Category Archives: Public health

Made up statistics on sugar tax

I woke up this morning to the sound of Radio 4 telling me that Cancer Research UK had done an analysis showing that a 20% tax on sugary drinks could reduce the number of obese people in the UK by 3.7 million by 2025. (That could be the start of the world’s worst ever blues song, but it isn’t.)

My first thought was that was rather surprising, as I wasn’t aware of any evidence on how sugar taxes impact on obesity. So I went hunting for the report with interest.

Bizarrely, Cancer Research UK didn’t link to the full report from their press release (once you’ve read the rest of this post, you may conclude that perhaps they were too embarrassed to let anyone see it), but I tracked it down here. Well, I’m not sure even that is the full report. It says it’s a “technical summary”, but the word “summary” makes me wonder if it is still not the full report. But that’s all that seems to be made publicly available.

There are a number of problems with this report. Christopher Snowdon has blogged about some of them here, but I want to focus on the extent to which the model is based on untested assumptions.

It turns out that the conclusions were indeed not based on any empirical data about how a sugar tax would impact on obesity, but on  a modelling study. This study made various assumptions about various things, principally the following:

  1. The price elasticity of demand for sugary drinks (ie the extent to which an increase in price reduces consumption)
  2. The extent to which a reduction in sugary drink consumption would reduce total calorie intake
  3. The effect of total calorie intake on body mass

The authors get 0/10 for transparent reporting for the first of those, as they don’t actually say what price elasticity they used. That’s pretty basic stuff, and not to report it is somewhat akin to reporting the results of a clinical trial of a new drug and not saying what dose of the drug you used.

However, the report does give a reference for their price elasticity data, namely this paper. I must say I don’t find the methods of that paper easy to follow. It’s not at all clear to me whether the price elasticities they calculated were actually based on empirical data or themselves the results of a modelling exercise. But the data that are used in that paper come from the period 2008 to 2010, when the UK was in the depths of  recession, and when it might be hypothesised that price elasticities were greater than in more economically buoyant times. They don’t give a single figure for price elasticity, but a range of 0.8 to 0.9. In other words, a 20% increase in the price of sugary drinks would be expected to lead to a 16-18% decrease in the quantity that consumers buy. At least in the depths of the worst recession since the 1930s.

That figure for price elasticity is a crucial input to the model, and if it is wrong, then the answers of the model will be wrong.

The next input is the extent to which a reduction in sugary drink consumption reduces total calorie intake.  Here, an assumption is made that total calorie intake is reduced by 60% of the amount of calories not consumed in sugary drinks. Or in other words, that if you forego the calories of a sugary drink, you only make up 40% of those from elsewhere.

Where does that 60% figure come from? Well, they give a reference to this paper. And how did that paper arrive at the 60% figure? Well, they in turn give a reference to this paper. And where did that get it from? As far as I can tell, it didn’t, though I note it reports the results of a clinical study in people trying to lose weight by dieting. Even if that 60% figure is based on actual data from that study, rather than just plucked out of thin air, I very much doubt that data on calorie substitution taken from people trying to lose weight would be applicable to the general population.

What about the third assumption, the weight loss effects of reduced calorie intake? We are told that reducing energy intake by 100 KJ per day results in 1 kg body weight loss. The citation given for that information is this study, which is another modelling study. Are none of the assumptions in this study based on actual empirical data?

A really basic part of making predictions by mathematical modelling is to use sensitivity analyses. The model is based on various assumptions, and sensitivity analyses answer the questions of what happens if those assumptions were wrong. Typically, the inputs to the model are varied over plausible ranges, and then you can see how the results are affected.

Unfortunately, no sensitivity analysis was done. This, folks, is real amateur hour stuff. The reason for the lack of sensitivity analysis is given in the report as follows:

“it was beyond the scope of this project to include an extensive sensitivity analysis. The microsimulation model is complex involving many thousands of calculations; therefore sensitivity analysis would require many thousands of consecutive runs using super computers to undertake this within a realistic time scale.”

That has to be one of the lamest excuses for shoddy methods I’ve seen in a long time. This is 2016. You don’t have to run the analysis on your ZX Spectrum.

So this result is based on a bunch of heroic assumptions which have little basis in reality, and the sensitivity of the model to those assumptions were not tested. Forgive me if I’m not convinced.

 

New alcohol guidelines

It has probably not escaped your attention that the Department of Health published new guidelines for alcohol consumption on Friday. These guidelines recommend lower limits than the previous guidelines, namely no more than 14 units per week. The figure is the same for men and women.

There are many odd things about these guidelines. But before I get into that, I was rightly picked up on a previous blogpost for not being clear about my own competing interests, so I’ll get those out of the way first, as I think it’s important.

I do not work either for the alcohol industry or in public health, so professionally speaking, I have no dog in this fight. However, at a personal level, I do like a glass of wine or two with my dinner, which I have pretty much every day. So my own drinking habits fall within the recommended limits of the previous guidelines (no more than 4 units per day for men), but under the new guidelines I would be classified as an excessive drinker. Do bear that in mind when reading this blogpost. I have tried to be as impartial as possible, but we are of course all subject to biases in the way we assess evidence, and I cannot claim that my assessment is completely unaffected by being classified as a heavy drinker under the new guidelines.

