false discovery rate
This piece is almost identical with today’s Spectator Health article.
This week there has been enormously wide coverage in the press for one of the worst papers on acupuncture that I’ve come across. As so often, the paper showed the opposite of what its title and press release, claimed. For another stunning example of this sleight of hand, try Acupuncturists show that acupuncture doesn’t work, but conclude the opposite: journal fails, published in the British Journal of General Practice).
Presumably the wide coverage was a result of the hypedup press release issued by the journal, BMJ Acupuncture in Medicine. That is not the British Medical Journal of course, but it is, bafflingly, published by the BMJ Press group, and if you subscribe to press releases from the real BMJ. you also get them from Acupuncture in Medicine. The BMJ group should not be mixing up press releases about real medicine with press releases about quackery. There seems to be something about quackery that’s clickbait for the mainstream media.
As so often, the press release was shockingly misleading: It said
Acupuncture may alleviate babies’ excessive crying Needling twice weekly for 2 weeks reduced crying time significantly
This is totally untrue. Here’s why.
Luckily the Science Media Centre was on the case quickly: read their assessment. The paper made the most elementary of all statistical mistakes. It failed to make allowance for the jelly bean problem. The paper lists 24 different tests of statistical significance and focusses attention on three that happen to give a P value (just) less than 0.05, and so were declared to be "statistically significant". If you do enough tests, some are bound to come out “statistically significant” by chance. They are false postives, and the conclusions are as meaningless as “green jelly beans cause acne” in the cartoon. This is called Phacking and it’s a well known cause of problems. It was evidently beyond the wit of the referees to notice this naive mistake. It’s very doubtful whether there is anything happening but random variability. And that’s before you even get to the problem of the weakness of the evidence provided by P values close to 0.05. There’s at least a 30% chance of such values being false positives, even if it were not for the jelly bean problem, and a lot more than 30% if the hypothesis being tested is implausible. I leave it to the reader to assess the plausibility of the hypothesis that a good way to stop a baby crying is to stick needles into the poor baby. If you want to know more about P values try Youtube or here, or here. 
One of the people asked for an opinion on the paper was George Lewith, the wellknown apologist for all things quackish. He described the work as being a "good sized fastidious well conducted study ….. The outcome is clear". Thus showing an ignorance of statistics that would shame an undergraduate.
On the Today Programme, I was interviewed by the formidable John Humphrys, along with the mandatory member of the flatearth society whom the BBC seems to feel obliged to invite along for "balance". In this case it was professional acupuncturist, Mike Cummings, who is an associate editor of the journal in which the paper appeared. Perhaps he’d read the Science media centre’s assessment before he came on, because he said, quite rightly, that
"in technical terms the study is negative" "the primary outcome did not turn out to be statistically significant"
to which Humphrys retorted, reasonably enough, “So it doesn’t work”. Cummings’ response to this was a lot of bluster about how unfair it was for NICE to expect a treatment to perform better than placebo. It was fascinating to hear Cummings admit that the press release by his own journal was simply wrong.
Listen to the interview here
Another obvious flaw of the study is that the nature of the control group. It is not stated very clearly but it seems that the baby was left alone with the acupuncturist for 10 minutes. A far better control would have been to have the baby cuddled by its mother, or by a nurse. That’s what was used by Olafsdottir et al (2001) in a study that showed cuddling worked just as well as another form of quackery, chiropractic, to stop babies crying.
Manufactured doubt is a potent weapon of the alternative medicine industry. It’s the same tactic as was used by the tobacco industry. You scrape together a few lousy papers like this one and use them to pretend that there’s a controversy. For years the tobacco industry used this tactic to try to persuade people that cigarettes didn’t give you cancer, and that nicotine wasn’t addictive. The main stream media obligingly invite the representatives of the industry who convey to the reader/listener that there is a controversy, when there isn’t.
Acupuncture is no longer controversial. It just doesn’t work see Acupuncture is a theatrical placebo: the end of a myth. Try to imagine a pill that had been subjected to well over 3000 trials without anyone producing convincing evidence for a clinically useful effect. It would have been abandoned years ago. But by manufacturing doubt, the acupuncture industry has managed to keep its product in the news. Every paper on the subject ends with the words "more research is needed". No it isn’t.
Acupuncture is prescientific idea that was moribund everywhere, even in China, until it was revived by Mao Zedong as part of the appalling Great Proletarian Revolution. Now it is big business in China, and 100 percent of the clinical trials that come from China are positive.
if you believe them, you’ll truly believe anything.
Followup
29 January 2017
Soon after the Today programme in which we both appeared, the acupuncturist, Mike Cummings, posted his reaction to the programme. I thought it worth posting the original version in full. Its petulance and abusiveness are quite remarkable.
I thank Cummings for giving publicity to the video of our appearance, and for referring to my Wikipedia page. I leave it to the reader to judge my competence, and his, in the statistics of clinical trials. And it’s odd to be described as a "professional blogger" when the 400+ posts on dcscience.net don’t make a penny in fact they cost me money. In contrast, he is the salaried medical director of the British Medical Acupuncture Society.
It’s very clear that he has no understanding of the error of the transposed conditional, nor even the mulltiple comparison problem (and neither, it seems, does he know the meaning of the word ‘protagonist’).
I ignored his piece, but several friends complained to the BMJ for allowing such abusive material on their blog site. As a result a few changes were made. The “baying mob” is still there, but the Wikipedia link has gone. I thought that readers might be interested to read the original unexpurgated version. It shows, better than I ever could, the weakness of the arguments of the alternative medicine community. To quote Upton Sinclair:
“It is difficult to get a man to understand something, when his salary depends upon his not understanding it.”
It also shows that the BBC still hasn’t learned the lessons in Steve Jones’ excellent “Review of impartiality and accuracy of the BBC’s coverage of science“. Every time I appear in such a programme, they feel obliged to invite a member of the flat earth society to propagate their makebelieve.
