Jacob Cohen has warned fellow psychologists about the problem of conducting studies with insufficient statistical power to demonstrate predicted effects in 1962. The problem is simple enough. An underpowered study has only a small chance to produce the correct result; that is, a statistically significant result when an effect is present.

Many researchers have ignored Cohen’s advice to conduct studies with at least 80% power, that is, an 80% probability to produce the correct result when an effect is present because they were willing to pay low odds. Rather than conducting a single powerful study with 80% power, it seemed less risky to conduct three underpowered studies with 30% power. The chances of getting a significant result are similar (the power to get a significant result in at least 1 out of 3 studies with 30% power is 66%). Moreover, the use of smaller samples is even less problematic if a study tests multiple hypotheses. With 80% power to detect a single effect, a study with two hypotheses has a 96% probability that at least one of the two effects will produce a significant result. Three studies allow for six hypotheses tests. With 30% power to detect at least one of the two effects in six attempts, power to obtain at least one significant result is 88%. Smaller samples also provide additional opportunities to increase power by increasing sample sizes until a significant result is obtained (optional stopping) or by eliminating outliers. The reason is that these questionable practices have larger effects on the results in smaller samples. Thus, for a long time researchers did not feel a need to conduct adequately powered studies because there was no shortage of significant results to report (Schimmack, 2012).

Psychologists have ignored the negative consequences of relying on underpowered studies to support their conclusions. The problem is that the reported p-values are no longer valid. A significant result that was obtained by conducting three studies no longer has a 5% chance to be a random event. By playing the sampling-error lottery three times, the probability of obtaining a significant result by chance alone is now 15%. By conducting three studies with two hypothesis tests, the probability of obtaining a significant result by chance alone is 30%. When researchers use questionable research practices, the probability of obtaining a significant result by chance can further increase. As a result, a significant result no longer provides strong statistical evidence that the result was not just a random event.

It would be easy to distinguish real effects from type-I errors (significant results when the null-hypothesis is true) by conducting replication studies. Even underpowered studies with 30% power will replicate in every third study. In contrast, when the null-hypothesis is true, type-I errors will replicate only in 1 out of 20 studies, when the criterion is set to 5%. This is what a 5% criterion means. There is only a 5% chance (1 out of 20) to get a significant result when the null-hypothesis is true. However, this self-correcting mechanism failed because psychologists considered failed replication studies as uninformative. The perverse logic was that failed replications are to be expected because studies have low power. After all, if a study has only 30% power, a non-significant result is more likely than a significant result. So, non-significant results in underpowered studies cannot be used to challenge a significant result in an underpowered study. By this perverse logic, even false hypothesis will only receive empirical support because only significant results will be reported, no matter whether an effect is present or not.

The perverse consequences of abusing statistical significance tests became apparent when Bem (2011) published 10 studies that appeared to demonstrate that people can anticipate random future events and that practicing for an exam after writing an exam can increase grades. These claims were so implausible that few researchers were willing to accept Bem’s claims despite his presentation of 9 significant results in 10 studies. Although the probability that this even occurred by chance alone is less than 1 in a billion, few researchers felt compelled to abandon the null-hypothesis that studying for an exam today can increase performance on yesterday’s exam.   In fact, most researchers knew all too well that these results could not be trusted because they were aware that published results are not an honest report of what happens in a lab. Thus, a much more plausible explanation for Bem’s incredible results was that he used questionable research practices to obtain significant results. Consistent with this hypothesis, closer inspection of Bem’s results shows statistical evidence that Bem used questionable research practices (Schimmack, 2012).

As the negative consequences of underpowered studies have become more apparent, interest in statistical power has increased. Computer programs make it easy to conduct power analysis for simple designs. However, so far power analysis has been limited to conventional statistical methods that use p-values and a criterion value to draw conclusions about the presence of an effect (Neyman-Pearson Significance Testing, NPST).

Some researchers have proposed Bayesian statistics as an alternative approach to hypothesis testing. As far as I know, these researchers have not provided tools for the planning of sample sizes. One reason is that Bayesian statistics can be used with optional stopping. That is, a study can be terminated early when a criterion value is reached. However, an optional stopping rule also needs a rule when data collection will be terminated in case the criterion value is not reached. It may sound appealing to be able to finish a study at any moment, but if this event is unlikely to occur in a reasonably sized sample, the study would produce an inconclusive result. Thus, even Bayesian statisticians may be interested in the effect of sample sizes on the ability to obtain a desired Bayes-Factor. Thus, I wrote some r-code to conduct power analysis for Bayes-Factors.

