking status and the onset of ulcerative colitis and the development of various nicotine dosage forms came the hypothesis that nicotine may play a protective role against the development of ulcerative colitis and maintenance of remission.
Hence, investigators began conducting clinical trials on the use of available nicotine dosage forms in the management of ulcerative colitis.”
“Overall, investigation of nicotine in the treatment of ulcerative colitis has yielded disappointing results.
CONCLUSION: Nicotine cannot be recommended as adjunctive or single therapy for the treatment of ulcerative colitis and will not alter current treatment options.”
http://www.ncbi.nlm.nih.gov/pubmed/10423604
Carbon Monoxide Soothes Inflammatory Bowel Disease
2006
“Doctors have long known that smokers rarely suffer from a common form of inflammatory bowel disease (IBD) called ulcerative colitis, but they didn’t know why.
A new study in the December 19 issue of The Journal of Experimental Medicine might help explain this apparent resistance. Scott Plevy and his colleagues at the University of Pittsburgh now show that carbon monoxide (CO), a component of cigarette smoke, helps shut down the intestinal inflammation that causes ulcerative colitis.”
“But recent scientific studies have shown that CO — at least at low concentrations — has a redeeming quality: it acts as an anti-inflammatory agent”
“The group traced the action of inhaled CO to a protein that is produced by immune cells called interleukin (IL)-12. IL-12 is normally produced during infection and helps activate the immune cells that fight off the invading pathogens.
But chronic production of IL-12 in the gut also drives the inflammation that causes ulcerative colitis.
Inhaled CO inhibited the production of IL-12, short-circuiting the disease-causing inflammation.”
https://www.sciencedaily.com/releases/2006/01/060103084934.htm
I don’t want the nightshade vegetables banned just because they contain nicotine and solanesol (“tar” I’m guessing)
Solanesol: a review of its resources, derivatives, bioactivities, medicinal applications, and biosynthesis
2015
“Solanesol, which mainly accumulates in solanaceous crops, including tobacco, tomato, potato, eggplant, and pepper plants, is a long-chain polyisoprenoid alcohol compound with nine isoprene units. Chemical synthesis of solanesol is difficult; therefore, solanesol is primarily extracted from solanaceous crops, particularly tobacco leaves. In plants, solanesol exists in both free and esterified forms, and its accumulation is influenced by genetic and environmental factors. Solanesol is widely used in the pharmaceutical industry as an intermediate for the synthesis of ubiquinone drugs, such as coenzyme Q10 and vitamin K2. Solanesol possesses antibacterial, antifungal, antiviral, anticancer, anti-inflammatory, and anti-ulcer activities, and solanesol derivatives also have anti-oxidant and antitumour activities, in addition to other bioactivities.”
https://link.springer.com/article/10.1007/s11101-015-9393-5#/page-1
I hope that wasn’t too long.
Another one posted before the date of MJM’s link, that might also be useful in explaining the missing smokers.
Nitric Oxide Inhibits the Replication Cycle of Severe Acute Respiratory Syndrome Coronavirus
ABSTRACT
“Nitric oxide (NO) is an important signaling molecule between cells which has been shown to have an inhibitory effect on some virus infections. The purpose of this study was to examine whether NO inhibits the replication cycle of the severe acute respiratory syndrome coronavirus (SARS CoV) in vitro. We found that an organic NO donor, S-nitroso-N-acetylpenicillamine, significantly inhibited the replication cycle of SARS CoV in a concentration-dependent manner. We also show here that NO inhibits viral protein and RNA synthesis. Furthermore, we demonstrate that NO generated by inducible nitric oxide synthase, an enzyme that produces NO, inhibits the SARS CoV replication cycle.”
https://jvi.asm.org/content/79/3/1966
Carl, you’ve pulled together some very good folks and good thinking here! It has truly been sad to see researchers finding results that in any truly unbiased scientific study would have been best described with language like this:
—
“This research indicates that smoking — for reasons possibly related to carbon monoxide, nicotine, nitric oxide, or other smoke elements — results in smokers resisting the development of symptomatic or moderate coronavirus possibly requiring hospitalization. However, for those patients (?how large a fraction?) who progress to pneumonia requiring mechanical ventilation, it appears that smokers (?perhaps only heavy or much older smokers or those with significant comorbidities?) are more likely to die from COVID-19 or comorbidities than nonsmokers.”
