Cohen’s d is biased

The R notebook associated with this post is available on github.

Cohen’s d is a popular measure of effect size. In the one-sample case, d is simply computed as the mean divided by the standard deviation (SD). For repeated measures, the same formula is applied to difference scores (see detailed presentation and explanation of variants in Lakens, 2013). 

Because d relies on a non-robust measure of central tendency (the mean), and a non-robust measure of dispersion (SD), it is a non-robust measure of effect size, meaning that a single observation can have a dramatic effect on its value, as explained here. Cohen’s d also makes very strict assumptions about the data, so it is only appropriate in certain contexts. As a consequence, it should not be used as the default measure of effect size, and more powerful and informative alternatives should be considered – see a few examples here. For comparisons across studies and meta-analyses, nothing will beat data-sharing though.

Here we look at another limitation of Cohen’s d: it is biased when we draw small samples. Bias is covered in detail in another post. In short, in the one-sample case, when Cohen’s d is estimated from a small sample, in the long run it tends to be larger than the population value. This over-estimation is due to a bias of SD, which tends to be lower than the population’s SD. Because the mean is not biased, when divided by an under-estimated SD, it leads to an over-estimated measure of effect size. The bias of SD is explained in intro stat books, in the section describing Student’s t. Not surprisingly it is never mentioned in the discussions of small n studies, as a limitation of effect size estimation…

In this demonstration, we sample with replacement 10,000 times from the ex-Gaussian distributions below, for various sample sizes, as explained here:


The table below shows the population values for each distribution. For comparison, we also consider a robust equivalent to Cohen’s d, in which the mean is replaced by the median, and SD is replaced by the percentage bend mid-variance (pbvar, Wilcox, 2017). As we will see, this robust alternative is also biased – there is no magic solution I’m afraid.

m:          600  600  600  600  600  600  600  600  600  600  600  600

md:        509  512  524  528  540  544  555  562  572  579  588  594

m-md:    92    88     76    72    60    55     45    38    29    21    12     6

m.den:   301  304  251  255  201  206  151  158  102  112  54     71

md.den: 216  224  180  190  145  157  110  126  76    95    44     68       2.0   2.0    2.4   2.4   3.0   2.9   4.0   3.8   5.9   5.4   11.1  8.5     2.4   2.3    2.9   2.8   3.7   3.5   5.0   4.5   7.5   6.1   13.3  8.8

m = mean

md = median

den = denominator

es = effect size = Cohen’s d = md / pbvar


Let’s look at the behaviour of d as a function of skewness and sample size.


Effect size d tends to decrease with increasing skewness, because SD tends to increase with skewness. Effect size also increases with decreasing sample size. This bias is stronger for samples from the least skewed distributions. This is counterintuitive, because one would think estimation tends to get worse with increased skewness. Let’s find out what’s going on.

Computing the bias normalises the effect sizes across skewness levels, revealing large bias differences as a function of skewness. Even with 100 observations, the bias (mean of 10,000 simulation iterations) is still slightly larger than zero for the least skewed distributions. This bias is not due to the mean, because we the sample mean is an unbiased estimator of the population mean.


Let’s check to be sure:


So the problem must be with the denominator:


Unlike the mean, the denominator of Cohen’s d, SD, is biased. Let’s look at bias directly.


SD is most strongly biased for small sample sizes and bias increases with skewness. Negative values indicate that sample SD tends to under-estimate the population values. This is because the sampling distribution of SD is increasingly skewed with increasing skewness and decreasing sample sizes. This can be seen in this plot of the 80% highest density intervals (HDI) for instance:


The sampling distribution of SD is increasingly skewed and variable with increasing skewness and decreasing sample sizes. As a result, the sampling distribution of Cohen’s d is also skewed. The bias is strongest in absolute term for the least skewed distributions because the sample SD is overall smaller for these distributions, resulting in overall larger effect sizes. Although SD is most biased for the most skewed distributions, SD is also overall much larger for them, resulting in much smaller effect sizes than those obtained for less skewed distributions. This strong attenuation of effect sizes with increasing skewness swamps the absolute differences in SD bias. This explains the counter-intuitive lower d bias for more skewed distributions.

As we saw previously, bias can be corrected using a bootstrap approach. Applied, to Cohen’s d, this technique does reduce bias, but it still remains a concern:


Finally, let’s look at the behaviour of a robust equivalent to Cohen’s d, the median normalised by the percentage bend mid-variance.


The median effect size shows a similar profile to the mean effect size. It is overall larger than the mean effect size because it uses a robust measure of spread, which is less sensitive to the long right tails of the skewed distributions we sample from.


The bias disappears quickly with increasing sample sizes, and quicker than for the mean effect size.

However, unlike what we observed for d, in this case the bias correction does not work for small samples, because the repetition of the same observations in some bootstrap samples leads to very large values of the denominator. It’s ok for n>=15, for which bias is relatively small anyway, so at least based on these simulations, I wouldn’t use bias correction for this robust effect size.



