We are delighted that our Analysis article (Power failure: why small sample size undermines the reliability of neuroscience. Nature Rev. Neurosci. 14, 365–376 (2013))1 has stimulated debate about the issues arising from low statistical power in neuroscience studies. Here, we take the opportunity to respond to some important points made by Quinlan (Misuse of power: in defence of small-scale science. Nature Rev. Neurosci. http://dx.doi.org/10.1038/nrn3475-c1 (2013))2, Ashton (Experimental power comes from powerful theories — the real problem in null hypothesis testing. Nature Rev. Neurosci. http://dx.doi.org/10.1038/nrn3475-c2 (2013))3 and Bacchetti (Small sample size is not the real problem. Nature Rev. Neurosci. http://dx.doi.org/10.1038/nrn3475-c3 (2013))4, and clarify our position on certain key issues raised in our original article1.
Quinlan2 draws a comparison between our observations and those made by Friston in his recent article5. However, we note that subsequent commentaries by Ingre6 and by Lindquist and colleagues7 echo many of the concerns that we raised and that Friston8 agreed that he was “convinced by most of their observations”. The main concern — originally raised by Friston5 and reiterated by Quinlan2 — is that high-powered studies will generate formally statistically significant differences for a 'trivial' effect. There are three important rejoinders to this concern. First, in studies with low statistical power, an observed effect will necessarily be large if it is to pass a pre-specified p-value threshold (typically 0.05), but this does not mean that the true effect will be large, or even exist at all. Second, the concern only applies if a p-value threshold (that is, typically 0.05) is used to either reject or (implicitly) accept the null hypothesis. As Ingre notes6, larger studies actually protect against inferences from trivial effect sizes by allowing a better estimation of the magnitude of the true effect. A shift in emphasis away from significance testing towards the use of effect sizes and confidence intervals would therefore improve matters — this is a point we return to below. Third, the true effect size is not known in advance; what is considered 'trivial' can only be determined when the effect size is known. For example, candidate gene studies are frequently quite small N studies, with the implicit assumption that common genetic variants will be associated with reasonably large effects. Over a decade of relatively fruitless research showed that this assumption is not correct; the magnitude of these effects turns out to be much smaller9, as has been borne out by more recent genome-wide association studies (GWASs), which are explicitly designed to be able to detect very small effects. Have these smaller effects turned out to be trivial? Not at all — in many cases, the genes that have been identified using well-powered GWAS methods have led to renewed interest in the role of the pathways implicated and have thereby generated genuinely new insights into disease mechanisms10. Moreover, learning that the effect sizes of common genetic variants on complex traits are very small has provided important fundamental insights into the genetic architecture of these traits11. Therefore, high power provides greater precision in the estimation of the actual effect size so that researchers can assess their importance or triviality with confidence.
Ashton3 makes the important point that specification in advance of the effect size being sought is rare, which precludes the use of a priori power analysis. He argues that we should be more “specific about the theoretical predictions that our experiments are designed to test”, which should include a prediction regarding the magnitude of the expected effect. This is related to our suggestion of placing greater emphasis on effect size and confidence intervals than on significance testing. Unfortunately, the use of significance testing in the absence of any mention of effect size, confidence intervals or prospective power remains the norm12. Some may argue that effect size is not relevant to the theoretical models they wish to test. That may be true if the models are imprecise about effect sizes. However, even in that case, data from low-powered studies are not useful for testing a theoretical model because they provide little opportunity to find conclusive evidence for or against a model and therefore provide limited scope for model refinement.
Bacchetti4 argues that if one could take care of all the associated biases that have been empirically documented to be far more prevalent in very small studies than in larger studies, then small studies (or even very small studies) would be unproblematic. We agree that it would be wonderful if small studies and their research environment were devoid of biases and if all small studies on a particular question of interest could be perfectly integrated. However, this has not happened; to achieve this would require a major restructuring of the incentives for publishing papers, and especially for publishing novel and positive findings13. Although we applaud efforts to reduce biases, we believe that some larger, more definitive studies are also needed to address the problems we describe in our original article. For example, the 'winner's curse' will remain a problem for small studies even if all biases are eliminated. We sympathize with the view that studies may not need to be enormous and that studies with modest (but not very small) sample sizes may occasionally have some advantages over studies with large sample sizes14. Also, in some cases (for example, when a disease is rare or when sample size is unavoidably constrained), small studies may be the best we can achieve, and the optimal design might include choices for type I and type II errors that do not necessarily correspond to the conventional 80% power at an α-level of 5%15. Moreover, we agree that inordinately large sample sizes can sometimes have high cost/yield ratios. Some fields within biomedicine that work with huge datasets with many thousands or even millions of participants and data points are currently experiencing this challenge. However, as we showed in our Analysis article, most neuroscience research is currently on the other end of this scale, with small, underpowered studies dominating. Finally, we do not advocate making decisions and interpreting results as a dichotomous 'success' or 'failure' on the basis of an absolute p = 0.05 threshold. However, this is the norm in much current scientific practice, and our Analysis article explored the implications of combining this approach with small N studies. Simply changing to another p-value threshold does not solve the problem.
