This blog post is heavily based on one of my first blog-posts in 2014 (Schimmack, 2014). The blog post reports a meta-analysis of ego-depletion studies that used the hand-grip paradigm. When I first heard about the hand-grip paradigm, I thought it was stupid because there is so much between-subject variance in physical strength. However, then I learned that it is the only paradigm that uses a pre-post design, which removes between-subject variance from the error term. This made the hand-grip paradigm the most interesting paradigm because it has the highest power to detect ego-depletion effects. I conducted a meta-analysis of the hand-grip studies and found clear evidence of publication bias. This finding is very damaging to the wider ego-depletion research because other studies used between-subject designs with small samples which have very low power to detect small effects.
This prediction was confirmed in meta-analyses by Carter,E.C., Kofler, L.M., Forster, D.E., and McCulloch,M.E. (2015) that revealed publication bias in ego-depletion studies with other paradigms.
The results also explain why attempts to show ego-depletion effects with within-subject designs failed (Francis et al., 2018). Within-subject designs increase power by removing fixed between-subject variance such as physical strength. However, given the lack of evidence with the hand-grip paradigm it is not surprising that within-subject designs also failed to show ego-depletion effects with other dependent variables in within-subject designs. Thus, these results further suggest that ego-depletion effects are too small to be used for experimental investigations of will-power.
Of course, Roy F. Baumeister doesn’t like this conclusion because his reputation is to a large extent based on the resource model of will-power. His response to the evidence that most of the evidence is based on questionable practices that produced illusory evidence has been to attack the critics (cf. Schimmack, 2019).
In 2016, he paid to publish a critique of Carter’s (2015) meta-analysis in Frontiers of Psychology (Cunningham & Baumeister, 2016). In this article, the authors question the results obtained by bias-tests that reveal publication bias and suggest that there is no evidence for ego-depletion effects.
Unfortunately, Cunningham and Baumeister’s (2016) article is cited frequently as if it contained some valid scientific arguments.
For example, Christodoulou, Lac, and Moore (2017) cite the article to dismiss the results of a PEESE analysis that suggests publication bias is present and there is no evidence that infants can add and subtract. Thus, there is a real danger that meta-analysts will use Cunningham & Baumeister’s (2016) article to dismiss evidence of publication bias and to provide false evidence for claims that rest on questionable research practices.
Fact Checking Cunningham and Baumeister’s Criticisms
Cunningham and Baumeister (2016) claim that results from bias tests are difficult to interpret, but there criticism is based on false arguments and inaccurate claims.
Confusing Samples and Populations
This scientifically sounding paragraph is a load of bull. The authors claim that inferential tests require sampling from a population and raise a question about the adequacy of a sample. However, bias tests do not work this way. They are tests of the population, namely the population of all of the studies that could be retrieved that tested a common hypothesis (e.g., all handgrip studies of ego-depletion). Maybe more studies exist than are available. Maybe the results based on the available studies differ from results if all studies were available, but that is irrelevant. The question is only whether the available studies are biased or not. So, why do we even test for significance? That is a good question. The test for significance only tells us whether bias is merely a product of random chance or whether it was introduced by questionable research practices. However, even random bias is bias. If a set of studies reports only significant results, and the observed power of the studies is only 70%, there is a discrepancy. If this discrepancy is not statistically significant, there is still a discrepancy. If it is statistically significant, we are allowed to attribute it to questionable research practices such as those that Baumeister and several others admitted using.
“We did run multiple studies, some of which did not work, and some of which worked better than others. You may think that not reporting the less successful studies is wrong, but that is how the field works.” (Roy Baumeister, personal email communication) (Schimmack, 2014).
Given the widespread use of questionable research practices in experimental social psychology, it is not surprising that bias-tests reveal bias. It is actually more surprising when these tests fail to reveal bias, which is most likely a problem of low statistical power (Renkewitz & Keiner, 2019).
Misunderstanding Power
The claims about power are not based on clearly defined constructs in statistics. Statistical power is a function of the strength of a signal (the population effect size) and the amount of noise (sampling error). Researches skills are not a part of statistical power. Results should be independent of a researcher. A researcher could of course pick procedures that maximize a signal (powerful interventions) or reduce sampling error (e.g., pre-post designs), but these factors play a role in the designing of a study. Once a study is carried out, the population effect size is what it was and the sampling error is what it was. Thus, honestly reported test statistics tell us about the signal-to-noise ratio in a study that was conducted. Skillful researchers would produce stronger test-statistics (higher t-values, F-values) than unskilled researchers. The problem for Baumeister and other ego-depletion researchers is that the t-values and F-values tend to be weak and suggest questionable research practices rather than skill produced significant results. In short, meta-analysis of test-statistics reveal whether researchers used skill or questionable research practices to produce significant results.
The reference to Morey (2013) suggests that there is a valid criticism of bias tests, but that is not the case. Power-based bias tests are based on sound statistical principles that were outlined by a statistician in the journal American Statistician (Sterling, Rosenbaum, & Weinkam, 1995). Building on this work, Jerry Brunner (professor of statistics) and I published theorems that provide the basis of bias tests like TES to reveal the use of questionable research practices (Brunner & Schimmack, 2019). The real challenge for bias tests is to estimate mean power without information about the population effect sizes. In this regard, TES is extremely conservative because it relies on a meta-analysis of observed effect sizes to estimate power. These effect sizes are inflated when questionable research practices were used, which makes the test conservative. However, there is a problem with TES when effect sizes are heterogeneous. This problem is avoided by alternative bias tests like the R-Index that I used to demonstrate publication bias in the handgrip studies of ego-depletion. In sum, bias tests like the R-Index and TES are based on solid mathematical foundations and simulation studies show that they work well in detecting the use of questionable research practices.
Confusing Absence of Evidence with Evidence of Absence
PET and PEESE are extension of Eggert’s regression test of publication bias. All methods relate sample sizes (or sampling error) to effect size estimates. Questionable research practices tend to introduce a negative correlation between sample size and effect sizes or a positive correlation between sampling error and effect sizes. The reason is that significance requires a signal to noise ratio of 2:1 for t-tests or 4:1 for F-tests to produce a significant result. To achieve this ratio with more noise (smaller sample, more sampling error), the signal has to be inflated more.
The novel contribution of PET and PEESE was to use the intercept of the regression model as an effect size estimate that corrects for publication bias. This estimate needs to be interpreted in the context of the sampling error of the regression model, using a 95%CI around the point estimate.
Carter et al. (2015) found that the 95%CI often included a value of zero, which implies that the data are too weak to reject the null-hypothesis. Such non-significant results are notoriously difficult to interpret because they neither support nor refute the null-hypothesis. The main conclusion that can be drawn from this finding is that the existing data are inconclusive.
