While I've tried to avoid selecting straw men for this analysis, I haven't been terribly rigorous in my selection criteria - the selection is in any case limited by the need to choose studies which are freely available to, thus checkable by, the public. To address this potential source of actual or perceived bias, I will make this commitment: should Hitchens care to propose, in comments to this post, any other paper which he considers invulnerable to my objections, or should any author of a paper on the topic propose theirs, I will respond with a post dedicated to analysing that paper.
The two papers represent the two specific sources of error which I discern in this area of research: first, the existence of a common predisposition, in the sense outlined previously, that influences both cannabis use and the emergence of schizophrenia; and second, the confusion of transient cannabis-related phenomena with evidence of schizophrenia.
Before proceeding, I'll mention two other matters.
First, a merely illustrative example of the context in which this research is proceeding. A review paper published in the Lancet, Moore et al., Cannabis use and risk of psychotic or affective mental health outcomes: a systematic review, states that
There is now sufficient evidence to warn young people that using cannabis could increase their risk of developing a psychotic illness later in life.
This is of some interest for two reasons: first, the statement is couched in terms which suggest that a long-sought objective of gaining 'sufficient evidence' has been reached. Second and perhaps more importantly, the standard of evidence reached is low. The best that can be said is that it is sufficient to warn young people that using cannabis could increase their risk. If doctors are to warn of everything that 'could increase risk', they are going to be spending a lot of time issuing warnings.
Cannabis and cancer
Second, in my previous post I did my best to answer Hitchens by honestly laying out the strongest case against cannabis that I consider justified. I said I've already mentioned that smoking cannabis carries a risk of cancer. It hardly need be added that I would assume it imposes the other major risks associated with smoking. In any case, in Europe cannabis is most commonly smoked mixed with tobacco
These remarks were cursory, since my primary concern was not with any cancer risk (as indicated by the quote I supplied from Hitchens: As for the risk of cancer, while it undoubtedly exists, it is not my principal concern).
Since reading my previous post, Hitchens has shown some early signs of shifting his emphasis - as is his unquestioned prerogative - from mental health to smoking-related dangers. In a recent comment he states: As for cannabis being a poison, it is plainly injurious to its users in many ways, especially when smoked ( as Mr Wilkinson concedes in his latest posting).
So to nip this in, so to speak, the bud, I'll slightly expand and clarify my remarks on cancer and cannabis. Any smoking almost certainly imposes - causes - an increased risk of cancer. Many things contain carcinogens (I seem to remember reading that bracken is among them). Smoke and other products of burning organic matter are among these: smoked meats and burned toast are believed to increase cancer risk, for example. So the likelihood is that cannabis smoke does the same. However, Cancer Research UK make it clear that the specific risks of cannabis smoke are not understood and are probably lower than those of tobacco.
Ben Goldacre, in his Bad Science column, points out that science correspondents - and indeed general reporters - seem to have averted their magpie eyes from a particularly bold and sensational claim for the low incidence of harm from cannabis smoking. I would approach this claim with caution, which is why I opted not to mention it in my previous post. But the report is out there, and while I'm going beyond a quick statement of my own best guess, I should mention it:
For textbook bad science we’d also want to see the media distorting research: overstating the stuff it likes, and ignoring stuff it doesn’t, especially negative findings. We used to read a lot about cannabis and lung cancer in the papers. The largest ever study of whether cannabis causes lung cancer reported its findings recently, to total UK media silence. Lifelong cannabis users, who had smoked more than 22,000 joints, showed no greater risk of cancer than people who had never smoked cannabis.
While no journalist has written a single word on that study, the Times did manage to make a front page story headed "Cocaine floods the playground: use of the addictive drug by children doubles in a year," out of their misinterpretation of a government report that showed nothing of the sort.
All this is of course about smoking. Cannabis, unlike tobacco (which, for example, causes mouth cancer when chewed) does not appear to be carcinogenic when it is not burned.
The tobacco-based component of the cancer risk associated with smoking is of course avoidable. If, as appears likely, the risks from cannabis smoking are in fact less than those of tobacco, this should be made public, and conditional advice offered: if you are going to take cannabis, don't smoke it; if you do choose to smoke it, don't add tobacco. Of course this presupposes well-informed and honest advice uncorrupted by the noble aim of churning out one-sided propaganda and squeamishly avoiding anything that might be seen as 'encouraging' or 'promoting' cannabis use.
