# Random measurement error and the replication crisis: A statistical analysis

This is a draft of a commentary on Loken and Gelman’s Science article “Measurement error and the replication crisis. Comments are welcome.

Random Measurement Error Reduces Power, Replicability, and Observed Effect Sizes After Selection for Significance

Ulrich Schimmack and Rickard Carlsson

In the article “Measurement error and the replication crisis” Loken and Gelman (LG) “caution against the fallacy of assuming that that which does not kill statistical significance makes it stronger” (1). We agree with the overall message that it is a fallacy to interpret observed effect size estimates in small samples as accurate estimates of population effect sizes.  We think it is helpful to recognize the key role of statistical power in significance testing.  If studies have less than 50% power, effect sizes must be inflated to be significant. Thus, all observed effect sizes in these studies are inflated.  Once power is greater than 50%, it is possible to obtain significance with observed effect sizes that underestimate the population effect size. However, even with 80% power, the probability of overestimation is 62.5%. [corrected]. As studies with small samples and small effect sizes often have less than 50% power (2), we can safely assume that observed effect sizes overestimate the population effect size. The best way to make claims about effect sizes in small samples is to avoid interpreting the point estimate and to interpret the 95% confidence interval. It will often show that significant large effect sizes in small samples have wide confidence intervals that also include values close to zero, which shows that any strong claims about effect sizes in small samples are a fallacy (3).

Although we agree with Loken and Gelman’s general message, we believe that their article may have created some confusion about the effect of random measurement error in small samples with small effect sizes when they wrote “In a low-noise setting, the theoretical results of Hausman and others correctly show that measurement error will attenuate coefficient estimates. But we can demonstrate with a simple exercise that the opposite occurs in the presence of high noise and selection on statistical significance” (p. 584).  We both read this sentence as suggesting that under the specified conditions random error may produce even more inflated estimates than perfectly reliable measure. We show that this interpretation of their sentence would be incorrect and that random measurement error always leads to an underestimation of observed effect sizes, even if effect sizes are selected for significance. We demonstrate this fact with a simple equation that shows that true power before selection for significance is monotonically related to observed power after selection for significance. As random measurement error always attenuates population effect sizes, the monotonic relationship implies that observed effect sizes with unreliable measures are also always attenuated.  We provide the formula and R-Code in a Supplement. Here we just give a brief description of the steps that are involved in predicting the effect of measurement error on observed effect sizes after selection for significance.

The effect of random measurement error on population effect sizes is well known. Random measurement error adds variance to the observed measures X and Y, which lowers the observable correlation between two measures. Random error also increases the sampling error. As the non-central t-value is the proportion of these two parameters, it follows that random measurement error always attenuates power. Without selection for significance, median observed effect sizes are unbiased estimates of population effect sizes and median observed power matches true power (4,5). However, with selection for significance, non-significant results with low observed power estimates are excluded and median observed power is inflated. The amount of inflation is proportional to true power. With high power, most results are significant and inflation is small. With low power, most results are non-significant and inflation is large.

Schimmack developed a formula that specifies the relationship between true power and median observed power after selection for significance (6). Figure 1 shows that median observed power after selection for significant is a monotonic function of true power.  It is straightforward to transform inflated median observed power into median observed effect sizes.  We applied this approach to Locken and Gelman’s simulation with a true population correlation of r = .15. We changed the range of sample sizes from 50 to 3050 to 25 to 1000 because this range provides a better picture of the effect of small samples on the results. We also increased the range of reliabilities to show that the results hold across a wide range of reliabilities. Figure 2 shows that random error always attenuates observed effect sizes, even after selection for significance in small samples. However, the effect is non-linear and in small samples with small effects, observed effect sizes are nearly identical for different levels of unreliability. The reason is that in studies with low power, most of the observed effect is driven by the noise in the data and it is irrelevant whether the noise is due to measurement error or unexplained reliable variance.