This main conclusion does not change when the number of studies is less than 20. Stanley and Doucouliagos (2014) were commenting on the trustworthiness of point estimates and confidence intervals in smaller samples. Smaller samples introduce more uncertainty and we should be cautious in the interpretation of results that suggest there is an effect because the assumptions of the model are violated. However, if the results already show that there is no evidence, small samples merely further increase uncertainty and make the existing evidence even less conclusive.
Aside from the issues regarding the interpretation of the intercept, Cunningham and Baumeister also fail to address the finding that sample sizes and effect sizes were negatively correlated. If this negative correlation is not caused by questionable research practices, it must be caused by something else. Cunningham and Baumeister fail to provide an answer to this important question.
No Evidence of Flair and Skill
Earlier Cunningham and Baumeister (2016) claimed that power depends on researchers’ skills and they argue that new investigators may be less skilled than the experts who developed paradigms like Baumeister and colleagues.
However, they then point out that Carter et al.’s (2015) examined lab as a moderator and found no difference between studies conducted by Baumeister and colleagues or other laboratories.
Thus, there is no evidence whatsoever that Baumeister and colleagues were more skillful and produced more credible evidence for ego-depletion than other laboratories. The fact that everybody got ego-depletion effects can be attributed to the widespread use of questionable research practices that made it possible to get significant results even for implausible phenomena like extrasensory perception (John et al., 2012; Schimmack, 2012). Thus, the large number of studies that support ego-depletion merely shows that everybody used questionable research practices like Baumeister did (Schimmack, 2014; Schimmack, 2016), which is also true for many other areas of research in experimental social psychology (Schimmack, 2019). Francis (2014) found that 80% of articles showed evidence that QRPs were used.
Handgrip Replicability Analysis
The meta-analysis included 18 effect sizes based on handgrip studies. Two unpublished studies (Ns = 24, 37) were not included in this analysis. Seeley & Gardner (2003)’s study was excluded because it failed to use a pre-post design, which could explain the non-significant result. The meta-analysis reported two effect sizes for this study. Thus, 4 effects were excluded and the analysis below is based on the remaining 14 studies.
All articles presented significant effects of will-power manipulations on handgrip performance. Bray et al. (2008) reported three tests; one was deemed not significant (p = .10), one marginally significant (.06), and one was significant at p = .05 (p = .01). The results from the lowest p-value were used. As a result, the success rate was 100%.
Median observed power was 63%. The inflation rate is 37% and the R-Index is 26%. An R-Index of 22% is consistent with a scenario in which the null-hypothesis is true and all reported findings are type-I errors. Thus, the R-Index supports Carter and McCullough’s (2014) conclusion that the existing evidence does not provide empirical support for the hypothesis that will-power manipulations lower performance on a measure of will-power.
The R-Index can also be used to examine whether a subset of studies provides some evidence for the will-power hypothesis, but that this evidence is masked by the noise generated by underpowered studies with small samples. Only 7 studies had samples with more than 50 participants. The R-Index for these studies remained low (20%). Only two studies had samples with 80 or more participants. The R-Index for these studies increased to 40%, which is still insufficient to estimate an unbiased effect size.
One reason for the weak results is that several studies used weak manipulations of will-power (e.g., sniffing alcohol vs. sniffing water in the control condition). The R-Index of individual studies shows two studies with strong results (R-Index > 80). One study used a physical manipulation (standing one leg). This manipulation may lower handgrip performance, but this effect may not reflect an influence on will-power. The other study used a mentally taxing (and boring) task that is not physically taxing as well, namely crossing out “e”s. This task seems promising for a replication study.
Power analysis with an effect size of d = .2 suggests that a serious empirical test of the will-power hypothesis requires a sample size of N = 300 (150 per cell) to have 80% power in a pre-post study of will-power.
Conclusion
Baumeister has lost any credibility as a scientist. He is pretending to engage in a scientific dispute about the validity of ego-depletion research, but he is ignoring the most obvious evidence that has accumulated during the past decade. Social psychologists have misused the scientific method and engaged in a silly game of producing significant p-values that support their claims. Data were never used to test predictions and studies that failed to support hypotheses were not published.
“We did run multiple studies, some of which did not work, and some of which worked better than others. You may think that not reporting the less successful studies is wrong, but that is how the field works.” (Roy Baumeister, personal email communication)
As a result, the published record lacks credibility and cannot be used to provide empirical evidence for scientific claims. Ego-depletion is a glaring example of everything that went wrong in experimental social psychology. This is not surprising because Baumeister and his students used questionable research practices more than other social psychologists (Schimmack, 2018). Now he is trying to to repress this truth, which should not surprise any psychologist familiar with motivated biases and repressive coping. However, scientific journals should not publish his pathetic attempts to dismiss criticism of his work. Cunningham and Baumeister’s article provides not a single valid scientific argument. Frontiers of Psychology should retract the article.
References
Carter,E.C.,Kofler,L.M.,Forster,D.E.,and McCulloch,M.E. (2015).A series of meta-analytic tests of the depletion effect: Self-control does not seem to rely on a limited resource. J. Exp.Psychol.Gen. 144, 796–815. doi:10.1037/xge0000083
Yuan, K.-H., & Maxwell, S. (2005). On the Post Hoc Power in Testing Mean Differences. Journal of Educational and Behavioral Statistics, 141–167
This blog post provides an accessible introduction to the concept of observed power. Most of the statistical points are based on based on Yuan and Maxwell’s (2005 excellent but highly technical article about post-hoc power. This bog post tries to explain statistical concepts in more detail and uses simulation studies to illustrate important points.
What is Power?
Power is defined as the long-run probability of obtaining significant results in a series of exact replication studies. For example, 50% power means that a set of 100 studies is expected to produce 50 significant results and 50 non-significant results. The exact numbers in an actual set of studies will vary as a function of random sampling error, just like 100 coin flips are not always going to produce a 50:50 split of heads and tails. However, as the number of studies increases, the percentage of significant results will be ever closer to the power of a specific study.
A priori power
Power analysis can be useful for the planning of sample sizes before a study is being conducted. A power analysis that is being conducted before a study is called a priori power analysis (before = a priori). Power is a function of three parameters: the actual effect size, sampling error, and the criterion value that needs to be exceeded to claim statistical significance. In between-subject designs, sampling error is determined by sample size alone. In this special case, power is a function of the true effect size, the significance criterion and sample size.
