In July, Laborjournal (‘LabTimes’), a free German monthly for life scientists (sort of a hybrid between the Economist and the British Tabloid The Sun), celebrated its 20th anniversary with a special issue. I was asked to contribute an article. In it I try to answer the question whether most published research findings are false, as John Ioannidis rhetorically asked in 2005.
To find out, you have to be able to read German, and click here for a pdf of the article (in German).
“Five sigma,” is the gold standard for statistical significance in physics for particle discovery. When the New Scientist reported about the putative confirmation of the Higgs boson, they wrote:
‘Five-sigma corresponds to a p-value, or probability, of 3×10-7, or about 1 in 3.5 million. There’s a 5-in-10 million chance that the Higgs is a fluke.’
Does that mean that p-values can tell us the probability of being correct about our hypotheses? Can we use p-values to decide about the truth (correctness) of hypotheses? Does p<0.05 mean that there is a smaller than 5 % chance that an experimental hypothesis is wrong?
Statistical power is a rare commodity in experimental biomedicine (see previous post), as most studies have very low n’s and are therefore severly underpowered. The concept of statistical power, although almost embarrassingly simple (for a very nice treatment see Button et al.), is shrouded in ignorance, mysteries and misunderstandings among many researchers. A simple definition states that Power is the probability that, given a specified true difference between two groups, the quantitative results of a study will be deemed statistically significant. The most common misunderstanding may be that power should only be a concern to the researcher if the Null hypothesis could not rejected (p>0.05). I need to deal with this dangerous fallacy in a future post. Another common albeit less perilous misunderstanding is that calculating post-hoc (or ‘retrospective )’ power can explain why an analysis did not achieve significance. Besides proving a severe bias of the researcher towards rejecting the Null hypothesis (‘There must be another reason for not obtaining a significant result than that the hypothesis is incorrect!), this is the equivalent of a statistical tautology. Of course the study was not powerful enough, this is why the result was not significant! To look at this from another standpoint: Provided enough n’s, the Null of every study must be reject. This by the way, is one of the most basic criticisms of Null hypothesis significance testing. Power calculations are useful for the design of studies, but not for their analysis. This was nicely explained by Steven Goodman in his classic article ‘Goodman The use of predicted confidence intervals when planning experiments and the misuse of power when interpreting results Ann IntMed 1994‘:
First, [post-hoc Power analysis] will always show that there is low power (< 50%) with respect to a nonsignificant difference, making tautological and uninformative the claim that a study is “underpowered” with respect to an observed nonsignificant result. Second, its rationale has an Alice-in-Wonderland feel, and any attempt to sort it out is guaranteed to confuse. The conundrum is the result of a direct collision between the incompatible pretrial and post-trial perspectives. […] Knowledge of the observed difference naturally shifts our perspective toward estimating differences, rather than deciding between them, and makes equal treatment of all nonsignificant results impossible. Once the data are in, the only way to avoid confusion is to not compress results into dichotomous significance verdicts and to avoid post hoc power estimates entirely.
NB: To avoid misunderstandings: Calculating the n’s needed in future experiments to achieve a certain statistical power based on effect sizes and variance obtained post – hoc from a (pilot) experiment is not called post-hoc power analysis (and the subject of this post), but rather sample size calculation.
For further reading:
I just stumbled into a very instructive example which illustrates that p-values should not be misinterpreted as measures of the probablity with which a research hypothesis is true. In 2011 the OPERA collaboration reported evidence that neutrinos travel faster than light, a finding which violates Einstein’s theory of relativity and if true would have shattered physics as we know it! Their analysis was significant at the 6 sigma level, even more stringent than the accepted but already brutal 5 sigma level of particle discovery (p=3.5 x 10-7). Extraordinary claims require extraordinary evidence ! The results were replicated by the same group, published, and hailed by the world scientific and lay press. A short while later it turned out that the GPS systems were not properly synchronized, and a cable was loose. Neutrinos are back at the speed of light, and we can learn from this that p-values are ignorant of simple systematic errors!