Beware of small sample sizes: they are associated with increased variability (see discussion in a clinical context here) and can accentuate the bias of some effect size estimates. If effect sizes tend to be reported more often if they pass some arbitrary threshold, for instance p < 0.05, then the literature will tend to over-estimate them (see demonstration here), a phenomenon exacerbated by small sample sizes (Button et al. 2013). 

Can’t say it enough: small n is bad for science if the goal is to provide accurate estimates of effect sizes.

To determine how the precision and accuracy of your results depend on sample size, the best approach is to perform simulations, providing some assumptions about the shape of the population distributions.


Button, K.S., Ioannidis, J.P., Mokrysz, C., Nosek, B.A., Flint, J., Robinson, E.S. & Munafo, M.R. (2013) Power failure: why small sample size undermines the reliability of neuroscience. Nature reviews. Neuroscience, 14, 365-376.

Lakens, D. (2013) Calculating and reporting effect sizes to facilitate cumulative science: a practical primer for t-tests and ANOVAs. Front Psychol, 4, 863.

Wilcox, R.R. (2017) Introduction to Robust Estimation and Hypothesis Testing. Academic Press, 4th edition., San Diego, CA.


Reaction times and other skewed distributions: problems with the mean and the median (part 3/4)

Bias is defined as the distance between the mean of the sampling distribution (here estimated using Monte-Carlo simulations) and the population value. In part 1 and part 2, we saw that for small sample sizes, the sample median provides a biased estimation of the population median, which can significantly affect group comparisons. However, this bias disappears with large sample sizes, and it can be corrected using a bootstrap bias correction. In part 3, we look in more detail at the shape of the sampling distributions, which was ignored by Miller (1988).

Sampling distributions

Let’s consider the sampling distributions of the mean and the median for different sample sizes and ex-Gaussian distributions with skewness ranging from 6 to 92 (Figure 1). When skewness is limited (6, top row), the sampling distributions are symmetric and centred on the population values: there is no bias. As we saw previously, with increasing sample size, variability decreases, which is why studies with larger samples provide more accurate estimations. The flip side is that studies with small samples are much noisier, which is why their results tend not to replicate…


Figure 1

When skewness is large (92, middle row), sampling distributions get more positively skewed with decreasing sample sizes. To better understand how the sampling distributions change with sample size, we turn to the last row of Figure 1, which shows 50% highest-density intervals (HDI). Each horizontal line is a HDI for a particular sample size. The labels contain the values of the interval boundaries. The coloured vertical tick inside the interval marks the median of the distribution. The red vertical line spanning the entire plot is the population value.

Means For small sample sizes, the 50% HDI is offset to the left of the population mean, and so is the median of the sampling distribution. This demonstrates that the typical sample mean tends to under-estimate the population mean – that is to say, the mean sampling distribution is median biased. This offset reduces with increasing sample size, but is still present even for n=100.

Medians With small sample sizes, there is a discrepancy between the 50% HDI, which is shifted to the left of the population median, and the median of the sampling distribution, which is shifted to the right of the population median. This contrasts with the results for the mean, and can be explained by differences in the shapes of the sampling distributions, in particular the larger skewness and kurtosis of the median sampling distribution compared to that of the mean (see code on github for extra figures). The offset between 50% HDI and the population reduces quickly with increasing sample size. For n=10, the median bias is already very small. From n=15, the median sample distribution is not median bias, which means that the typical sample median is not biased.

Another representation of the sampling distributions is provided in Figure 2: 50% HDI are shown as a function of sample size. For both the mean and the median, bias increase with increasing skewness and decreasing sample size. Skewness also increases the asymmetry of the sampling distributions, but more for the mean than median.


Figure 2

So what’s going on here? Is the mean also biased?  According to the standard definition of bias, which is based on the distance between the population mean and the average of the sampling distribution of the mean, the mean is not biased. But this definition applies to the long run, after we replicate the same experiment many times. In practice, we never do that. So what happens in practice, when we perform only one experiment? In that case, the median of the sampling distribution provides a better description of the typical experiment than the mean of the distribution. And the median of the sample distribution of the mean is inferior to the population mean when sample size is small. So if you conduct one small n experiment and compute the mean of a skewed distribution, you’re likely to under-estimate the true value.

Is the median biased after all? The median is indeed biased according to the standard definition. However, with small n, the typical median (represented by the median of the sampling distribution of the median) is close to the population median, and the difference disappears for even relatively small sample sizes. 

Is it ok to use the median then?

If the goal is to accurately estimate the central tendency of a RT distribution, while protecting against the influence of outliers, the median is far more efficient than the mean (Wilcox & Rousselet, 2018). Providing sample sizes are large enough, bias is actually not a problem, and the typical bias is actually very small, as we’ve just seen. So, if you have to choose between the mean and the median, I would go for the median without hesitation.

