March 05, 2017

Sample size statement translation

Here are a couple of statements about the justification of the sample size from reports of clinical trials in high-impact journals (I think one is from JAMA and the other from NEJM):

We estimated that a sample size of 3000 … would provide 90% power to detect an absolute difference of 6.3 percentage points in the rate of [outcome] between the [intervention] group and the placebo group.

The study was planned to detect a difference of 1.1 points in the [outcome score] between the 2 interventions with a significance level of .05 and a power level of 90%.

There is nothing remarkable about these at all; they were just the first two that I came across in rummaging through my files. Statements like this are almost always found in clinical trial reports.

A translation, of the first one:

“We estimated that if we recruited 3000 participants and the true absolute difference between intervention and placebo is 6.3 percentage points, then if we assumed that there was no difference between the groups, the probability (under this assumption of no difference) of getting data that were as unusual or more unusual than those we actually obtained would be less than 0.05 in 90% of a long series of replications of the trial.”

That’s what it actually means but I guess most clinicians and researchers would find that pretty impenetrable. An awful lot is hidden by the simple word “detect” in the sample size justification statements. I suspect the language (“detect a difference”) feeds into the misunderstandings of ”significant” results – it’s a real difference, not due to chance, etc.


February 11, 2017

Andrew Gelman agrees with me!

Follow-up to The Fragility Index for clinical trials from Evidence-based everything

I’ve slipped in my plan to do a new blog post every week, but here’s a quick interim one.

I blogged about the fragility index a few months back (http://blogs.warwick.ac.uk/simongates/entry/the_fragility_index/). Andrew Gelman has also blogged about this, and thought much the same as I did (OK, I did ask him what he thought).

See here: http://andrewgelman.com/2017/01/03/statistics-meets-bureaucracy/


December 14, 2016

Bayesian methods and trials in rare and common diseases

One of the places that Bayesian methods have made some progress in the clinical trials world is in very rare diseases. And it’s true, traditional methods are hopeless in this situation, where you can never get enough recruits to get anywhere near the sample size that traditional methods demand for an “adequately powered” study, and it’s unlikely that a result will be “statistically significant”. Bayesian methods really help here, because they give you a result in terms of probability that a treatment is superior. This is good for two main reasons. First, it’s helpful to quantify the probability of benefit, and its size and uncertainty. This tells us a lot more than simply dichotomising it into “significant” and “non-significant”, with the unstated assumption that “significant” means clinically useful. Second, there isn’t a fixed probability of benefit that means an intervention should be used; it will vary from situation to situation. For example, if there is almost no cost to using a treatment, it might only need a small probability of being better to be worthwhile. If we don’t estimate this probability we can’t make this sort of judgement.

But (and this is something I have experienced several times now in a variety of places so I think it is real) – this seems to have had an unfortunate side effect. A perception seems to have grown that Bayesian methods are something to consider using when a “proper” trial (with all of the usual stuff: interpretation based on p < 0.05 in a null hypothesis test, fixed pre-planned sample size based on a significance test, 80% or 90% power and so on) isn’t feasible. In reality, the ability to quantify probability of benefit would be helpful in just about all situations, even (or especially) large Phase 3 trials that are looking for modest treatment benefits. How many of these trials don’t “achieve statistical significance” but have results that would show a 70% or 80% probability of benefit? They might still provide good enough evidence to make decisions about treatments (based on, for example, cost-effectiveness), but at the moment they tend to get labelled as “non-significant” or “negative trials.”


November 12, 2016

“The probability that the results are due to chance”

One of the (wrong) explanations that you often see of what a p-value means is “the probability that data have arisen by chance.” I think people may struggle to see why this is wrong, as I did for a long time. A p-value is the probability of getting the data (or more extreme data) if the null hypothesis (no difference) is correct – right? So that would mean the specific result you got must have been due to chance variation, doesn’t it? So why isn’t the p-value the probability that the result was due to chance?

The problem is that there are two ways of interpreting “the probability that a result is due to chance.”
1. The probability that chance or random variation was the process that produced the result;
2. The probability of getting the specific data (or more extreme data) that you got in your experiment, if chance was the only process operating.

The second of these is what the p-value tells you; but the first is the interpretation that most people give it. The p-value tells you nothing about the process that produced the result, because it is calculated on the assumption that the null hypothesis is correct.


November 03, 2016

Statistical significance and decision–making

One of the defences of the use of traditional “null hypothesis significance testing” (NHST) in clinical trials is that, at some point, it is necessary to make a decision about whether a treatment should be used, and “statistical significance” gives us a way of doing that. I hear versions of this argument on a regular basis.

But the argument has always seemed to me to be ridiculous. Even if significance tests could tell you that the null hypothesis was wrong (they can’t), that doesn’t give you any basis for a sensible decision. A null hypothesis being wrong doesn’t tell you whether the treatment has a big enough effect to be worth implementing, and it takes no account of other important things, like cost-effectiveness, safety, feasibility or patient acceptability. Not a good basis for what are potentially life and death decisions.

But don’t listen to me: listen to The American Statistical Association. Their Statement on Statistical Significance and P-Values from earlier this year addresses exactly this point. The third of their principles is:

“Scientific conclusions and business or policy decisions should not be based only on whether a p-value passes a specific threshold.”

Pretty unambiguous, I think.


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:
https://healthmanagement.org/c/cardio/news/danish-trial-icds-in-non-ischaemic-heart-failure
http://www.medscape.com/viewarticle/868065
http://www.tctmd.com/show.aspx?id=136105

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 (including cardiac and other causes), 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
http://www.nejm.org/doi/full/10.1056/NEJMoa1608029


October 02, 2016

Classical statistics revisited

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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:
https://alexanderetz.com/2015/08/03/the-general-public-has-no-idea-what-statistically-significant-means/


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.


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