Note also that if cannabis were legalised, vaporiser technology would no doubt be improved. Furthermore, in the longer term, other smokeless delivery mechanisms for THC might well be developed.
Oh yes - one more thing. The cancer research site (final paragraph) also mentions the sensational news that the active constituents of cannabis have been found to kill cancer cells. Unlike most initial findings about possible cancer cures and antagonists, this does not seem to have been widely reported in the press. The bad news is that smoking draw is not thought to increase house prices, though since I've mentioned the possibility, it would be irresponsible not to speculate.
Back to the analysis of Reefer Madness studies:
The past few decades' hunt for a causal relationship leading from cannabis use to schizophrenia was prompted by some findings from a cohort study of Swedish conscripts. This, in the classic pattern, was an exciting result which has been followed by a 'decline effect'. I will focus on a follow-up study which purports to address the obvious issues with the initial finding.
Zammit et al., 'Self reported cannabis use as a risk factor for schizophrenia in Swedish conscripts of 1969: historical cohort study'
This paper seems to avoid the problem of transient cannabis-related effects:
It is unlikely that cases diagnosed as schizophrenia in this cohort were either toxic psychoses induced by cannabis (or amphetamine) or acute, transient drug induced psychoses, given the restrictive tradition in Sweden regarding the diagnosis of schizophrenia.17 Satisfactory validity of schizophrenia diagnoses in a small sample from this cohort has been observed,8 and ICD-8 diagnoses from the register have shown high specificity with criteria for schizophrenia as defined in DSM-III (Diagnostic and Statistical Manual of Mental Disorders, third edition).
However, I shall argue that the paper not only suffers from a failure adequately to control for 'common predisposition', but exhibits positive signs of being compromised by that failure. Along the way, I'll point out some other problems which I consider typical of this research programme, and which in some cases tend to indicate the influence of a certain degree of confirmation bias.
These findings, say the authors, are in keeping with accumulating evidence that cannabis has detrimental effects on mental health in some people
The use of the expression 'In keeping with' may be somewhat revealing. It suggests that conforming to that conclusion is seen as tending to validate the findings presented - the analysis has succeeded! This is related to the phenomenon of publication bias discussed before - in the 'honeymoon' period, the only interesting finding is one that appears to support the promising new hypothesis. Given that an ongoing longitudinal study permits re-analyses of what is for the most part the same previously analysed data, one must hope that no prejudice has been allowed to influence the choice of refinements to the analysis.
So, what did this study (one of many derived from the same data set), find? Let's look first at the summary (which is all that most people who cite the paper will probably read):
Results: Cannabis was associated with an increased risk of developing schizophrenia in a dose dependent fashion both for subjects who had ever used cannabis (adjusted odds ratio for linear trend of increasing frequency 1.2, 95% confidence interval 1.1 to 1.4, P<0.001), and for subjects who had used only cannabis and no other drugs (adjusted odds ratio for linear trend 1.3, 1.1 to 1.5, P<0.015). The adjusted odds ratio for using cannabis >50 times was 6.7 (2.1 to 21.7) in the cannabis only group. Similar results were obtained when analysis was restricted to subjects developing schizophrenia after five years after conscription, to exclude prodromal cases.
These result mentions dose dependence: this is regarded as a key concept in assessing causality (though not by any means either necessary or sufficient to establish it) in contexts such as this. The 'adjusted odds ratio for linear dependence' is meant to be a summary measure of the differences in odds between members of any one usage category and those of the one immediately above it.
The higher figure for this linear relationship between 'dose' and frequency of schizophrenia - 1.3 - comes from the subset of data that relates to those who had not reported taking common illegal drugs other than cannabis. The idea of separating out this data is not made entirely explicit - but would seem to be aimed at eliminating any confounding by use of other drugs such as methamphetamine. If that is the case, then such a decision ought to be committed to before running analysis. Instead, the approach seems to have been: analyse both sets of data , take a sneaky peek, and only then decide which one to draw attention to. Such an approach would utterly undermine the evidential validity of any findings. The figure of 6.7 has been cherry-picked on this basis, the corresponding figure for all drugs (3.1) not being reported.
Anyway, let's take a look at the figures from which this linear relationship is derived, using odds ratios for each usage category as adjusted for some potentially confounding factors.