—
THAT is how I believe these findings SHOULD be described by professional and neutral researchers seeking to expand and share the knowledge that would help people with regard to coronavirus. Instead, it appears that what we are seeing is either that
A) The smoking data is simply not being gathered or is subsequently removed altogether due to its ‘undesirable’ medical implications. (examples if such exist?)
OR
B) The smoking data and its implications are simply being ignored in the research analytical text (examples?).
OR
C) The smoking data and its correlations that indicate a connection between smoking and more desirable outcomes in those exposed to possible infection are being expressed unclearly and/or are heavily downplayed as simply artifactual, unimportant, or needing further evaluation before anything can be said — without any mention of what the initial evaluation might indicate if the subject matter was less politically charged.
If my perception is correct, if we are indeed seeing A, B, or C in action in this time of emergency, I believe the researchers involved, as well as the funders or institutions that exert pressure for the treatment of science in such a political fashion, should be strongly and officially reprimanded and penalized. Additionally, the researchers themselves should speak to their failure in this regard and note what pressures may have led to that failure.
– MJM
IMPORTANT ADDENDUM: At one point in this posting you mention that
“carbon monoxide, a toxic gas found in car exhaust is still dangerous, and it is very difficult to gauge a safe dose for patients.”
but fail to point out that smokers routinely administer perfectly safe doses of carbon monoxide to themselves. While the overall long-term negative health effects of smoking may overshadow the desirable effects specific to dealing with coronavirus, it is up to individuals and patients to choose among medical treatment options that offer varying degrees of help while also offering various outcomes involving discomfort, pain, sacrifice, or chances of failure. For that choice to be sound, patients or potential patients must be given a fair and honest assessment of the positives and negatives with regard to smoking and CoVid-19.
Like it or not, researchers, doctors, and social activists simply DO NOT have the right to make such decisions for free individuals or to manipulate their research designs or findings in order to manipulate free individuals toward specific decisions based upon faulty information or its presentation.
– MJM
Is there not a further puzzle in these data in that in even if there were
no difference between hospitalisations according to smoking status this
would be odd given that smokers are in theory more likely to have diseases
that would put them in hospital if they have COVID 19.
So if such a protective effect exists it could actually be stronger than these numbers suggest or it could be that smokers are generally more healthy than non-smokers or a combination of the two.
However, to my knowledge no country in the world publishes anonymised data of disease rates according to smoking status. The UK has had these data for decades but never published them, to my knowledge, as I am sure many other countries do. Instead non-randomised samples are used such as the CPS II study, which is not terribly helpful as if we knew what the numbers were in the real world then we could make a better assessment of any relationship between COVID 19 and hospitalisations. And what the real differences are for chronic diseases according to status.
One of the big problems with this data is the whole question of who might end up in the dataset if particular things happened with them. This is the deeper question than the “are their differential probabilities of someone ending up in the sample if they meet the criterion (selection bias)”. Lots of people (far from all!) doing this stuff seem to understand the latter question. Only the most serious epidemiologists seem to recognize the former question and… let’s just say that they are not well-represented in tobacco research.
So you are right that smokers are more likely to be hospitalized as a result of X, for whatever unfortunate event befalls them, than nonsmokers of the same age and gender. One of the many things we don’t know from the ad hoc (and possibly full-on dishonest) data gathering is anything about whether someone was perhaps already hospitalized or on the verge of it when they entered the dataset.