The problem for researchers is that power depends on the effect size in the population (e.g., the true correlation between height and weight amongst Canadians in 2015). The population effect size is sometimes called the true effect size. Imagine that somebody would actually obtain data from everybody in a population. In this case, there is no sampling error and the correlation is the true correlation in the population. However, typically researchers use much smaller samples and the goal is to estimate the correlation in the population on the basis of a smaller sample. Unfortunately, power depends on the correlation in the population, which is unknown to a researcher planning a study. Therefore, researchers have to estimate the true effect size to compute an a priori power analysis.
Cohen (1988) developed general guidelines for the estimation of effect sizes. For example, in studies that compare the means of two groups, a standardized difference of half a standard deviation (e.g., 7.5 IQ points on an iQ scale with a standard deviation of 15) is considered a moderate effect. Researchers who assume that their predicted effect has a moderate effect size, can use d = .5 for an a priori power analysis. Assuming that they want to claim significance with the standard criterion of p < .05 (two-tailed), they would need N = 210 (n =105 per group) to have a 95% chance to obtain a significant result (GPower). I do not discuss a priori power analysis further because this blog post is about observed power. I merely introduced a priori power analysis to highlight the difference between a priori power analysis and a posteriori power analysis, which is the main topic of Yuan and Maxwell’s (2005) article.
A Posteriori Power Analysis: Observed Power
Observed power computes power after a study or several studies have been conducted. The key difference between a priori and a posteriori power analysis is that a posteriori power analysis uses the observed effect size in a study as an estimate of the population effect size. For example, assume a researcher found a correlation of r = .54 in a sample of N = 200 Canadians. Instead of guessing the effect size, the researcher uses the correlation observed in this sample as an estimate of the correlation in the population. There are several reasons why it might be interesting to conduct a power analysis after a study. First, the power analysis might be used to plan a follow up or replication study. Second, the power analysis might be used to examine whether a non-significant result might be the result of insufficient power. Third, observed power is used to examine whether a researcher used questionable research practices to produce significant results in studies that had insufficient power to produce significant results.
In sum, observed power is an estimate of the power of a study based on the observed effect size in a study. It is therefore not power that is being observed, but the effect size that is being observed. However, because the other parameters that are needed to compute power are known (sample size, significance criterion), the observed effect size is the only parameter that needs to be observed to estimate power. However, it is important to realize that observed power does not mean that power was actually observed. Observed power is still an estimate based on an observed effect size because power depends on the effect size in the population (which remains unobserved) and the observed effect size in a sample is just an estimate of the population effect size.
A Posteriori Power Analysis after a Single Study
Yuan and Maxwell (2005) examined the statistical properties of observed power. The main question was whether it is meaningful to compute observed power based on the observed effect size in a single study.
The first statistical analysis of an observed mean difference is to examine whether the study produced a significant result. For example, the study may have examined whether music lessons produce an increase in children’s IQ. The study had 95% power to produce a significant difference with N = 176 participants and a moderate effect size (d = .5; IQ = 7.5).
One possibility is that the study actually produced a significant result. For example, the observed IQ difference was 5 IQ points. This is less than the expected difference of 7.5 points and corresponds to a standardized effect size of d = .3. Yet, the t-test shows a highly significant difference between the two groups, t(208) = 3.6, p = 0.0004 (1 / 2513). The p-value shows that random sampling error alone would produce differences of this magnitude or more in only 1 out of 2513 studies. Importantly, the p-value only makes it very likely that the intervention contributed to the mean difference, but it does not provide information about the size of the effect. The true effect size may be closer to the expected effect size of 7.5 or it may be closer to 0. The true effect size remains unknown even after the mean difference between the two groups is observed. Yet, the study provides some useful information about the effect size. Whereas the a priori power analysis relied exclusively on guess-work, observed power uses the effect size that was observed in a reasonably large sample of 210 participants. Everything else being equal, effect size estimates based on 210 participants are more likely to match the true effect size than those based on 0 participants.
The observed effect size can be entered into a power analysis to compute observed power. In this example, observed power with an effect size of d = .3 and N = 210 (n = 105 per group) is 58%. One question examined by Yuan and Maxwell (2005) is whether it can be useful to compute observed power after a study produced a significant result.
The other question is whether it can be useful to compute observed power when a study produced a non-significant result. For example, assume that the estimate of d = 5 is overly optimistic and that the true effect size of music lessons on IQ is a more modest 1.5 IQ points (d = .10, one-tenth of a standard deviation). The actual mean difference that is observed after the study happens to match the true effect size exactly. The difference between the two groups is not statistically significant, t(208) = .72, p = .47. A non-significant result is difficult to interpret. On the one hand, the means trend in the right direction. On the other hand, the mean difference is not statistically significant. The p-value suggests that a mean difference of this magnitude would occur in every second study by chance alone even if music intervention had no effect on IQ at all (i.e., the true effect size is d = 0, the null-hypothesis is true). Statistically, the correct conclusion is that the study provided insufficient information regarding the influence of music lessons on IQ. In other words, assuming that the true effect size is closer to the observed effect size in a sample (d = .1) than to the effect size that was used to plan the study (d = .5), the sample size was insufficient to produce a statistically significant result. Computing observed power merely provides some quantitative information to reinforce this correct conclusion. An a posteriori power analysis with d = .1 and N = 210, yields an observed power of 11%. This suggests that the study had insufficient power to produce a significant result, if the effect size in the sample matches the true effect size.
Yuan and Maxwell (2005) discuss false interpretations of observed power. One false interpretation is that a significant result implies that a study had sufficient power. Power is a function of the true effect size and observed power relies on effect sizes in a sample. 50% of the time, effect sizes in a sample overestimate the true effect size and observed power is inflated. It is therefore possible that observed power is considerably higher than the actual power of a study.
Another false interpretation is that low power in a study with a non-significant result means that the hypothesis is correct, but that the study had insufficient power to demonstrate it. The problem with this interpretation is that there are two potential reasons for a non-significant result. One of them, is that a study had insufficient power to show a significant result when an effect is actually present (this is called the type-II error). The second possible explanation is that the null-hypothesis is actually true (there is no effect). A non-significant result cannot distinguish between these two explanations. Yet, it remains true that the study had insufficient power to test these hypotheses against each other. Even if a study had 95% power to show an effect if the true effect size is d = .5, it can have insufficient power if the true effect size is smaller. In the example, power decreased from 95% assuming d = .5, to 11% assuming d = .1.