It’s more complicated though. In an extensive series of simulations, Ratcliff (1993) demonstrated that when performing standard group ANOVAs, the median can lack power compared to other estimators. Ratcliff’s simulations involved ANOVAs on group means, in which for each participant, very few trials (7 to 12) are available for each condition. Based on the simulations, Ratcliff recommended data transformations or computing the mean after applying specific cut-offs to maximise power. However, these recommendations should be considered with caution because the results could be very different with more realistic sample sizes. Also, standard ANOVA on group means are not robust, and alternative techniques should be considered (Wilcox 2017). Data transformations are not ideal either, because they change the shape of the distributions, which contains important information about the nature of the effects. Also, once data are transformed, inferences are made on the transformed data, not on the original ones, an important caveat that tends to be swept under the carpet in articles’ discussions… Finally, truncating distributions introduce bias too, especially with the mean – see next section (Miller 1991; Ulrich & Miller 1994)!

At this stage, I don’t see much convincing evidence against using the median of RT distributions, if the goal is to use only one measure of location to summarise the entire distribution. Clearly, a better alternative is to not throw away all that information, by studying how entire distributions differ (Rousselet et al. 2017). For instance, explicit modelling of RT distributions can be performed with the excellent brms R package.

Other problems with the mean

In addition to being median biased, and a poor measure of central tendency for asymmetric distributions, the mean is also associated with several other important problems. Standard procedures using the mean lack of power, offer poor control over false positives, and lead to inaccurate confidence intervals. Detailed explanations of these problems are provided in Field & Wilcox (2017) and Wilcox & Rousselet (2018) for instance. For detailed illustrations of the problems associated with means in the one-sample case, when dealing with skewed distributions, see the companion reproducibility package on figshare.

If that was not enough, common outlier exclusion techniques lead to bias estimation of the mean (Miller, 1991). When applied to skewed distributions, removing any values more than 2 or 3 SD from the mean affects slow responses more than fast ones. As a consequence, the sample mean tends to underestimate the population mean. And this bias increases with sample size because the outlier detection technique does not work for small sample sizes, which results from the lack of robustness of the mean and the SD. The bias also increases with skewness. Therefore, when comparing distributions that differ in sample size, or skewness, or both, differences can be masked or created, resulting in inaccurate quantification of effect sizes.

Truncation using absolute thresholds (for instance RT < 300 ms or RT > 1,200 ms) also leads to potentially severe bias of the mean, median, standard deviation and skewness of RT distributions (Ulrich & Miller 1994). The median is much less affected by truncation bias than the mean though.

In the next and final post of this series, we will explore sampling bias in a real dataset, to see how much of a problem we’re really dealing with. Until then, thanks for reading.

[GO TO POST 4/4]


Field, A.P. & Wilcox, R.R. (2017) Robust statistical methods: A primer for clinical psychology and experimental psychopathology researchers. Behav Res Ther, 98, 19-38.

Miller, J. (1988) A warning about median reaction time. J Exp Psychol Hum Percept Perform, 14, 539-543.

Miller, J. (1991) Reaction-Time Analysis with Outlier Exclusion – Bias Varies with Sample-Size. Q J Exp Psychol-A, 43, 907-912.

Ratcliff, R. (1993) Methods for dealing with reaction time outliers. Psychol Bull, 114, 510-532.

Rousselet, G.A., Pernet, C.R. & Wilcox, R.R. (2017) Beyond differences in means: robust graphical methods to compare two groups in neuroscience. The European journal of neuroscience, 46, 1738-1748.

Ulrich, R. & Miller, J. (1994) Effects of Truncation on Reaction-Time Analysis. Journal of Experimental Psychology-General, 123, 34-80.

Wilcox, R.R. (2017) Introduction to Robust Estimation and Hypothesis Testing. Academic Press, 4th edition., San Diego, CA.

Wilcox, R.R. & Rousselet, G.A. (2018) A Guide to Robust Statistical Methods in Neuroscience. Curr Protoc Neurosci, 82, 8 42 41-48 42 30.

A quick review of Reader et al. EJN 2018

Here is a quick review of a paper that just came out in the European Journal of Neuroscience. I flagged one concern on Twitter, and the authors asked me to elaborate, so here I provide a short assessment of the sort I write when scanning through a paper I get to edit for the journal. This short assessment would then be added to the reviewers’ comments in my decision letter, or would be used as feedback as part of an editorial rejection.

Repetitive transcranial magnetic stimulation reveals a role for the left inferior parietal lobule in matching observed kinematics during imitation
Reader et al. EJN 2018

Participants: please report min, max, median age

Instead of splitting the analysis between hand and finger gestures, it would have been more powerful to perform a hierarchical analysis including a gesture factor. This sort of item analysis could dramatically alter the outcome of your analyses:

If the separate analysis of different gestures was not planned, then the sub-analyses must be corrected for multiple comparisons. In your case, it seems that most effects would not be significant, following the usual arbitrary p<0.05 cut-off.

The permutation + t-test procedure to investigate sequences is quite good. It would probably give you more power to include the size of the t values, by computing cluster sums, instead of cluster lengths. Also, you could consider TFCE, which provides a cluster free approach, with Matlab code available:

The multiple sequence tests should be corrected for multiple comparisons, for instance by using a maximum cluster sum statistics, where the max is taken across all comparisons.

The use of t-tests on means should be justified.

