“If you torture the data long enough, it will confess.”
Given the recent discussion on optional stopping and Bayes, I wanted to solicit opinions on the following thought experiment.Researcher A collects tap water samples in a city, tests them for lead, and stops collecting data once a t-test comparing the mean lead level to a “safe” level is significant at p <.05. After this optional stopping, researcher A computes a Bayesian posterior (with weakly informative prior), and reports the median of the posterior as the best estimate of the lead level in the city.Researcher B collects the same amount of water samples but with a pre-specified N, and then also computes a Bayesian estimate.Researcher C collects water samples from every single household in the city (effectively collecting the whole population).Hopefully we can all agree that the best estimate of the mean lead level in the city is obtained by researcher C. But do you think that the estimate of researcher B is closer to the one from researcher C and should be preferred over the estimate of researcher A? What – if anything – does this tell us about optional stopping and its influence on Bayesian estimates?
Let’s simulate the scenario (R code provided below) with the following settings:
Here are the compute mean levels in our 8 combinations (true value = 3):
|Sampling plan||PubBias||Naive mean||Weighted mean|
Concerning the sequential procedures described here, some authors have raised concerns that these procedures result in biased effect size estimates (e.g., Bassler et al., 2010, J. Kruschke, 2014). We believe these concerns are overstated, for at least two reasons.First, it is true that studies that terminate early at the H1 boundary will, on average, overestimate the true effect. This conditional bias, however, is balanced by late terminations, which will, on average, underestimate the true effect. Early terminations have a smaller sample size than late terminations, and consequently receive less weight in a meta-analysis. When all studies (i.e., early and late terminations) are considered together, the bias is negligible (Berry, Bradley, & Connor, 2010; Fan, DeMets, & Lan, 2004; Goodman, 2007; Schönbrodt et al., 2015). Hence, the sequential procedure is approximately unbiased overall.Second, the conditional bias of early terminations is conceptually equivalent to the bias that results when only significant studies are reported and non-significant studies disappear into the file drawer (Goodman, 2007). In all experimental designs –whether sequential, non-sequential, frequentist, or Bayesian– the average effect size inevitably increases when one selectively averages studies that show a larger-than-average effect size. Selective publishing is a concern across the board, and an unbiased research synthesis requires that one considers significant and non-significant results, as well as early and late terminations.Although sequential designs have negligible unconditional bias, it may nevertheless be desirable to provide a principled “correction” for the conditional bias at early terminations, in particular when the effect size of a single study is evaluated. For this purpose, Goodman (2007) outlines a Bayesian approach that uses prior expectations about plausible effect sizes. This approach shrinks extreme estimates from early terminations towards more plausible regions. Smaller sample sizes are naturally more sensitive to prior-induced shrinkage, and hence the proposed correction fits the fact that most extreme deviations from the true value are found in very early terminations that have a small sample size (Schönbrodt et al., 2015).
If the p-value is < .05, then the probability of falsely rejecting the null hypothesis is <5%, right? That means, a maximum of 5% of all significant results is a false-positive (that’s what we control with the α rate).
Well, no. As you will see in a minute, the “false discovery rate” (aka. false-positive rate), which indicates the probability that a significant p-value actually is a false-positive, usually is much higher than 5%.
Oakes (1986) asked the following question to students and senior scientists:
You have a p-value of .01. Is the following statement true, or false?
You know, if you decide to reject the null hypothesis, the probability that you are making the wrong decision.
The answer is “false” (you will learn why it’s false below). But 86% of all professors and lecturers in the sample who were teaching statistics (!) answered this question erroneously with “true”. Gigerenzer, Kraus, and Vitouch replicated this result in 2000 in a German sample (here, the “statistics lecturer” category had 73% wrong). Hence, it is a wide-spread error to confuse the p-value with the false discovery rate.
To answer the question “What’s the probability that a significant p-value indicates a true effect?”, we have to look at the positive predictive value (PPV) of a significant p-value. The PPV indicates the proportion of significant p-values which indicate a real effect amongst all significant p-values. Put in other words: Given that a p-value is significant: What is the probability (in a frequentist sense) that it stems from a real effect?