In conclusion, we believe that our commentary clarifies how random measurement error contributes to the replication crisis.  Consistent with classic test theory, random measurement error always attenuates population effect sizes. This reduces statistical power to obtain significant results. These non-significant results typically remain unreported. The selective reporting of significant results leads to the publication of inflated effect size estimates. It would be a fallacy to consider these effect size estimates reliable and unbiased estimates of population effect sizes and to expect that an exact replication study would also produce a significant result.  The reason is that replicability is determined by true power and observed power is systematically inflated by selection for significance.  Our commentary also provides researchers with a tool to correct for the inflation by selection for significance. The function in Figure 1 can be used to deflate observed effect sizes. These deflated observed effect sizes provide more realistic estimates of population effect sizes when selection bias is present. The same approach can also be used to correct effect size estimates in meta-analyses (7).

References

1. Loken, E., & Gelman, A. (2017). Measurement error and the replication crisis. Science,

355 (6325), 584-585. [doi: 10.1126/science.aal3618]

2. Cohen, J. (1962). The statistical power of abnormal-social psychological research: A review. Journal of Abnormal and Social Psychology, 65, 145-153, http://dx.doi.org/10.1037/h004518

3. Cohen, J. (1994). The earth is round (p < .05). American Psychologist, 49, 997-1003. http://dx.doi.org/10.1037/0003-066X.49.12.99

4. Schimmack, U. (2012). The ironic effect of significant results on the credibility of multiple-study articles. Psychological Methods, 17(4), 551-566. http://dx.doi.org/10.1037/a0029487

5. Schimmack, U. (2016). A revised introduction to the R-Index. https://replicationindex.wordpress.com/2016/01/31/a-revised-introduction-to-the-r-index

6. Schimmack, U. (2017). How selection for significance influences observed power. https://replicationindex.wordpress.com/2017/02/21/how-selection-for-significance-influences-observed-power/

7. van Assen, M.A., van Aert, R.C., Wicherts, J.M. (2015). Meta-analysis using effect size distributions of only statistically significant studies. Psychological Methods, 293-309. doi: 10.1037/met0000025.

################################################################

#### R-CODE ###

################################################################

### sample sizes

N = seq(25,500,5)

### true population correlation

true.pop.r = .15

### reliability

rel = 1-seq(0,.9,.20)

### create matrix of population correlations between measures X and Y.

obs.pop.r = matrix(rep(true.pop.r*rel),length(N),length(rel),byrow=TRUE)

### create a matching matrix of sample sizes

N = matrix(rep(N),length(N),length(rel))

### compute non-central t-values

ncp.t = obs.pop.r / ( (1-obs.pop.r^2)/(sqrt(N – 2)))

### compute true power

true.power = pt(ncp.t,N-2,qt(.975,N-2))

###  Get Inflated Observed Power After Selection for Significance

inf.obs.pow = pnorm(qnorm(true.power/2+(1-true.power),qnorm(true.power,qnorm(.975))),qnorm(.975))

### Transform Into Inflated Observed t-values

inf.obs.t = qt(inf.obs.pow,N-2,qt(.975,N-2))

### Transform inflated observed t-values into inflated observed effect sizes

inf.obs.es = (sqrt(N + 4*inf.obs.t^2 -2) – sqrt(N – 2))/(2*inf.obs.t)

### Set parameters for Figure

x.min = 0

x.max = 500

y.min = 0.10

y.max = 0.45

ylab = “Inflated Observed Effect Size”

title = “Effect of Selection for Significance on Observed Effect Size”

### Create Figure

for (i in 1:length(rel)) {

print(i)

plot(N[,1],inf.obs.es[,i],type=”l”,xlim=c(x.min,x.max),ylim=c(y.min,y.max),col=col[i],xlab=”Sample Size”,ylab=”Median Observed Effect Size After Selection for Significance”,lwd=3,main=title)

segments(x0 = 600,y0 = y.max-.05-i*.02, x1 = 650,col=col[i], lwd=5)

text(730,y.max-.05-i*.02,paste0(“Rel = “,format(rel[i],nsmall=1)))

par(new=TRUE)

}

abline(h = .15,lty=2)

##################### THE END #################################

# Dr. Ulrich Schimmack’s Blog about Replicability

For generalization, psychologists must finally rely, as has been done in all the older sciences, on replication” (Cohen, 1994).