The results are presented mostly using t and p values, and whether an arbitrary p<0.05 threshold was reached. Results would be better presented by focusing on effect sizes, in their original units, individual differences, and mentioning t and p values only in passing, as pieces of evidence without a special status.

It’s great to use figures with scatterplots; however, for paired designs it is essential to also show distributions of pairwise differences. See guidelines for instance here:

The little stars and crosses should be removed from all figures. The emphasis should be on effect sizes and individual differences, which are best portrayed by showing scatterplots of pairwise differences. Also, using different tests, whether parametric or not, would give different p values, so the exact p values are only indicative, especially if the goal is to determine if <0.05.

The discussion should better qualify the results. For instance, this conclusion uses p values to incorrectly imply that the null hypothesis can be accepted, and that effect sizes were zero:
“Whilst stimulation did not influence imitation accuracy, there was some evidence for differences between accuracy in meaningful and meaningless action performance.”

The sample size is rather small, so the discussion should mention the risk of effect sizes being completely off.

To have to contact the corresponding author to get data and code is not a good short term or long term solution. Instead, please upload the material to a third-party repository.

“the fact that” is an awful construction that can be avoided by rephrasing. For instance:
“may reflect the fact that the differences”
“may reflect that the differences”

Reaction times and other skewed distributions: problems with the mean and the median (part 2/4)

As we saw in the previous post, the sample median is biased when sampling from skewed distributions. The bias increases with decreasing sample size. According to Miller (1988), because of this bias, group comparison can be affected if the two groups differ in skewness or sample size, or both. As a result, real differences can be lowered or increased, and non-existent differences suggested. In Miller’s own words:

“An important practical consequence of the bias in median reaction time is that sample medians must not be used to compare reaction times across experimental conditions when there are unequal numbers of trials in the conditions.”

Here we will see that this advice is wrong for two reasons.

We assess the problem using a simulation in which we draw samples of same or different sizes from populations that differ in skewness or not. We use the same 12 distributions used by Miller (1988), as described previously.

Group 2 has size 200 and is sampled from the distribution with the least skewness.

Group 1 has size 10 to 200, in increments of 10, and is sampled from the 12 distributions.

After 10,000 iterations, here are the results for the mean:


All the bias values are near zero, as expected. The shaded area shows the upper part of the mean’s bias 50% HDI (highest density interval), when group 1 and group 2 have the same, least, skewness (6). This interval shows the location of the bulk of the 10,000 simulations. The same area is shown in the next figures. Again, this is a reminder that bias is defined in the long run: a single experiment (one of our simulation iterations) can be far off the population value, especially with small sample sizes.

Here are the results for the median:


As in the previous figure, the shaded area shows the upper part of the mean’s bias 50% HDI, when group 1 and group 2 have the same skewness. Bias increases with skewness and sample size difference and is particularly large for n = 10. However, if the two groups have the same skewness (skewness 6), there is almost no bias even when group 2 has 200 observations and group 1 only has 10. So it seems Miller’s (1988) warning about differences in sample sizes was inappropriate, because the main factor causing bias is skewness.

Next, let’s find out if we can correct the bias. Bias correction is performed in 2 ways:

  • using the bootstrap

  • using subsamples, following Miller’s suggestion.

Miller (1988) suggested:

“Although it is computationally quite tedious, there is a way to use medians to reduce the effects of outliers without introducing a bias dependent on sample size. One uses the regular median from Condition F and compares it with a special “average median” (Am) from Condition M. To compute Am, one would take from Condition M all the possible subsamples of Size f where f is the number of trials in Condition F. For each subsample one computes the subsample median. Then, Am is the average, across all possible subsamples, of the subsample medians. This procedure does not introduce bias, because all medians are computed on the basis of the same sample (subsample) size.”

Using all possible subsamples would take far too long. For instance, if one group has 5 observations and the other group has 20 observations, there are 15504 (choose(20,5)) subsamples to consider. Slightly larger sample sizes would force us to consider millions of subsamples. So instead we compute K random subsamples. I arbitrarily set K to 1,000. Although this is not what Miller (1988) suggested, the K loop shortcut should reduce bias to some extent if it is due to sample size differences. Here are the results:


The K loop approach has only a small effect on bias. The reason is simple: the main cause of the bias is not a difference in sample size, it is a difference in skewness. This skewness difference can be handled by the bootstrap. Here is what we get using 200 bootstrap resamples for each simulation iteration:


The bootstrap bias correction works very well. The median’s bias is still a bit larger than the mean’s bias for n = 10 in some conditions. For instance, for the most skewed distribution and n = 10, the mean’s bias is -0.51, whereas the median’s bias after bias correction is 0.73. None of them are exactly zero and the absolute values are very similar. At most, for n = 10, the median’s maximum bias across distributions is 1.85 ms, whereas the mean’s is 0.7 ms.


Miller’s (1988) advice was inappropriate because, when comparing two groups, bias originates from a conjunction of differences in skewness and in sample size, not from differences in sample size alone. Although, in practice it might well be that skewed distributions from different conditions/groups tend to differ in skewness, in which case unequal sample sizes will exacerbate the bias. To be cautious, when sample size is relatively small, it would be useful to report median effects with and without bootstrap bias correction.