Cannabis use odds ratio
2-4 times: 1.9
5-10 times 1.7
11-50 times 0.8
>50 times 6.7
[*no instances of schizophrenia - dividing by zero means the sums won't work, but intuitively the probability would, if anything, come out as zero]
I don't think anyone is going to suggest that this is a series from which one would expect to derive a finding of a positive linear relationship indicating dose-dependence. The central portion of the series suggests a flat or gently declining relationship, assuming - charitably - that the '11-50' figure is a fluke, as the confidence interval (0.1 - 6.9, reflecting the fact that the result derives from a single instance of schizophrenia) might suggest. However, the cardinal rule of statistical evidence - as opposed to exploratory analysis, which should be clearly labelled as such - is that you don't second-guess the results of the predetermined analysis, so if the authors have followed this basic methodological precept, one must accept this result as one finds it, simply noting that the 95% confidence interval covers the range from 1.0 to 1.5.
(As with most of these studies, I wouldn't have started from here. Distinguishing between 'once, '2-4 times' and '5-10 times' seems to impose at least one more distinction than any real differences could justify.)
The one figure which (or rather the data underlying which) is clearly responsible for the finding of a positive linear relationship is the last one - 6.7. Indeed, as we've seen, this figure is reported on its own, so impressive is it. Since the authors of the paper seem happy to give this figure special attention rather than sticking to (what one hopes was) the predetermined plan of calculating a linear relationship, I'll feel free to take an exploratory rather than evidentiary approach.
As we've seen, this is more than twice the corresponding figure for those who had taken other 'street' drugs. But the point of excluding poly-drug-users was to remove a source of confounding - that is, use of other drugs is expected to be associated with increased statistical risk:
The association between cannabis and schizophrenia persisted even after adjusting for use of alcohol, cigarettes, and other drugs, all of which are likely to be indicative of risk taking behaviour. This implies that a shared risk factor (be it biological, genetic, or through personality traits) for developing schizophrenia and for using psychoactive substances does not adequately explain the association observed.
Yet the finding is that risk - for the heaviest use category - is much lower in the 'any drugs' group.
What could account for this? It seems vanishingly unlikely that taking other drugs would directly halve the risk. So, clinging as we must to the idea that the figures are meaningful at all, we can only conclude that there is something else about those who take only cannabis that increases their risk level. It's not - so far as the data can tell us - that they take more cannabis.
The authors do not mention this point, despite drawing special attention to the result - a result which as we've seen, Murray subsequently touted in the press. Why not? Surely some comment is called for in the course of this - exploratory and speculative - discussion of a single figure.
One important possibility is that the behaviour pattern of using cannabis relatively heavily without trying any other drugs is associated with personality traits or other psychological factors which are precursor or prodromal forerunners of schizophrenia, or otherwise associated with it. In other words the data suggests that the common predisposition hypothesis would be worth investigating.
The authors recognise that common predisposition is an important possibility which needs to be addressed. They do not join me in speculating that this specific pattern of use might be especially relevant, nor that further investigation would be in order - common predisposition, for a true believer like Murray, is a possibility to be eliminated, not entertained.
So in an attempt to eliminate common predisposition as a factor, the authors re-run the analysis deleting all those subjects diagnosed with schizophrenia within five years of the initial survey in which drug use was assessed.
But this branch of the analysis did not exclude subjects who had used drugs other than cannabis. One wonders why this should be, since the point of that exclusion was supposed to be to control for the confounding effects of such poly-drug use. The appearance is of sleight of hand. Open the left hand - nothing in here. A bit of fumbling behind the back, and - nothing in the right hand either!
But perhaps the authors forgot to try this analysis on 'cannabis only' data. I must point out for the benefit of suspicious observers that there is no evidence to suggest that they did try it, but gave in to the ever-present temptation to discard inconvenient - too low, or implausibly high - results as 'anomalous' or 'implausible'. I would caution against even suggesting that this may have happened, since not only would that invalidate these results, but it would tend to cast a long shadow of impropriety over all the authors' work in this area.
In any case, the authors say Similar results were obtained when analysis was restricted to subjects developing schizophrenia after five years after conscription, to exclude prodromal cases ('prodromal cases' here corresponding to what I refer to as common predisposition).