So, how were the new guidelines developed? This was a mixture of empirical evidence, mathematical modelling, and the judgement of the guidelines group. They were reasonably explicit about this process, and admit that the guidelines are “both pragmatic and evidence based”, so they get good marks for being transparent about their overall thinking.

However, it was not always easy to figure out what evidence was used, so they get considerably less good marks for being transparent about the precise evidence that led to the guidelines. It’s mostly available if you look hard enough, but the opacity of the referencing is disappointing. Very few statements in the guidelines document are explicitly referenced. But as far as I can tell, most of the evidence comes from two other documents, “A summary of the evidence of the health and social impacts of alcohol consumption” (see the document “Appendix 3 CMO Alcohol Guidelines Summary of evidence.pdf” within the zip file that you can download here) ,and the report of the Sheffield modelling group.

The specific way in which “14 units per week” was derived was as follows. The guidelines team investigated what level of alcohol consumption would be associated with no more than an “acceptable risk”, which is fair enough. Two definitions of “acceptable risk” were used, based on recent work in developing alcohol guidelines in Canada and Australia. The Canadian definition of acceptable risk was a relative risk of alcohol-related mortality of 1, in other words, the point at which the overall risk associated with drinking, taking account of both beneficial and harmful effects, was the same as the risk for a non-drinker. The Australian definition of acceptable risk was that the proportion of deaths in the population attributable to alcohol, assuming that everyone in the population drinks at the recommended limit, is 1%. In practice, both methods gave similar results, so choosing between them is not important.

To calculate the the levels of alcohol that would correspond to those risks, a mathematical model was used which incorporated empirical data on 43 diseases which are known to be associated with alcohol consumption. Risks for each were considered, and the total mortality attributable to alcohol was calculated from those risks (although the precise mathematical calculations used were not described in sufficient detail for my liking).

These results are summarised in the following table (table 1 in both the guidelines document and the Sheffield report). Results are presented separately for men and women, and also separately depending on how many days each week are drinking days. The more drinking days you have per week for the same weekly total, the less you have on any given day. So weekly limits are higher if you drink 7 days per week than if you drink 1 day per week, because of the harm involved with binge drinking if you have your entire weekly allowance on just one day.

Table 1

Assuming that drinking is spread out over a few days a week, these figures are roughly in the region of 14, so that is where the guideline figure comes from. The same figure is now being used for men and women.

Something you may have noticed about the table above is that it implies the safe drinking limits are lower for men than for women. You may think that’s a bit odd. I think that’s a bit odd too.

Nonetheless, the rationale is explained in the report. We are told (see paragraph 46 of the guidelines document) that the risks of immediate harm from alcohol consumption, usually associated with binge-drinking in a single session, “are greater for men than for women, in part because of men’s underlying risk taking behaviours”. That sounds reasonably plausible, although no supporting evidence is offered for the statement.

To be honest, I find this result surprising. According to table 6 on page 35 of the Sheffield modelling report, deaths from the chronic effects of alcohol (eg cancer) are about twice as common as deaths from the acute affects of alcohol (eg getting drunk and falling under a bus). We also know that women are more susceptible than men to the longer term effect of alcohol. And yet it appears that the acute effects dominate this analysis.

Unfortunately, although the Sheffield report is reasonably good at explaining the inputs to the mathematical model, specific details of how the model works are not presented. So it is impossible to know why the results come out in this surprising way and whether it is reasonable.

There are some other problems with the model.

I think the most important one is that the relationship between alcohol consumption and risk was often assumed to be linear. This strikes me as a really bad assumption, perhaps best illustrated with the following graph (figure 11 on page 45 of the Sheffield report).

Figure 11

This shows how the risk of hospital admission for acute alcohol-related causes increases as a function of peak day consumption, ie the amount of alcohol drunk in a single day.

A few moments’ thought suggest that this is not remotely realistic.

The risk is expressed as a relative risk, in other words how many times more likely you are to be admitted to hospital for an alcohol-related cause than you are on a day when you drink no alcohol at all. Presumably they consider that there is a non-zero risk when you don’t drink at all, or a relative risk would make no sense. Perhaps that might be something like being injured in a road traffic crash where you were perfectly sober but the other driver was drunk.

But it’s probably safe to say that the risk of being hospitalised for an alcohol-related cause when you have not consumed any alcohol is low. The report does not make it clear what baseline risk they are using, but let’s assume conservatively that the daily risk is 1 in 100, or 1%. That means that you would expect to be admitted to hospital for an alcohol-related cause about 3 times a year if you don’t drink at all. I haven’t been admitted to hospital 3 times in the last year (or even once, in fact) for an alcohol related cause, and I’ve even drunk alcohol on most of those days. I doubt my experience of lack of hospitalisation is unusual. So I think it’s probably safe to assume that 1% is a substantial overestimate of the true baseline risk.

Now let’s look at the top right of the graph. That suggests that my relative risk of being admitted to hospital for an alcohol-related cause would be 6 times higher if I drink 50 units in a day. In other words, that my risk would be 6%. And remember that that is probably a massive overestimate.

Now, 50 units of alcohol is roughly equivalent to a bottle and a half of vodka. I don’t know about you, but I’m pretty sure that if I drank a bottle and a half of vodka in a single session then my chances of being hospitalised – if I survived that long – would be close to 100%.