Finally, data & code are available on github.

[GO TO POST 3/4]

Reaction times and other skewed distributions: problems with the mean and the median (part 1/4)

In this series of 4 posts, I replicate, expand and discuss the results from

Miller, J. (1988) A warning about median reaction time. J Exp Psychol Hum Percept Perform, 14, 539-543.

Part 1 = replicate Miller’s simulations + apply bootstrap bias correction

Part 2 = expand Miller’s simulations to group comparison

Part 3 = problems with the mean

Part 4 = application to a large dataset

Data & code are available on github.

Reaction times (RT) and many other quantities in neuroscience & psychology are skewed. This asymmetry tends to differ among experimental conditions, such that a measure of central tendency and a measure of spread are insufficient to capture how conditions differ. Instead, to understand the potentially rich differences among distributions, it is advised to consider multiple quantiles of the distributions (Doksum 1974; Pratte et al. 2010; Rousselet et al. 2017), or to model the shapes of the distributions (Heathcote et al. 1991; Rouder et al. 2005; Palmer et al. 2011; Matzke et al. 2013). Yet, it is still common practice to summarise reaction time distributions using a single number, most often the mean: that one value for each participant and each condition can then be entered into a group ANOVA to make statistical inferences. Because of the skewness of reaction times, the mean is however a poor measure of central tendency: skewness shifts the mean away from the bulk of the distribution, an effect that can be amplified by the presence of outliers or a thick right tail. For instance, in the figure below, the median better represents the typical observation than the mean because it is closer to the bulky part of the distribution.


Mean and median for a very right skewed distribution. The distribution is bounded to the left and has a long right tail. This is an ex-Gaussian distribution, which is popular to model the shape of reaction time distributions, even though the matching between its parameters and mental processes can be debated (Sternberg, 2014).

So the median appears to be a better choice than the mean if the goal is to have a single value to tell us about the location of most observations in a skewed distribution. The choice between the mean and the median is however more complicated. It could be argued that because the mean is sensitive to skewness, outliers and the thickness of the right tail, it is better able to capture changes in the shapes of the distributions among conditions. But the use of a single value to capture shape differences will lead to intractable analyses because the same mean could correspond to various shapes. Instead, a multiple quantile approach or explicit shape modelling should be used.

The mean and the median differ in another important aspect: for small sample sizes, the sample mean is unbiased, whereas the sample median is biased (see illustrations in previous post). Concretely, if we perform many times the same RT experiment, and for each experiment we compute the mean and the median, the average mean will be very close to the population mean. As the number of experiments increases, the average sample mean will converge to the exact population mean. This is not the case for the median when sample size is small.

The reason for this bias is explain by Miller (1988):

“Like all sample statistics, sample medians vary randomly (from sample to sample) around the true population median, with more random variation when the sample size is smaller. Because medians are determined by ranks rather than magnitudes of scores, the population percentiles of sample medians vary symmetrically around the desired value of 50%. For example, a sample median is just as likely to be the score at the 40th percentile in the population as the score at the 60th percentile. If the original distribution is positively skewed, this symmetry implies that the distribution of sample medians will also be positively skewed. Specifically, unusually large sample medians (e.g., 60th percentile) will be farther above the population median than unusually small sample medians (e.g., 40th percentile) will be below it. The average of all possible sample medians, then, will be larger than the true median, because sample medians less than the true value will not be small enough to balance out the sample medians greater than the true value. Naturally, the more the distribution is skewed, the greater will be the bias in the sample median.”

To illustrate the sample median’s bias, Miller (1988) employed 12 ex-Gaussian distributions that differ in skewness. The distributions are illustrated in the next figure, and colour-coded using the difference between the mean and the median as a non-parametric measure of skewness.


Here are the parameters of the 12 distributions with the associated population parameters.



The first figure in this post used the most skewed distribution of the 12, with parameters (300, 20, 300).

To estimate bias, we run a simulation in which we sample with replacement 10,000 times from each of the 12 distributions. We take random samples of sizes 4, 6, 8, 10, 15, 20, 25, 35, 50 and 100, as did Miller. For each random sample, we compute the mean and the median. For each sample size and ex-Gaussian parameter, the bias is then defined as the difference between the mean of the 10,000 sample estimates and the population value.

First, we check that the mean is not biased:


Each line shows the results for one type of ex-Gaussian distribution: the mean of 10,000 simulations for different sample sizes. The grey area marks the 50% highest-density interval (HDI) of the 10,000 simulations for the least skewed distribution (the same interval is shown in the next two figures for comparison). The interval shows the variability across simulations and highlights an important aspect of the results: bias is a long-run property of an estimator; there is no guarantee that one value from a single experiment will be close to the population value. Also, the variability among samples increases with decreasing sample size, which is why results across small n experiments can differ substantially.

Here are the median bias estimates in table format:



Columns = sample sizes; rows = skewness


The values are very close to the values reported in Miller 1998:


An illustration is easier to grasp:


As reported by Miller (1988), bias can be quite large and it gets worse with decreasing sample sizes and increasing skewness.

