October 12, 2016

“Something is rotten in the state of Denmark”

The DANISH trial (in which, pleasingly, the D stands for “Danish”, and it was conducted in Denmark too), evaluated the use of Implantable Cardioverter Defibrillators (ICD) in patients with heart failure that was not due to ischaemic heart disease. The idea of the intervention is that it can automatically restart the heart in the event of a sudden cardiac arrest – so it might help these patients, who are at increased risk of their heart stopping suddenly (obviously there is a lot more clinical detail to this).

The trial recruited 1116 patients and found that the primary outcome (death from any cause) occurred in 120/556 (21.6%) in the ICD group and 131/560 (23.4%) in control; a hazard ratio of 0.87, 95% CI 0.68, 1.12. The conclusion was (from the abstract):

“prophylactic ICD implantation … was not associated with a significantly lower long-term rate of death from any cause than was usual clinical care”;

and from the end of the paper:

“prophylactic ICD implantation … was not found to reduce longterm mortality.”

Note, in passing, the subtle change from “no significant difference” in the abstract, which at least has a chance of being interpreted as a statement about statistics, to “not found to reduce mortality” – a statement about the clinical effects. Of course the result doesn’t mean that, but the error is so common as to be completely invisible.

Reporting of the trial mostly put it across as showing no survival improvement, for example:

The main issue in this trial, however, was that the ICD intervention DID reduce sudden cardiac death, which is what the intervention is supposed to do: 24/556 (4.3%) in the ICD group and 46/560 (8.2% in control), hazard ratio 0.50 (0.31, 0.82). All cardiovascular deaths (sudden and non-sudden) were also reduced in the ICD group, but not by so much: HR 0.77 (0.57, 1.05). You might expect a result like this if the ICD reduced sudden cardiac deaths, but in addition to this both groups have similar risk of non-sudden cardiac death. When all deaths are counted, the difference in the outcome that the intervention can affect starts getting swamped by outcomes that it doesn’t reduce. The sudden cardiac deaths make up a small proportion of the total, so the overall difference between the groups is dominated by deaths that weren’t likely to differ between the groups, and the difference in all-cause mortality is much smaller (and “non-significant”). So all of the results seem consistent with the intervention reducing the thing it is intended to reduce, by quite a lot, but there also being a lot of deaths due to other causes that aren’t affected by the intervention. To get my usual point in, if Bayesian methods were used, you would find a substantially greater probability of benefit for the intervention for cardiovascular death and all-cause mortality.

All-cause death was chosen as the primary outcome, and following convention, the conclusions are based on this. But the conclusion is sensitive to the choice of primary outcome: if sudden cardiac death had been the primary outcome, the trial would have been regarded as “positive”.

So, finally, to get around to the general issues. It is the convention in trials to nominate a single “primary outcome”, which is used for calculating a target sample size and for drawing the main conclusions of the study. Usually this comes down to saying there was benefit (“positive trial”) if the result gets a p-value of less than 0.05, and not if the p-value exceeds 0.05 (“negative trial”). The expectation is that a single primary outcome will be nominated (sometimes you can get away with two), but that means that the conclusions of the trial will be sensitive to this choice. I think the reason for having a single primary outcome stems from concerns over type I errors if lots of outcomes are analysed. You could them claim a “positive” trial and treatment effectiveness if any of them turned out “significant” – though obviously restricting yourself to a single primary outcome is a pretty blunt instrument for addressing multiple analysis issues.

There are lots of situations where it isn’t clear that a single outcome is sufficient for drawing conclusions from a trial, as in DANISH: the intervention should help by reducing sudden cardiac death, but that won’t be any help if it increases deaths for other reasons – so both sudden cardiac deaths and overall deaths are important. Good interpretation isn’t helped by the conventions (=bad habits) of equating “statistical significance” with clinical importance, and labelling the treatment as effective or not based on a single primary outcome.

Reference for DANISH trial: N Engl J Med 2016; 375:1221-1230, September 29, 2016

October 02, 2016

Classical statistics revisited


I’ve written before about the use of the term “classical” to refer to traditional frequentist statistics. I recently found that E.T Jaynes had covered this ground over 30 years ago. In “The Intuitive Inadequacy of Classical Statistics” [1] he writes:

“What variety of statistics is meant by classical? J.R. Oppenheimer held that in science the word “classical” has a special meaning: “[…] it means “wrong”. That is, the classical theory is the one which is wrong, but which was held yesterday to be right.”