Acupuncture for infantile colic – misdirection in the media or overreaction from a sceptic blogger?26 Jan, 17  by Dr Mike Cummings So there has been a big response to this paper press released by BMJ on behalf of the journal Acupuncture in Medicine. The response has been influenced by the usual characters – retired professors who are professional bloggers and vocal critics of anything in the realm of complementary medicine. They thrive on oiling up and flexing their EBM muscles for a baying mob of fellow sceptics (see my ‘stereotypical mental image’ here). Their target in this instant is a relatively small trial on acupuncture for infantile colic.[1] Deserving of being press released by virtue of being the largest to date in the field, but by no means because it gave a definitive answer to the question of the efficacy of acupuncture in the condition. We need to wait for an SR where the data from the 4 trials to date can be combined. So what about the research itself? I have already said that the trial was not definitive, but it was not a bad trial. It suffered from underrecruiting, which meant that it was underpowered in terms of the statistical analysis. But it was prospectively registered, had ethical approval and the protocol was published. Primary and secondary outcomes were clearly defined, and the only change from the published protocol was to combine the two acupuncture groups in an attempt to improve the statistical power because of under recruitment. The fact that this decision was made after the trial had begun means that the results would have to be considered speculative. For this reason the editors of Acupuncture in Medicine insisted on alteration of the language in which the conclusions were framed to reflect this level of uncertainty. DC has focussed on multiple statistical testing and p values. These are important considerations, and we could have insisted on more clarity in the paper. P values are a guide and the 0.05 level commonly adopted must be interpreted appropriately in the circumstances. In this paper there are no definitive conclusions, so the p values recorded are there to guide future hypothesis generation and trial design. There were over 50 p values reported in this paper, so by chance alone you must expect some to be below 0.05. If one is to claim statistical significance of an outcome at the 0.05 level, ie a 1:20 likelihood of the event happening by chance alone, you can only perform the test once. If you perform the test twice you must reduce the p value to 0.025 if you want to claim statistical significance of one or other of the tests. So now we must come to the predefined outcomes. They were clearly stated, and the results of these are the only ones relevant to the conclusions of the paper. The primary outcome was the relative reduction in total crying time (TC) at 2 weeks. There were two significance tests at this point for relative TC. For a statistically significant result, the p values would need to be less than or equal to 0.025 – neither was this low, hence my comment on the Radio 4 Today programme that this was technically a negative trial (more correctly ‘not a positive trial’ – it failed to disprove the null hypothesis ie that the samples were drawn from the same population and the acupuncture intervention did not change the population treated). Finally to the secondary outcome – this was the number of infants in each group who continued to fulfil the criteria for colic at the end of each intervention week. There were four tests of significance so we need to divide 0.05 by 4 to maintain the 1:20 chance of a random event ie only draw conclusions regarding statistical significance if any of the tests resulted in a p value at or below 0.0125. Two of the 4 tests were below this figure, so we say that the result is unlikely to have been chance alone in this case. With hindsight it might have been good to include this explanation in the paper itself, but as editors we must constantly balance how much we push authors to adjust their papers, and in this case the editor focussed on reducing the conclusions to being speculative rather than definitive. A significant result in a secondary outcome leads to a speculative conclusion that acupuncture ‘may’ be an effective treatment option… but further research will be needed etc… Now a final word on the 3000 plus acupuncture trials that DC loves to mention. His point is that there is no consistent evidence for acupuncture after over 3000 RCTs, so it clearly doesn’t work. He first quoted this figure in an editorial after discussing the largest, most statistically reliable metaanalysis to date – the Vickers et al IPDM.[2] DC admits that there is a small effect of acupuncture over sham, but follows the standard EBM mantra that it is too small to be clinically meaningful without ever considering the possibility that sham (gentle acupuncture plus context of acupuncture) can have clinically relevant effects when compared with conventional treatments. Perhaps now the best example of this is a network metaanalysis (NMA) using individual patient data (IPD), which clearly demonstrates benefits of sham acupuncture over usual care (a variety of best standard or usual care) in terms of healthrelated quality of life (HRQoL).[3] 
30 January 2017
I got an email from the BMJ asking me to take part in a BMJ HeadtoHead debate about acupuncture. I did one of these before, in 2007, but it generated more heat than light (the only good thing to come out of it was the joke about leprechauns). So here is my polite refusal.
Hello Thanks for the invitation, Perhaps you should read the piece that I wrote after the Today programme Why don’t you do these Head to Heads about genuine controversies? To do them about homeopathy or acupuncture is to fall for the “manufactured doubt” stratagem that was used so effectively by the tobacco industry to promote smoking. It’s the favourite tool of snake oil salesman too, and th BMJ should see that and not fall for their tricks. Such pieces night be good clickbait, but they are bad medicine and bad ethics. All the best David 
This post arose from a recent meeting at the Royal Society. It was organised by Julie Maxton to discuss the application of statistical methods to legal problems. I found myself sitting next to an Appeal Court Judge who wanted more explanation of the ideas. Here it is.
Some preliminaries
The paper that I wrote recently was a review of the problems associated with the interpretation of screening tests and tests of significance. It doesn’t allude to legal problems explicitly, though the problems are the same in principle. It is open access, at
http://rsos.royalsocietypublishing.org/content/1/3/140216
In that paper I was interested in the false positive rate (also known as the false discovery rate) in tests of significance. It turned out to be alarmingly large. That has serious consequences for the credibility of the scientific literature. In legal terms, the false positive rate means the proportion of cases in which, on the basis of the evidence, a suspect is found guilty when in fact they are innocent. That has even more serious consequences.
Although most of what I want to say can be said without much algebra, it would perhaps be worth getting two things clear before we start.
The rules of probability.
(1) To get any understanding, it’s essential to understand the rules of probabilities, and, in particular, the idea of conditional probabilities. One source would be my old book, Lectures on Biostatistics (now free), The account on pages 19 to 24 give a pretty simple (I hope) description of what’s needed. Briefly, a vertical line is read as “given”, so Prob(evidence  not guilty) means the probability that the evidence would be observed given that the suspect was not guilty.
(2) Another potential confusion in this area is the relationship between odds and probability. The relationship between the probability of an event occurring, and the odds on the event can be illustrated by an example. If the probability of being righthanded is 0.9, then the probability of being not being righthanded is 0.1. That means that 9 people out of 10 are righthanded, and one person in 10 is not. In other words for every person who is not righthanded there are 9 who are righthanded. Thus the odds that a randomlyselected person is righthanded are 9 to 1. In symbols this can be written
\[ \mathrm{probability=\frac{odds}{1 + odds}} \]
In the example, the odds on being righthanded are 9 to 1, so the probability of being righthanded is 9 / (1+9) = 0.9.
Conversely,
\[ \mathrm{odds =\frac{probability}{1 – probability}} \]
In the example, the probability of being righthanded is 0.9, so the odds of being righthanded are 0.9 / (1 – 0.9) = 0.9 / 0.1 = 9 (to 1).
With these preliminaries out of the way, we can proceed to the problem.
The legal problem
The first problem lies in the fact that the answer depends on Bayes’ theorem. Although that was published in 1763, statisticians are still arguing about how it should be used to this day. In fact whenever it’s mentioned, statisticians tend to revert to internecine warfare, and forget about the user.
Bayes’ theorem can be stated in words as follows
\[ \mathrm{\text{posterior odds ratio} = \text{prior odds ratio} \times \text{likelihood ratio}} \]
“Posterior odds ratio” means the odds that the person is guilty, relative to the odds that they are innocent, in the light of the evidence, and that’s clearly what one wants to know. The “prior odds” are the odds that the person was guilty before any evidence was produced, and that is the really contentious bit.
Sometimes the need to specify the prior odds has been circumvented by using the likelihood ratio alone, but, as shown below, that isn’t a good solution.
The analogy with the use of screening tests to detect disease is illuminating.
Screening tests
A particularly straightforward application of Bayes’ theorem is in screening people to see whether or not they have a disease. It turns out, in many cases, that screening gives a lot more wrong results (false positives) than right ones. That’s especially true when the condition is rare (the prior odds that an individual suffers from the condition is small). The process of screening for disease has a lot in common with the screening of suspects for guilt. It matters because false positives in court are disastrous.
The screening problem is dealt with in sections 1 and 2 of my paper. or on this blog (and here). A bit of animation helps the slides, so you may prefer the Youtube version: (It deals with screening tests up to 8’45”).