Based on these results, Miller made this recommendation:

“An important practical consequence of the bias in median reaction time is that sample medians must not be used to compare reaction times across experimental conditions when there are unequal numbers of trials in the conditions.”

According to Google Scholar, Miller (1988) has been cited 172 times. A look at some of the oldest and most recent citations reveals that his advice has been followed.

For instance, Lavie (1995) noted:

“In the following experiments I used the mean RTs for each participant rather than the medians, as the increase in number of go/no-go errors under the high-load conditions resulted in a different number of responses in between conditions (see Miller, 1988).”

Tipper et al. (1992):

Analysis by Miller (1988) shows that for large numbers of trials, differences in the numbers between conditions […] has no impact on the medians obtained.

More recently, Robinson et al. (2018):

“[…] comparing medians among conditions with an unequal number of trials may lead to false positives (Miller, 1988)”

Du et al. (2017):

“We chose the mean rather than median of RT as […] the sample median may provide a biased estimation of RT (Miller, 1988)”

The list goes on. Also, in a review paper, Whelan (2008), cited 324 times, reiterates the advice:

“The median should never be used on RT data to compare conditions with different numbers of trials.”

However, there are several problems with Miller’s advice. In particular, using the mean leads to many issues with estimation and statistical inferences, as we will see in the 3rd post. In this post, we tackle one key omission from Miller’s assessment: the bias of the sample median can be corrected, using a percentile bootstrap bias correction, as described in this previous post.

For each iteration in the simulation, bias correction was performed using 200 bootstrap samples. Here are the bias corrected results:


The bias correction works very well on average, except for the smallest sample sizes. The failure of the bias correction for very small n is not surprising, because the shape of the sampling distribution cannot be properly estimated by the bootstrap from so few observations. From n = 10, the bias values are very close to those observed for the mean. So it seems that in the long-run, we can eliminate the bias of the sample median by using a simple bootstrap procedure. As we will see in the next post, the bootstrap bias correction is also effective when comparing two groups.

Update: 06 Feb 2018

Finally, let’s have a look at how well bias correction works as a function of sample size and skewness. The smaller the sample size, the less the bootstrap can estimate the sampling distribution and its bias. Ideally, after bias correction, we would expect the sample medians to be centred around zero, with limited variability. This ideal situation could look something like that:


Here we’re considering the most skewed distribution with the smallest sample size. The x-axis shows the median bias before bias correction, whereas the y-axis shows the median bias after bias correction. In this ideal case, the correction works extremely well irrespective of the original bias (average bias is the red vertical line). As a result, the average bias after bias correction is very near zero (horizontal green line).

The reality is very different. The bias correction is only partially effective and is inhomogeneous.


Let’s add some markup to help understand what’s going on.


If the original bias is negative, after correction, the median tends to be even more negative, so over corrected in the wrong direction (lower left triangle).

If the original bias is positive, after correction, the median is either:
– over corrected in the right direction (lower right triangle)
– under corrected in the right direction (middle right triangle)
– over corrected in the wrong direction (upper right triangle)

This pattern remains, although attenuated, if we consider the largest sample size.


Or if we consider the least skewed distribution.


We can look at the different patterns as a function of sample size and skewness.

The figure below shows the probability of over correcting in the wrong direction given that the original bias is negative (lower left triangle of the marked up figure).


In the ideal situation illustrated previously, the expected proportion of over correction in the wrong direction, given an original negative bias, is 6.7%. So here we clearly have an overrepresentation of these cases. When the original bias is negative, in most cases the bootstrap is unable to correct in the right direction. The situation gets worse with increasing skewness and smaller sample sizes.

The figure below shows the probability of under correcting in the right direction given that the original bias is positive (middle right triangle of the marked up figure)


In the ideal situation illustrated previously, the expected proportion of under correction in the right direction, given an original positive bias, is 44.7 %. So here, we have an overrepresentation of these cases. When the original bias is positive, in too many cases the bootstrap corrects in the right direction, but it under-corrects. The situation gets worse with increasing skewness and smaller sample sizes.

Ok, so bias correction is imperfect and it varies a lot, it part depending on whether the sample median fell above or below the unknown population median. Think using the mean is safer? There are several strong arguments to the contrary – more in another post.

[GO TO POST 2/4]


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Can someone tell if a person is alive or dead based on a photograph?

In this post I review the now retracted paper:

Delorme A, Pierce A, Michel L and Radin D (2016) Prediction of Mortality Based on Facial Characteristics. Front. Hum. Neurosci. 10:173. doi: 10.3389/fnhum.2016.00173

In typical Frontiers’ style, the reason for the retraction is obscure.

In December 2016, I made negative comments about the paper on Twitter. Arnaud Delorme (first author, and whom I’ve known for over 20 years), got in touch, asking for clarifications about my points. I said I would write something eventually, so there it goes.

The story is simple: some individuals claim to be able to determine if a person is alive or dead based on a photograph. The authors got hold of 12 such individuals and asked them to perform a dead/alive/don’t know discrimination task. EEG was measured while participants viewed 394 photos of individuals alive or dead (50/50).