So how similar were those results? Here are the results in which the dependent variable (schizophrenia diagnosis) is not stratified according to time of diagnosis (remember, this is data that includes those who had taken other drugs):
Diagnosis at any time:
Cannabis use odds ratio
2-4 times 0.9
5-10 times 1.4
11-50 times 2.2
>50 times 3.1
Linear trend for frequency of use: 1.2
And here are the results from which subjects diagnosed within five years are excluded
Diagnosis after 5 years:
Cannabis use odds ratio
2-4 times 0.9
5-10 times 1
11-50 times 2.1
>50 times 2.5
Linear trend for frequency of use: 1.2
This time, a sanity check by inspection of the adjusted figures appears to confirm - rather than flatly contradict - the proposed linear relationship, at least. Notice though that according to these odds ratios, taking cannabis up to four times actually appears to be associated with a reduction in chances of being diagnosed with schizophrenia. But of course no-one is going to suggest that a low level of cannabis use might protect one from schizophrenia!
But note too that notwithstanding the authors' description of the findings as 'similar', the odds ratio is lower in the second data set. Where has that effect size gone? Well, obviously it's lurking in the data that was excluded. Although they choose not to draw too much attention to it in their executive summary, the authors also ran the analysis for data that excludes those diagnosed after five years. That is, they looked directly at those cases diagnosed within five years, in which - and this is the whole point of this part of the analysis - common disposition is considered to be a potential factor. Let's have a look at that data.
Diagnosis within 5 years:
Cannabis use odds ratio
2-4 times 1
5-10 times 2.6
11-50 times 2.8
>50 times 4.7
Linear trend for frequency of use: 1.3
We can see that the effect sizes are indeed substantially higher than the data for diagnosis at any time. This is a group which the authors themselves chose to sequester as potentially subject to confounding or reverse causation arising from a 'common predisposition' effect. They give the clear impression that this stratification of the data has no significant effect (comparable results were 'similar' despite it). And yet this is not the case. There appears to be a substantial difference here, which confirms that the main analysis and thus the results reported, does not adequately control for common predisposition.
[UPDATE 22 JUL 2011:
At least it seems to confirm this, if we accept that the whole point of this analysis is to check that common predisposition has been eliminated as a factor. If this is a test which can eliminate but not establish the presence of this source of error, it seems a handy kind of test.
Certainly the authors explain this finding away:
The association between use of cannabis and schizophrenia was stronger in subjects who were first admitted within five years of conscription. One explanation is that subjects with a prodrome of schizophrenia at conscription may have increased their cannabis use, perhaps as a means of self medication. But all subjects were screened at conscription, and we adjusted for other psychiatric problems recorded at that time. The relation with cannabis use was also observed in the later onset group, admitted more than five years after conscription. It seems more likely that the reduced association in the group with later onset is due to misclassification, as the number of people who discontinued cannabis use accumulated over time.
The authors mention common predisposition as just 'one explanation' despite the fact that testing for that phenomenon was the whole point of the exercise. They then provide reasons for disregarding the possibility: but if those reasons were good enough, there would have been no point in performing the exercise of stratifying by time of diagnosis. The actual explanation offered for the difference in the figures would actually be quite a convincing one - except that no attempt is made to quantify the effect (discontinuation of cannabis use) suggested, so it is impossible to determine how large the difference would have to be before the authors would accept that their data had failed the test - a test they specifically introduce - for robustness to the hypothesis of common predisposition.
These observations expose the analysis as dodging one of the main issues which need to be addressed, and which it purports to address, and thus to have greater validity than past studies. The explanation offered for this failure is not substantiated, and consists of the hypothesis that since initial data gathering, there will be a tendency for cannabis use to drop off over time. In the absence of any evidence to support the applicability and extent of such an effect, though, the explanation is of doubtful import.
The authors also discuss the major problem of inadequate data in more general terms. One might well have concluded at the design phase that the data has simply not captured sufficient information for further attempts at extracting a conclusion to be worthwhile. The authors instead state rather baldly that the poor quality of the data is not likely to be a problem:
We are limited in that we have only data regarding use of cannabis before conscription. But if the pattern of increased initiation and reduced cessation of drug use seen in the schizophrenia group persisted after the time of conscription, this would result in us underestimating the effect size of cannabis.
Fewer subjects in this cohort claimed to have used cannabis and other illicit drugs compared with similar cohorts that used anonymous questionnaires. The effect of under-reporting would again result in an underestimate of the true effect size.
Does this amount to anything more than special pleading? Are the authors just saying that since this data is not much good, the inconvenient result is not to be trusted, while other results are sound? Certainly the fact that the problem is explained away so cursorily (in fact, not only explained away but even described as tending to strengthen the findings!) leaves something to be desired.