The code uses the Bayes-Factor package in r for the default Bayesian t-test (see also blog post on Replication-Index blog). The code is posted at the end of this blog. Here I present results for typical sample sizes in the between-subject design for effect sizes ranging from 0 (the null-hypothesis is true) to Cohen’s d = .5 (a moderate effect). Larger effect sizes are not reported because large effects are relatively easy to detect.

The first table shows the percentage of studies that meet a specified criterion value based on 10,000 simulations of a between-subject design. For Bayes-Factors the criterion values are 3 and 10. For p-values the criterion values are .05, .01, and .001. For Bayes-Factors, a higher number provides stronger support for a hypothesis. For p-values, lower values provide stronger support for a hypothesis. For p-values, percentages correspond to the power of a study. Bayesian statistics has no equivalent concept, but percentages can be used in the same way. If a researcher aims to provide empirical support for a hypothesis with a Bayes-Factor greater than 3 or 10, the table gives the probability of obtaining the desired outcome (success) as a function of the effect size and sample size.

d   n     N     3   10     .05 .01     .001
.5   20   40   17   06     31     11     02
.4   20   40   12   03     22     07     01
.3   20   40   07   02     14     04     00
.2   20   40   04   01     09     02     00
.1   20   40   02   00     06     01     00
.0   20   40   33   00     95     99   100

For an effect size of zero, the interpretation of results switches. Bayes-Factors of 1/3 or 1/10 are interpreted as evidence for the null-hypothesis. The table shows how often Bayes-Factors provide support for the null-hypothesis as a function of the effect size, which is zero, and sample size. For p-values, the percentage is 1 – p. That is, when the effect is zero, the p-value will correctly show a non-significant result with a probability of 1 – p and it will falsely reject the null-hypothesis with the specified type-I error.

Typically, researchers do not interpret non-significant results as evidence for the null-hypothesis. However, it is possible to interpret non-significant results in this way, but it is important to take the type-II error rate into account. Practically, it makes little difference whether a non-significant result is not interpreted or whether it is taken as evidence for the null-hypothesis with a high type-II error probability. To illustrate this consider a study with N = 40 (n = 20 per group) and an effect size of d = .2 (a small effect). As there is a small effect, the null-hypothesis is false. However, the power to detect this effect in a small sample is very low. With p = .05 as the criterion, power is only 9%. As a result, there is a 91% probability to end up with a non-significant result even though the null-hypothesis is false. This probability is only slightly lower than the probability to get a non-significant result when the null-hypothesis is true (95%). Even if the effect size were d = .5, a moderate effect, power is only 31% and the type-II error rate is 69%. With type-II error rates of this magnitude, it makes practically no difference whether a null-hypothesis is accepted with a warning that the type-II error rate is high or whether the non-significant result is simply not interpreted because it provides insufficient information about the presence or absence of small to moderate effects.

The main observation in Table 1 is that small samples provide insufficient information to distinguish between the null-hypothesis and small to moderate effects. Small studies with N = 40 are only meaningful to demonstrate the presence of moderate to large effects, but they have insufficient power to show effects and insufficient power to show the absence of effects. Even when the null-hypothesis is true, a Bayes-Factor of 3 is reached only 33% of the time. A Bayes-Factor of 10 is never reached because the sample size is too small to provide such strong evidence for the null-hypothesis when the null-hypothesis is true. Even more problematic is that a Bayes-Factor of 3 is reached only 17% of the time when a moderate effect is present. Thus, the most likely outcome in small samples is an inconclusive result unless a strong effect is present. This means that Bayes-Factors in these studies have the same problem as p-values. They can only provide evidence that an effect is present when a strong effect is present, but they cannot provide sufficient evidence for the null-hypothesis when the null-hypothesis is true.

d   n     N     3   10     .05 .01     .001
.5   50 100   49   29     68     43     16
.4   50 100   30   15     49     24     07
.3   50 100   34   18     56     32     12
.2   50 100   07   02     16     05     01
.1   50 100   03   01     08     02     00
.0   50 100   68   00     95     99   100

In Table 2 the sample size has been increased to N = 100 participants (n = 50 per cell). This is already a large sample size by past standards in social psychology. Moreover, in several articles Wagenmakers has implemented a stopping rule that terminates data collection at this point. The table shows that a sample size of N = 100 in a between-subject design has modest power to demonstrate even moderate effect sizes of d = .5 with a Bayes-Factor of 3 as a criterion (49%). In comparison, a traditional p-value of .05 would provide 68% power.