Here are some of the methodological problems.


Participants were from California. Some photographs were of US politicians outside California. Participants did not recognise any individuals from the photographs, but unconscious familiarity could still influence behaviour and EEG – who knows?

More importantly, if participants make general claims about their abilities, why not use photographs of individuals from another country altogether? Even better, another culture?


The average group performance of the participants was 53.6%. So as a group, they really can’t do the task. (If you want to argue they can, I challenge you to seek treatment from a surgeon with  a 53.6% success record.) Yet, a t-test is reported with p=0.005. Let’s not pay too much attention to the inappropriateness of t-tests for percent correct data. The crucial point is that the participants did not make a claim about their performance as a group: each one of them claimed to be able to tease apart the dead from the living based on photographs. So participants should be assessed individually. Here are the individual performances:

(52.3, 56.7, 53.3, 56.0, 56.6, 51.8, 61.3, 55.3, 50.0, 51.6, 49.5, 49.4)

5 participants have results flagged as significant. One in particular has a performance of 61.3% correct. So how does it compare to participants without super abilities? Well, astonishingly, there is no control group! (Yep, and that paper was peer-reviewed.)

Given the extra-ordinary claims made by the participants, I would have expected a large sample of control participants, to clearly demonstrate that the “readers” perform well beyond normal. I would also have expected the readers to be tested on multiple occasions, to demonstrate the reliability of the effect.

There are two other problems with the behavioural performance:

  • participants’ responses were biased towards the ‘dead’ response, so a sensitivity analysis, such as a d’ or a non-parametric equivalent should have been used.

  • performance varied a lot across the 3 sets of images that composed the 394 photographs. This suggests that the results are not image independent, which could in part be due to the 3 sets containing different proportions of dead and alive persons.


The ERP analyses were performed at the group level using a 2 x 2 design: alive/dead x correct/incorrect classification. One effect is reported with p<0.05: a larger amplitude for incorrect than correct around 100 ms post-stimulus, only for pictures of dead persons. A proper spatial-temporal cluster correction for multiple comparison was applied. There is no clear interpretation of the effect in the paper, except a quick suggestion that it could be due to low-level image properties or an attention effect. A non-specific attention effect is possible, because sorting ERPs based on behavioural performance can be misleading, as explained here. The effect could also be a false positive – in the absence of replication and comparison to a control group, it’s impossible to tell.

To be frank, I don’t understand why EEG was measured at all. I guess if the self-proclaimed readers could do the task at all, it would be interesting to look at the time-course of the brain activity related to the task. But the literature on face recognition shows very little modulation due to identity, except in priming tasks or using SSVEP protocols – so not likely to show anything with single image presentations. If there was something to exploit, the analysis should be performed at the participant level, perhaps using multivariate logistic regression, with cross-validation, to demonstrate a link between brain activity and image type. Similarly to behaviour, each individual result from the “readers” should be compared to a large set of control results, from participants who cannot perform the behavioural task.


In conclusion, this paper should never have been sent for peer-review. That would have saved everyone involved a lot of time. There is nothing in the paper supporting the authors’ conclusion:

“Our results support claims of individuals who report that some as-yet unknown features of the face predict mortality. The results are also compatible with claims about clairvoyance warrants further investigation.”

If the authors are serious about studying clairvoyance, they should embark on a much more ambitious study. To save time and money, I would suggest to drop EEG from the study, to focus on the creation of a large bank of images from various countries and cultures and repeated measurements of readers and many controls.

What can we learn from 10,000 experiments?

The code and a notebook for this post are available on github.

Before we conduct an experiment, we decide on a number of trials per condition, and a number of participants, and then we hope that whatever we measure comes close to the population values we’re trying to estimate. In this post I’ll use a large dataset to illustrate how close we can get to the truth – at least in a lexical decision task. The data are from the French lexicon project:

Ferrand, L., New, B., Brysbaert, M., Keuleers, E., Bonin, P., Meot, A., Augustinova, M. & Pallier, C. (2010) The French Lexicon Project: lexical decision data for 38,840 French words and 38,840 pseudowords. Behav Res Methods, 42, 488-496.

After discarding participants who clearly did not pay attention, we have 967 participants who performed a word/non-word discrimination task. Each participant has about 1000 trials per condition. I only consider the reaction time (RT) data, but correct/incorrect data are also available. Here are RT distributions for 3 random participants (PXXX refers to their ID number in the dataset):




The distributions are positively skewed, as expected for RT data, and participants tend to be slower in the non-word condition compared to the word condition. Usually, a single number is used to summarise each individual RT distribution. From 1000 values to 1, that’s some serious data compression. (For alternative strategies to compare RT distributions, see for instance this paper). In psychology, the mean is often used, but here the median gives a better indication of the location of the typical observation. Let’s use both. Here is the distribution across participants of median RT for the word and non-word conditions:


And the distribution of median differences:


Interestingly, the differences between the medians of the two conditions is also skewed: that’s because the two distributions tend to differ in skewness.