Discrepancies in the publication of clinical trials of bone marrow stem cell therapy in cardiology scale linearly with effect size! This is the shocking but not so surprising result of a study in BMJ that found over 600 discrepancies in 133 reports from 49 trials. Trials without discrepancies (only 5!) reported neutral results (i.e. no effect of therapy on enhancement of ejection fraction). The most spectacular treatment effects were found in those trials with the highest number of discrepancies (30 and more).
In the current issue of PLOS Biology Kimmelman, Mogil, and Dirnagl argue that distinguishing between exploratory and confirmatory preclinical research will improve translation: ‘Preclinical researchers confront two overarching agendas related to drug development: selecting interventions amid a vast field of candidates, and producing rigorous evidence of clinical promise for a small number of interventions. They suggest that each challenge is best met by two different, complementary modes of investigation. In the first (exploratory investigation), researchers should aim at generating robust pathophysiological theories of disease. In the second (confirmatory investigation), researchers should aim at demonstrating strong and reproducible treatment effects in relevant animal models. Each mode entails different study designs, confronts different validity threats, and supports different kinds of inferences. Research policies should seek to disentangle the two modes and leverage their complementarity. In particular, policies should discourage the common use of exploratory studies to support confirmatory inferences, promote a greater volume of confirmatory investigation, and customize design and reporting guidelines for each mode.’
Still not convinced that US spending on science, space, and technology correlates with suicides by hanging, strangulation and suffocation? Or that the number of people who drowned by falling into a swimming-pool highly correlates with the number of films Nicolas Cage appeared in? Check Spurious Correlations, a website that teaches you to understand the difference between correlation and causation!
Research on animals generally lacks transparent reporting of study design and implementation, as well as results. As a consequene of poor reporting, we are facing problems in replicating published findings, publication of underpowered studies and excessive false positives or false negatives, publication bias, and as a result difficulties in translating promising preclinical results into effective therapies for human disease. To improve the situation, in 2010 the ARRIVE guidelines for the reporting of animal research (www.nc3rs.org.uk/ARRIVEpdf) were formulated, which were adopted by over 300 scientifc journals, including the Journal of Cerebral Blood Flow and Metabolism (www.nature.com/jcbfm). Four years after, Baker et al. ( PLoS Biol 12(1): e1001756. doi:10.1371/journal.pbio.1001756) have systematically investigated the effect of the implementation of the ARRIVE guidelines on reporting of in vivo research, with a particular focus on the multiple sclerosis field. The results are highly disappointing:
‘86%–87% of experimental articles do not give any indication that the animals in the study were properly randomized, and 95% do not demonstrate that their study had a sample size sufficient to detect an effect of the treatment were there to be one. Moreover, they show that 13% of studies of rodents with experimental autoimmune encephalomyelitis (an animal model of multiple sclerosis) failed to report any statistical analyses at all, and 55% included inappropriate statistics.. And while you might expect that publications in ‘‘higher ranked’’ journals would have better reporting and a more rigorous methodology, Baker et al. reveal that higher ranked journals (with an impact factor greater than ten) are twice as likely to report either no or inappropriate statistics’ (Editorial by Eisen et al., PLoS Biol 12(1): e1001757. doi:10.1371/journal.pbio.1001757).
It is highly likely that other fields in biomedicine have a similar dismal record. Clearly, there is a need for journal editors and publishers to enforce the ARRIVE guidelines and to monitor its implementation!
Das Heft 3 des Laborjournals enthält einen sehr brauchbaren Artikel zur (nicht-) Reproduzierbarkeit von Ergebnissen. Sorry, in German only….
Due to small group sizes and presence of substantial bias experimental medicine produces a large number of false positive results (see previous post). It has been claimed that 50 – 90 % of all results may be false (see previous post). In support of these claims is the staggerlingly low number of experiments that can be replicated. But what are the chances to reproduce a finding that is actually true?