Yuan and Maxell’s Demonstration of Systematic Bias in Observed Power
Yuan and Maxwell focus on a design in which a sample mean is compared against a population mean and the standard deviation is known. To modify the original example, a researcher could recruit a random sample of children, do a music lesson intervention and test the IQ after the intervention against the population mean of 100 with the population standard deviation of 15, rather than relying on the standard deviation in a sample as an estimate of the standard deviation. This scenario has some advantageous for mathematical treatments because it uses the standard normal distribution. However, all conclusions can be generalized to more complex designs. Thus, although Yuan and Maxwell focus on an unusual design, their conclusions hold for more typical designs such as the comparison of two groups that use sample variances (standard deviations) to estimate the variance in a population (i.e., pooling observed variances in both groups to estimate the population variance).
Yuan and Maxwell (2005) also focus on one-tailed tests, although the default criterion in actual studies is a two-tailed test. Once again, this is not a problem for their conclusions because the two-tailed criterion value for p = .05 is equivalent to the one-tailed criterion value for p = .025 (.05 / 2). For the standard normal distribution, the value is z = 1.96. This means that an observed z-score has to exceed a value of 1.96 to be considered significant.
To illustrate this with an example, assume that the IQ of 100 children after a music intervention is 103. After subtracting the population mean of 100 and dividing by the standard deviation of 15, the effect size is d = 3/15 = .2. Sampling error is defined by 1 / sqrt (n). With a sample size of n = 100, sampling error is .10. The test-statistic (z) is the ratio of the effect size and sampling error (.2 / .1) = 2. A z-score of 2 is just above the critical value of 2, and would produce a significant result, z = 2, p = .023 (one-tailed; remember criterion is .025 one-tailed to match .05 two-tailed). Based on this result, a researcher would be justified to reject the null-hypothesis (there is no effect of the intervention) and to claim support for the hypothesis that music lessons lead to an increase in IQ. Importantly, this hypothesis makes no claim about the true effect size. It merely states that the effect is greater than zero. The observed effect size in the sample (d = .2) provides an estimate of the actual effect size but the true effect size can be smaller or larger than the effect size in the sample. The significance test merely rejects the possibility that the effect size is 0 or less (i.e., music lessons lower IQ).
Entering a non-centrality parameter of 3 for a generic z-test in G*power yields the following illustration of a non-central distribution.
Illustration of non-central distribution using G*Power output
The red curve shows the standard normal distribution for the null-hypothesis. With d = 0, the non-centrality parameter is also 0 and the standard normal distribution is centered over zero.
The blue curve shows the non-central distribution. It is the same standard normal distribution, but now it is centered over z = 3. The distribution shows how z-scores would be distributed for a set of exact replication studies, where exact replication studies are defined as studies with the same true effect size and sampling error.
The figure also illustrates power by showing the critical z-score of 1.96 with a green line. On the left side are studies where sampling error reduced the observed effect size so much that the z-score was below 1.96 and produced a non-significant result (p > .025 one-tailed, p > .05, two-tailed). On the right side are studies with significant results. The area under the curve on the left side is called type-II error or beta-error). The area under the curve on the right side is called power (1 – type-II error). The output shows that beta error probability is 15% and Power is 85%.
In sum, the formula
states that power for a given true effect size is the area under the curve to the right side of a critical z-score for a standard normal distribution that is centered over the non-centrality parameter that is defined by the ratio of the true effect size over sampling error.
[personal comment: I find it odd that sampling error is used on the right side of the formula but not on the left side of the formula. Power is a function of the non-centrality parameter and not just the effect size. Thus I would have included sqrt (n) also on the left side of the formula].
Because the formula relies on the true effect size, it specifies true power given the (unknown) population effect size. To use it for observed power, power has to be estimated based on the observed effect size in a sample.
The important novel contribution of Yuan and Maxwell (2005) was to develop a mathematical formula that relates observed power to true power and to find a mathematical formula for the bias in observed power.
The formula implies that the amount of bias is a function of the unknown population effect size. Yuan and Maxwell make several additional observations about bias. First, bias is zero when true power is 50%. The second important observation is that systematic bias is never greater than 9 percentage points. The third observation is that power is overestimated when true power is less than 50% and underestimated when true power is above 50%. The last observation has important implications for the interpretation of observed power.
50% power implies that the test statistic matches the criterion value. For example, if the criterion is p < .05 (two-tailed), 50% power is equivalent to p = .05. If observed power is less than 50%, a study produced a non-significant result. A posteriori power analysis might suggest that observed power is only 40%. This finding suggests that the study was underpowered and that a more powerful study might produce a significant result. Systematic bias implies that the estimate of 40% is more likely to be an overestimation than an underestimation. As a result, bias does not undermine the conclusion. Rather observed power is conservative because the actual power is likely to be even less than 40%.
The alternative scenario is that observed power is greater than 50%, which implies a significant result. In this case, observed power might be used to argue that a study had sufficient power because it did produce a significant result. Observed power might show, however, that observed power is only 60%. This would indicate that there was a relatively high chance to end up with a non-significant result. However, systematic bias implies that observed power is more likely to underestimate true power than to overestimate it. Thus, true power is likely to be higher. Again, observed power is conservative when it comes to the interpretation of power for studies with significant results. This would suggest that systematic bias is not a serious problem for the use of observed power. Moreover, the systematic bias is never more than 9 percentage-points. Thus, observed power of 60% cannot be systematically inflated to more than 70%.
In sum, Yuan and Maxwell (2005) provided a valuable analysis of observed power and demonstrated analytically the properties of observed power.
Practical Implications of Yuan and Maxwell’s Findings
Based on their analyses, Yuan and Maxwell (2005) draw the following conclusions in the abstract of their article.
Using analytical, numerical, and Monte Carlo approaches, our results show that the estimated power does not provide useful information when the true power is small. It is almost always a biased estimator of the true power. The bias can be negative or positive. Large sample size alone does not guarantee the post hoc power to be a good estimator of the true power.
Unfortunately, other scientists often only read the abstract, especially when the article contains mathematical formulas that applied scientists find difficult to follow. As a result, Yuan and Maxwell’s (2005) article has been cited mostly as evidence that it observed power is a useless concept. I think this conclusion is justified based on Yuan and Maxwell’s abstract, but it does not follow from Yuan and Maxwell’s formula of bias. To make this point, I conducted a simulation study that paired 25 sample sizes (n = 10 to n = 250) and 20 effect sizes (d = .05 to d = 1) to create 500 non-centrality parameters. Observed effect sizes were randomly generated for a between-subject design with two groups (df = n*2 – 2). For each non-centrality parameter, two simulations were conducted for a total of 1000 studies with heterogeneous effect sizes and sample sizes (standard errors). The results are presented in a scatterplot with true power on the x-axis and observed power on the y-axis. The blue line shows prediction of observed power from true power. The red curve shows the biased prediction based on Yuan and Maxwell’s bias formula.