The rest of my paper applies similar ideas to tests of significance. In that case the prior probability is the probability that there is in fact a real effect, or, in the legal case, the probability that the suspect is guilty before any evidence has been presented. This is the slippery bit of the problem both conceptually, and because it’s hard to put a number on it.
But the examples below show that to ignore it, and to use the likelihood ratio alone, could result in many miscarriages of justice.
In the discussion of tests of significance, I took the view that it is not legitimate (in the absence of good data to the contrary) to assume any prior probability greater than 0.5. To do so would presume you know the answer before any evidence was presented. In the legal case a prior probability of 0.5 would mean assuming that there was a 50:50 chance that the suspect was guilty before any evidence was presented. A 50:50 probability of guilt before the evidence is known corresponds to a prior odds ratio of 1 (to 1) If that were true, the likelihood ratio would be a good way to represent the evidence, because the posterior odds ratio would be equal to the likelihood ratio.
It could be argued that 50:50 represents some sort of equipoise, but in the example below it is clearly too high, and if it is less that 50:50, use of the likelihood ratio runs a real risk of convicting an innocent person.
The following example is modified slightly from section 3 of a book chapter by Mortera and Dawid (2008). Philip Dawid is an eminent statistician who has written a lot about probability and the law, and he’s a member of the legal group of the Royal Statistical Society.
My version of the example removes most of the algebra, and uses different numbers.
Example: The island problem
The “island problem” (Eggleston 1983, Appendix 3) is an imaginary example that provides a good illustration of the uses and misuses of statistical logic in forensic identification.
A murder has been committed on an island, cut off from the outside world, on which 1001 (= N + 1) inhabitants remain. The forensic evidence at the scene consists of a measurement, x, on a “crime trace” characteristic, which can be assumed to come from the criminal. It might, for example, be a bit of the DNA sequence from the crime scene.
Say, for the sake of example, that the probability of a random member of the population having characteristic x is P = 0.004 (i.e. 0.4% ), so the probability that a random member of the population does not have the characteristic is 1 – P = 0.996. The mainland police arrive and arrest a random islander, Jack. It is found that Jack matches the crime trace. There is no other relevant evidence.
How should this match evidence be used to assess the claim that Jack is the murderer? We shall consider three arguments that have been used to address this question. The first is wrong. The second and third are right. (For illustration, we have taken N = 1000, P = 0.004.)
(1) Prosecutor’s fallacy
Prosecuting counsel, arguing according to his favourite fallacy, asserts that the probability that Jack is guilty is 1 – P , or 0.996, and that this proves guilt “beyond a reasonable doubt”.
The probability that Jack would show characteristic x if he were not guilty would be 0.4% i.e. Prob(Jack has x  not guilty) = 0.004. Therefore the probability of the evidence, given that Jack is guilty, Prob(Jack has x  Jack is guilty), is one 1 – 0.004 = 0.996.
But this is Prob(evidence  guilty) which is not what we want. What we need is the probability that Jack is guilty, given the evidence, P(Jack is guilty  Jack has characteristic x).
To mistake the latter for the former is the prosecutor’s fallacy, or the error of the transposed conditional.
Dawid gives an example that makes the distinction clear.
“As an analogy to help clarify and escape this common and seductive confusion, consider the difference between “the probability of having spots, if you have measles” which is close to 1 and “the probability of having measles, if you have spots” which, in the light of the many alternative possible explanations for spots, is much smaller.”
(2) Defence counterargument
Counsel for the defence points out that, while the guilty party must have characteristic x, he isn’t the only person on the island to have this characteristic. Among the remaining N = 1000 innocent islanders, 0.4% have characteristic x, so the number who have it will be NP = 1000 x 0.004 = 4 . Hence the total number of islanders that have this characteristic must be 1 + NP = 5 . The match evidence means that Jack must be one of these 5 people, but does not otherwise distinguish him from any of the other members of it. Since just one of these is guilty, the probability that this is Jack is thus 1/5, or 0.2— very far from being “beyond all reasonable doubt”.
(3) Bayesian argument
The probability of the having characteristic x (the evidence) would be Prob(evidence  guilty) = 1 if Jack were guilty, but if Jack were not guilty it would be 0.4%, i.e. Prob(evidence  not guilty) = P. Hence the likelihood ratio in favour of guilt, on the basis of the evidence, is
\[ LR=\frac{\text{Prob(evidence }  \text{ guilty})}{\text{Prob(evidence }\text{ not guilty})} = \frac{1}{P}=250 \]
In words, the evidence would be 250 times more probable if Jack were guilty than if he were innocent. While this seems strong evidence in favour of guilt, it still does not tell us what we want to know, namely the probability that Jack is guilty in the light of the evidence: Prob(guilty  evidence), or, equivalently, the odds ratio the odds of guilt relative to odds of innocence, given the evidence,
To get that we must multiply the likelihood ratio by the prior odds on guilt, i.e. the odds on guilt before any evidence is presented. It’s often hard to get a numerical value for this. But in our artificial example, it is possible. We can argue that, in the absence of any other evidence, Jack is no more nor less likely to be the culprit than any other islander, so that the prior probability of guilt is 1/(N + 1), corresponding to prior odds on guilt of 1/N.
We can now apply Bayes’s theorem to obtain the posterior odds on guilt:
\[ \text {posterior odds} = \text{prior odds} \times LR = \left ( \frac{1}{N}\right ) \times \left ( \frac{1}{P} \right )= 0.25 \]
Thus the odds of guilt in the light of the evidence are 4 to 1 against. The corresponding posterior probability of guilt is
\[ Prob( \text{guilty }  \text{ evidence})= \frac{1}{1+NP}= \frac{1}{1+4}=0.2 \]
This is quite small –certainly no basis for a conviction.
This result is exactly the same as that given by the Defence Counterargument’, (see above). That argument was simpler than the Bayesian argument. It didn’t explicitly use Bayes’ theorem, though it was implicit in the argument. The advantage of using the former is that it looks simpler. The advantage of the explicitly Bayesian argument is that it makes the assumptions more clear.
In summary The prosecutor’s fallacy suggested, quite wrongly, that the probability that Jack was guilty was 0.996. The likelihood ratio was 250, which also seems to suggest guilt, but it doesn’t give us the probability that we need. In stark contrast, the defence counsel’s argument, and equivalently, the Bayesian argument, suggested that the probability of Jack’s guilt as 0.2. or odds of 4 to 1 against guilt. The potential for wrong conviction is obvious.
Conclusions.
Although this argument uses an artificial example that is simpler than most real cases, it illustrates some important principles.
(1) The likelihood ratio is not a good way to evaluate evidence, unless there is good reason to believe that there is a 50:50 chance that the suspect is guilty before any evidence is presented.
(2) In order to calculate what we need, Prob(guilty  evidence), you need to give numerical values of how common the possession of characteristic x (the evidence) is the whole population of possible suspects (a reasonable value might be estimated in the case of DNA evidence), We also need to know the size of the population. In the case of the island example, this was 1000, but in general, that would be hard to answer and any answer might well be contested by an advocate who understood the problem.
These arguments lead to four conclusions.
(1) If a lawyer uses the prosecutor’s fallacy, (s)he should be told that it’s nonsense.