We can do the same for the mean:


Mean differences:


With this large dataset, we can play a very useful game. Let’s pretend that the full dataset is our population that we’re trying to estimate. Across all trials and all participants, the population medians are:

Word = 679.5 ms
Non-word = 764 ms
Difference = 78.5

the population means are:

Word = 767.6 ms
Non-word = 853.2 ms
Difference = 85.5

Now, we can perform experiments by sampling with replacement from our large population. I think we can all agree that a typical experiment does not have 1,000 trials per condition, and certainly does not have almost 1,000 participants! So what happens if we perform experiments in which we collect smaller sample sizes? How close can we get to the truth?

10,000 experiments: random samples of participants only

In the first simulation, we use all the trials (1,000) available for each participant but vary how many participants we sample from 10 to 100, in steps of 10. For each sample size, we draw 10,000 random samples of participants from the population, and we compute the mean and the median. For consistency, we compute group means of individual means, and group medians of individual medians. We have 6 sets of results to consider: for the word condition, the non-word condition, their difference; for the mean and for the median. Here are the results for the group medians in the word condition. The vertical red line marks the population median for the word condition.


With increasing sample size, we gain in precision: on average the result of each experiment is closer to the population value. With a small sample size, the result of a single experiment can be quite far from the population. This is not surprising, and also explains why estimates from small n experiments tend to disagree, especially between an original study and subsequent replications.

To get a clearer sense of how close the estimates are to the population value, it is useful to consider highest density intervals (HDI). A HDI is the shorted interval that contains a certain proportion of observations: it shows the location of the bulk of the observations. Here we consider 50% HDI:


In keeping with the previous figure, the intervals get smaller with increasing sample size. The intervals are also asymmetric: the right side is always closer to the population value than the left side. That’s because the sampling distributions are asymmetric. This means that the typical experiment will tend to under-estimate the population value.

We observe a similar pattern for the non-word condition, with the addition of two peaks in the distribution from n = 40. I’m not sure what’s causing it, or if it is a common shape. One could check by analysing the lexicon project data from other countries. Any volunteers? One thing for sure: the two peaks are caused by the median, because they are absent from the mean distributions (see notebook on github).


Finally, we can consider the distributions of group medians of median differences:


Not surprisingly, it has a similar shape to the previous distributions. It shows a landscape of expected effects. It would be interesting to see where the results of other, smaller, experiments fall in that distribution. The distribution could also be used to plan experiments to achieve a certain level of precision. This is rather unusual given the common obsession for statistical power. But experiments should be predominantly about quantifying effects, so a legitimate concern is to determine how far we’re likely to be from the truth in a given experiment. Using our simulated distribution of experiments, we can determine the probability of the absolute difference between an experiment and the population value to be larger than some cut-offs. In the figure below, we look at cut-offs from 5 ms to 50 ms, in steps of 5.


The probability of being wrong by at least 5 ms is more than 50% for all sample sizes. But 5 ms is probably not a difference folks studying lexical decision would worry about. It might be an important difference in other fields. 10 ms might be more relevant: I certainly remember a conference in which group differences of 10 ms between attention conditions were seriously discussed, and their implications for theories of attention considered. If we care about a resolution of at least 10 ms, n=30 still gives us 44% chance of being wrong…

(If someone is looking for a cool exercise: you could determine the probability of two random experiments to differ by at least certain amounts.)

We can also look at the 50% HDI of the median differences:


As previously noted, the intervals shrink with increasing sample size, but are asymmetric, suggesting that the typical experiment will under-estimate the population difference. This asymmetry disappears for larger samples of group means:


Anyway, these last figures really make me think that we shouldn’t make such a big deal out of any single experiment, given the uncertainty in our measurements.

10,000 experiments: random samples of trials and participants

In the previous simulation, we sampled participants with replacement, using all their 1,000 trials. Typical experiments use fewer trials. Let say I plan to collect data from 20 participants, with 100 trials per condition. What does the sampling distribution look like? Using our large dataset, we can sample trials and participants to find out. Again, for consistency, group means are computed from individual means, and group medians are computed from individual medians. Here are the sampling distributions of the mean and the median in the word condition:


The vertical lines mark the population values. The means are larger than the medians because of the positive skewness of RT distributions.

In the non-word condition:


And the difference distributions:


Both distributions are slightly positively skewed, and their medians fall to the left of the population values. The spread of expected values is quite large.

Similarly to simulation 1, we can determine the probability of being wrong by at least 5 ms, which is 39%. For 10 ms, the probability is 28%, and for 20 ms 14%. But that’s assuming 20 participants and 100 trials per condition. A larger simulation could investigate many combinations of sample sizes…

Finally, we consider the 50% HDI, which are both asymmetric with respect to the population values and with similar lengths:



To answer the question from the title, I think the main things we can learn from the simulated sampling distributions above are:
– to embrace uncertainty
– modesty in our interpretations
– healthy skepticism about published research
One way to highlight uncertainty in published research would be to run simulations using descriptive statistics from the articles, to illustrate the range of potential outcomes that are compatible with the results. That would make for interesting stories I’m sure.