DEFINITION OF REPLICABILITYIn empirical studies with random error variance replicability refers to the probability of a study with a significant result to produce a significant result again in an exact replication study of the first study using the same sample size and significance criterion.

BLOGS BY YEAR:  20192018, 2017, 2016, 2015, 2014

Featured Blog of the Month (January, 2019):
Why Ionnidis’s Claim “Most published research findings are false” is false

TOP TEN BLOGS

1. 2018 Replicability Rankings of 117 Psychology Journals (2010-2018)

Rankings of 117 Psychology Journals according to the average replicability of a published significant result. Also includes detailed analysis of time trends in replicability from 2010 to 2018).

This post presented the first replicability ranking and explains the methodology that is used to estimate the typical power of a significant result published in a journal.  The post provides an explanation of the new method to estimate observed power based on the distribution of test statistics converted into absolute z-scores.  The method has been developed further to estimate power for a wider range of z-scores by developing a model that allows for heterogeneity in power across tests.  A description of the new method will be published when extensive simulation studies are completed.

The R-Index can be used to predict whether a set of published results will replicate in a set of exact replication studies. It combines information about the observed power of the original studies with information about the amount of inflation in observed power due to publication bias (R-Index = Observed Median Power – Inflation). The R-Index has predicted the outcome of actual replication studies.

The Test of Insufficient Variance is the most powerful test of publication bias and/or dishonest reporting practices. It can be used even if only two independent statistical results are available, although power to detect bias increases with the number of studies. After converting test results into z-scores, z-scores are expected to have a variance of one.   Unless power is very high, some of these z-scores will not be statistically significant (z .05 two-tailed).  If these non-significant results are missing, the variance shrinks, and TIVA detects that the variance is insufficient.  The observed variance is compared against the expected variance of 1 with a left-tailed chi-square test. The usefulness of TIVA is illustrated with Bem’s (2011) “Feeling the Future” data.

5.  MOST VIEWED POST (with comment by Noble Laureate Daniel Kahneman)

This blog post examines the replicability of priming studies cited in Daniel Kahneman’s popular book “Thinking fast and slow.”   The results suggest that many of the cited findings are difficult to replicate.

Stereotype-threat has been used by social psychologists to explain gender differences in math performance. Accordingly, the stereotype that men are better at math than women is threatening to women and threat leads to lower performance.  This theory has produced a large number of studies, but a recent meta-analysis showed that the literature suffers from publication bias and dishonest reporting.  After correcting for these effects, the stereotype-threat effect was negligible.  This blog post shows a low R-Index for the first article that appeared to provide strong support for stereotype-threat.  These results show that the R-Index can warn readers and researchers that reported results are too good to be true.

7.  An attempt at explaining null-hypothesis testing and statistical power with 1 figure and 1500 words.   Null-hypothesis significance testing is old, widely used, and confusing. Many false claims have been used to suggest that NHST is a flawed statistical method. Others argue that the method is fine, but often misunderstood. Here I try to explain NHST and why it is important to consider power (type-II errors) using a picture from the free software GPower.

Some Bayesian statisticians have proposed Bayes-Factors to provide evidence for a Null-Hypothesis (i.e., there is no effect).  They used Bem’s (2011) “Feeling the Future” data to argue that Bayes-Factors would have demonstrated that extra-sensory perception does not exist.  This blog post shows that Bayes-Factors depend on the specification of the alternative hypothesis and that support for the null-hypothesis is often obtained by choosing an unrealistic alternative hypothesis (e.g., there is a 25% probability that effect size is greater than one standard deviation, d > 1).  As a result, Bayes-Factors can favor the null-hypothesis when there is an effect, but the effect size is small (d = .2).  A Bayes-Factor in favor of the null is more appropriately interpreted as evidence that the alternative hypothesis needs to decrease the probabilities assigned to large effect sizes. The post also shows that Bayes-Factors based on a meta-analysis of Bem’s data provide misleading evidence that an effect is present because Bayesian statistics do not take publication bias and dishonest reporting practices into account.