So I don’t think that a linear function is realistic. I don’t have any data on the actual risk, but I would expect it to look something more like this:

Alcohol graph

Here we see that the risk is negligible at low levels of alcohol consumption, then increases rapidly once you get into the range of serious binge drinking, and approaches 100% as you consume amounts of alcohol unlikely to be compatible with life. The precise form of that graph is something I have just guessed at, but I’m pretty sure it’s a more reasonable guess than a linear function.

A mathematical model is only as good as the data used as inputs to the model and the assumptions used in the modelling. Although the data used are reasonably clearly described and come mostly from systematic reviews of the literature, the way in which the data are modelled is not sufficiently clear, and also makes some highly questionable assumptions. Although some rudimentary sensitivity analyses were done, no sensitivity analyses were done using risk functions other than linear ones.

So I am not at all sure I consider the results of the mathematical modelling trustworthy. Especially when it comes up with the counter-intuitive result that women can safely drink more than men, which contradicts most of the empirical research in this area.

But perhaps more importantly, I am also puzzled why it was felt necessary to go through a complex modelling process in the first place.

It seems to me that the important question here is how does your risk of premature death depend on your alcohol consumption. That, at any rate, is what was modelled.

But there is no need to model it: we actually have empirical data. A systematic review of 34 prospective studies by Di Castelnuovo et al published in 2006 looked at the relationship between alcohol consumption and mortality. This is what it found (the lines on either side of the male and female lines are 99% confidence intervals).

Systematic review

This shows that the level of alcohol consumption associated with no increased mortality risk compared with non-drinkers is about 25 g/day for women and 40 g/day for men. A standard UK unit is 8 g of alcohol, so that converts to about 22 units per week for women and 35 units per week for men: not entirely dissimilar to the previous guidelines.

Some attempt is made to explain why the data on all cause mortality have not been used, but I do not find them convincing (see page 7 of the summary of evidence).

One problem we are told is that “most of the physiological mechanisms that have been suggested to explain the protective effect of moderate drinking only apply for cohorts with overall low levels of consumption and patterns of regular drinking that do not vary”. That seems a bizarre criticism. The data show that there is a protective effect only at relatively low levels of consumption, and that once consumption increases, so does the risk. So of course the protective effect only applies at low levels of consumption. As for the “patterns of regular drinking”, the summary makes the point that binge drinking is harmful. Well, we know that. The guidelines already warn of the dangers of binge drinking. It seems odd therefore, to also reject the findings for people who split their weekly consumption evenly over the week and avoid binge drinking, as this is exactly what the guidelines say you should do.

I do not understand why studies which apply to people who follow safe drinking guidelines are deemed to be unsuitable for informing safe drinking guidelines. That makes no sense to me.

The summary also mentions the “sick quitter hypothesis” as a reason to mistrust the epidemiological data. The sick quitter hypothesis suggests that the benefits of moderate drinking compared with no drinking may have been overestimated in epidemiological studies, as non-drinkers may include recovering alcoholics and other people who have given up alcohol for health reasons, and therefore include an unusually unhealthy population.

The hypothesis seems reasonable, but it is not exactly a new revelation to epidemiologists, and has been thoroughly investigated. The systematic review by Di Castelnuovo reported a sensitivity analysis including only studies which excluded former drinkers from their no-consumption category. That found a lower beneficial effect on mortality than in the main analysis, but the protective effect was still unambiguously present. The point at which drinkers had the same risk as non-drinkers in that analysis was about 26 units per week (this is an overall figure: separate figures for men and women were not presented in the sensitivity analysis).

A systematic review specifically of cardiovascular mortality by Ronksley et al published in 2011 also ran a sensitivity analysis where only lifelong non-drinkers were used as the reference category, and found it made little difference to the results.

So although the “sick quitter hypothesis” sounds like a legitimate concern, in fact it has been investigated and is not a reason to distrust the results of the epidemiological analyses.

So all in all, I really do not follow the logic of embarking on a complex modelling exercise instead of using readily available empirical data. Granted, the systematic review by Di Castelnuovo et al is 10 years old now, but surely a more appropriate response to that would have been to commission an updated systematic review rather than ignore the systematic review evidence on mortality altogether and go down a different and problematic route.

Does any of this matter? After all, the guidelines are not compulsory. If my own reading of the evidence tells me I can quite safely drink 2 glasses of wine with my dinner most nights, I am completely free to do so.

Well, I think this does matter. If the government are going to publish guidelines on healthy behaviours, I think it is important that they be as accurate and evidence-based as possible. Otherwise the whole system of public health guidelines will fall into disrepute, and then it is far less likely that even sensible guidelines will be followed.

What is particularly concerning here is the confused messages the guidelines give about whether moderate drinking has benefits. From my reading of the literature, it certainly seems likely that there is a health benefit at low levels of consumption. That, at any rate, is the obvious conclusion from Di Castelnuovo et al’s systematic review.

And yet the guidelines are very unclear about this. While even the Sheffield model used to support the guidelines shows decreased risks at low levels of alcohol consumption (and those decreased risks would extend to substantially higher drinking levels if you base your judgement on the systematic review evidence), the guidelines themselves say that such decreased risks do not exist.