“… in other fields, “classical” carries the opposite connotations of “having great and timeless merit." Classical music, sculpture and architecture are the kind I like.”

Jaynes follows convention, and Oppenheimer, in the article and means traditional stats by “classical”. I guess the Oppenheimer meaning should be understood more generally.

[1] Epistemologia VII (1984) Special Issue. Probability, Statistics and Inductive Logic pp 43-74

September 23, 2016

Radio 4 does statistical significance

There was an item on “Today” on Radio 4 on 22 September about Family Drug and Alcohol Courts – which essentially are a different type of court system for dealing with issues about the care of children in families affected by drugs and alcohol. I know nothing about the topic, but it seems they offer a much more supportive approach and are claimed to be more successful at keeping parents off drugs and alcohol and reducing disruption to family life.

This item featured an interview with one of the authors, Mary Ryan, of a new report comparing the effectiveness of Family Drug and Alcohol Courts with the standard system: keeping children with their parents, and keeping parents off drugs and alcohol. Twice she said that differences they found were “statistically significant”, emphasising the “statistically”, and the phrase was also repeated by the Radio 4 presenter.

I would be pretty confident that the presenter, almost all of the audience, and very possibly Mary Ryan, have no idea what the technical meaning of “statistically significant” is. But the words have everyday meanings that we understand, and when put together they sound as though a result must be important, impressive and reliable. It’s “significant” – that means it’s important, right? And it’s not just ordinary significance, but “statistical” significance – that means that it’s backed up by statistics, which is science, so we can be sure it’s true.

I don’t know for sure, but I would guess that this is the sort of understanding that most people would take from a discussion on Radio 4 of “statistically significant” results. It’s a problem of using familiar words to refer to specific technical concepts; people can understand the words without understanding the concept.

Just after writing this I came across this blog post from Alex Etz which confirms what I thought, with numbers and everything:

September 22, 2016

Feel the Significance

Pleasantly mangled interpretation of p-values that I came across recently:
(STT is Student t-test and WTT is Wilcoxon t-test)

“The two-tailed z-tests produced calculated p-values of < 1.0 × 10−6 for STT and
WTT at α = 0.05. As the calculated p-values are much less than α, the Null Hypothesis is rejected which therefore proves that there is a significant difference between the two groups, i.e. low and high risk.”

From: Batty CA, et al (2015) Use of the Analysis of the Volatile Faecal Metabolome in Screening for Colorectal Cancer. PLoS ONE 10(6): e0130301. doi:10.1371/journal.pone.0130301

June 24, 2016

The Fragility Index for clinical trials

Disclaimer: The tone of this post may have been affected by the results of the British EU referendum.

There has been considerable chat and Twittering about the “fragility index” so I thought I’d take a look. The basic idea is this: researchers get excited about “statistically significant” (p<0.05) results, the standard belief being that if you’ve found “significance” then you have found a real effect. [this is of course wrong, for lots of reasons] But some “significant” results are more reliable than others. For example, if you have a small number of events in your trial, it would only require a few patients to have had different outcomes to tip a “significant” result into “non-significance”. So it would be useful to have a measure of the robustness of statistically significant results, so that readers will get a sense of how reliable they are. The Fragility Index (FI) aims to provide this. It is calculated as the number of patients that would have had to have had different outcomes in order to render the result “non-significant” (p > 0.05). So if a trial had 5/100 with the main outcome in one group and 18/100 in the other, the p-value would be 0.007 (pretty significant, huh?). The fragility index would be 3 (according to the handy online calculator www.fragilityindex.com, which will calculate your p-value to 15 decimal places): only three of the intervention group non-events would need to have been events to raise the p-value above 0.05.

There’s a paper introducing this idea, from 2014:
Walsh M et al. The statistical significance of randomized controlled trial results is frequently fragile: a case for a Fragility Index. J Clin Epidemiol. 2014 Jun;67(6):622-8. doi: 0.1016/j.jclinepi.2013.10.019. Epub 2014 Feb 5.

