bang on about statistical power because it indirectly raises the odds of a false positive. In brief, it forces you to do more tests to reach a statistical conclusion, stuffing the file drawer and thus making published results appear more certain than they are. In detail, see John Borghi or Ioannidis (2005). In comic, see Maki Naro.

The concept of statistical power has been known since 1928, the wasteful consequences of low power since 1962, and yet there’s no sign that scientists are upping their power levels. This is a representative result:

Our results indicate that the average statistical power of studies in the field of neuroscience is probably no more than between ~8% and ~31%, on the basis of evidence from diverse subfields within neuro-science. If the low average power we observed across these studies is typical of the neuroscience literature as a whole, this has profound implications for the field. A major implication is that the likelihood that any nominally significant finding actually reflects a true effect is small.

Button, Katherine S., et al. “Power failure: why small sample size undermines the reliability of neuroscience.” Nature Reviews Neuroscience 14.5 (2013): 365-376.

The most obvious consequence of low power is a failure to replicate. If you rarely try to replicate studies, you’ll be blissfully unaware of the problem; once you take replications seriously, though, you’ll suddenly find yourself in a “replication crisis.”

You’d think this would result in calls for increased statistical power, with the occasional call for a switch in methodology to a system that automatically incorporates power. But it’s also led to calls for more replications.

As a condition of receiving their PhD from any accredited institution, graduate students in psychology should be required to conduct, write up, and submit for publication a high-quality replication attempt of at least one key finding from the literature, focusing on the area of their doctoral research.
Everett, Jim AC, and Brian D. Earp. “A tragedy of the (academic) commons: interpreting the replication crisis in psychology as a social dilemma for early-career researchers.” Frontiers in psychology 6 (2015).

Much has been made of preregistration, publication of null results, and Bayesian statistics as important changes to how we do business. But my view is that there is relatively little value in appending these modifications to a scientific practice that is still about one-off findings; and applying them mechanistically to a more careful, cumulative practice is likely to be more of a hindrance than a help. So what do we do? …

Cumulative study sets with internal replication.

If I had to advocate for a single change to practice, this would be it.

There’s an intuitive logic to this: currently less than one in a hundred papers are replications of prior work, so there’s plenty of room for expansion; many key figures like Ronald Fisher and Jerzy Neyman have emphasized the necessity of replications; and it doesn’t require any modification of technique; and the “replication crisis” is primarily about replications. It sounds like an easy, feel-good solution to the problem.

But then I read this paper:

Smaldino, Paul E., and Richard McElreath. “The Natural Selection of Bad Science.” arXiv preprint arXiv:1605.09511 (2016).

It starts off with a meta-analysis of meta-analyses of power, and comes to the same conclusion as above.

We collected all papers that contained reviews of statistical power from published papers in the social, behavioural and biological sciences, and found 19 studies from 16 papers published between 1992 and 2014. … We focus on the statistical power to detect small effects of the order d=0.2, the kind most commonly found in social science research. …. Statistical power is quite low, with a mean of only 0.24, meaning that tests will fail to detect small effects when present three times out of four. More importantly, statistical power shows no sign of increase over six decades …. The data are far from a complete picture of any given field or of the social and behavioural sciences more generally, but they help explain why false discoveries appear to be common. Indeed, our methods may overestimate statistical power because we draw only on published results, which were by necessity sufficiently powered to pass through peer review, usually by detecting a non-null effect.

Rather than leave it at that, though, the researchers decided to simulate the pursuit of science. They set up various “labs” that exerted different levels of effort to maintain methodological rigor, killed off labs that didn’t publish much and replaced them with mutations of labs that published more, and set the simulation spinning.

We ran simulations in which power was held constant but in which effort could evolve (μw=0, μe=0.01). Here selection favoured labs who put in less effort towards ensuring quality work, which increased publication rates at the cost of more false discoveries … . When the focus is on the production of novel results and negative findings are difficult to publish, institutional incentives for publication quantity select for the continued degradation of scientific practices.

That’s not surprising. But then they started tinkering with replication rates. To begin with, replications were done 1% of the time, were guaranteed to be published, and having one of your results fail to replicate would exact a terrible toll.

We found that the mean rate of replication evolved slowly but steadily to around 0.08. Replication was weakly selected for, because although publication of a replication was worth only half as much as publication of a novel result, it was also guaranteed to be published. On the other hand, allowing replication to evolve could not stave off the evolution of low effort, because low effort increased the false-positive rate to such high levels that novel hypotheses became more likely than not to yield positive results … . As such, increasing one’s replication rate became less lucrative than reducing effort and pursuing novel hypotheses.

So it was time for extreme measures: force the replication rate to high levels, to the point that 50% of all studies were replications. All that happened was that it took longer for the overall methodological effort to drop and false positives to bloom.

Replication is not sufficient to curb the natural selection of bad science because the top performing labs will always be those who are able to cut corners. Replication allows those labs with poor methods to be penalized, but unless all published studies are replicated several times (an ideal but implausible scenario), some labs will avoid being caught. In a system such as modern science, with finite career opportunities and high network connectivity, the marginal return for being in the top tier of publications may be orders of magnitude higher than an otherwise respectable publication record.

Replication isn’t enough. The field of science needs to incorporate more radical reforms that encourage high methodological rigor and greater power.