The guideline itself says “The risk of developing a range of diseases (including, for example, cancers of the mouth, throat, and breast) increases with any amount you drink on a regular basis”. That is true, but it ignore the fact that it is not true for other diseases. To mention only the harms of alcohol and ignore the benefits in the guidelines seems a dishonest way to present data. Surely the net effect is what is important.

Paragraph 30 of the guidelines document says “there is no level of drinking that can be recommended as completely safe long term”, which is also an odd thing to say when moderate levels of drinking have a lower risk than not drinking at all.

There is no doubt that the evidence on alcohol and health outcomes is complex. For obvious reasons, there have been no long-term randomised controlled trials, so we have to rely on epidemiological research with all its limitations. So I do not pretend for a moment that developing guidelines on what is a safe amount of alcohol to drink is easy.

But despite that, I think the developers of these guidelines could have done better.

Dangerous nonsense about vaping

If you thought you already had a good contender for “most dangerous, irresponsible, and ill-informed piece of health journalism of 2015”, then I’m sorry to tell you that it has been beaten into second place at the last minute.

With less than 36 hours left of 2015, I am confident that this article by Sarah Knapton in the Telegraph will win the title.

The article is titled “E-cigarettes are no safer than smoking tobacco, scientists warn”. The first paragraph is

“Vaping is no safer that [sic] smoking, scientists have warned after finding that e-cigarette vapour damages DNA in ways that could lead to cancer.”

There are such crushing levels of stupid in this article it’s hard to know where to start. But perhaps I’ll start by pointing out that a detailed review of the evidence on vaping by Public Health England, published earlier this year, concluded that e-cigarettes are about 95% less harmful than smoking.

If you dig into the detail of that review, you find that most of the residual 5% is the harm of nicotine addiction. It’s debatable whether that can really be called a harm, given that most people who vape are already addicted to nicotine as a result of years of smoking cigarettes.

But either way, the evidence shows that vaping, while it may not be 100% safe (though let’s remember that nothing is 100% safe: even teddy bears kill people), is considerably safer than smoking. This should not be a surprise. We have a pretty good understanding of what the toxic components of cigarette smoke are that cause all the damage, and most of those are either absent from e-cigarette vapour or present at much lower concentrations.

So the question of whether vaping is 100% safe is not the most relevant thing here. The question is whether it is safer than smoking. Nicotine addiction is hard to beat, and if a smoker finds it impossible to stop using nicotine, but can switch from smoking to vaping, then that is a good thing for that person’s health.

Now, nothing is ever set in stone in science. If new evidence comes along, we should always be prepared to revise our beliefs.

But obviously to go from a conclusion that vaping is 95% safer than smoking to concluding they are both equally harmful would require some pretty robust evidence, wouldn’t it?

So let’s look at the evidence Knapton uses as proof that all the previous estimates were wrong and vaping is in fact as harmful as smoking.

The paper it was based on is this one, published in the journal Oral Oncology.  (Many thanks to @CaeruleanSea for finding the link for me, which had defeated me after Knapton gave the wrong journal name in her article.)

The first thing to notice about this is that it is all lab based, using cell cultures, and so tells us little about what might actually happen in real humans. But the real kicker is that if we are going to compare vaping and smoking and conclude that they are as harmful as each other, then the cell cultures should have been exposed to equivalent amounts of e-cigarette vapour and cigarette smoke.

The paper describes how solutions were made by drawing either the vapour or smoke through cell media. We are then told that the cells were treated with the vaping medium every 3 days for up to 8 weeks. So presumably the cigarette medium was also applied every 3 days, right?

Well, no. Not exactly. This is what the paper says:

“Because of the high toxicity of cigarette smoke extract, cigarette-treated samples of each cell line could only be treated for 24 h.”

Yes, that’s right. The cigarette smoke was applied at a much lower intensity, because otherwise it killed the cells altogether. So how can you possibly conclude that vaping is no worse than smoking, when smoking is so harmful it kills the cells altogether and makes it impossible to do the experiment?

And yet despite that, the cigarettes still had a larger effect than the vaping. It is also odd that the results for cigarettes are not presented at all for some of the assays. I wonder if that’s because it had killed the cells and made the assays impossible? As primarily a clinical researcher, I’m not an expert in lab science, but not showing the results of your positive control seems odd to me.

But the paper still shows that the e-cigarette extract was harming cells, so that’s still a worry, right?

Well, there is the question of dose. It’s hard for me to know from the paper how realistic the doses were, as this is not my area of expertise, but the press release accompanying this paper (which may well be the only thing that Knapton actually read before writing her article) tells us the following:

“In this particular study, it was similar to someone smoking continuously for hours on end, so it’s a higher amount than would normally be delivered,”

Well, most things probably damage cells in culture if used at a high enough dose, so I don’t think this study really tells us much. All it tells us is that cigarettes do far more damage to cell cultures than e-cigarette vapour does. Because, and I can’t emphasise this point enough, THEY COULDN’T DO THE STUDY WITH EQUIVALENT DOSES OF CIGARETTE SMOKE BECAUSE IT KILLED ALL THE CELLS.

