Tag Archives: Meta-Analysis

Using the R-index to detect questionable research practices in SSRI studies

Amna Shakil and Ulrich Schimmack

In 2008, Turner and colleagues (2008) examined the presence of publication bias in clinical trials of antidepressants. They found that out of 74 FDA-registered studies, 51% showed positive results. However, positive results were much more likely to be published, as 94% of the published results were positive. There were two reasons for the inflated percentage of positive results. First, negative results were not published. Second, negative results were published as positive results. Turner and colleagues’ (2008) results received a lot of attention and cast doubt on the effectiveness of anti-depressants.

A year after Turner and colleagues (2008) published their study, Moreno, Sutton, Turner, Abrams, Cooper and Palmer (2009) examined the influence of publication bias on the effect-size estimate in clinical trials of antidepressants. They found no evidence of publication bias in the FDA-registered trials, leading the researchers to conclude that the FDA data provide an unbiased gold standard to examine biases in the published literature.

The effect size for treatment with anti-depressants in the FDA data was g = 0.31, 95% confidence interval 0.27 to 0.35. In contrast, the uncorrected average effect size in the published studies was g = 0.41, 95% confidence interval 0.37 to 0.45. This finding shows that publication bias inflates effect size estimates by 32% ((0.41 – 0.31)/0.31).

Moreno et al. (2009) also used regression analysis to obtain a corrected effect size estimate based on the biased effect sizes in the published literature. In this method, effect sizes are regressed on sampling error under the assumption that studies with smaller samples (and larger sampling error) have more bias. The intercept is used as an estimate of the population effect size when sampling error is zero. This correction method yielded an effect size estimate of g = 0.29, 95% confidence interval 0.23 to 0.35, which is similar to the gold standard estimate (.31).

The main limitation of the regression method is that other factors can produce a correlation between sample size and effect size (e.g., higher quality studies are more costly and use smaller samples). To avoid this problem, we used an alternative correction method that does not make this assumption.

The method uses the R-Index to examine bias in a published data set. The R-Index increases as statistical power increases and it decreases when publication bias is present. To obtain an unbiased effect size estimate, studies are selected to maximize the R-Index.

Since the actual data files were not available, graphs A and B from Moreno et al.’s (2009) study were used to obtain information about effect size and sample error of all the FDA-registered and the published journal articles.

The FDA-registered studies had the success rate of 53% and the observed power of 56%, resulting in an inflation of close to 0. The close match between the success rate and observed confirms FDA studies are not biased. Given the lack of bias (inflation), the most accurate estimate of the effect size is obtained by using all studies.

The published journal articles had a success rate of 86% and the observed power of 73%, resulting in the inflation rate of 12%. The inflation rate of 12% confirms that the published data set is biased. The R-Index subtracts the inflation rate from observed power to correct for inflation. Thus, the R-Index for the published studies is 73-12 = 61. The weighted effect size estimate was d = .40.

The next step was to select sets of studies to maximize the R-Index. As most studies were significant, the success rate could not change much. As a result, most of the increase would be achieved by selecting studies with higher sample sizes in order to increase power. The maximum R-Index was obtained for a cut-off point of N = 225. This left 14 studies with a total sample size of 4,170 participants. The success rate was 100% with median observed power of 85%. The Inflation was still 15%, but the R-Index was higher than it was for the full set of studies (70 vs. 61). The weighted average effect size in the selected set of powerful studies was d = .34. This result is very similar to the gold standard in the FDA data. The small discrepancy can be attributed to the fact that even studies with 85% power still have a small bias in the estimation of the true effect size.

In conclusion, our alternative effect size estimation procedure confirms Moreno et al.’s (2009) results using an alternative bias-correction method and shows that the R-Index can be a valuable tool to detect and correct for publication bias in other meta-analyses.

These results have important practical implications. The R-Index confirms that published clinical trials are biased and can provide false information about the effectiveness of drugs. It is therefore important to ensure that clinical trials are preregistered and that all results of clinical trials are published. The R-Index can be used to detect violations of these practices that lead to biased evidence. Another important finding is that clinical trials of antidepressants do show effectiveness and that antidepressants can be used as effective treatments of depression. The presence of publication bias should not be used to claim that antidepressants lack effectiveness.

References

Moreno, S. G., Sutton, A. J., Turner, E. H., Abrams, K. R., Cooper, N. J., Palmer, T. M., & Ades, A. E. (2009). Novel methods to deal with publication biases: secondary analysis of antidepressant trials in the FDA trial registry database and related journal publications. Bmj, 339, b2981.