(2) If a lawyer advocates conviction on the basis of likelihood ratio alone, s(he) should be asked to justify the implicit assumption that there was a 50:50 chance that the suspect was guilty before any evidence was presented.
(3) If a lawyer uses Defence counterargument, or, equivalently, the version of Bayesian argument given here, (s)he should be asked to justify the estimates of the numerical value given to the prevalence of x in the population (P) and the numerical value of the size of this population (N). A range of values of P and N could be used, to provide a range of possible values of the final result, the probability that the suspect is guilty in the light of the evidence.
(4) The example that was used is the simplest possible case. For more complex cases it would be advisable to ask a professional statistician. Some reliable people can be found at the Royal Statistical Society’s section on Statistics and the Law.
If you do ask a professional statistician, and they present you with a lot of mathematics, you should still ask these questions about precisely what assumptions were made, and ask for an estimate of the range of uncertainty in the value of Prob(guilty  evidence) which they produce.
Postscript: real cases
Another paper by Philip Dawid, Statistics and the Law, is interesting because it discusses some recent real cases: for example the wrongful conviction of Sally Clark because of the wrong calculation of the statistics for Sudden Infant Death Syndrome.
On Monday 21 March, 2016, Dr Waney Squier was struck off the medical register by the General Medical Council because they claimed that she misrepresented the evidence in cases of Shaken Baby Syndrome (SBS).
This verdict was questioned by many lawyers, including Michael Mansfield QC and Clive Stafford Smith, in a letter. “General Medical Council behaving like a modern inquisition”
The latter has already written “This shaken baby syndrome case is a dark day for science – and for justice“..
The evidence for SBS is based on the existence of a triad of signs (retinal bleeding, subdural bleeding and encephalopathy). It seems likely that these signs will be present if a baby has been shake, i.e Prob(triad  shaken) is high. But this is irrelevant to the question of guilt. For that we need Prob(shaken  triad). As far as I know, the data to calculate what matters are just not available.
It seem that the GMC may have fallen for the prosecutor’s fallacy. Or perhaps the establishment won’t tolerate arguments. One is reminded, once again, of the definition of clinical experience: "Making the same mistakes with increasing confidence over an impressive number of years." (from A Sceptic’s Medical Dictionary by Michael O’Donnell. A Sceptic’s Medical Dictionary BMJ publishing, 1997).
Appendix (for nerds). Two forms of Bayes’ theorem
The form of Bayes’ theorem given at the start is expressed in terms of odds ratios. The same rule can be written in terms of probabilities. (This was the form used in the appendix of my paper.) For those interested in the details, it may help to define explicitly these two forms.
In terms of probabilities, the probability of guilt in the light of the evidence (what we want) is
\[ \text{Prob(guilty }  \text{ evidence}) = \text{Prob(evidence }  \text{ guilty}) \frac{\text{Prob(guilty })}{\text{Prob(evidence })} \]
In terms of odds ratios, the odds ratio on guilt, given the evidence (which is what we want) is
\[ \frac{ \text{Prob(guilty }  \text{ evidence})} {\text{Prob(not guilty }  \text{ evidence}} =
\left ( \frac{ \text{Prob(guilty)}} {\text {Prob((not guilty)}} \right )
\left ( \frac{ \text{Prob(evidence }  \text{ guilty})} {\text{Prob(evidence }  \text{ not guilty}} \right ) \]
or, in words,
\[ \text{posterior odds of guilt } =\text{prior odds of guilt} \times \text{likelihood ratio} \]
This is the precise form of the equation that was given in words at the beginning.
A derivation of the equivalence of these two forms is sketched in a document which you can download.
Followup
23 March 2016
It’s worth pointing out the following connection between the legal argument (above) and tests of significance.
(1) The likelihood ratio works only when there is a 50:50 chance that the suspect is guilty before any evidence is presented (so the prior probability of guilt is 0.5, or, equivalently, the prior odds ratio is 1).
(2) The false positive rate in signiifcance testing is close to the P value only when the prior probability of a real effect is 0.5, as shown in section 6 of the P value paper.
However there is another twist in the significance testing argument. The statement above is right if we take as a positive result any P < 0.05. If we want to interpret a value of P = 0.047 in a single test, then, as explained in section 10 of the P value paper, we should restrict attention to only those tests that give P close to 0.047. When that is done the false positive rate is 26% even when the prior is 0.5 (and much bigger than 30% if the prior is smaller –see extra Figure), That justifies the assertion that if you claim to have discovered something because you have observed P = 0.047 in a single test then there is a chance of at least 30% that you’ll be wrong. Is there, I wonder, any legal equivalent of this argument?
Chalkdust is a magazine published by students of maths from UCL Mathematics department. Judging by its first issue, it’s an excellent vehicle for popularisation of maths. I have a piece in the second issue
You can view the whole second issue on line, or download a pdf of the whole issue. Or a pdf of my bit only: On the Perils of P values.
The piece started out as another exposition of the interpretation of P values, but the whole of the first part turned into an explanation of the principles of randomisation tests. It beats me why anybody still does a Student’s t test. The idea of randomisation tests is very old. They are as powerful as t tests when the assumptions of the latter are fulfilled but a lot better when the assumptions are wrong (in the jargon, they are uniformlymostpowerful tests).
Not only that, but you need no mathematics to do a randomisation test, whereas you need a good deal of mathematics to follow Student’s 1908 paper. And the randomisation test makes transparently clear that random allocation of treatments is a basic and essential assumption that’s necessary for the the validity of any test of statistical significance.
I made a short video that explains the principles behind the randomisation tests, to go with the printed article (a bit of animation always helps).
When I first came across the principals of randomisation tests, i was entranced by the simplicity of the idea. Chapters 6 – 9 of my old textbook were written to popularise them. You can find much more detail there.
In fact it’s only towards the end that I reiterate the idea that P values don’t answer the question that experimenters want to ask, namely: if I claim I have made a discovery because P is small, what’s the chance that I’ll be wrong?
If you want the full story on that, read my paper. The story it tells is not very original, but it still isn’t known to most experimenters (because most statisticians still don’t teach it on elementary courses). The paper must have struck a chord because it’s had over 80,000 full text views and more than 10,000 pdf downloads. It reached an altmetric score of 975 (since when it has been mysteriously declining). That’s gratifying, but it is also a condemnation of the use of metrics. The paper is not original and it’s quite simple, yet it’s had far more "impact" than anything to do with my real work.
If you want simpler versions than the full paper, try this blog (part 1 and part 2), or the Youtube video about misinterpretation of P values.
The R code for doing 2sample randomisation tests
You can download a pdf file that describes the two R scripts. There are two different R programs.
One resamples randomly a specified number of times (the default is 100,000 times, but you can do any number). Download two_sample_rantest.R
The other uses every possible sample in the case of the two samples of 10 observations,it gives the distribution for all 184,756 ways of selecting 10 observations from 20. Download 2samplerantestexact.R
The launch party
Today the people who organise Chalkdust magazine held a party in the mathematics department at UCL. The editorial director is a graduate student in maths, Rafael Prieto Curiel. He was, at one time in the Mexican police force (he said he’d suffered more crime in London than in Mexico City). He, and the rest of the team, are deeply impressive. They’ve done a terrific job. Support them.