A charitable explanation of how Knapton could write such nonsense might be that she simply took the press release on trust (to be clear, the press release also makes the claim that vaping is as dangerous as smoking) and didn’t have time to check it. But leaving aside the question of whether a journalist on a major national newspaper should be regurgitating press releases without any kind of fact checking, I note that many people (myself included) have been pointing out to Knapton on Twitter that there are flaws in the article, and her response has been not to engage with such criticism, but to insist she is right and to block anyone who disagrees: the Twitter equivalent of the “la la la I’m not listening” argument.

It seems hard to come up with any explanation other than that Knapton likes to write a sensational headline and simply doesn’t care whether it’s true, or, more importantly, what harm the article may do.

And make no mistake: articles like this do have the potential to cause harm. It is perfectly clear that, whether or not vaping is completely safe, it is vastly safer than smoking. It would be a really bad outcome if smokers who were planning to switch to vaping read Knapton’s article and thought “oh, well if vaping is just as bad as smoking, maybe I won’t bother”. Maybe some of those smokers will then go on to die a horrible death of lung cancer, which could have been avoided had they switched to vaping.

Is Knapton really so ignorant that she doesn’t realise that is a possible consequence of her article, or does she not care?

And in case you doubt that anyone would really be foolish enough to believe such nonsense, I’m afraid there is evidence that people do believe it. According to a survey by Action on Smoking and Health (ASH), the proportion of people who believe that vaping is as harmful or more harmful than smoking increased from 14% in 2014 to 22% in 2015. And in the USA, the figures may be even worse: this study found 38% of respondents thought e-cigarettes were as harmful or more harmful than smoking. (Thanks again to @CaeruleanSea for finding the links to the surveys.)

I’ll leave the last word to Deborah Arnott, Chief Executive of ASH:

“The number of ex-smokers who are staying off tobacco by using electronic cigarettes is growing, showing just what value they can have. But the number of people who wrongly believe that vaping is as harmful as smoking is worrying. The growth of this false perception risks discouraging many smokers from using electronic cigarettes to quit and keep them smoking instead which would be bad for their health and the health of those around them.”

The Independent’s anti-vaccine scaremongering

Last weekend The Independent published a ridiculous piece of antivaccine scaremongering by Paul Gallagher on their front page. They report the story of girls who became ill after receiving HPV vaccine, and strongly imply that the HPV vaccine was the cause of the illnesses, flying in the face of massive amounts of scientific evidence to the contrary.

I could go on at length about how dreadful, irresponsible, and scientifically illiterate the article was, but I won’t, because Jen Gunter and jdc325 have already done a pretty good job of that. You should go and read their blogposts. Do it now.

Right, are you back? Let’s carry on then.

What I want to talk about today is the response I got from the Independent when I emailed the editor of the Independent on Sunday, Lisa Markwell, to suggest that they might want to publish a rebuttal to correct the dangerous misinformation in the original article. Ms Markwell was apparently too busy to reply to a humble reader, so my reply was from the deputy editor, Will Gore.  Here it is below, with my annotations.

Dear Dr Jacobs

Thank you for contacting us about an article which appeared in last weekend’s Independent on Sunday.

Media coverage of vaccine programmes – including reports on concerns about real or perceived side-effects – is clearly something which must be carefully handled; and we are conscious of the potential pitfalls. Equally, it is important that individuals who feel their concerns have been ignored by health care professionals have an outlet to explain their position, provided it is done responsibly.

I’d love to know what they mean by “provided it is done responsibly”. I think a good start would be not to stoke anti-vaccine conspiracy theories with badly researched scaremongering. Obviously The Independent has a different definition of “responsibly”. I have no idea what that definition might be, though I suspect it includes something about ad revenue.

On this occasion, the personal story of Emily Ryalls – allied to the comparatively large number of ADR reports to the MHRA in regard to the HPV vaccine – prompted our attention. We made clear that no causal link has been established between the symptoms experienced by Miss Ryalls (and other teenagers) and the HPV vaccine. We also quoted the MHRA at length (which says the possibility of a link remains ‘under review’), as well as setting out the views of the NHS and Cancer Research UK.

Oh, seriously? You “made it clear that no causal link has been established”? Are we even talking about the same article here? The one I’m talking about has the headline “Thousands of teenage girls enduring debilitating illnesses after routine school cancer vaccination”. On what planet does that make it clear that the link was not causal?

I think what they mean by “made it clear that no causal link has been established” is that they were very careful with their wording not to explicitly claim a causal link, while nonetheless using all the rhetorical tricks at their disposal to make sure a causal link was strongly implied.

Ultimately, we were not seeking to argue that vaccines – HPV, or others for that matter – are unsafe.

No, you’re just trying to fool your readers into thinking they’re unsafe. So that’s all right then.

Equally, it is clear that for people like Emily Ryalls, the inexplicable onset of PoTS has raised questions which she and her family would like more fully examined.

And how does blaming it on something that is almost certainly not the real cause help?

Moreover, whatever the explanation for the occurrence of PoTS, it is notable that two years elapsed before its diagnosis. Miss Ryalls’ family argue that GPs may have failed to properly assess symptoms because they were irritated by the Ryalls mentioning the possibility of an HPV connection.

I don’t see how that proves a causal link with the HPV vaccine. And anyway, didn’t you just say that you were careful to avoid claiming a causal link?