The most important observation is that observed power varies widely as a function of random sampling error in the observed effect sizes. In comparison, the systematic bias is relatively small. Moreover, observed power at the extremes clearly distinguishes between low powered (< 25%) and high powered (> 80%) power. Observed power is particularly informative when it is close to the maximum value of 100%. Thus, observed power of 99% or more strongly suggests that a study had high power. The main problem for posteriori power analysis is that observed effect sizes are imprecise estimates of the true effect size, especially in small samples. The next section examines the consequences of random sampling error in more detail.
Standard Deviation of Observed Power
Awareness has been increasing that point estimates of statistical parameters can be misleading. For example, an effect size of d = .8 suggests a strong effect, but if this effect size was observed in a small sample, the effect size is strongly influenced by sampling error. One solution to this problem is to compute a confidence interval around the observed effect size. The 95% confidence interval is defined by sampling error times 1.96; approximately 2. With sampling error of .4, the confidence interval could range all the way from 0 to 1.6. As a result, it would be misleading to claim that an effect size of d = .8 in a small sample suggests that the true effect size is strong. One solution to this problem is to report confidence intervals around point estimates of effect sizes. A common confidence interval is the 95% confidence interval. A 95% confidence interval means that there is a 95% probability that the population effect size is contained in the 95% confidence interval around the (biased) effect size in a sample.
To illustrate the use of confidence interval, I computed the confidence interval for the example of music training and IQ in children. The example assumes that the IQ of 100 children after a music intervention is 103. After subtracting the population mean of 100 and dividing by the standard deviation of 15, the effect size is d = 3/15 = .2. Sampling error is defined by 1 / sqrt (n). With a sample size of n = 100, sampling error is .10. To compute a 95% confidence interval, sampling error is multiplied with the z-scores that capture 95% of a standard normal distribution, which is 1.96. As sampling error is .10, the values are -.196 and .196. Given an observed effect size of d = .2, the 95% confidence interval ranges from .2 – .196 = .004 to .2 + .196 = .396.
A confidence interval can be used for significance testing by examining whether the confidence interval includes 0. If the 95% confidence interval does not include zero, it is possible to reject the hypothesis that the effect size in the population is 0, which is equivalent to rejecting the null-hypothesis. In the example, the confidence interval ends at d = .004, which implies that the null-hypothesis can be rejected. At the upper end, the confidence interval ends at d = .396. This implies that the empirical results also would reject hypotheses that the population effect size is moderate (d = .5) or strong (d = .8).
Confidence intervals around effect sizes are also useful for posteriori power analysis. Yuan and Maxwell (2005) demonstrated that confidence interval of observed power is defined by the observed power of the effect sizes that define the confidence interval of effect sizes.
The figure below illustrates the observed power for the lower bound of the confidence interval in the example of music lessons and IQ (d = .004).
The figure shows that the non-central distribution (blue) and the central distribution (red) nearly perfectly overlap. The reason is that the observed effect size (d = .004) is just slightly above the d-value of the central distribution when the effect size is zero (d = .000). When the null-hypothesis is true, power equals the type-I error rate (2.5%) because 2.5% of studies will produce a significant result by chance alone and chance is the only factor that produces significant results. When the true effect size is d = .004, power increases to 2.74 percent.
Remember that this power estimate is based on the lower limit of a 95% confidence interval around the observed power estimate of 50%. Thus, this result means that there is a 95% probability that the true power of the study is 2.5% when observed power is 50%.
The next figure illustrates power for the upper limit of the 95% confidence interval.
In this case, the non-central distribution and the central distribution overlap very little. Only 2.5% of the non-central distribution is on the left side of the criterion value, and power is 97.5%. This finding means that there is a 95% probability that true power is not greater than 97.5% when observed power is 50%.
Taken these results together, the results show that the 95% confidence interval around an observed power estimate of 50% ranges from 2.5% to 97.5%. As this interval covers pretty much the full range of possible values, it follows that observed power of 50% in a single study provides virtually no information about the true power of a study. True power can be anywhere between 2.5% and 97.5% percent.
The next figure illustrates confidence intervals for different levels of power.
The data are based on the same simulation as in the previous simulation study. The green line is based on computation of observed power for the d-values that correspond to the 95% confidence interval around the observed (simulated) d-values.
The figure shows that confidence intervals for most observed power values are very wide. The only accurate estimate of observed power can be achieved when power is high (upper right corner). But even 80% true power still has a wide confidence interval where the lower bound is below 20% observed power. Firm conclusions can only be drawn when observed power is high.
For example, when observed power is 95%, a one-sided 95% confidence interval (guarding only against underestimation) has a lower bound of 50% power. This finding would imply that observing power of 95% justifies the conclusion that the study had at least 50% power with an error rate of 5% (i.e., in 5% of the studies the true power is less than 50%).
The implication is that observed power is useless unless observed power is 95% or higher.
In conclusion, consideration of the effect of random sampling error on effect size estimates provides justification for Yuan and Maxwell’s (2005) conclusion that computation of observed power provides relatively little value. However, the reason is not that observed power is a problematic concept. The reason is that observed effect sizes in underpowered studies provide insufficient information to estimate observed power with any useful degree of accuracy. The same holds for the reporting of observed effect sizes that are routinely reported in research reports and for point estimates of effect sizes that are interpreted as evidence for small, moderate, or large effects. None of these statements are warranted when the confidence interval around these point estimates is taken into account. A study with d = .80 and a confidence interval of d = .01 to 1.59 does not justify the conclusion that a manipulation had a strong effect because the observed effect size is largely influenced by sampling error.
In conclusion, studies with large sampling error (small sample sizes) are at best able to determine the sign of a relationship. Significant positive effects are likely to be positive and significant negative effects are likely to be negative. However, the effect sizes in these studies are too strongly influenced by sampling error to provide information about the population effect size and therewith about parameters that depend on accurate estimation of population effect sizes like power.
Meta-Analysis of Observed Power
One solution to the problem of insufficient information in a single underpowered study is to combine the results of several underpowered studies in a meta-analysis. A meta-analysis reduces sampling error because sampling error creates random variation in effect size estimates across studies and aggregation reduces the influence of random factors. If a meta-analysis of effect sizes can produce more accurate estimates of the population effect size, it would make sense that meta-analysis can also increase the accuracy of observed power estimation.
Yuan and Maxwell (2005) discuss meta-analysis of observed power only briefly.