The main argument for using Bayesian statistics is that it can also provide evidence for the null-hypothesis. With a criterion value of BF = 3, the default test correctly favors the null-hypothesis 68% of the time (see last row of the table). However, the sample size is too small to produce Bayes-Factors greater than 10. In sum, the default-Bayesian t-test with N = 100 can be used to demonstrate the presence of a moderate to large effects and with a criterion value of 3 it can be used to provide evidence for the null-hypothesis when the null-hypothesis is true. However it cannot be used to demonstrate that provide evidence for small to moderate effects.

The Neyman-Pearson approach to significance testing would reveal this fact in terms of the type-I I error rates associated with non-significant results. Using the .05 criterion, a non-significant result would be interpreted as evidence for the null-hypothesis. This conclusion is correct in 95% of all tests when the null-hypothesis is actually true. This is higher than the 68% criterion for a Bayes-Factor of 3. However, the type-II error rates associated with this inference when the null-hypothesis is false are 32% for d = .5, 51% for d = .4, 44% for d = .3, 84% for d = .2, and 92% for d = .1. If we consider effect size of d = .2 as important enough to be detected (small effect size according to Cohen), the type-II error rate could be as high as 84%.

In sum, a sample size of N = 100 in a between-subject design is still insufficient to test for the presence of a moderate effect size (d = .5) with a reasonable chance to find it (80% power). Moreover, a non-significant result is unlikely to occur for moderate to large effect sizes, but the sample size is insufficient to discriminate accurately between the null-hypothesis and small to moderate effects. A Bayes-Factor greater than 3 in favor of the null-hypothesis is most likely to occur when the null-hypothesis is true, but it can also occur when a small effect is present (Simonsohn, 2015).

The next table increases the total sample size to 200 for a between-subject design. The pattern doesn’t change qualitatively. So the discussion will be brief and focus on the power of a study with 200 participants to provide evidence for small to moderate effects and to distinguish small to moderate effects from the null-hypothesis.

d   n     N     3   10     .05 .01     .001
.5 100 200   83   67     94     82     58
.4 100 200   60   41     80     59     31
.3 100 200   16   06     31     13     03
.2 100 200   13   06     29     12     03
.1 100 200   04   01     11     03     00
.0 100 200   80   00     95     95     95  

Using Cohen’s guideline of 80% success rate (power), a study with N = 200 participants has sufficient power to show a moderate effect of d = .5 with p = .05, p = .01, and Bayes-Factor = 3 as criterion values. For d = .4, only the criterion value of p = .05 has sufficient power. For all smaller effects, the sample size is still too small to have 80% power. A sample of N = 200 also provides 80% power to provide evidence for the null-hypothesis with a Bayes-Factor of 3. Power for a Bayes-Factor of 10 is still 0 because this value cannot be reached with N = 200. Finally, with N = 200, the type-II error rate for d = .5 is just shy of .05 (1 – .94 = .06). Thus, it is justified to conclude from a non-significant result with a 6% error rate that the true effect size cannot be moderate to large (d >= .5). However, type-II error rates for smaller effect sizes are too high to test the null-hypothesis against these effect sizes.

d   n     N     3   10     .05 .01     .001
.5 200 400   99   97   100     99     95
.4 200 400   92   82     98     92     75
.3 200 400   64   46     85     65     36
.2 200 400   27   14     52     28     10
.1 200 400   05   02     17     06     01
.0 200 400   87   00     95     99     95

The next sample size doubles the number of participants. The reason is that sampling error decreases in a log-function and large increases in sample sizes are needed to further decrease sampling error. A sample size of N = 200 yields a standard error of 2 / sqrt(200) = .14. (14/100 of a standard deviation). A sample size of N = 400 is needed to reduce this to .10 (2 / sqrt (400) = 2 / 20 = .10; 2/10 of a standard deviation).   This is the reason why it is so difficult to find small effects.

Even with N = 400, power is only sufficient to show effect sizes of .3 or greater with p = .05, or effect sizes of d = .4 with p = .01 or Bayes-Factor 3. Only d = .5 can be expected to meet the criterion p = .001 more than 80% of the time. Power for Bayes-Factors to show evidence for the null-hypothesis also hardly changed. It increased from 80% to 87% with Bayes-Factor = 3 as criterion. The chance to get a Bayes-Factor of 10 is still 0 because the sample size is too small to produce such extreme values. Using Neyman-Pearson’s approach with a 5% type-II error rate as criterion, it is possible to interpret non-significant results as evidence that the true effect size cannot be .4 or larger. With a 1% criterion it is possible to say that a moderate to large effect would produce a significant result 99% of the time and the null-hypothesis would produce a non-significant result 99% of the time.