Moreover, the numbers of ADR reports in respect of HPV do appear notably higher than for other vaccination programmes (even though, as the quote from the MHRA explained, the majority may indeed relate to ‘known risks’ of vaccination; and, as you argue, there may be other particular explanations).

Yes, there are indeed other explanations. What a shame you didn’t mention them in your story. Perhaps if you had done, your claim to be careful not to imply a causal link might look a bit more plausible. But I suppose you don’t like the facts to get in the way of a good story, do you?

The impact on the MMR programme of Andrew Wakefield’s flawed research (and media coverage of it) is always at the forefront of editors’ minds whenever concerns about vaccines are raised, either by individuals or by medical studies. But our piece on Sunday was not in the same bracket.

No, sorry, it is in exactly the same bracket. The media coverage of MMR vaccine was all about hyping up completely evidence-free scare stories about the risks of MMR vaccine. The present story is all about hyping up completely evidence-free scare stories about the risk of HPV vaccine. If you’d like to explain to me what makes those stories different, I’m all ears.

It was a legitimate item based around a personal story and I am confident that our readers are sophisticated enough to understand the wider context and implications.

Kind regards

Will Gore
Deputy Managing Editor

If Mr Gore seriously believes his readers are sophisticated enough to understand the wider context, then he clearly hasn’t read the readers’ comments on the article. It is totally obvious that a great many readers have inferred a causal relationship between the vaccine and subsequent illness from the article.

I replied to Mr Gore about that point, to which he replied that he was not sure the readers’ comments are representative.

Well, that’s true. They are probably not. But they don’t need to be.

There are no doubt some readers of the article who are dyed-in-the-wool anti-vaccinationists. They believed all vaccines are evil before reading the article, and they still believe all vaccines are evil. For those people, the article will have had no effect.

Many other readers will have enough scientific training (or just simple common sense) to realise that the article is nonsense. They will not infer a causal relationship between the vaccine and the illnesses. All they will infer is that The Independent is spectacularly incompetent at reporting science stories and that it would be really great if The Independent could afford to employ someone with a science GCSE to look through some of their science articles before publishing them. They will also not be harmed by the article.

But there is a third group of readers. Some people are not anti-vaccine conspiracy theorists, but nor do they have science training. They probably start reading the article with an open mind. After reading the article, they may decide that HPV vaccine is dangerous.

And what if some of those readers are teenage girls who are due for the vaccination? What if they decide not to get vaccinated? What if they subsequently get HPV infection, and later die of cervical cancer?

Sure, there probably aren’t very many people to whom that description applies. But how many is an acceptable number? Perhaps Gallagher, Markwell, and Gore would like to tell me how many deaths from cervical cancer would be a fair price to pay for writing the article?

It is not clear to me whether Gallagher, Markwell, and Gore are simply unaware of the harm that such an article can do, or if they are aware, and simply don’t care. Are they so naive as to think that their article doesn’t promote an anti-vaccinationist agenda, or do they think that clicks on their website and ad revenue are a more important cause than human life?

I really don’t know which of those possibilities I think is more likely, nor would I like to say which is worse.

Is smoking plunging children into poverty?

If we feel it necessary to characterise ourselves as being “pro” or “anti” certain things, I would unambiguously say that I am anti-smoking. Smoking is a vile habit. I don’t like being around people who are smoking. And as a medical statistician, I am very well aware of the immense harm that smoking does to the health of smokers and those unfortunate enough to be exposed to their smoke.

So it comes as a slight surprise to me that I find myself writing what might be seen as a pro-smoking blogpost for the second time in just a few weeks.

But this blogpost is not intended to be pro-smoking: it is merely anti the misuse of statistics by some people in the anti-smoking lobby. Just because you are campaigning against a bad thing does not give you a free pass to throw all notions of scientific rigour and social responsibility to the four winds.

An article appeared yesterday on the Daily Mail website with the headline:

“Smoking not only kills, it plunges children into POVERTY because parents ‘prioritise cigarettes over food'”

and a similar, though slightly less extreme, version appeared in the Independent:

“Smoking parents plunging nearly half a million children into poverty, says new research”

According to the Daily Mail, parents are failing to feed their children because they are spending money on cigarettes instead of food. The Independent is not quite so explicit in claiming that, but it’s certainly implied.

Regular readers of this blog will no doubt already have guessed that those articles are based on some research which may have been vaguely related to smoking and poverty, but which absolutely did not show that any children were going hungry because of their parents’ smoking habits. And they would be right.

The research behind these stories is this paper by Belvin et al. There are a number of problems with it, and particularly with the way their findings have been represented in the media.

The idea of children being “plunged into poverty” came from looking at the number of families with at least one smoker who were just above the poverty line. Poverty in this case is defined as a household income less than 60% of the median household income (taking into account family size). If the amount families above the poverty line spent on cigarettes took their remaining income after deducting their cigarette expenditure below the poverty line, then they were regarded as being taken into poverty by smoking.

Now, for a start, Belvin et al did not actually measure how much any family just above the poverty line spent on smoking. They made a whole bunch of estimates and extrapolations from surveys that were done for different purposes. So that’s one problem for a start.