What is the schizophrenia group, in which it is suggested the pattern of increased initiation and reduced cessation of drug use...[might persist]...after the time of conscription? The authors seem, despite themselves, to be saying that those who will turn out to be diagnosed with schizophrenia are more likely to start and less likely to stop using cannabis - that is, that the schizophrenia outcome determines the degree of cannabis use. This is how one would frame it if one were to presuppose reverse (schizophrenia -> cannabis) causation, or more generally the common disposition thesis. These people are going to get schizophrenia, therefore they are more likely to use cannabis.
That is the only justification for supposing that unmeasured cannabis use would be found to be greater among the 'schizophrenia group' than among the rest of the sample. Without that assumption - an assumption directly at odds with the authors' claim to have eliminated this source of error - there is no justification for supposing that the unknown data would strengthen the findings.
Transient effects of cannabis
Murray also had a hand in in one rehashing of the data from the Dunedin multidisciplinary health and development study conducted in New Zealand: Arseneault et al., 'Cannabis use in adolescence and risk for adult psychosis: longitudinal prospective study'
The study attempted to control for the common predisposition effect by the inadequate method of examining self-reported 'psychotic symptoms' at age 11. I won't go into this further.
The more interesting aspect of the study is in the measurement of outcomes other than clear diagnoses of schizophrenia. The paper states:
Logistic regression analyses showed that people who used cannabis by age 15 were four times as likely to have a diagnosis of schizophreniform disorder at age 26 than controls. After psychotic symptoms at age 11 were controlled for, the risk for adult schizophreniform disorder remained higher among those who used cannabis at age 15; however, this risk was reduced by 31% and was no longer significant.
'Schizophreniform disorder', as I understand it, differs from schizophrenia in that it is diagnosed on the basis of a single month's symptoms, and is less serious in terms of functional impairment. It is often an interim diagnosis in reponse to early stages of schizophrenia, but one third of those diagnosed with schizophreniform disorder do not develop schizophrenia. This is an instance of the slippage in severity of measured outcomes which I mentioned in the previous post, and which would tend to, in a memorable phrase, 'hide the decline' in effect sizes. Still, this is a relatively unimportant point.
Rather, the key issue here is that After psychotic symptoms at age 11 were controlled for... - that is, once the statistical analysis was completed - ...this risk was reduced by 31% and was no longer significant.
Statistical significance is, as the name suggests, the sine qua non of statistical inference - and again, this is only based on a crude and inadequate control of 'psychotic symptoms' at age 11.
Having failed to find an increase in risk of schizophreniform disorder, the authors turn to other symptoms:
Multiple linear regression analyses showed that cannabis users by age 15 and by age 18 had more schizophrenia symptoms than controls at age 26 (table). These results remained significant after psychotic symptoms at age 11 were controlled for. The effect was stronger with earlier use.
Looking at the table of results, it uis clear that just as in the case of the Zimmer study examined above, two different sets of factors were adjusted for: here, other drug use, and self-reported psychotic symptoms at age 11. And just as in that study there seems a curious coyness about adjusting for both factors together. But the key point here is that these statistics were based on a study which assessed psychiatric symptoms at age 26 with a standardised interview schedule to obtain DSM-IV (diagnostic and statistical manual of mental disorders, 4th edition) diagnoses
This sounds impressive, but in fact what it means is that the data was gathered by lay interviewers using a standardised diagnostic checklist. Such a checklist aims to gather sufficient information for a statistical algorithm to generate diagnoses, without the need for the opinion of a medic. In order to do this, many minor and peripheral 'symptoms' are included. This is useful if these symptoms are properly weighted and then tested against a threshold to determine the presence or absence of a certain condition (one may certainly question the validity of this approach to diagnosis, but that is not my point here). It is not however very useful when the individual symptoms are counted outside the diagnostic framework, and used to determine degrees of schizophrenia-likeness. That project is deeply questionable - it is not too much of a simplification to say that we are dealing with diagnosing people as being 'a little bit schizophrenic'.
The specific problem with this approach is that many of the minor 'symptoms' or indicators are likely to be slightly better represented among those who are under the influence of cannabis, or have been so recently, or are such heavy users that their daily functioning has become impaired in ways that have no connection to schizophrenia. This was not controlled for in this study, and given that we are talking about very small numbers and marginal statistical trends, seems highly likely to have provided false positive findings of schizophrenia-likeness.
This concludes my remarks on scientific evidence of cannabis-related harm, for this round of debate anyway. In the following paper, I will address moral and policy arguments, including Hitchens's own non-scientific theories about certain social harms which he attributes to cannabis.