Doubling the sample size to N = 800 reduces sampling error from SE = .1 to SE = .07.

d   n     N     3     10     .05   .01     .001
.5 400 800 100 100   100  100     100
.4 400 800 100   99   100  100       99
.3 400 800   94   86     99     95      82
.2 400 800   54   38     81     60      32
.1 400 800   09   04     17     06      01
.0 400 800   91   52     95     95      95

A sample size of N = 800 is sufficient to have 80% power to detect a small effect according to Cohen’s classification of effect sizes (d = .2) with p = .05 as criterion. Power to demonstrate a small effect with Bayes-Factor = 3 as criterion is only 54%. Power to demonstrate evidence for the null-hypothesis with Bayes-Factor = 3 as criterion increased only slightly from 87% to 91%, but a sample size of N = 100 is sufficient to produce Bayes-Factors greater than 10 in favor of the null-hypothesis 52% of the time. Thus, researchers who aim for this criterion value need to plan their studies with N = 800. Smaller samples cannot produce these values with the default Bayesian t-test. Following Neyman-Pearson, a non-significant result can be interpreted as evidence that the true effect cannot be larger than d = .3, with a type-II error rate of 1%.

Conclusion

A common argument in favor of Bayes-Factors has been that Bayes-Factors can be used to test the null-hypothesis, whereas p-values can only reject the null-hypothesis. There are two problems with this claim. First, it confuses Null-Significance-Testing (NHST) and Neyman-Pearson-Significance-Testing (NPST). NPST also allows researchers to accept the null-hypothesis. In fact, it makes it easier to accept the null-hypothesis because every non-significant result favors the null-hypothesis. Of course, this does not mean that all non-significant results show that the null-hypothesis is true. In NPST the error of falsely accepting the null-hypothesis depends on the amount of sampling error. The tables here make it possible to compare Bayes-Factors and NPST. No matter which statistical approach is being used, it is clear that meaningful evidence for the null-hypothesis requires rather large samples. The r-code below can be used to compute power for different criterion values, effect sizes, and sample sizes. Hopefully, this will help researchers to better plan sample sizes and to better understand Bayes-Factors that favor the null-hypothesis.

########################################################################
###                       R-Code for Power Analysis for Bayes-Factor and P-Values                ###
########################################################################

## setup
library(BayesFactor)         # Load BayesFactor package
rm(list = ls())                       # clear memory

## set parameters
nsim = 10000      #set number of simulations
es 1 favor effect)
BF10_crit = 3      #set criterion value for BF favoring effect (> 1 = favor null)
p_crit = .05          #set criterion value for two-tailed p-value (e.g., .05

## computations
Z <- matrix(rnorm(groups*n*nsim,mean=0,sd=1),nsim,groups*n)   # create observations
Z[,1:n] <- Z[,1:n] + es                                                                                                #add effect size
tt <- function(x) {                                                                                                       #compute t-statistic (t-test)
oes <- mean(x[1:n])                                                                                    #compute mean group 1
if (groups == 2) oes = oes – mean(x[(n+1):(2*n)])                                  #compute mean for 2 groups
oes <- oes / sd(x[1:n*groups])                                                                  #compute observed effect size
t <- abs(oes) / (groups / sqrt(n*groups))                                                 #compute t-value
}

t <- apply(Z,1,function(x) tt(x))                                                                                 #get t-values for all simulations
df <- t – t + n*groups-groups                                                                                    #get degrees of freedom
p2t <- (1 – pt(abs(t),df))*2                                                                                         #compute two-tailed p-value
getBF <- function(x) {                                                                                                 #function to get Bayes-Factor
t <- x[1]
df <- x[2]
bf <- exp(ttest.tstat(t,(df+2)/2,(df+2)/2,rscale=rsc)$bf)
}              # end of function to get Bayes-Factor

input = matrix(cbind(t,df),,2)                                                                  # combine t and df values
BF10 <- apply(input,1, function(x) getBF(x) )                                        # get BF10 for all simulations
powerBF10 = length(subset(BF10, BF10 > BF10_crit))/nsim*100        # % results support for effect
powerBF01 = length(subset(BF10, BF10 < 1/BF10))/nsim*100            # % results support for null
powerP = length(subset(p2t, p2t < .05))/nsim*100                                # % significant, p < p-criterion

##output of results
cat(
” Power to support effect with BF10 >”,BF10_crit,”: “,powerBF10,
“\n”,
“Power to support null with BF01 >”,BF01_crit,” : “,powerBF01,
“\n”,
“Power to show effect with p < “,p_crit,” : “,powerP,
“\n”)