The party cakes
Rafael Prieto doing the introduction
Rafael Prieto doing the introduction
Rafael Prieto and me
I got the T shirt
Decoding the T shirt
The top line is "I" because that’s the usual symbol for the square root of 1.
The second line is one of many equations that describe a heart shape. It can be plotted by calculating a matrix of values of the left hand side for a range of values of x and y. Then plot the contour for a values x and y for which the left hand side is equal to 1. Download R script for this. (Method suggested by Rafael Prieto Curiel.) 

Followup
5 November 2015
The MannWhitney test
I was stimulated to write this followup because yesterday I was asked by a friend to comment on the fact that five different tests all gave identical P values, P = 0.0079. The paper in question was in Science magazine (see Fig. 1), so it wouldn’t surprise me if the statistics were done badly, but in this case there is an innocent explanation.
The Chalkdust article, and the video, are about randomisation tests done using the original observed numbers, so look at them before reading on. There is a more detailed explanation in Chapter 9 of Lectures on Biostatistics. Before it became feasible to do this sort of test, there was a simpler, and less efficient, version in which the observations were ranked in ascending order, and the observed values were replaced by their ranks. This was known as the Mann Whitney test. It had the virtue that because all the ‘observations’ were now integers, the number of possible results of resampling was limited so it was possible to construct tables to allow one to get a rough P value. Of course, replacing observations by their ranks throws away some information, and now that we have computers there is no need to use a MannWhitney test ever. But that’s what was used in this paper.
In the paper (Fig 1) comparisons are made between two groups (assumed to be independent) with 5 observations in each group. The 10 observations are just the ranks, 1, 2, 3, 4, 5, 6, 7, 8, 9, 10.
To do the randomisation test we select 5 of these numbers at random for sample A, and the other 5 are sample B. (Of course this supposes that the treatments were applied randomly in the real experiment, which is unlikely to be true.) In fact there are only 10!/(5!.5!) = 252 possible ways to select a sample of 5 from 10, so it’s easy to list all of them. In the case where there is no overlap between the groups, one group will contain the smallest observations (ranks 1, 2, 3, 4, 5, and the other group will contain the highest observations, ranks 6, 7, 8, 9, 10.
In this case, the sum of the ‘observations’ in group A is 15, and the sum for group B is 40.These add to the sum of the first 10 integers, 10.(10+1)/2 = 55. The mean (which corresponds to a difference between means of zero) is 55/2 = 27.5.
There are two ways of getting an allocation as extreme as this (first group low, as above, or second group low, the other tail of the distribution). The two tailed P value is therefore 2/252 = 0.0079. This will be the result whenever the two groups don’t overlap, regardless of the numerical values of the observations. It’s the smallest P value the test can produce with 5 observations in each group.
The whole randomisation distribution looks like this
In this case, the abscissa is the sum of the ranks in sample A, rather than the difference between means for the two groups (the latter is easily calculated from the former). The red line shows the observed value, 15. There is only one way to get a total of 15 for group A: it must contain the lowest 5 ranks (group A = 1, 2, 3, 4, 5). There is also only one way to get a total of 16 (group A = 1, 2, 3, 4, 6),and there are two ways of getting a total of 17 (group A = 1, 2, 3, 4, 7, or 1, 2, 3, 5, 6), But there are 20 different ways of getting a sum of 27 or 28 (which straddle the mean, 27.5). The printout (.txt file) from the R program that was used to generate the distribution is as follows.
Randomisation test: exact calculation all possible samples INPUTS: exact calculation: all possible samples OUTPUTS Result of t test 
Some problems. Figure 1 alone shows 16 twosample comparisons, but no correction for multiple comparisons seems to have been made. A crude Bonferroni correction would require replacement of a P = 0.05 threshold with P = 0.05/16 = 0.003. None of the 5 tests that gave P = 0.0079 reaches this level (of course the whole idea of a threshold level is absurd anyway).
Furthermore, even a single test that gave P = 0.0079 would be expected to have a false positive rate of around 10 percent
In the course of thinking about metrics, I keep coming across cases of overpromoted research. An early case was “Why honey isn’t a wonder cough cure: more academic spin“. More recently, I noticed these examples.
“Effect of Vitamin E and Memantine on Functional Decline in Alzheimer Disease".(Spoiler very little), published in the Journal of the American Medical Association. ”
and ” Primary Prevention of Cardiovascular Disease with a Mediterranean Diet” , in the New England Journal of Medicine (which had second highest altmetric score in 2013)
and "Sleep Drives Metabolite Clearance from the Adult Brain", published in Science
In all these cases, misleading press releases were issued by the journals themselves and by the universities. These were copied out by hardpressed journalists and made headlines that were certainly not merited by the work. In the last three cases, hyped up tweets came from the journals. The responsibility for this hype must eventually rest with the authors. The last two papers came second and fourth in the list of highest altmetric scores for 2013
Here are to two more very recent examples. It seems that every time I check a highly tweeted paper, it turns out that it is very second rate. Both papers involve fMRI imaging, and since the infamous dead salmon paper, I’ve been a bit sceptical about them. But that is irrelevant to what follows.
Boost your memory with electricity
That was a popular headline at the end of August. It referred to a paper in Science magazine:
“Targeted enhancement of corticalhippocampal brain networks and associative memory” (Wang, JX et al, Science, 29 August, 2014)
This study was promoted by the Northwestern University "Electric current to brain boosts memory". And Science tweeted along the same lines.
Science‘s link did not lead to the paper, but rather to a puff piece, "Rebooting memory with magnets". Again all the emphasis was on memory, with the usual entirely speculative stuff about helping Alzheimer’s disease. But the paper itself was behind Science‘s paywall. You couldn’t read it unless your employer subscribed to Science.

All the publicity led to much retweeting and a big altmetrics score. Given that the paper was not open access, it’s likely that most of the retweeters had not actually read the paper. 

When you read the paper, you found that is mostly not about memory at all. It was mostly about fMRI. In fact the only reference to memory was in a subsection of Figure 4. This is the evidence.
That looks desperately unconvincing to me. The test of significance gives P = 0.043. In an underpowered study like this, the chance of this being a false discovery is probably at least 50%. A result like this means, at most, "worth another look". It does not begin to justify all the hype that surrounded the paper. The journal, the university’s PR department, and ultimately the authors, must bear the responsibility for the unjustified claims.
Science does not allow online comments following the paper, but there are now plenty of sites that do. NHS Choices did a fairly good job of putting the paper into perspective, though they failed to notice the statistical weakness. A commenter on PubPeer noted that Science had recently announced that it would tighten statistical standards. In this case, they failed. The age of postpublication peer review is already reaching maturity
Boost your memory with cocoa
Another glamour journal, Nature Neuroscience, hit the headlines on October 26, 2014, in a paper that was publicised in a Nature podcast and a rather uninformative press release.
"Enhancing dentate gyrus function with dietary flavanols improves cognition in older adults. Brickman et al., Nat Neurosci. 2014. doi: 10.1038/nn.3850.".
The journal helpfully lists no fewer that 89 news items related to this study. Mostly they were something like “Drinking cocoa could improve your memory” (Kat Lay, in The Times). Only a handful of the 89 reports spotted the many problems.