9. Hidden figures: Replication failures in the stereotype threat literature.  A widespread problem is that failed replication studies are often not published. This blog post shows that another problem is that failed replication studies are ignored even when they are published.  Selective publishing of confirmatory results undermines the credibility of science and claims about the importance of stereotype threat to explain gender differences in mathematics.

10. My journey towards estimation of replicability.  In this blog post I explain how I got interested in statistical power and replicability and how I developed statistical methods to reveal selection bias and to estimate replicability.

# Meta-Analysis of Observed Power: Comparison of Estimation Methods

Meta-Analysis of Observed Power

Citation: Dr. R (2015). Meta-analysis of observed power. R-Index Bulletin, Vol(1), A2.

In a previous blog post, I presented an introduction to the concept of observed power. Observed power is an estimate of the true power on the basis of observed effect size, sampling error, and significance criterion of a study. Yuan and Maxwell (2005) concluded that observed power is a useless construct when it is applied to a single study, mainly because sampling error in a single study is too large to obtain useful estimates of true power. However, sampling error decreases as the number of studies increases and observed power in a set of studies can provide useful information about the true power in a set of studies.

This blog post introduces various methods that can be used to estimate power on the basis of a set of studies (meta-analysis). I then present simulation studies that compare the various estimation methods in terms of their ability to estimate true power under a variety of conditions. In this blog post, I examine only unbiased sets of studies. That is, the sample of studies in a meta-analysis is a representative sample from the population of studies with specific characteristics. The first simulation assumes that samples are drawn from a population of studies with fixed effect size and fixed sampling error. As a result, all studies have the same true power (homogeneous). The second simulation assumes that all studies have a fixed effect size, but that sampling error varies across studies. As power is a function of effect size and sampling error, this simulation models heterogeneity in true power. The next simulations assume heterogeneity in population effect sizes. One simulation uses a normal distribution of effect sizes. Importantly, a normal distribution has no influence on the mean because effect sizes are symmetrically distributed around the mean effect size. The next simulations use skewed normal distributions. This simulation provides a realistic scenario for meta-analysis of heterogeneous sets of studies such as a meta-analysis of articles in a specific journal or articles on different topics published by the same author.

Observed Power Estimation Method 1: The Percentage of Significant Results

The simplest method to determine observed power is to compute the percentage of significant results. As power is defined as the long-range percentage of significant results, the percentage of significant results in a set of studies is an unbiased estimate of the long-term percentage. The main limitation of this method is that the dichotomous measure (significant versus insignificant) is likely to be imprecise when the number of studies is small. For example, two studies can only show observed power values of 0, 25%, 50%, or 100%, even if true power were 75%. However, the percentage of significant results plays an important role in bias tests that examine whether a set of studies is representative. When researchers hide non-significant results or use questionable research methods to produce significant results, the percentage of significant results will be higher than the percentage of significant results that could have been obtained on the basis of the actual power to produce significant results.

Observed Power Estimation Method 2: The Median

Schimmack (2012) proposed to average observed power of individual studies to estimate observed power. Yuan and Maxwell (2005) demonstrated that the average of observed power is a biased estimator of true power. It overestimates power when power is less than 50% and it underestimates true power when power is above 50%. Although the bias is not large (no more than 10 percentage points), Yuan and Maxwell (2005) proposed a method that produces an unbiased estimate of power in a meta-analysis of studies with the same true power (exact replication studies). Unlike the average that is sensitive to skewed distributions, the median provides an unbiased estimate of true power because sampling error is equally likely (50:50 probability) to inflate or deflate the observed power estimate. To avoid the bias of averaging observed power, Schimmack (2014) used median observed power to estimate the replicability of a set of studies.