The problem with that explanation is that it happened for SARS in 2003-2004, then COVID-19 in 2019-2020. And nothing in between (of course you can cherry pick a study or two with an odd sample but not every single one). Especially not MERS for which you can find plenty of studies heralding it as a risk factor. MERS doesn’t require ACE2, while SARS and SARS2 do.
Pingback: Sackstark! | Corona Virus – Leute, raucht um euer Leben
Hi, again, please post this with my name
I couldn’t avoid noticing an interesting example on how similar (not identical) demographic observations are not similarly reported when one of them involves smoking.
Observation (1) 68% of COVID-19 deaths in Chicago were African Americans, yet African Americans make only about 30% of the general population (in Chicago). 33% of those hospitalized in the USA are African Americans, but the latter are only 13% of the USA population. Source: CDC, Chicago Department of Public Health
Observation (2) 1.3% and 2.3% of COVID-19 hospitalized are respectively smokers and ex-smokers (CDC study) with smokers and ex-smokers respectively making 13.8% and 22% of the USA population
In Observation (1) nobody would question the fact that socioeconomic factors, discrimination and poverty have a detrimental effect on how COVID-19 is affecting African Americans. Yet, in Observation (2), there is a lot of resistance to even contemplate that smoking or nicotine could be playing some protective role.
Yes, I agree that these observations are not directly comparable, but notice that there is a lot of missing information both (statistical covariates, confounding, etc). Yet, one is taken at face value and the other is contested.
Pingback: Corona – ein Nichtrauchervirus? – Netzwerk Rauchen e.V.
Today I learnt
What is the role of interleukin-6 (IL-6) inhibitors in the treatment of coronavirus disease 2019 (COVID-19)?
“Interleukin-6 (IL-6) inhibitors may ameliorate severe damage to lung tissue caused by cytokine release in patients with serious COVID-19 infections. Several studies have indicated a “cytokine storm” with release of IL-6, IL-1, IL-12, and IL-18, along with tumor necrosis factor alpha (TNFα) and other inflammatory mediators. The increased pulmonary inflammatory response may result in increased alveolar-capillary gas exchange, making oxygenation difficult in patients with severe illness.”
https://www.medscape.com/answers/2500114-197455/what-is-the-role-of-interleukin-6-il-6-inhibitors-in-the-treatment-of-coronavirus-disease-2019-covid-19
And found
Carbon monoxide inhibits IL-17-induced IL-6 production through the MAPK pathway in human pulmonary epithelial cells.
2005
“Herein, we examine the production of cytokine IL-6 induced by IL-17 and the effect of CO on IL-17-induced IL-6 production in human pulmonary epithelial cell A549. We first show that IL-17 can induce A549 cells to release IL-6 and that CO can markedly inhibit IL-17-induced IL-6 production.”
https://www.ncbi.nlm.nih.gov/pubmed/16003000
I’m not on twitter so I’m putting it here.
Small study in Germany: https://www.aerzteblatt.de/int/archive/article/213455
Look at the patient characteristics – 8 of 50 under “nicotine abuse”. Of these 5 with “former nicotine abuse”, 3 with “ongoing nicotine abuse. Non of the latter developed ARDS.
Interesting, no?
https://www.telegraph.co.uk/news/2020/04/23/smokers-four-times-less-likely-contract-covid-19-prompting-nicotine/
All,
For those who haven’t seen it, Farsalinos et al. offer this editorial outlining their hypothesis that nicotine is the plaver in the inverse association between smoking & Covid-19. It’s a pre-proof and will likely have some refinements before it emerges in final form: https://www.sciencedirect.com/science/article/pii/S2214750020302924#bib0435 Editorial: Nicotine and SARS-CoV-2: COVID-19 may be a disease of the nicotinic cholinergic system
Open Access – Available Online 30 April 2020
Konstantinos Farsalinos, Raymond Niaura, Jacques Le Houezec, Anastasia Barbouni, … Konstantinos Poulas