A problem in a meta-analysis of observed power is that observed power is not only subject to random sampling error, but also systematically biased. As a result, the average of observed power across a set of studies would also be systematically biased. However, the reason for the systematic bias is the non-symmetrical distribution of observed power when power is not 50%. To avoid this systematic bias, it is possible to compute the median. The median is unbiased because 50% of the non-central distribution is on the left side of the non-centrality parameter and 50% is on the right side of the non-centrality parameter. Thus, the median provides an unbiased estimate of the non-centrality parameter and the estimate becomes increasingly accurate as the number of studies in a meta-analysis increases.
The next figure shows the results of a simulation with the same 500 studies (25 sample sizes and 20 effect sizes) that were simulated earlier, but this time each study was simulated to be replicated 1,000 times and observed power was estimated by computing the average or the median power across the 1,000 exact replication studies.
Purple = average observed power; Orange = median observed power
The simulation shows that Yuan and Maxwell’s (2005) bias formula predicts the relationship between true power and the average of observed power. It also confirms that the median is an unbiased estimator of true power and that observed power is a good estimate of true power when the median is based on a large set of studies. However, the question remains whether observed power can estimate true power when the number of studies is smaller.
The next figure shows the results for a simulation where estimated power is based on the median observed power in 50 studies. The maximum discrepancy in this simulation was 15 percentage points. This is clearly sufficient to distinguish low powered studies (<50% power) from high powered studies (>80%).
To obtain confidence intervals for median observed power estimates, the power estimate can be converted into the corresponding non-centrality parameter of a standard normal distribution. The 95% confidence interval is defined as the standard deviation divided by the square root of the number of studies. The standard deviation of a standard normal distribution equals 1. Hence, the 95% confidence interval for a set of studies is defined by
Lower Limit = Normal (InverseNormal (power) – 1.96 / sqrt(k))
Upper Limit = Normal (inverseNormal(power) + 1.96 / sqrt(k))
Interestingly, the number of observations in a study is irrelevant. The reason is that larger samples produce smaller confidence intervals around an effect size estimate and increase power at the same time. To hold power constant, the effect size has to decrease and power decreases exponentially as effect sizes decrease. As a result, observed power estimates do not become more precise when sample sizes increase and effect sizes decrease proportionally.
The next figure shows simulated data for 1000 studies with 20 effect sizes (0.05 to 1) and 25 sample sizes (n = 10 to 250). Each study was repeated 50 times and the median value was used to estimate true power. The green lines are the 95% confidence interval around the true power value. In real data, the confidence interval would be drawn around observed power, but observed power does not provide a clear mathematical function. The 95% confidence interval around the true power values is still useful because it predicts how much observed power estimates can deviate from true power. 95% of observed power values are expected to be within the area that is defined by lower and upper bound of the confidence interval. The Figure shows that most values are within the area. This confirms that sampling error in a meta-analysis of observed power is a function of the number of studies. The figure also shows that sampling error is greatest when power is 50%. In the tails of the distribution range restriction produces more precise estimates more quickly.
With 50 studies, the maximum absolute discrepancy is 15 percentage points. This level of precision is sufficient to draw broad conclusions about the power of a set of studies. For example, any median observed power estimate below 65% is sufficient to reveal that a set of studies had less power than Cohen’s recommended level of 80% power. A value of 35% would strongly suggest that a set of studies was severely underpowered.
Conclusion
Yuan and Maxwell (2005) provided a detailed statistical examination of observed power. They concluded that observed power typically provides little to no useful information about the true power of a single study. The main reason for this conclusion was that sampling error in studies with low power is too large to estimate true power with sufficient precision. The only precise estimate of power can be obtained when sampling error is small and effect sizes are large. In this case, power is near the maximum value of 1 and observed power correctly estimates true power as being close to 1. Thus, observed power can be useful when it suggests that a study had high power.
Yuan and Maxwell’s (2005) also showed that observed power is systematically biased unless true power is 50%. The amount of bias is relatively small and even without this systematic bias, the amount of random error is so large that observed power estimates based on a single study cannot be trusted.
Unfortunately, Yuan and Maxwell’s (2005) article has been misinterpreted as evidence that observed power calculations are inherently biased and useless. However, observed power can provide useful and unbiased information in a meta-analysis of several studies. First, a meta-analysis can provide unbiased estimates of power because the median value is an unbiased estimator of power. Second, aggregation across studies reduces random sampling error, just like aggregation across studies reduces sampling error in meta-analyses of effect sizes.
Implications
The demonstration that median observed power provides useful information about true power is important because observed power has become a valuable tool in the detection of publication bias and other biases that lead to inflated estimates of effect sizes. Starting with Sterling, Rosenbaum, and Weinkam ‘s(1995) seminal article, observed power has been used by Ioannidis and Trikalinos (2007), Schimmack (2012), Francis (2012), Simonsohn (2014), and van Assen, van Aert, and Wicherts (2014) to draw inferences about a set of studies with the help of posteriori power analysis. The methods differ in the way observed data are used to estimate power, but they all rely on the assumption that observed data provide useful information about the true power of a set of studies. This blog post shows that Yuan and Maxwell’s (2005) critical examination of observed power does not undermine the validity of statistical approaches that rely on observed data to estimate power.
Future Directions
This blog post focussed on meta-analysis of exact replication studies that have the same population effect size and the same sample size (sampling error). It also assumed that the set of studies is a representative set of studies. An important challenge for future research is to examine the statistical properties of observed power when power varies across studies (heterogeneity) and when publication bias and other biases are present. A major limitation of existing methods is that these methods assume a fixed population effect size (Ioannidis and Trikalinos (2007), Francis (2012), Simonsohn (2014), and van Assen, van Aert, and Wicherts (2014). At present, the Incredibility index (Schimmack, 2012) and the R-Index (Schimmack, 2014) have been proposed as methods for sets of studies that are biased and heterogeneous. An important goal for future research is to evaluate these methods in simulation studies with heterogeneous and biased sets of data.
It has been known for decades that published results tend to be biased (Sterling, 1959). For most of the past decades this inconvenient truth has been ignored. In the past years, there have been many suggestions and initiatives to increase the replicability of reported scientific findings (Asendorpf et al., 2013). One approach is to examine published research results for evidence of questionable research practices (see Schimmack, 2014, for a discussion of existing tests). This blog post introduces a new test of bias in reported research findings, namely the Test of Insufficient Variance (TIVA).
TIVA is applicable to any set of studies that used null-hypothesis testing to conclude that empirical data provide support for an empirical relationship and reported a significance test (p-values).