Observed Power Estimation Method 3: P-Curve’s KS Test

Another method is implemented in Simonsohn’s (2014) pcurve. Pcurve was developed to obtain an unbiased estimate of a population effect size from a biased sample of studies. To achieve this goal, it is necessary to determine the power of studies because bias is a function of power. The pcurve estimation uses an iterative approach that tries out different values of true power. For each potential value of true power, it computes the location (quantile) of observed test statistics relative to a potential non-centrality parameter. The best fitting non-centrality parameter is located in the middle of the observed test statistics. Once a non-central distribution has been found, it is possible to assign each observed test-value a cumulative percentile of the non-central distribution. For the actual non-centrality parameter, these percentiles have a uniform distribution. To find the best fitting non-centrality parameter from a set of possible parameters, pcurve tests whether the distribution of observed percentiles follows a uniform distribution using the Kolmogorov-Smirnov test. The non-centrality parameter with the smallest test statistics is then used to estimate true power.

Observed Power Estimation Method 4: P-Uniform

van Assen, van Aert, and Wicherts (2014) developed another method to estimate observed power. Their method is based on the use of the gamma distribution. Like the pcurve method, this method relies on the fact that observed test-statistics should follow a uniform distribution when a potential non-centrality parameter matches the true non-centrality parameter. P-uniform transforms the probabilities given a potential non-centrality parameter with a negative log-function (-log[x]). These values are summed. When probabilities form a uniform distribution, the sum of the log-transformed probabilities matches the number of studies. Thus, the value with the smallest absolute discrepancy between the sum of negative log-transformed percentages and the number of studies provides the estimate of observed power.

Observed Power Estimation Method 5: Averaging Standard Normal Non-Centrality Parameter

In addition to these existing methods, I introduce to novel estimation methods. The first new method converts observed test statistics into one-sided p-values. These p-values are then transformed into z-scores. This approach has a long tradition in meta-analysis that was developed by Stouffer et al. (1949). It was popularized by Rosenthal during the early days of meta-analysis (Rosenthal, 1979). Transformation of probabilities into z-scores makes it easy to aggregate probabilities because z-scores follow a symmetrical distribution. The average of these z-scores can be used as an estimate of the actual non-centrality parameter. The average z-score can then be used to estimate true power. This approach avoids the problem of averaging power estimates that power has a skewed distribution. Thus, it should provide an unbiased estimate of true power when power is homogenous across studies.

Observed Power Estimation Method 6: Yuan-Maxwell Correction of Average Observed Power

Yuan and Maxwell (2005) demonstrated a simple average of observed power is systematically biased. However, a simple average avoids the problems of transforming the data and can produce tighter estimates than the median method. Therefore I explored whether it is possible to apply a correction to the simple average. The correction is based on Yuan and Maxwell’s (2005) mathematically derived formula for systematic bias. After averaging observed power, Yuan and Maxwell’s formula for bias is used to correct the estimate for systematic bias. The only problem with this approach is that bias is a function of true power. However, as observed power becomes an increasingly good estimator of true power in the long run, the bias correction will also become increasingly better at correcting the right amount of bias.

The Yuan-Maxwell correction approach is particularly promising for meta-analysis of heterogeneous sets of studies such as sets of diverse studies in a journal. The main advantage of this method is that averaging of power makes no assumptions about the distribution of power across different studies (Schimmack, 2012). The main limitation of averaging power was the systematic bias, but Yuan and Maxwell’s formula makes it possible to reduce this systematic bias, while maintaining the advantage of having a method that can be applied to heterogeneous sets of studies.

RESULTS

Homogeneous Effect Sizes and Sample Sizes

The first simulation used 100 effect sizes ranging from .01 to 1.00 and 50 sample sizes ranging from 11 to 60 participants per condition (Ns = 22 to 120), yielding 5000 different populations of studies. The true power of these studies was determined on the basis of the effect size, sample size, and the criterion p < .025 (one-tailed), which is equivalent to .05 (two-tailed). Sample sizes were chosen so that average power across the 5,000 studies was 50%. The simulation drew 10 random samples from each of the 5,000 populations of studies. Each sample of a study simulated a between-subject design with the given population effect size and sample size. The results were stored as one-tailed p-values. For the meta-analysis p-values were converted into z-scores. To avoid biases due to extreme outliers, z-scores greater than 5 were set to 5 (observed power = .999).