I think there are good and bad aspects to this. On the positive side, it’s good that people are thinking about the reliability of “significant” results and acknowledging that just achieving significance doesn’t mean that you’ve found anything important. But to me the Fragility Index doesn’t get you much further forward. If you find a low Fragility Index, what do you do with that information? We have always known that significance when there are few events is unreliable. The problem is really judging that there is a qualitative difference between results that are “significant” and “non-significant”, a zombie myth that the Fragility Index doesn’t do anything to dispel. The justification is that judging results by “significance” is an ingrained habit that isn’t going to go away in a hurry, so the FI will highlight unreliable results and help people to avoid mistakes in interpretation. I have some sympathy with that view, but really, the problem is with the use of significance testing, and we should be promoting things that will help us to move away from this, rather than introducing new procedures that seem to validate it.

There are some things in the paper that I really didn’t like, for example: “The concept of a threshold P-value to determine statistical significance aids our interpretation of trial results.” Really? How exactly does it do that? It just creates an artificial dichotomy based on a nonsensical criterion. The paper tries to explain in the next sentence: “It allows us to distill the complexities of probability theory into a threshold value that informs whether a true difference likely exists”. I have no idea what the first part of that means, but the second part is just dead wrong. No p-value will ever tell you “whether a true difference likely exists” because they are calculated on the assumption that the difference is zero. This is just perpetuating one of the common and disastrous misinterpretations of p-values, and it is pretty surprising that this set of authors gets it wrong. Or maybe it isn’t, considering that almost everyone else does.

April 14, 2016

NEJM letter and cardiac arrest trial

I recently had a letter in the New England Journal of Medicine, about a trial they had published that compared continuous versus interrupted chest compressions during resuscitation after cardiac arrest. Interrupted compressions are standard care - the interruptions are for ventilations to oxygenate the blood, prior to resuming chest compressions to keep it circulating. The issue was that the result of the trial was 0.7% better survival in the interrupted-compression group, with 95% CI from -1.5% to 0.1%. So the data are suggesting a probable benefit to interrupted compressions. However, on Twitter the NEJM announced this as “no difference”, no doubt because the difference was not “statistically significant”. So I wrote pointing out that this wasn’t a good interpretation, and the dichotomy into “significant” and “non-significant” is pretty unhelpful in situations where the results are close to “significance”. Bayesian methods have a huge advantage here, in that they can actually quantify the probability of benefit. An 80% probability that the treatment is beneficial is a lot more useful than “non-significance”, and might lead to very different actions.

The letter was published along with a very brief reply from the authors (they were probably constrained, as I was in the original letter, by a tiny word limit): “Bayesian analyses of trials are said to offer some advantages over traditional frequentist analyses. A limitation of the former is that different people have different prior beliefs about the effect of treatment. Alternative interpretations of our results offered by others show that there was not widespread clinical consensus on these prior beliefs. We are not responsible for how the trial results were interpreted on Twitter.”

Taking the last point first: no, the authors did not write the Twitter post. But they also did not object to it. I'm not accusing them of making the error that non-significance = no difference, but it is so common that it usually - as here - passes without comment. But it's just wrong.

Their initial point about priors illustrates a common view, that Bayesian analysis is about incorporating individual prior beliefs into the analysis. While you can do this, it is neither necessary nor a primary aim. As Andrew Gelman has said (and I have repeated before); prior information not prior beliefs. We want to base a prior on the information that we have at the start of the trial, and if that is no information, then that’s fine. However, we almost always do have some information on what the treatment effect might plausibly be. For example, it’s very unusual to find an odds ratio of 10 in any trial, so an appropriate prior would make effects of this (implausible) size unlikely. More importantly, in this case, getting too hung up on priors is a bit irrelevant, because the trial was so huge (over 20,000 participants) that the data will completely swamp any reasonable prior.

It isn’t possible to re-create the analysis from the information in the paper, as it was a cluster-randomised trial with crossover, which needs to be taken into account. Just using the outcome data for survival to discharge in a quick and dirty Bayesian analysis, though, gives a 95% credible interval of something like from 0.84 to 1.00, with a probability of the odds ratio being less than 1 of about 98%. That probably isn’t too far away from the correct result, and suggests pretty strongly that survival may be a bit worse in the continuous compression group. “No difference” just doesn’t seem like an adequate summary to me.