Rosenthal (1978) developed a method to combine results of several independent studies by converting p-values into z-scores. This conversion uses the well-known fact that p-values correspond to the area under the curve of a normal distribution. Rosenthal did not discuss the relation between these z-scores and power analysis. Z-scores are observed scores that should follow a normal distribution around the non-centrality parameter that determines how much power a study has to produce a significant result. In the Figure, the non-centrality parameter is 2.2. This value is slightly above a z-score of 1.96, which corresponds to a two-tailed p-value of .05. A study with a non-centrality parameter of 2.2 has 60% power. In specific studies, the observed z-scores vary as a function of random sampling error. The standardized normal distribution predicts the distribution of observed z-scores. As observed z-scores follow the standard normal distribution, the variance of an unbiased set of z-scores is 1. The Figure on top illustrates this with the nine purple lines, which are nine randomly generated z-scores with a variance of 1.
In a real data set the variance can be greater than 1 for two reasons. First, if the nine studies are exact replication studies with different sample sizes, larger samples will have a higher non-centrality parameter than smaller samples. This variance in the true non-centrality variances adds to the variance produced by random sampling error. Second, a set of studies that are not exact replication studies can have variance greater than 1 because the true effect sizes can vary across studies. Again, the variance in true effect sizes produces variance in the true non-centrality parameters that add to the variance produced by random sampling error. In short, the variance is 1 in exact replication studies that also hold the sample size constant. When sample sizes and true effect sizes vary, the variance in observed z-scores is greater than 1. Thus, an unbiased set of z-scores should have a minimum variance of 1.
If the variance in z-scores is less than 1, it suggests that the set of z-scores is biased. One simple reason for insufficient variance is publication bias. If power is 50% and the non-centrality parameter matches the significance criterion of 1.96, 50% of studies that were conducted would not be significant. If these studies are omitted from the set of studies, variance decreases from 1 to .36. Another reason for insufficient variance is that researchers do not report non-significant results or used questionable research practices to inflate effect size estimates. The effect is that variance in observed z-scores is restricted. Thus, insufficient variance in observed z-scores reveals that the reported results are biased and provide an inflated estimate of effect size and replicability.
In small sets of studies, insufficient variance may be due to chance alone. It is possible to quantify how lucky a researcher was to obtain significant results with insufficient variance. This probability is a function of two parameters: (a) the ratio of the observed variance (OV) in a sample over the population variance (i.e., 1), and (b) the number of z-scores minus 1 as the degrees of freedom (k -1).
The product of these two parameters follows a chi-square distribution with k-1 degrees of freedom.
Formula 1: Chi-square = OV * (k – 1) with k-1 degrees of freedom.
Example 1:
Bem (2011) published controversial evidence that appear to demonstrate precognition. Subsequent studies failed to replicate these results (Galak et al.,, 2012) and other bias tests show evidence that the reported results are biased Schimmack (2012). For this reason, Bem’s article provides a good test case for TIVA.
The article reported results of 10 studies with 9 z-scores being significant at p < .05 (one-tailed). The observed variance in the 10 z-scores is 0.19. Using Formula 1, the chi-square value is chi^2 (df = 9) = 1.75. Importantly, chi-square tests are usually used to test whether variance is greater than expected by chance (right tail of the distribution). The reason is that variance is not expected to be less than the variance expected by chance because it is typically assumed that a set of data is unbiased. To obtain a probability of insufficient variance, it is necessary to test the left-tail of the chi-square distribution. The corresponding p-value for chi^2 (df = 9) = 1.75 is p = .005. Thus, there is only a 1 out of 200 probability that a random set of 10 studies would produce a variance as low as Var = .19.
This outcome cannot be attributed to publication bias because all studies were published in a single article. Thus, TIVA supports the hypothesis that the insufficient variance in Bem’s z-scores is the result of questionable research methods and that the reported effect size of d = .2 is inflated. The presence of bias does not imply that the true effect size is 0, but it does strongly suggest that the true effect size is smaller than the average effect size in a set of studies with insufficient variance.
Example 2:
Vohs et al. (2006) published a series of studies that he results of nine experiments in which participants were reminded of money. The results appeared to show that “money brings about a self-sufficient orientation.” Francis and colleagues suggested that the reported results are too good to be true. An R-Index analysis showed an R-Index of 21, which is consistent with a model in which the null-hypothesis is true and only significant results are reported.
Because Vohs et al. (2006) conducted multiple tests in some studies, the median p-value was used for conversion into z-scores. The p-values and z-scores for the nine studies are reported in Table 2. The Figure on top of this blog illustrates the distribution of the 9 z-scores relative to the expected standard normal distribution.
Table 2
Study p z
Study 1 .026 2.23
Study 2 .050 1.96
Study 3 .046 1.99
Study 4 .039 2.06
Study 5 .021 2.99
Study 6 .040 2.06
Study 7 .026 2.23
Study 8 .023 2.28
Study 9 .006 2.73
The variance of the 9 z-scores is .054. This is even lower than the variance in Bem’s studies. The chi^2 test shows that this variance is significantly less than expected from an unbiased set of studies, chi^2 (df = 8) = 1.12, p = .003. An unusual event like this would occur in only 1 out of 381 studies by chance alone.
In conclusion, insufficient variance in z-scores shows that it is extremely likely that the reported results overestimate the true effect size and replicability of the reported studies. This confirms earlier claims that the results in this article are too good to be true (Francis et al., 2014). However, TIVA is more powerful than the Test of Excessive Significance and can provide more conclusive evidence that questionable research practices were used to inflate effect sizes and the rate of significant results in a set of studies.
Conclusion
TIVA can be used to examine whether a set of published p-values was obtained with the help of questionable research practices. When p-values are converted into z-scores, the variance of z-scores should be greater or equal to 1. Insufficient variance suggests that questionable research practices were used to avoid publishing non-significant results; this includes simply not reporting failed studies.
At least within psychology, these questionable research practices are used frequently to compensate for low statistical power and they are not considered scientific misconduct by governing bodies of psychological science (APA, APS, SPSP). Thus, the present results do not imply scientific misconduct by Bem or Vohs, just like the use of performance enhancing drugs in sports is not illegal unless a drug is put on an anti-doping list. However, jut because a drug is not officially banned, it does not mean that the use of a drug has no negative effects on a sport and its reputation.
One limitation of TIVA is that it requires a set of studies and that variance in small sets of studies can vary considerably just by chance. Another limitation is that TIVA is not very sensitive when there is substantial heterogeneity in true non-centrality parameters. In this case, the true variance in z-scores can mask insufficient variance in random sampling error. For this reason, TIVA is best used in conjunction with other bias tests. Despite these limitations, the present examples illustrate that TIVA can be a powerful tool in the detection of questionable research practices. Hopefully, this demonstration will lead to changes in the way researchers view questionable research practices and how the scientific community evaluates results that are statistically improbable. With rejection rates at top journals of 80% or more, one would hope that in the future editors will favor articles that report results from studies with high statistical power that obtain significant results that are caused by the predicted effect.