The six estimation methods were then used to compute observed power on the basis of samples of 10 studies. The following figures show observed power as a function of true power. The green lines show the 95% confidence interval for different levels of true power. The figure also includes red dashed lines for a value of 50% power. Studies with more than 50% observed power would be significant. Studies with less than 50% observed power would be non-significant. The figures also include a blue line for 80% true power. Cohen (1988) recommended that researchers should aim for a minimum of 80% power. It is instructive how accurate estimation methods are in evaluating whether a set of studies met this criterion.

The histogram shows the distribution of true power across the 5,000 populations of studies.

The histogram shows that the simulation covers the full range of power. It also shows that high-powered studies are overrepresented because moderate to large effect sizes can achieve high power for a wide range of sample sizes. The distribution is not important for the evaluation of different estimation methods and benefits all estimation methods equally because observed power is a good estimator of true power when true power is close to the maximum (Yuan & Maxwell, 2005).

The next figure shows scatterplots of observed power as a function of true power. Values above the diagonal indicate that observed power overestimates true power. Values below the diagonal show that observed power underestimates true power.

Visual inspection of the plots suggests that all methods provide unbiased estimates of true power. Another observation is that the count of significant results provides the least accurate estimates of true power. The reason is simply that aggregation of dichotomous variables requires a large number of observations to approximate true power. The third observation is that visual inspection provides little information about the relative accuracy of the other methods. Finally, the plots show how accurate observed power estimates are in meta-analysis of 10 studies. When true power is 50%, estimates very rarely exceed 80%. Similarly, when true power is above 80%, observed power is never below 50%. Thus, observed power can be used to examine whether a set of studies met Cohen’s recommended guidelines to conduct studies with a minimum of 80% power. If observed power is 50%, it is nearly certain that the studies did not have the recommended 80% power.

To examine the relative accuracy of different estimation methods quantitatively, I computed bias scores (observed power – true power). As bias can overestimate and underestimate true power, the standard deviation of these bias scores can be used to quantify the precision of various estimation methods. In addition, I present the mean to examine whether a method has large sample accuracy (i.e. the bias approaches zero as the number of simulations increases). I also present the percentage of studies with no more than 20% points bias. Although 20% bias may seem large, it is not important to estimate power with very high precision. When observed power is below 50%, it suggests that a set of studies was underpowered even if the observed power estimate is an underestimation.

The quantitative analysis also shows no meaningful differences among the estimation methods. The more interesting question is how these methods perform under more challenging conditions when the set of studies are no longer exact replication studies with fixed power.

Homogeneous Effect Size, Heterogeneous Sample Sizes

The next simulation simulated variation in sample sizes. For each population of studies, sample sizes were varied by multiplying a particular sample size by factors of 1 to 5.5 (1.0, 1.5,2.0…,5.5). Thus, a base-sample-size of 40 created a range of sample sizes from 40 to 220. A base-sample size of 100 created a range of sample sizes from 100 to 2,200. As variation in sample sizes increases the average sample size, the range of effect sizes was limited to a range from .004 to .4 and effect sizes were increased in steps of d = .004. The histogram shows the distribution of power in the 5,000 population of studies.

The simulation covers the full range of true power, although studies with low and very high power are overrepresented.

The results are visually not distinguishable from those in the previous simulation.

The quantitative comparison of the estimation methods also shows very similar results.

In sum, all methods perform well even when true power varies as a function of variation in sample sizes. This conclusion may not generalize to more extreme simulations of variation in sample sizes, but more extreme variations in sample sizes would further increase the average power of a set of studies because the average sample size would increase as well. Thus, variation in effect sizes poses a more realistic challenge for the different estimation methods.