What constitutes an appropriate sample size will depend on the magnitude of the effect being sought. In some cases, a small sample will suffice. However, our Analysis article suggests that these are the exception rather than the rule. It is therefore prudent to assume that the average sample size should increase. Incorporating advance specification of the magnitude of the effect being sought into our theoretical models and analysis plans, and reporting effect sizes and confidence intervals alongside exact p values (rather than p = NS or p < 0.05) would also improve the strength of scientific inference.
Button, K. S. et al. Power failure: why small sample size undermines the reliability of neuroscience. Nature Rev. Neurosci. 14, 365–376 (2013).
Quinlan, P. T. Misuse of power: in defence of small-scale science. Nature Rev. Neurosci. http://dx.doi.org/10.1038/nrn3475-c1 (2013).
Ashton, J. C. Experimental power comes from powerful theories — the real problem in null hypothesis testing. Nature Rev. Neurosci. http://dx.doi.org/10.1038/nrn3475-c2 (2013).
Bacchetti, P. Small sample size is not the real problem. Nature Rev. Neurosci. http://dx.doi.org/10.1038/nrn3475-c3 (2013).
Friston, K. Ten ironic rules for non-statistical reviewers. Neuroimage 61, 1300–1310 (2012).
Ingre, M. Why small low-powered studies are worse than large high-powered studies and how to protect against “trivial” findings in research: Comment on Friston (2012). Neuroimage http://dx.doi.org/10.1016/j.neuroimage.2013.03.030 (2013).
Lindquist, M. A., Caffo, B. & Crainiceanu, C. Ironing out the statistical wrinkles in “ten ironic rules”. Neuroimage http://dx.doi.org/10.1016/j.neuroimage.2013.02.056 (2013).
Friston, K. Sample size and the fallacies of classical inference. Neuroimage http://dx.doi.org/10.1016/j.neuroimage.2013.02.057 (2013).
Flint, J. & Munafò, M. R. Candidate and non-candidate genes in behavior genetics. Curr. Opin. Neurobiol. 23, 57–61 (2013).
Fowler, C. D., Lu, Q., Johnson, P. M., Marks, M. J. & Kenny, P. J. Habenular α5 nicotinic receptor subunit signalling controls nicotine intake. Nature 471, 597–601 (2011).
Munafò, M. R. & Flint, J. Dissecting the genetic architecture of human personality. Trends Cogn. Sci. 15, 395–400 (2011).
Tressoldi, P. E., Giofre, D., Sella, F. & Cumming, G. High impact = high statistical standards? Not necessarily so. PLoS ONE 8, e56180 (2013).
Nosek, B. A., Spies, J. R. & Motyl, M. Scientific Utopia: II. Restructuring incentives and practices to promote truth over publishability. Persp. Psychol. Sci. 7, 615–631 (2012).
Inthout, J., Ioannidis, J. P. & Borm, G. F. Obtaining evidence by a single well-powered trial or several modestly powered trials. Stat. Methods Med. Res. http://dx.doi.org/10.1177/0962280212461098 (2012).
Ioannidis, J. P., Hozo, I. & Djulbegovic, B. Optimal type I and type II error pairs when the available sample size is fixed. J. Clin. Epidemiol. http://dx.doi.org/10.1016/j.jclinepi.2013.03.002 (2013).
The authors declare no competing financial interests.
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Button, K., Ioannidis, J., Mokrysz, C. et al. Confidence and precision increase with high statistical power. Nat Rev Neurosci 14, 585 (2013). https://doi.org/10.1038/nrn3475-c4
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