My letter and the authors’ reply are here: http://www.nejm.org/doi/full/10.1056/NEJMc1600144

The original trial report is here: Nichol G, Leroux B, Wang H, et al. Trial of continuous or interrupted chest compressions during CPR. N Engl J Med 2015;373:2203-2214 http://www.nejm.org/doi/full/10.1056/NEJMoa1509139

December 09, 2015

Why do they say that?

A thing I've heard several times is that Bayesian methods might be advantageous for Phase 2 trials but not for Phase 3. I've struggled to understand why people would think that. To me, the advantage of Bayesian methods comes in the fact that the methods make sense, answer relevant questions and give understandable answers, which seem just as important in Phase 3 trials as in Phase 2.

One of my colleagues gave me his explanation, which I will paraphrase. He made two points:

1. Decision-making processes are different after Phase 2 and Phase 3 trials; folowing Phase 2 decisions about whether to proceed further are made by researchers or research funders, but after Phase 3 decisons (about use of therapies presumably) are taken by "society" in the form of regulators or healthcare providers. This makes the Bayesian approach harder as it is harder to formulate a sensible prior (for Phase 3 I think he means).

2. In Phase 3 trials sample sizes are larger so the prior is almost always swamped by the data, so Bayesian methods don't add anything.

My answer to point 1: Bayesian methods are about more than priors. I think this criticism comes from the (limited and in my view somewhat misguided) view of priors as a personal belief. That is one way of specifying them but not the most useful way. As Andrew Gelman has said, prior INFORMATION not prior BELIEF. And you can probably specify information in pretty much the same way for both Phase 2 and Phase 3 trials.

My answer to point 2: Bayesian methods aren't just about including prior information in the analysis (though they are great for doing that if you want to). I'll reiterate my reasons for preferring them that I gave earlier - the methods make sense, answer relevant questions and give understandable answers. Why would you want to use a method that doesn't answer the question and nobody understands? Also, If you DO have good prior information, you can reach an answer more quickly by incorporating that in the analysis - which we kind of do by doing trials and then combining them with others in meta-analyses; but doing it the Bayesian way would be neater and more efficient.

September 18, 2015

Even heroes get it wrong sometimes

I recently read David Sackett's 2004 paper from Evidence-based Medicine “Superiority trials, non-inferiority trials, and prisoners of the 2-sided null hypothesis “ (Evid Based Med 2004;9:38-39 doi:10.1136/ebm.9.2.38). [links don’t seem to be working, will edit later if I can].

In it I found this:

“As it happened, our 1-sided analysis revealed that the probability that our nurse practitioners’ patients were worse off (by ⩾5%) than our general practitioners’ patients was as small as 0.008.”

I’m pretty sure that 0.008 probability isn’t from a Bayesian analysis and is a misinterpretation of a p-value. It isn’t the probability of the null hypothesis being false! It really isn’t! Obviously that got past the reviewers of this manuscript without comment.

Edit: I've got the paper now. It's a result from a one-tailed test for non-inferiority. The null hypothesis is that the intervention group was worse by 5% or more on their measure of function, p=0.008 so they reject the hypothesis of inferiority. But, as usual, that's the probability of getting the data (or more extreme data) if the null hypothesis is true - not the probability of the null hypothesis.

May 02, 2015

New test can predict cancer. Oh no it can't!

A story in several UK papers including the Telegraph suggests that a test measuring telomere length can predict who will develop cancer "up to 13 years" before it appears. Some of the re-postings have (seemingly by a process of Chinese whispers) elaborated this into "A test that can predict with 100 per cent accuracy whether someone will develop cancer up to 13 years in the future has been devised by scientists" (New Zealand Herald) - which sounds pretty unlikely.

What they are talking about is this study, which analysed telomere lengths in a cohort of people, some of whom developed cancer.

It's hard to know where to start with this. there are two levels of nonsense going on here; the media hype, which has very little to do with the results of the study, and the study itself, which seems to come to conclusions that are way beyond what the data suggest, through a combination of over-reliance on sgnificance testing, poor methodology and wishful thinking. I'll leave the media hype to one side, as it's well-established that reporting of studies often bears little relation to what the study actually did; in this case, there was no "test" and no "100% accuracy". But what about what the researchers really found out, or thought they did?