Heterogeneous, Normally Distributed Effect Sizes

The next simulation used a random normal distribution of true effect sizes. Effect sizes were simulated to have a reasonable but large variation. Starting effect sizes ranged from .208 to 1.000 and increased in increments of .008. Sample sizes ranged from 10 to 60 and increased in increments of 2 to create 5,000 populations of studies. For each population of studies, effect sizes were sampled randomly from a normal distribution with a standard deviation of SD = .2. Extreme effect sizes below d = -.05 were set to -.05 and extreme effect sizes above d = 1.20 were set to 1.20. The first histogram of effect sizes shows the 50,000 population effect sizes. The histogram on the right shows the distribution of true power for the 5,000 sets of 10 studies.

The plots of observed and true power show that the estimation methods continue to perform rather well even when population effect sizes are heterogeneous and normally distributed.

The quantitative comparison suggests that puniform has some problems with heterogeneity. More detailed studies are needed to examine whether this is a persistent problem for puniform, but given the good performance of the other methods it seems easier to use these methods.

Heterogeneous, Skewed Normal Effect Sizes

The next simulation puts the estimation methods to a stronger challenge by introducing skewed distributions of population effect sizes. For example, a set of studies may contain mostly small to moderate effect sizes, but a few studies examined large effect sizes. To simulated skewed effect size distributions, I used the rsnorm function of the fGarch package. The function creates a random distribution with a specified mean, standard deviation, and skew. I set the mean to d = .2, the standard deviation to SD = .2, and skew to 2. The histograms show the distribution of effect sizes and the distribution of true power for the 5,000 sets of studies (k = 10).

This time the results show differences between estimation methods in the ability of various estimation methods to deal with skewed heterogeneity. The percentage of significant results is unbiased, but is imprecise due to the problem of averaging dichotomous variables. The other methods show systematic deviations from the 95% confidence interval around the true parameter. Visual inspection suggests that the Yuan-Maxwell correction method has the best fit.

This impression is confirmed in quantitative analyses of bias. The quantitative comparison confirms major problems with the puniform estimation method. It also shows that the median, p-curve, and the average z-score method have the same slight positive bias. Only the Yuan-Maxwell corrected average power shows little systematic bias.

To examine biases in more detail, the following graphs plot bias as a function of true power. These plots can reveal that a method may have little average bias, but has different types of bias for different levels of power. The results show little evidence of systematic bias for the Yuan-Maxwell corrected average of power.

The following analyses examined bias separately for simulation with less or more than 50% true power. The results confirm that all methods except the Yuan-Maxwell correction underestimate power when true power is below 50%. In contrast, most estimation methods overestimate true power when true power is above 50%. The exception is puniform which still underestimated true power. More research needs to be done to understand the strange performance of puniform in this simulation. However, even if p-uniform could perform better, it is likely to be biased with skewed distributions of effect sizes because it assumes a fixed population effect size.

Conclusion

This investigation introduced and compared different methods to estimate true power for a set of studies. All estimation methods performed well when a set of studies had the same true power (exact replication studies), when effect sizes were homogenous and sample sizes varied, and when effect sizes were normally distributed and sample sizes were fixed. However, most estimation methods were systematically biased when the distribution of effect sizes was skewed. In this situation, most methods run into problems because the percentage of significant results is a function of the power of individual studies rather than the average power.

The results of these analyses suggest that the R-Index (Schimmack, 2014) can be improved by simply averaging power and then applying the Yuan-Maxwell correction. However, it is important to realize that the median method tends to overestimate power when power is greater than 50%. This makes it even more difficult for the R-Index to produce an estimate of low power when power is actually high. The next step in the investigation of observed power is to examine how different methods perform in unrepresentative (biased) sets of studies. In this case, the percentage of significant results is highly misleading. For example, Sterling et al. (1995) found percentages of 95% power, which would suggest that studies had 95% power. However, publication bias and questionable research practices create a bias in the sample of studies that are being published in journals. The question is whether other observed power estimates can reveal bias and can produce accurate estimates of the true power in a set of studies.