(The false discovery rate simply is 1-PPV: the probability that a significant p-value stems from a population with null effect).
That is, we are interested in a conditional probability Prob(effect is real | p-value is significant).
Inspired by Colquhoun (2014) one can visualize this conditional probability in the form of a tree-diagram (see below). Let’s assume, we carry out 1000 experiments for 1000 different research questions. We now have to make a couple of prior assumptions (which you can make differently in the app we provide below). For now, we assume that 30% of all studies have a real effect and the statistical test used has a power of 35% with an α level set to 5%. That is of the 1000 experiments, 300 investigate a real effect, and 700 a null effect. Of the 300 true effects, 0.35*300 = 105 are detected, the remaining 195 effects are non-significant false-negatives. On the other branch of 700 null effects, 0.05*700 = 35 p-values are significant by chance (false positives) and 665 are non-significant (true negatives).
This path is visualized here (completely inspired by Colquhoun, 2014):
Now we can compute the false discovery rate (FDR): 35 of (35+105) = 140 significant p-values actually come from a null effect. That means, 35/140 = 25% of all significant p-values do not indicate a real effect! That is much more than the alleged 5% level (see also Lakens & Evers, 2014, and Ioannidis, 2005)
Together with Michael Zehetleitner I developed an interactive app that computes and visualizes these numbers. For the computations, you have to choose 4 parameters.
Let’s go through the settings!
Now, what is a good setting for the a priori proportion of true hypotheses? It’s certainly not near 100% – in this case only trivial and obvious research questions would be investigated, which is obviously not the case. On the other hand, the rate can definitely drop close to zero. For example, in pharmaceutical drug development “only one in every 5,000 compounds that makes it through lead development to the stage of pre-clinical development becomes an approved drug” (Wikipedia). Here, only 0.02% of all investigated hypotheses are true.
Furthermore, the number depends on the field – some fields are highly speculative and risky (i.e., they have a low prior probability), some fields are more cumulative and work mostly on variations of established effects (i.e., in these fields a higher prior probability can be expected).
But given that many journals in psychology exert a selection pressure towards novel, surprising, and counter-intuitive results (which a priori have a low probability of being true), I guess that the proportion is typically lower than 50%. My personal grand average gut estimate is around 25%.
That’s easy. The default α level usually is 5%, but you can play with the impact of stricter levels on the FDR!
The average power in psychology has been estimated at 35% (Bakker, van Dijk, & Wicherts, 2012). An median estimate for neuroscience is at only 21% (Button et al., 2013). Even worse, both estimates can be expected to be inflated, as they are based on the average published effect size, which almost certainly is overestimated due to the significance filter (Ioannidis, 2008). Hence, the average true power is most likely smaller. Let’s assume an estimate of 25%.
Finally, let’s add some realism to the computations. We know that researchers employ “researchers degrees of freedom”, aka. questionable research practices, to optimize their p-value, and to push a “nearly significant result” across the magic boundary. How many reported significant p-values would not have been significant without p-hacking? That is hard to tell, and probably also field dependent. Let’s assume that 15% of all studies are p-hacked, intentionally or unintentionally.
When these values are defined, the app computes the FDR and PPV and shows a visualization:
With these settings, only 39% of all significant studies are actually true!
Wait – what was the success rate of the Reproducibility Project: Psychology? 36% of replication projects found a significant effect in a direct replication attempt. Just a coincidence? Maybe. Maybe not.
The formula to compute the FDR and PPV are based on Ioannidis (2005: “Why most published research findings are false“). A related, but different approach, was proposed by David Colquhoun in his paper “An investigation of the false discovery rate and the misinterpretation of p-values” [open access]. He asks: “How should one interpret the observation of, say, p=0.047 in a single experiment?”. The Ioannidis approach implemented in the app, in contrast, asks: “What is the FDR in a set of studies with p <= .05 and a certain power, etc.?”. Both approaches make sense, but answer different questions.