The paper makes two major claims:

1. "Age-related BTL attrition was faster in cancer cases pre-diagnosis than in cancer-free participants" (that's verbatim from their abstract);

2. "all participants had similar age-adjusted BTL 8–14 years pre-diagnosis, followed by decelerated attrition in cancer cases resulting in longer BTL three and four years pre-diagnosis" (also vebatim from their abstract, edited to remove p-values).

They studied a cohort of 579 initially cancer-free US veterans who were followed up annually between 1999 and 2012, with blood being taken 1-4 times from each participant. About half had only one or two blood samples, so there isn't much in the way of within-patient comparisons of telomere length over time. Telomere length was measured from these blood samples (this was some kind of average, but I'll assume intra-individual variation isn't important).

Figure 1 illustrates the first result:

Full-size image (36 K)

The regression lines do look as though there is a steeper slope through the cancer group, and the interaction is "significant" (p-0.032 when unadjusted and p=0.017 adjusted) - but what is ignored in the interpretation is the enormous scatter around both of the regression lines. Without the lines on the graph you wouldn't be able to tell whether there was any difference in the slopes. Additionally, as relatively few participants had multiple readings, it isn't possible to do the analysis of comparing within-patient measures of change in telomere length, which might be less noisy. Instead we have an analysis of average telomere length at each age, with a changing set of patients. So, on this evidence, it is hard to imagine how this could ever be a useful test that would be any good for distinguishing people who will develop cancer from those who will not. The claim of a difference seems to come entirely from the "statistical significance" of the interaction.

The second claim, that in people who develop cancer BTL stops declining and reaches a plateau 3-4 years pre-diagnosis, derives from their Figure 2:

Full-size image (47 K)

Again, the claim derives from the difference between the two lines being "statistically significant" at 3-5 years pre-diagnosis, and not elsewhere. But looking at the red line, it really doesn't look like a steady decline, followed by a plateau in the last few years. If anything, the telomere length is high in the last few years, and the "significance" is caused by particularly low values in the cancer-free group in those years. I'm not sure that this plot is showing what they think it shows; the x-axis for the cancer group is years pre-diagnosis, but for the non-cancer group it is years pre-censoring, so it seems likely that the non-cancer group will be older at each point on the x axis. Diagnoses of cancer could happen at any time, whereas most censoring is likely to happen at or near the end of the study. If BTL declines with age, that could potentially produce this sort of effect. So I'm pretty unconvinced. The claim seems to result from looking primarily at "statistical significance" of comparisons at each time point, which seems to have trumped any sense-checking.

April 09, 2015

Journal statistical instructions – is that it??

Writing about web page http://www.resuscitationjournal.com/content/authorinfo

I submitted a manuscript to the journal Resuscitation recently. It's a pretty well-regarded medical journal, with an impact factor (for 2013) of 3.96, so a publication there would be a good solid paper. While formatting the manuscript I had a look at the statistical section of the Instructions for Authors. This is what I found:

"Statistical Methods
* Use nonparametric methods to compare groups when the distribution of the dependent variable is not normal.
* Use measures of uncertainty (e.g. confidence intervals) consistently.
* Report two-sided P values except when one-sided tests are required by study design (e.g., non-inferiority trials). Report P values larger than 0.01 to two decimal places, those between 0.01 and 0.001 to three decimal places; report P values smaller than 0.001 as P<0.001."

That's it! 69 words (including the title), more than half of which (43) are about reporting of p-values. I really don't think that many people would find this very useful (for example, what does "use measures of uncertainty consistently" mean?). Moreover, it seems to start from the premise that statistical analysis IS null hypothesis significance testing, and there are lots of reasons to take issue with that point of view. And finally (for now) it is questionable whether two-sided tests are usually the right thing to do, as we are usually interested in whether a treatment is better than another, not in whether it is different (not bothered whether it is better or worse) - won't get further in to that now but suffice to say it is a live issue.

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  • Hi Tom Sorry for delay in replying – taken out by family issues then holiday for the last month or s… by Simon Gates on this entry
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