In 1998 Baumeister and colleagues introduced a laboratory experiment to study will-power. Participants are assigned to one of two conditions. In one condition, participants have to exert will-power to work on an effortful task. The other condition is a control condition with a task that does not require will-power. After the manipulation all participants have to perform a second task that requires will-power. The main hypothesis is that participants who already used will-power on the first task will perform more poorly on the second task than participants in the control condition.
In 2010, a meta-analysis examined the results of studies that had used this paradigm (Hagger Wood, & Chatzisarantis, 2010). The meta-analysis uncovered 198 studies with a total of 10,782 participants. The overall effect size in the meta-analysis suggested strong support for the hypothesis with an average effect size of d = .62.
However, the authors of the meta-analysis did not examine the contribution of publication bias to the reported results. Carter and McCullough (2013) compared the percentage of significant results to average observed power. This test showed clear evidence that studies with significant results and inflated effect sizes were overrepresented in the meta-analysis. Carter and McCullough (2014) used meta-regression to examine bias (Stanley and Doucouliagos, 2013). This approach relies on the fact that several sources of reporting bias and publication bias produce a correlation between sampling error and effect size. When effect sizes are regressed on sampling error, the intercept provides an estimate of the unbiased effect size; that is the effect size when sampling error in the population when sampling error is zero. Stanley and Doucouliagos (2013) use two regression methods. One method uses sampling error as a predictor (PET). The other method uses the sampling error squared as a predictor (PEESE). Carter and McCullough (2013) used both methods. PET showed bias and there was no evidence for the key hypothesis. PEESE also showed evidence of bias, but suggested that the effect is present.
There are several problems with the regression-based approach as a way to correct for biases (Replication-Index, December 17, 2014). One problem is that other factors can produce a correlation between sampling error and effect sizes. In this specific case, it is possible that effect sizes vary across experimental paradigms. Hagger and Chatzisarantis (2014) use these problems to caution readers that it is premature to disregard an entire literature on ego-depletion. The R-Index can provide some additional information about the empirical foundation of ego-depletion theory.
The analyses here focus on the handgrip paradigm because this paradigm has high power to detect moderate to strong effects because these studies measured handgrip strengths before and after the manipulation of will-power. Based on published studies, it is possible to estimate the retest correlation of handgrip performance (r~ .8). Below are some a priori power analysis with common sample sizes and Cohen’s effect sizes of small, moderate, and large effect sizes.
The power analysis shows that the pre-post design is very powerful to detect moderate to large effect sizes. Even with a sample size of just 40 participants (20 per condition), power is 71%. If reporting bias and publication bias exclude 30% non-significant results from the evidence, observed power is inflated to 82%. The comparison of success rate (100%) and observed power (82%) leads to an estimated inflation rate of 18%) and an R-Index is 64% (82% – 18%). Thus a moderate effect size in studies with 40 or more participants is expected to produce an R-Index greater than 64%.
However, with typical sample sizes of less than 120 participants, the expected rate of significant results is less than 50%. With N = 80 and true power of 31%, the reporting of only significant results would boost the observed power to 64%. The inflation rate would be 30% and the R-Index would be 39%. In this case, the R-Index overestimates true power by 9%. Thus, an R-Index less than 50% suggests that the true effect size is small or that the null-hypothesis is true (importantly, the null-hypothesis refers to the effect in the handgrip-paradigm, not to the validity of the broader theory that it becomes more difficult to sustain effort over time).
R-Analysis
The meta-analysis included 18 effect sizes based on handgrip studies. Two unpublished studies (Ns = 24, 37) were not included in this analysis. Seeley & Gardner (2003)’s study was excluded because it failed to use a pre-post design, which could explain the non-significant result. The meta-analysis reported two effect sizes for this study. Thus, 4 effects were excluded and the analysis below is based on the remaining 14 studies.
All articles presented significant effects of will-power manipulations on handgrip performance. Bray et al. (2008) reported three tests; one was deemed not significant (p = .10), one marginally significant (.06), and one was significant at p = .05 (p = .01). The results from the lowest p-value were used. As a result, the success rate was 100%.
Median observed power was 63%. The inflation rate is 37% and the R-Index is 26%. An R-Index of 22% is consistent with a scenario in which the null-hypothesis is true and all reported findings are type-I errors. Thus, the R-Index supports Carter and McCullough’s (2014) conclusion that the existing evidence does not provide empirical support for the hypothesis that will-power manipulations lower performance on a measure of will-power.
The R-Index can also be used to examine whether a subset of studies provides some evidence for the will-power hypothesis, but that this evidence is masked by the noise generated by underpowered studies with small samples. Only 7 studies had samples with more than 50 participants. The R-Index for these studies remained low (20%). Only two studies had samples with 80 or more participants. The R-Index for these studies increased to 40%, which is still insufficient to estimate an unbiased effect size.
One reason for the weak results is that several studies used weak manipulations of will-power (e.g., sniffing alcohol vs. sniffing water in the control condition). The R-Index of individual studies shows two studies with strong results (R-Index > 80). One study used a physical manipulation (standing one leg). This manipulation may lower handgrip performance, but this effect may not reflect an influence on will-power. The other study used a mentally taxing (and boring) task that is not physically taxing as well, namely crossing out “e”s. This task seems promising for a replication study.
Power analysis with an effect size of d = .2 suggests that a serious empirical test of the will-power hypothesis requires a sample size of N = 300 (150 per cell) to have 80% power in a pre-post study of will-power.
Conclusion
The R-Index of 14 will-power studies with the powerful pre-post handgrip paradigm confirms Carter and McCullough’s (2014) conclusion that a meta-analysis of will-power studies (Hagger Wood, & Chatzisarantis, 2010) provided an inflated estimate of the true effect size and that the existing studies provide no empirical support for the effect of will-power manipulations on a second effortful task. The existing studies have insufficient statistical power to distinguish a true null-effect from a small effect (d = .2). Power analysis suggest that future studies should focus on strong manipulations of will-power and use sample sizes of N = 300 participants.
Limitation
This analysis examined only a small set of studies in the meta-analysis that used handgrip performance as dependent variable. Other studies may show different results, but these studies often used a simple between-subject design with small samples. This paradigm has low power to detect even moderate effect sizes. It is therefore likely that the R-Index will also confirm Carter and McCullough’s (2014) conclusion.