Turner, E. H., Matthews, A. M., Linardatos, E., Tell, R. A., & Rosenthal, R. (2008). Selective publication of antidepressant trials and its influence on apparent efficacy. New England Journal of Medicine, 358(3), 252-260.

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When Exact Replications Are Too Exact: The Lucky-Bounce-Test for Pairs of Exact Replication Studies

Imagine an NBA player has an 80% chance to make one free throw. What is the chance that he makes both free throws? The correct answer is 64% (80% * 80%).

Now consider the possibility that it is possible to distinguish between two types of free throws. Some free throws are good; they don’t touch the rim and make a swishing sound when they go through the net (all net). The other free throws bounce of the rim and go in (rattling in).

What is the probability that an NBA player with an 80% free throw percentage makes a free throw that is all net or rattles in? It is more likely that an NBA player with an 80% free throw average makes a perfect free throw because a free throw that rattles in could easily have bounded the wrong way, which would lower the free throw percentage. To achieve an 80% free throw percentage, most free throws have to be close to perfect.

Let’s say the probability of hitting the rim and going in is 30%. With an 80% free throw average, this means that the majority of free throws are in the close-to-perfect category (20% misses, 30% rattle-in, 50% close-to-perfect).

What does this have to do with science? A lot!

The reason is that the outcome of a scientific study is a bit like throwing free throws. One factor that contributes to a successful study is skill (making correct predictions, avoiding experimenter errors, and conducting studies with high statistical power). However, another factor is random (a lucky or unlucky bounce).

The concept of statistical power is similar to an NBA players’ free throw percentage. A researcher who conducts studies with 80% statistical power is going to have an 80% success rate (that is, if all predictions are correct). In the remaining 20% of studies, a study will not produce a statistically significant result, which is equivalent to missing a free throw and not getting a point.

Many years ago, Jacob Cohen observed that researchers often conduct studies with relatively low power to produce a statistically significant result. Let’s just assume right now that a researcher conducts studies with 60% power. This means, researchers would be like NBA players with a 60% free-throw average.

Now imagine that researchers have to demonstrate an effect not only once, but also a second time in an exact replication study. That is researchers have to make two free throws in a row. With 60% power, the probability to get two significant results in a row is only 36% (60% * 60%). Moreover, many of the freethrows that are made rattle in rather than being all net. The percentages are about 40% misses, 30% rattling in and 30% all net.

One major difference between NBA players and scientists is that NBA players have to demonstrate their abilities in front of large crowds and TV cameras, whereas scientists conduct their studies in private.

Imagine an NBA player could just go into a private room, throw two free throws and then report back how many free throws he made and the outcome of these free throws determine who wins game 7 in the playoff finals. Would you trust the player to tell the truth?

If you would not trust the NBA player, why would you trust scientists to report failed studies? You should not.

It can be demonstrated statistically that scientists are reporting more successes than the power of their studies would justify (Sterling et al., 1995; Schimmack, 2012). Amongst scientists this fact is well known, but the general public may not fully appreciate the fact that a pair of exact replication studies with significant results is often just a selection of studies that included failed studies that were not reported.

Fortunately, it is possible to use statistics to examine whether the results of a pair of studies are likely to be honest or whether failed studies were excluded. The reason is that an amateur is not only more likely to miss a free throw. An amateur is also less likely to make a perfect free throw.

Based on the theory of statistical power developed by Nyman and Pearson and popularized by Jacob Cohen, it is possible to make predictions about the relative frequency of p-values in the non-significant (failure), just significant (rattling in), and highly significant (all net) ranges.

As for made-free-throws, the distinction between lucky and clear successes is somewhat arbitrary because power is continuous. A study with a p-value of .0499 is very lucky because p = .501 would have been not significant (rattled in after three bounces on the rim). A study with p = .000001 is a clear success. Lower p-values are better, but where to draw the line?

As it turns out, Jacob Cohen’s recommendation to conduct studies with 80% power provides a useful criterion to distinguish lucky outcomes and clear successes.

Imagine a scientist conducts studies with 80% power. The distribution of observed test-statistics (e.g. z-scores) shows that this researcher has a 20% chance to get a non-significant result, a 30% chance to get a lucky significant result (p-value between .050 and .005), and a 50% chance to get a clear significant result (p < .005). If the 20% failed studies are hidden, the percentage of results that rattled in versus studies with all-net results are 37 vs. 63%. However, if true power is just 20% (an amateur), 80% of studies fail, 15% rattle in, and 5% are clear successes. If the 80% failed studies are hidden, only 25% of the successful studies are all-net and 75% rattle in.