Another problem is that absolutely nowhere did Belvin et al look at expenditure on food. There is no evidence whatsoever from their study that any family left their children hungry, and certainly not that smoking was the cause. Claiming that parents were prioritising smoking over food is not even remotely supported by the study, as it’s just not something that was measured at all.

Perhaps the most pernicious problem is the assumption that poverty was specifically caused by smoking. I expect many families with an income above 60% of the median spend some of their money on something other than feeding their children. Perhaps some spend their money on beer. Perhaps others spend money on mobile phone contracts. Or maybe on going to the cinema. Or economics textbooks. Or pretty much anything else you can think of that is not strictly essential. Any of those things could equally be regarded as “plunging children into poverty” if deducting it from expenditure left you below median income.

So why single out smoking?

I have a big problem with this. I said earlier that I thought smoking was a vile habit. But there is a big difference between believing smoking is a vile habit and believing smokers are vile people. They are not. They are human beings. To try to pin the blame on them for their children’s poverty (especially in the absence of any evidence that their children are actually going hungry) is troubling. I am not comfortable with demonising minority groups. It wouldn’t be OK if the group in question were, say, Muslims, and it’s not OK when the group is smokers.

There are many and complex causes of poverty. But blaming the poor is really not the response of a civilised society.

The way this story was reported in the Daily Mail is, not surprisingly, atrocious. But it’s not entirely their fault. The research was filtered through Nottingham University’s press office before it got to the mainstream media, and I’m afraid to say that Nottingham University are just as guilty here. Their press release states

“The reserch [sic] suggests that parents are likely to forgo basic household and food necessities in order to fund their smoking addiction.”

No, the research absolutely does not suggest that, because the researchers didn’t measure it. In fact I think Nottingham University are far more guilty than the Daily Mail. An academic institution really ought to know better than to misrepresent the findings of their research in this socially irresponsible way.

Are strokes really rising in young people?

I woke up to the news this morning that there has been an alarming increase in the number of strokes in people aged 40-54.

My first thought was “this has been sponsored by a stroke charity, so they probably have an interest in making the figures seem alarming”. So I wondered how robust the research was that led to this conclusion.

The article above did not link to a published paper describing the research. So I looked on the Stroke Association’s website. There, I found a press release. This press release also didn’t link to any published paper, which makes me think that there is no published paper. It’s hard to believe a press release describing a new piece of research would fail to tell you if it had been published in a respectable journal.

The press release describes data on hospital admissions provided by the NHS, which shows that the number of men aged 40 to 54 admitted to hospital with strokes increased from 4260 in the year 2000 to to 6221 in 2014, and the equivalent figures for women were an increase from 3529 to 4604.

Well, yes, those figures are certainly substantial increases. But there could be various different reasons for them, some worrying, others reassuring.

It is possible, as the press release certainly wants us to believe, that the main reason for the increase is that strokes are becoming more common. However, it is also possible that recognition of stroke has improved, or that stroke patients are more likely now to get the hospital treatment they need than in the past. Both of those latter explanations would be good things.

So how do the stroke association distinguish among those possibilities?

Well, they don’t. The press release says “It is thought that the rise is due to increasing sedentary and unhealthy lifestyles, and changes in hospital admission practice.”

“It is thought that”? Seriously? Who thinks that? And why do they think it?

It’s nice that the Stroke Association acknowledge the possibility that part of the reason might be changes in hospital admission practice, but given that the title of the press release is “Stroke rates soar among men and women in their 40s and 50s” (note: not “Rates of hospital admission due to stroke soar”), there can be no doubt which message the Stroke Association want to emphasise.

I’m sorry, but they’re going to need better evidence than “it is thought that” to convince me they have teased out the relative contributions of different factors to the rise in hospital admissions.

Vaping among teenagers

Vaping, or use of e-cigarettes, has the potential to be a huge advance in public health. It provides an alternative to smoking that allows addicted smokers to get their nicotine fix without exposing them to all the harmful chemicals in cigarette smoke. This is a development that should be welcomed with open arms by everyone in the public health community, though oddly, it doesn’t seem to be. Many in the public health community are very much against vaping. The reasons for that might make an interesting blogpost for another day.

But today, I want to talk about a piece of research into vaping among teenagers that’s been in the news a lot today.

Despite the obvious upside of vaping, there are potential downsides. The concern is that it may be seen as a “gateway” to smoking. There is a theoretical risk that teenagers may be attracted to vaping and subsequently take up smoking. Obviously that would be a thoroughly bad thing for public health.

Clearly, it is an area that is important to research so that we can better understand what the downside might be of vaping.

So I was interested to see that a study has been published today that looks specifically at smoking among teenagers. Can that help to shed light on these important questions?

Looking at some of the stories in the popular media, you might think it could. We are told that e-cigs are the “alcopops of the nicotine world“, that there are “high rates of usage among secondary school pupils” and that e-cigs are “encouraging people to take up smoking“.

Those claims are, to use a technical term, bollocks.

Let’s look at what the researchers actually did. They used cross sectional questionnaire data in which a single question was asked about vaping: “have you ever tried or purchased e-cigarettes?”