A puff piece from Columbia University’s PR department quoted the senior author, Dr Small, making the dramatic claim that
“If a participant had the memory of a typical 60yearold at the beginning of the study, after three months that person on average had the memory of a typical 30 or 40yearold.”
Like anything to do with diet, the paper immediately got circulated on Twitter. No doubt most of the people who retweeted the message had not read the (paywalled) paper. The links almost all led to inaccurate press accounts, not to the paper itself. 

But some people actually read the paywalled paper and postpublication review soon kicked in. Pubmed Commons is a good site for that, because Pubmed is where a lot of people go for references. Hilda Bastian kicked off the comments there (her comment was picked out by Retraction Watch). Her conclusion was this.
"It’s good to see claims about dietary supplements tested. However, the results here rely on a chain of yettobevalidated assumptions that are still weakly supported at each point. In my opinion, the immodest title of this paper is not supported by its contents."
(Hilda Bastian runs the Statistically Funny blog “The comedic possibilities of clinical epidemiology are known to be limitless”, and also a Scientific American blog about risk, Absolutely Maybe.)
NHS Choices spotted most of the problems too, in "A mug of cocoa is not a cure for memory problems". And so did Ian Musgrave of the University of Adelaide who wrote "Most Disappointing Headline Ever (No, Chocolate Will Not Improve Your Memory)",
Here are some of the many problems.
 The paper was not about cocoa. Drinks containing 900 mg cocoa flavanols (as much as in about 25 chocolate bars) and 138 mg of (−)epicatechin were compared with much lower amounts of these compounds
 The abstract, all that most people could read, said that subjects were given "high or low cocoa–containing diet for 3 months". Bit it wasn’t a test of cocoa: it was a test of a dietary "supplement".
 The sample was small (37ppeople altogether, split between four groups), and therefore underpowered for detection of the small effect that was expected (and observed)
 The authors declared the result to be "significant" but you had to hunt through the paper to discover that this meant P = 0.04 (hint it’s 6 lines above Table 1). That means that there is around a 50% chance that it’s a false discovery.
 The test was short only three months
 The test didn’t measure memory anyway. It measured reaction speed, They did test memory retention too, and there was no detectable improvement. This was not mentioned in the abstract, Neither was the fact that exercise had no detectable effect.
 The study was funded by the Mars bar company. They, like many others, are clearly looking for a niche in the huge "supplement" market,
The claims by the senior author, in a Columbia promotional video that the drink produced "an improvement in memory" and "an improvement in memory performance by two or three decades" seem to have a very thin basis indeed. As has the statement that "we don’t need a pharmaceutical agent" to ameliorate a natural process (aging). High doses of supplements are pharmaceutical agents.
To be fair, the senior author did say, in the Columbia press release, that "the findings need to be replicated in a larger study—which he and his team plan to do". But there is no hint of this in the paper itself, or in the title of the press release "Dietary Flavanols Reverse AgeRelated Memory Decline". The time for all the publicity is surely after a wellpowered study, not before it.
The high altmetrics score for this paper is yet another blow to the reputation of altmetrics.
One may well ask why Nature Neuroscience and the Columbia press office allowed such extravagant claims to be made on such a flimsy basis.
What’s going wrong?
These two papers have much in common. Elaborate imaging studies are accompanied by poor functional tests. All the hype focusses on the latter. These led me to the speculation ( In Pubmed Commons) that what actually happens is as follows.
 Authors do big imaging (fMRI) study.
 Glamour journal says coloured blobs are no longer enough and refuses to publish without functional information.
 Authors tag on a small human study.
 Paper gets published.
 Hyped up press releases issued that refer mostly to the add on.
 Journal and authors are happy.
 But science is not advanced.
It’s no wonder that Dorothy Bishop wrote "Highimpact journals: where newsworthiness trumps methodology".
It’s time we forgot glamour journals. Publish open access on the web with open comments. Postpublication peer review is working
But boycott commercial publishers who charge large amounts for open access. It shouldn’t cost more than about £200, and more and more are essentially free (my latest will appear shortly in Royal Society Open Science).
Followup
Hilda Bastian has an excellent post about the dangers of reading only the abstract "Science in the Abstract: Don’t Judge a Study by its Cover"
4 November 2014
I was upbraided on Twitter by Euan Adie, founder of Almetric.com, because I didn’t click through the altmetric symbol to look at the citations "shouldn’t have to tell you to look at the underlying data David" and "you could have saved a lot of Google time". But when I did do that, all I found was a list of media reports and blogs pretty much the same as Nature Neuroscience provides itself.
More interesting, I found that my blog wasn’t listed and neither was PubMed Commons. When I asked why, I was told "needs to regularly cite primary research. PubMed, PMC or repository links”. But this paper is behind a paywall. So I provide (possibly illegally) a copy of it, so anyone can verify my comments. The result is that altmetric’s dumb algorithms ignore it. In order to get counted you have to provide links that lead nowhere.
So here’s a link to the abstract (only) in Pubmed for the Science paper http://www.ncbi.nlm.nih.gov/pubmed/25170153 and here’s the link for the Nature Neuroscience paper http://www.ncbi.nlm.nih.gov/pubmed/25344629
It seems that altmetrics doesn’t even do the job that it claims to do very efficiently.
It worked. By later in the day, this blog was listed in both Nature‘s metrics section and by altmetrics. com. But comments on Pubmed Commons were still missing, That’s bad because it’s an excellent place for postpublications peer review.
This post is now a bit out of date: there is a summary of my more recent efforts (papers, videos and pop stuff) can be found on Prof Sivilotti’s OneMol pages.
What follows is a simplified version of part of a paper that appeared as a preprint on arXiv in July. It appeared as a peerreviewed paper on 19th November 2014, in the new Royal Society Open Science journal. If you find anything wrong, or obscure, please email me. Be vicious.
There is also a simplified version, given as a talk on Youtube..
It’s a followup to my very first paper, which was written in 1959 – 60, while I was a fourth year undergraduate(the history is at a recent blog). I hope this one is better.
‘". . . before anything was known of Lydgate’s skill, the judgements on it had naturally been divided, depending on a sense of likelihood, situated perhaps in the pit of the stomach, or in the pineal gland, and differing in its verdicts, but not less valuable as a guide in the total deficit of evidence" ‘George Eliot (Middlemarch, Chap. 45)
"The standard approach in teaching, of stressing the formal definition of a pvalue while warning against its misinterpretation, has simply been an abysmal failure” Sellke et al. (2001) `The American Statistician’ (55), 62–71
The last post was about screening. It showed that most screening tests are useless, in the sense that a large proportion of people who test positive do not have the condition. This proportion can be called the false discovery rate. You think you’ve discovered the condition, but you were wrong.
Very similar ideas can be applied to tests of significance. If you read almost any scientific paper you’ll find statements like "this result was statistically significant (P = 0.047)". Tests of significance were designed to prevent you from making a fool of yourself by claiming to have discovered something, when in fact all you are seeing is the effect of random chance. In this case we define the false discovery rate as the probability that, when a test comes out as ‘statistically significant’, there is actually no real effect.
You can also make a fool of yourself by failing to detect a real effect, but this is less harmful to your reputation.