One problem with using this test to draw conclusions about the outcome of a pair of exact replication studies is that true power is unknown. To avoid this problem, it is possible to compute the maximum probability of a rattling-in result. As it turns out, the optimal true power to maximize the percentage of lucky outcomes is 66% power. With true power of 66%, one would expect 34% misses (p > .05), 32% lucky successes (.050 < p < .005), and 34% clear successes (p < .005).

LuckyBounceTest

For a pair of exact replication studies, this means that there is only a 10% chance (32% * 32%) to get two rattle-in successes in a row. In contrast, there is a 90% chance that misses were not reported or that an honest report of successful studies would have produced at least one all-net result (z > 2.8, p < .005).

Example: Unconscious Priming Influences Behavior

I used this test to examine a famous and controversial set of exact replication studies. In Bargh, Chen, and Burrows (1996), Dr. Bargh reported two exact replication studies (studies 2a and 2b) that showed an effect of a subtle priming manipulation on behavior. Undergraduate students were primed with words that are stereotypically associated with old age. The researchers then measured the walking speed of primed participants (n = 15) and participants in a control group (n = 15).

The two studies were not only exact replications of each other; they also produced very similar results. Most readers probably expected this outcome because similar studies should produce similar results, but this false belief ignores the influence of random factors that are not under the control of a researcher. We do not expect lotto winners to win the lottery again because it is an entirely random and unlikely event. Experiments are different because there could be a systematic effect that makes a replication more likely, but in studies with low power results should not replicate exactly because random sampling error influences results.

Study 1: t(28) = 2.86, p = .008 (two-tailed), z = 2.66, observed power = 76%
Study 2: t(28) = 2.16, p = .039 (two-tailed), z = 2.06, observed power = 54%

The median power of these two studies is 65%. However, even if median power were lower or higher, the maximum probability of obtaining two p-values in the range between .050 and .005 remains just 10%.

Although this study has been cited over 1,000 times, replication studies are rare.

One of the few published replication studies was reported by Cesario, Plaks, and Higgins (2006). Naïve readers might take the significant results in this replication study as evidence that the effect is real. However, this study produced yet another lucky success.

Study 3: t(62) = 2.41, p = .019, z = 2.35, observed power = 65%.

The chances of obtaining three lucky successes in a row is only 3% (32% *32% * 32*). Moreover, with a median power of 65% and a reported success rate of 100%, the success rate is inflated by 35%. This suggests that the true power of the reported studies is considerably lower than the observed power of 65% and that observed power is inflated because failed studies were not reported.

The R-Index corrects for inflation by subtracting the inflation rate from observed power (65% – 35%). This means the R-Index for this set of published studies is 30%.

This R-Index can be compared to several benchmarks.

An R-Index of 22% is consistent with the null-hypothesis being true and failed attempts are not reported.

An R-Index of 40% is consistent with 30% true power and all failed attempts are not reported.

It is therefore not surprising that other researchers were not able to replicate Bargh’s original results, even though they increased statistical power by using larger samples (Pashler et al. 2011, Doyen et al., 2011).

In conclusion, it is unlikely that Dr. Bargh’s original results were the only studies that they conducted. In an interview, Dr. Bargh revealed that the studies were conducted in 1990 and 1991 and that they conducted additional studies until the publication of the two studies in 1996. Dr. Bargh did not reveal how many studies they conducted over the span of 5 years and how many of these studies failed to produce significant evidence of priming. If Dr. Bargh himself conducted studies that failed, it would not be surprising that others also failed to replicate the published results. However, in a personal email, Dr. Bargh assured me that “we did not as skeptics might presume run many studies and only reported the significant ones. We ran it once, and then ran it again (exact replication) in order to make sure it was a real effect.” With a 10% probability, it is possible that Dr. Bargh was indeed lucky to get two rattling-in findings in a row. However, his aim to demonstrate the robustness of an effect by trying to show it again in a second small study is misguided. The reason is that it is highly likely that the effect will not replicate or that the first study was already a lucky finding after some failed pilot studies. Underpowered studies cannot provide strong evidence for the presence of an effect and conducting multiple underpowered studies reduces the credibility of successes because the probability of this outcome to occur even when an effect is present decreases with each study (Schimmack, 2012). Moreover, even if Bargh was lucky to get two rattling-in results in a row, others will not be so lucky and it is likely that many other researchers tried to replicate this sensational finding, but failed to do so. Thus, publishing lucky results hurts science nearly as much as the failure to report failed studies by the original author.