The first thing to note is that the statistics are about the number of teenagers who have ever tried vaping. So they will be included in the statistics if they tried it once. Perhaps they were at a party and they had a single puff on a mate’s e-cig. The study gives us absolutely no information on the proportion of teenagers who vaped regularly. So to conclude “high rates of usage” just isn’t backed up by any evidence. Overall, about 1 in 5 of the teenagers answered yes to the question. Without knowing how many of those became regular users, it becomes very hard to draw any conclusions from the study.

But it gets worse.

The claim that vaping is encouraging people to take up smoking isn’t even remotely supported by the data. To do that, you would need to know what proportion of teenagers who hadn’t previously smoked try vaping, and subsequently go on to start smoking. Given that the present study is a cross sectional one (ie participants were studied only at a single point in time), it provides absolutely no information on that.

Even if you did know that, it wouldn’t tell you that vaping was necessarily a gateway to smoking. Maybe teenagers who start vaping and subsequently start smoking would have smoked anyway. To untangle that, you’d ideally need a randomised trial of areas in which vaping is available and areas in which it isn’t, though I can’t see that ever being done. The next best thing would be to look at changes in the prevalence of smoking among teenagers before and after vaping became available. If it increased after vaping became available, that might give you some reason to think vaping is acting as a gateway to smoking. But the current study provides absolutely no information to help with this question.

I’ve filed post this under “Dodgy reporting”, and of course the journalists who wrote about the study in such uncritical terms really should have known better, but actually I think the real fault lies here with the authors of the paper. In their conclusions, they write “Findings suggest that e-cigarettes are being accessed by teenagers more for experimentation than smoking cessation.”

No, they really don’t show that at all. Of those teenagers who had tried e-cigs, only 15.8% were never-smokers. And bear in mind that most of the overall sample (61.2%) were never-smokers. That suggests that e-cigs are far more likely to be used by current or former smokers than by non-smokers. In fact while only 4.9% of never smokers had tried e-cigs, (remember, that may mean only trying them once), 50.7% of ex-smokers had tried them. So a more reasonable conclusion might be that vaping is helping ex-smokers to quit, though in fact I don’t think it’s possible even to conclude that much from a cross-sectional study that didn’t measure whether vaping was a one-off puff or a habit.

While there are some important questions to be asked about how vaping is used by teenagers, I’m afraid this new study does absolutely nothing to help answer them.

 Update 1 April:

It seems I’m not the only person in the blogosphere to pick up some of the problems with the way this study has been spun. Here’s a good blogpost from Clive Bates, which as well as making several important points in its own right also contains links to some other interesting comment on the study.

 

Plain packaging for tobacco

Plain packaging for tobacco is in the news today. The idea behind it is that requiring tobacco manufacturers to sell cigarettes in unbranded packages, where all the branding has been replaced by prominent health warnings, will reduce the number of people who smoke, and thereby benefit public health.

But will it work?

That’s an interesting question. There’s a lot of research that’s been done, though it’s fair to say none of it is conclusive. For example, there has been research on how it affects young people’s perceptions of cigarettes and on what happened to the number of people looking for help with quitting smoking after plain packaging was introduced in Australia.

But for me, those are not the most interesting pieces of evidence.

What tells me that plain packaging is overwhelmingly likely to be an extremely effective public health measure is that the tobacco industry are strongly opposed to it. They probably know far more about the likely effects than the rest of us: after all, for me, it’s just a matter of idle curiosity, but for them, millions of pounds of their income depends on it. So the fact they are against it tells us plenty.

Let’s look in a little more detail at exactly what it tells us. Advertising and branding generally has 2 related but distinguishable aims for a company that sells something. One aim is to increase their share of the market, in other words to sell more of their stuff than their competitors in the same market. The other is to increase the overall size of the market, so that they sell more, and their competitors sell more as well. Both those things can be perfectly good reasons for a company to spend their money on advertising and branding.

But the difference between those 2 aims is crucial here.

If the point of cigarette branding were just to increase market share without affecting the overall size of the market, then the tobacco industry should be thoroughly in favour of a ban. Advertising and branding budgets, when the overall size of the market is constant, are a classic prisoner’s dilemma. If all tobacco companies spend money on branding, they will all have pretty much the same share as if no-one did, so they will gain nothing, but they will spend money on branding, so they’re worse off than if they didn’t. However, they can’t afford not to spend money on branding, as then they would lose market share to their competitors, who are still spending money on it.

The ideal situation for the tobacco industry in that case would be that no-one would spend any money on branding. But how can you achieve that? For all the companies to agree not to spend money on branding might be an illegal cartel, and there’s always a risk that someone would break the agreement to increase their market share.

A government-mandated ban solves that problem nicely. If all your competitors are forced not to spend money on branding, then you don’t have to either. All the tobacco companies win.

So if that were really the situation, then you would expect the tobacco companies to be thoroughly in favour of it. But they’re not. So that tells me that we are not in the situation where the total market size is constant.

The tobacco companies must believe, and I’m going to assume here that they know what they’re doing, that cigarette branding affects the overall size of the market. If branding could increase the overall size of the market (or more realistically when smoking rates in the UK are on a long-term decline, stop it shrinking quite as fast), then it would be entirely rational for the tobacco companies to oppose mandatory plain packaging.

I don’t know about you, but that’s all the evidence I need to convince me that plain packaging is overwhelmingly likely to be an effective public health measure.