It’s very common for people to claim that an effect is real, not just chance, whenever the test produces a P value of less than 0.05, and when asked, it’s common for people to think that this procedure gives them a chance of 1 in 20 of making a fool of themselves. Leaving aside that this seems rather too often to make a fool of yourself, this interpretation is simply wrong.
The purpose of this post is to justify the following proposition.
If you observe a P value close to 0.05, your false discovery rate will not be 5%. It will be at least 30% and it could easily be 80% for small studies.

This makes slightly less startling the assertion in John Ioannidis’ (2005) article, Why Most Published Research Findings Are False. That paper caused quite a stir. It’s a serious allegation. In fairness, the title was a bit misleading. Ioannidis wasn’t talking about all science. But it has become apparent that an alarming number of published works in some fields can’t be reproduced by others. The worst offenders seem to be clinical trials, experimental psychology and neuroscience, some parts of cancer research and some attempts to associate genes with disease (genomewide association studies). Of course the selfcorrecting nature of science means that the false discoveries get revealed as such in the end, but it would obviously be a lot better if false results weren’t published in the first place.
How can tests of significance be so misleading?
Tests of statistical significance have been around for well over 100 years now. One of the most widely used is Student’s t test. It was published in 1908. ‘Student’ was the pseudonym for William Sealy Gosset, who worked at the Guinness brewery in Dublin. He visited Karl Pearson’s statistics department at UCL because he wanted statistical methods that were valid for testing small samples. The example that he used in his paper was based on data from Arthur Cushny, the first holder of the chair of pharmacology at UCL (subsequently named the A.J. Clark chair, after its second holder)
The outcome of a significance test is a probability, referred to as a P value. First, let’s be clear what the P value means. It will be simpler to do that in the context of a particular example. Suppose we wish to know whether treatment A is better (or worse) than treatment B (A might be a new drug, and B a placebo). We’d take a group of people and allocate each person to take either A or B and the choice would be random. Each person would have an equal chance of getting A or B. We’d observe the responses and then take the average (mean) response for those who had received A and the average for those who had received B. If the treatment (A) was no better than placebo (B), the difference between means should be zero on average. But the variability of the responses means that the observed difference will never be exactly zero. So how big does it have to be before you discount the possibility that random chance is all you were seeing. You do the test and get a P value. Given the ubiquity of P values in scientific papers, it’s surprisingly rare for people to be able to give an accurate definition. Here it is.
The P value is the probability that you would find a difference as big as that observed, or a still bigger value, if in fact A and B were identical.

If this probability is low enough, the conclusion would be that it’s unlikely that the observed difference (or a still bigger one) would have occurred if A and B were identical, so we conclude that they are not identical, i.e. that there is a genuine difference between treatment and placebo.
This is the classical way to avoid making a fool of yourself by claiming to have made a discovery when you haven’t. It was developed and popularised by the greatest statistician of the 20th century, Ronald Fisher, during the 1920s and 1930s. It does exactly what it says on the tin. It sounds entirely plausible.
What could possibly go wrong?
Another way to look at significance tests
One way to look at the problem is to notice that the classical approach considers only what would happen if there were no real effect or, as a statistician would put it, what would happen if the null hypothesis were true. But there isn’t much point in knowing that an event is unlikely when the null hypothesis is true unless you know how likely it is when there is a real effect.
We can look at the problem a bit more realistically by means of a tree diagram, very like that used to analyse screening tests, in the previous post.
In order to do this, we need to specify a couple more things.
First we need to specify the power of the significance test. This is the probability that we’ll detect a difference when there really is one. By ‘detect a difference’ we mean that the test comes out with P < 0.05 (or whatever level we set). So it’s analogous with the sensitivity of a screening test. In order to calculate sample sizes, it’s common to set the power to 0.8 (obviously 0.99 would be better, but that would often require impracticably large samples).
The second thing that we need to specify is a bit trickier, the proportion of tests that we do in which there is a real difference. This is analogous to the prevalence of the disease in the population being tested in the screening example. There is nothing mysterious about it. It’s an ordinary probability that can be thought of as a longterm frequency. But it is a probability that’s much harder to get a value for than the prevalence of a disease.
If we were testing a series of 30C homeopathic pills, all of the pills, regardless of what it says on the label, would be identical with the placebo controls so the prevalence of genuine effects, call it P(real), would be zero. So every positive test would be a false positive: the false discovery rate would be 100%. But in real science we want to predict the false discovery rate in less extreme cases.
Suppose, for example, that we test a large number of candidate drugs. Life being what it is, most of them will be inactive, but some will have a genuine effect. In this example we’d be lucky if 10% had a real effect, i.e. were really more effective than the inactive controls. So in this case we’d set the prevalence to P(real) = 0.1.
We can now construct a tree diagram exactly as we did for screening tests.
Suppose that we do 1000 tests. In 90% of them (900 tests) there is no real effect: the null hypothesis is true. If we use P = 0.05 as a criterion for significance then, according to the classical theory, 5% of them (45 tests) will give false positives, as shown in the lower limb of the tree diagram. If the power of the test was 0.8 then we’ll detect 80% of the real differences so there will be 80 correct positive tests.
The total number of positive tests is 45 + 80 = 125, and the proportion of these that are false positives is 45/125 = 36 percent. Our false discovery rate is far bigger than the 5% that many people still believe they are attaining.
In contrast, 98% of negative tests are right (though this is less surprising because 90% of experiments really have no effect).
The equation
You can skip this section without losing much.
As in the case of screening tests, this result can be calculated from an equation. The same equation works if we substitute power for sensitivity, P(real) for prevalence, and siglev for (1 – specificity) where siglev is the cut off value for "significance", 0.05 in our examples.
The false discovery rate (the probability that, if a “signifcant” result is found, there is actually no real effect) is given by
\[FDR = \frac{siglev\left(1P(real)\right)}{power.P(real) + siglev\left(1P(real)\right) }\; \]
In the example above, power = 0.8, siglev = 0.05 and P(real) = 0.1, so the false discovery rate is
\[\frac{0.05 (10.1)}{0.8 \times 0.1 + 0.05 (10.1) }\; = 0.36 \]
So 36% of “significant” results are wrong, as found in the tree diagram.
Some subtleties
The argument just presented should be quite enough to convince you that significance testing, as commonly practised, will lead to disastrous numbers of false positives. But the basis of how to make inferences is still a matter that’s the subject of intense controversy among statisticians, so what is an experimenter to do?
It is difficult to give a consensus of informed opinion because, although there is much informed opinion, there is rather little consensus. A personal view follows. Colquhoun (1970), Lectures on Biostatistics, pp 9495.
This is almost as true now as it was when I wrote it in the late 1960s, but there are some areas of broad agreement.
There are two subtleties that cause the approach outlined above to be a bit contentious. The first lies in the problem of deciding the prevalence, P(real). You may have noticed that if the frequency of real effects were 50% rather than 10%, the approach shown in the diagram would give a false discovery rate of only 6%, little different from the 5% that’s embedded in the consciousness of most experimentalists.
But this doesn’t get us off the hook, for two reasons. For a start, there is no reason at all to think that there will be a real effect there in half of the tests that we do. Of course if P(real) were even bigger than 0.5, the false discovery rate would fall to zero, because when P(real) = 1, all effects are real and therefore all positive tests are correct.