Dr. Bargh also failed to realize how lucky he was to obtain his results, in his response to a published failed-replication study by Doyen. Rather than acknowledging that failures of replication are to be expected, Dr. Bargh criticized the replication study on methodological grounds. There would be a simple solution to test Dr. Bargh’s hypothesis that he is a better researcher and that his results are replicable when the study is properly conducted. He should demonstrate that he can replicate the result himself.

In an interview, Tom Bartlett asked Dr. Bargh why he didn’t conduct another replication study to demonstrate that the effect is real. Dr. Bargh’s response was that “he is aware that some critics believe he’s been pulling tricks, that he has a “special touch” when it comes to priming, a comment that sounds like a compliment but isn’t. “I don’t think anyone would believe me,” he says.” The problem for Dr. Bargh is that there is no reason to believe his original results, either. Two rattling-in results alone do not constitute evidence for an effect, especially when this result could not be replicated in an independent study. NBA players have to make free-throws in front of a large audience for a free-throw to count. If Dr. Bargh wants his findings to count, he should demonstrate his famous effect in an open replication study. To avoid embarrassment, it would be necessary to increase the power of the replication study because it is highly unlikely that even Dr. Bargh can continuously produce significant results with samples of N = 30 participants. Even if the effect is real, sampling error is simply too large to demonstrate the effect consistently. Knowledge about statistical power is power. Knowledge about post-hoc power can be used to detect incredible results. Knowledge about a priori power can be used to produce credible results.

Swish!

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 YMCA fig1that 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.

YMCA fig2

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 quantitatiYMCA fig12ve 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.

YMCA fig4

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.

YMCA fig5

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

YMCA fig6

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.

YMCA fig7

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.

YMCA fig9

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.

YMCA fig8

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).

YMCA fig10

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.

YMCA fig11

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.

YMCA fig12

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.

YMCA fig13

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.

YMCA fig14

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.

An Introduction to Observed Power based on Yuan and Maxwell (2005)

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).

YM formula1

Entering a non-centrality parameter of 3 for a generic z-test in G*power yields the following illustration of  a non-central distribution.

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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%.

YM formula2

In sum, the formulaYM formula3

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.

YM formula4

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.

YM figure2

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.

YM formula5

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).

YM figure3

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.

YM figure4

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.

YM figure5

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.

YM figure6

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.

YM figure7

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%).

YM figure8

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.

YM figure9

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.

The Test of Insufficient Variance (TIVA): A New Tool for the Detection of Questionable Research Practices

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.

Bem_p_ZThe 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.

The R-Index of Ego-Depletion Studies with the Handgrip Paradigm

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.

HandgripPoewr

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.

 HandgripRindex

 

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.

The R-Index of Nicotine-Replacement-Therapy Studies: An Alternative Approach to Meta-Regression

Stanley and Doucouliagos (2013) demonstrated how meta-regression can be used to obtain unbiased estimates of effect sizes from a biased set of original studies. The regression approach relies on the fact that small samples often need luck or questionable practices to produce significant results, whereas large samples can show true effects without the help of luck and questionable practices. If questionable practices or publication bias are present, effect sizes in small samples are inflated and this bias is evident in a regression of effect sizes on sampling error. When bias is present, the intercept of the regression equation can provide a better estimate of the average effect size in a set of studies.

One limitation of this approach is that other factors can also produce a correlation between effect size and sampling error. Another problem is that the regression equation can only approximate the effect of bias on effect size estimates.

The R-Index can complement meta-regression in several ways. First, it can be used to examine whether a correlation between effect size and sampling error reflects bias. If small samples have higher effect sizes due to bias, they should also yield more significant results than the power of these studies justifies. If this is not the case, the correlation may simply show that smaller samples examined stronger effects. Second, the R-Index can be used as an alternative way to estimate unbiased effect sizes that does not rely on the relationship between sample size and effect size.

The usefulness of the R-Index is illustrated with Stanley and Doucouliagos (2013) meta-analysis of the effectiveness of nicotine replacement therapy (the patch). Table A1 lists sampling errors and t-values of 42 studies. Stanley and Doucouliagos (2013) found that the 42 studies suggested a reduction in smoking by 93%, but that effectiveness decreased to 22% in a regression that controlled for biased reporting of results. This suggests that published studies inflate the true effect by more than 300%.

I entered the t-values and standard errors into the R-Index spreadsheet. I used sampling error to estimate sample sizes and degrees of freedom (2 / sqrt [N]). I used one-tailed t-tests to allow for negative t-values because the sign of effects is known in a meta-analysis of studies that try to show treatment effects. Significance was tested using p = .025, which is equivalent to using .050 in the test of significance for two-tailed tests (z > 1.96).

The R-Index for all 42 studies was 27%. The low R-Index was mostly explained by the low power of studies with small samples. Median observed power was just 34%. The number of significant results was only slightly higher 40%. The inflation rate was only 7%.

As studies with low power add mostly noise, Stanley (2010) showed that it can be preferable to exclude them from estimates of actual effect sizes. The problem is that it is difficult to find a principled way to determine which studies should be included or excluded. One solution is to retain only studies with large samples. The problem with this approach is that this often limits a meta-analysis to a small set of studies.

One solution is to compute the R-Index for different sets of studies and to base conclusions on the largest unbiased set of studies. For the 42 studies of nicotine replacement therapy, the following effect size estimates were obtained (effect sizes are d-values, d = t * se).

NicotinePatch

The results show the highest R-Index for studies with more than 80 participants. For these studies, observed power is 83% and the percentage of significant results is also 83%, suggesting that this set of studies is an unbiased sample of studies. The weighted average effect size for this set of studies is d = .44. The results also show that the weighted average effect size does not change much as a function of the selection of studies. When all studies are included, there is evidence of bias (8% inflation) and the weighted average effect size is inflated, but the amount of inflation is small (d = .56 vs. d = .44, difference d = .12).

The small amount of bias appears to be inconsistent with Stanley and Doucouliagos (2013) estimate that an uncorrected meta-analysis overestimates the true effect size by over 300% (93% vs. 22% RR). I therefore also examined the log(RR) values in Table 1a.

The average is .68 (compared to the simple mean reported as .66); the median is .53 and the weighted average is .49.   The regression-corrected estimate reported by Stanley and Doucouliagos (2013) is .31. The weighted mean for studies with more than 80 participants is .43. It is now clear why Stanley and Doucouliagos (2013) reported a large effect of the bias correction. First, they used the simple mean as a comparison standard (.68 vs. 31). The effect would be smaller if they had used the weighted mean as a comparison standard (.49 vs. .31). Another factor is that the regression procedure produces a lower estimate than the R-Index approach (.31 vs. 43). More research is needed to compare these results, but the R-Index has a simple logic. When there is no evidence of bias, the weighted average provides a reasonable estimate of the true effect size.

Conclusion

Stanley and Doucouliagos (2013) used regression of effect sizes on sampling error to reveal biases and to obtain an unbiased estimate of the typical effect size in a set of studies. This approach provides a useful tool in the fight against biased reporting of research results. One limitation of this approach is that other factors can produce a correlation between sampling error and effect size. The R-Index can be used to examine how much reporting biases contribute to this correlation. The R-Index can also be used to obtain an unbiased estimate of effect size by computing a weighted average for a select set of studies with a high R-Index.

A meta-analysis of 42 studies of nicotine replacement theory illustrates this approach. The R-Index for the full set of studies was low (24%). This reveals that many studies had low power to demonstrate an effect. These studies provide little information about effectiveness because non-significant results are just as likely to be type-II errors as demonstrations of low effectiveness.

The R-Index increased when studies with larger samples were selected. The maximum R-Index was obtained for studies with at least 80 participants. In this case, observed power was above 80% and there was no evidence of bias. The weighted average effect size for this set of studies was only slightly lower than the weighted average effect size for all studies (log(RR) = .43 vs. .49, RR = 54% vs. 63%, respectively). This finding suggests that smokers who use a nicotine patch are about 50% more likely to quit smoking than smokers without a nicotine patch.

The estimate of 50% risk reduction challenges Stanley and Doucouliagos’s (2013) preferred estimate that bias correction “reduces the efficacy of the patch to only 22%.” The R-Index suggests that this bias-corrected estimate is itself biased.

Another important conclusion is that studies with low power are wasteful and uninformative. They generate a lot of noise and are likely to be systematically biased and they contribute little to a meta-analysis that weights studies by sample size. The best estimate of effect size was based on only 6 out of 42 studies. Researchers should not conduct studies with low power and editors should not publish studies with low power.