There is also a more subtle point. If we are trying to interpret the result of a single test that comes out with a P value of, say, P = 0.047, then we should not be looking at all significant results (those with P < 0.05), but only at those tests that come out with P = 0.047. This can be done quite easily by simulating a long series of t tests, and then restricting attention to those that come out with P values between, say, 0.045 and 0.05. When this is done we find that the false discovery rate is at least 26%. That’s for the best possible case where the sample size is good (power of the test is 0.8) and the prevalence of real effects is 0.5. When, as in the tree diagram, the prevalence of real effects is 0.1, the false discovery rate is 76%. That’s enough to justify Ioannidis’ statement that most published results are wrong.
One problem with all of the approaches mentioned above was the need to guess at the prevalence of real effects (that’s what a Bayesian would call the prior probability). James Berger and colleagues (Sellke et al., 2001) have proposed a way round this problem by looking at all possible prior distributions and so coming up with a minimum false discovery rate that holds universally. The conclusions are much the same as before. If you claim to have found an effects whenever you observe a P value just less than 0.05, you will come to the wrong conclusion in at least 29% of the tests that you do. If, on the other hand, you use P = 0.001, you’ll be wrong in only 1.8% of cases. Valen Johnson (2013) has reached similar conclusions by a related argument.
A threesigma rule
As an alternative to insisting on P < 0.001 before claiming you’ve discovered something, you could use a 3sigma rule. In other words, insist that an effect is at least three standard deviations away from the control value (as opposed to the two standard deviations that correspond to P = 0.05).
The three sigma rule means using P= 0.0027 as your cut off. This, according to Berger’s rule, implies a false discovery rate of (at least) 4.5%, not far from the value that many people mistakenly think is achieved by using P = 0.05 as a criterion.
Particle physicists go a lot further than this. They use a 5sigma rule before announcing a new discovery. That corresponds to a P value of less than one in a million (0.57 x 10^{−6}). According to Berger’s rule this corresponds to a false discovery rate of (at least) around 20 per million. Of course their experiments can’t be randomised usually, so it’s as well to be on the safe side.
Underpowered experiments
All of the problems discussed so far concern the nearideal case. They assume that your sample size is big enough (power about 0.8 say) and that all of the assumptions made in the test are true, that there is no bias or cheating and that no negative results are suppressed. The reallife problems can only be worse. One way in which it is often worse is that sample sizes are too small, so the statistical power of the tests is low.
The problem of underpowered experiments has been known since 1962, but it has been ignored. Recently it has come back into prominence, thanks in large part to John Ioannidis and the crisis of reproducibility in some areas of science. Button et al. (2013) said
“We optimistically estimate the median statistical power of studies in the neuroscience field to be between about 8% and about 31%”
This is disastrously low. Running simulated t tests shows that with a power of 0.2, not only do you have only a 20% chance of detecting a real effect, but that when you do manage to get a "significant" result there is a 76% chance that it’s a false discovery.
And furthermore, when you do find a "significant" result, the size of the effect will be overestimated by a factor of nearly 2. This "inflation effect" happens because only those experiments that happen, by chance, to have a largerthanaverage effect size will be deemed to be "significant".
What should you do to prevent making a fool of yourself?
The simulated t test results, and some other subtleties, will be described in a paper, and/or in a future post. But I hope that enough has been said here to convince you that there are real problems in the sort of statistical tests that are universal in the literature.
The blame for the crisis in reproducibility has several sources.
One of them is the selfimposed publishorperish culture, which values quantity over quality, and which has done enormous harm to science.
The misassessment of individuals by silly bibliometric methods has contributed to this harm. Of all the proposed methods, altmetrics is demonstrably the most idiotic. Yet some vicechancellors have failed to understand that.
Another is scientists’ own vanity, which leads to the PR department issuing disgracefully hyped up press releases.
In some cases, the abstract of a paper states that a discovery has been made when the data say the opposite. This sort of spin is common in the quack world. Yet referees and editors get taken in by the ruse (e.g see this study of acupuncture).
The reluctance of many journals (and many authors) to publish negative results biases the whole literature in favour of positive results. This is so disastrous in clinical work that a pressure group has been started; altrials.net "All Trials Registered  All Results Reported".
Yet another problem is that it has become very hard to get grants without putting your name on publications to which you have made little contribution. This leads to exploitation of young scientists by older ones (who fail to set a good example). Peter Lawrence has set out the problems.
And, most pertinent to this post, a widespread failure to understand properly what a significance test means must contribute to the problem. Young scientists are under such intense pressure to publish, they have no time to learn about statistics.
Here are some things that can be done.
 Notice that all statistical tests of significance assume that the treatments have been allocated at random. This means that application of significance tests to observational data, e.g. epidemiological surveys of diet and health, is not valid. You can’t expect to get the right answer. The easiest way to understand this assumption is to think about randomisation tests (which should have replaced t tests decades ago, but which are still rare). There is a simple introduction in Lectures on Biostatistics (chapters 8 and 9). There are other assumptions too, about the distribution of observations, independence of measurements), but randomisation is the most important.
 Never, ever, use the word "significant" in a paper. It is arbitrary, and, as we have seen, deeply misleading. Still less should you use "almost significant", "tendency to significant" or any of the hundreds of similar circumlocutions listed by Matthew Hankins on his Still not Significant blog.
 If you do a significance test, just state the P value and give the effect size and confidence intervals (but be aware that this is just another way of expressing the P value approach: it tells you nothing whatsoever about the false discovery rate).
 Observation of a P value close to 0.05 means nothing more than ‘worth another look’. In practice, one’s attitude will depend on weighing the losses that ensue if you miss a real effect against the loss to your reputation if you claim falsely to have made a discovery.
 If you want to avoid making a fool of yourself most of the time, don’t regard anything bigger than P < 0.001 as a demonstration that you’ve discovered something. Or, slightly less stringently, use a threesigma rule.
Despite the gigantic contributions that Ronald Fisher made to statistics, his work has been widely misinterpreted. We must, however reluctantly, concede that there is some truth in the comment made by an astute journalist:
"The plain fact is that 70 years ago Ronald Fisher gave scientists a mathematical machine for turning baloney into breakthroughs, and °flukes into funding. It is time to pull the plug". Robert Matthews Sunday Telegraph, 13 September 1998.
There is now a video on Youtube that attempts to explain explain simply the essential ideas.
Followup
31 March 2014 I liked Stephen Senn’s first comment on twitter (the twitter stream is storified here). He said " I may have to write a paper ‘You may believe you are NOT a Bayesian but you’re wrong’". I maintain that the analysis here is merely an exercise in conditional probabilities. It bears a formal similarity to a Bayesian argument, but is free of more contentious parts of the Bayesian approach. This is amplified in a comment, below.
4 April 2014
I just noticed that my first boss, Heinz Otto Schild.in his 1942 paper about the statistical analysis of 2+2 dose biological assays (written while he was interned at the beginning of the war) chose to use 99% confidence limits, rather than the now universal 95% limits. The later are more flattering to your results, but Schild was more concerned with precision than selfpromotion.