Tag Archives: Power

Questionable Research Practices: Definition, Detection, and Recommendations for Better Practices

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The term “questionable research practices” (QRPs) was popularized in an article by John, Loewenstein, and Prelec (2012).
The authors distinguish between fraud and QRPs. Fraud is typically limited to cases in which researchers create false data. In contrast, QRPs typically involve the exclusion of data that are inconsistent with a theoretical hypothesis.  QRPs are treated differently than fraud because QRPs can sometimes be used for legitimate purposes.

For example, a data entry error may produce a large outlier that leads to a non-significant result when all data are included in the analysis.  The results are significant when the outlier is removed.  Statistical textbook often advise to exclude outliers for this reason.  However, removal of outliers becomes a QRP when it is used selectively.  That is, outliers are not removed when a result is significant or when the outlier helps to produce a significant result, but outliers are removed when removal of outliers helps to get a significant result.

The use of QRPs is damaging because published results provide false impressions about the replicability of empirical results and misleading evidence about the size of an effect.

Below is a list of QRPs.

Selective reporting of (dependent) variables.  For example, a researcher may include 10 items to measure depression.  Typically, the 10 items are averaged to get the best measure of depression.  However, if this analysis does not produce a significant result, the researcher can conduct analyses of each individual item or average items that trend in the right direction.  By creating different dependent variables after the study is completed, a researcher increases the chances of obtaining a significant result that will not replicate in a replication study with the same dependent variable.

A simple solution to preventing this QRP is to ask authors to use well-established measures as dependent variables and/or to ask for pre-registration of all measures that are relevant to the test of a theoretical hypothesis (i.e., it is not necessary to specify that the study also asked about handedness because handedness is not a measure of depression).

Deciding whether to collect more data after looking to see whether the results will be significant.  It is difficult to distinguish random variation from a true effect in small samples.  At the same time, it can be a costly waste of resources (or even unethical in animal research) to conduct studies with large samples, when the effect can be detected in a smaller sample.  It is also difficult to know a priori how large a sample should be to obtain a significant result.  It therefore seems reasonable to check data while they are being collected for significance.  If an effect does not seem to be present in a reasonably large sample size, it may be better to abandon a study.  None of these practices are problematic unless a researcher constantly checks for significance and stops data collection immediately after the data show a significant result.  This practice capitalizes on sampling error and the experiment will typically stop when sampling error inflates the true effect size.

A simple solution to this problem is to set some a priori rules about the end of data collection.  For example, a researcher may calculate sample size based on a rough power analysis.  Based on an optimistic assumption that the true effect is large, the data will be checked when the study has 80% power for a large effect (d = .8).  If this does not result in a significant result, the researcher continues with the revised hypothesis that the true effect is moderate and then checks the data again when 80% power for a moderate effect is reached.  If this does not result in a significant result, the researcher may give up or continue with the revised hypothesis that the true effect is small.  This procedure would allow researchers to use an optimal amount of resources.  Moreover, they can state there sampling strategy openly so that meta-analysts can make corrections for the small amount of biases that is still introduced by this reasonable form of optional stopping.

Failing to disclose experimental conditions.   There are no justifiable reasons for the exclusion of conditions.  Evidently, researchers are not going to exclude conditions that are consistent with theoretical predictions. So, the exclusion of conditions can only produce results that are overly consistent with theoretical predictions.  If there are reasonable doubts about a condition (e.g., a manipulation check shows that it did not work), the condition can be included and it can be explained why the results may not conform to predictions).

A simple solution to the problem of conditions with unexpected results is that researchers may include too many conditions in their design.  A 2 x 2 x 2 factorial design has 8 cells, which allows for 28 comparisons of means. What are the chances that all of these 28 comparisons produce results that are consistent with theoretical predictions?

Another simple solution is to avoid the use of statistical methods with low power.  To demonstrate a three-way interaction requires a lot more data than to demonstrate that a pattern of means is consistent with an a priori theoretically predicted pattern.

In a paper reporting selectively studies that worked.

There is no reason for excluding studies that did not work. Excluding studies that were planned as demonstrations of an effect need to be reported. Otherwise the published evidence provides an overly positive picture of the robustness of a phenomenon and effect sizes are inflated.

Just like failed conditions, failed studies can be reported if there is a plausible explanation why it failed whereas other studies worked.  However, to justify this claim, it should be demonstrated that the effects in failed and successful studies are really significantly different (a significant moderator effect).  If this is not the case, there is no reason to treat failed and successful studies as different from each other.

A simple solution to this problem is to conduct studies with high statistical power because the main reason for failed studies is that studies have low power.  If a study has only 30% power, only one out of three studies will produce a significant result. The other two studies are likely to produce a type-II error (not show a significant result when the effect exists).  Rather than throwing away the two failed studies, a researcher should have conducted one study with higher power.  Another solution is to report all three studies and to test for significance only in a meta-analysis across the three studies.

In a paper, rounding off a p-value just above .054 and claim that it is below .05.   This is a minor problem. It is silly to change a p-value, but it does not bias a meta-analysis of effect sizes because researchers do not change effect size information.  Moreover, it would be even more silly not to change the p-value and conclude that there is no effect, which is often the case when results are not significant.  After all, a p-value of .054 means that the effect in this study would have occurred if the true effect is zero or has the opposite sign.

If a type-I error probability of 5.4% is considered too high, it would be possible to collect more data and test again with a larger sample (taking multiple testing into account).

Moreover, this problem should arise very infrequently. Even if a study is underpowered and has only 50% power, only 2% of p-values are expected to fall into the narrow range between .050 and .054.

In a paper, reporting an unexpected finding as having been predicted from the start.   I am sure some statisticians disagree with me and I may be wrong about this one, but I simply do not understand how a statistical analysis of some data cares about the expectations of a researcher.  Say, I analyze some data and find a significant effect in the data.  How can this effect be influenced by the way I report it later?  It may be a type-I error or it is not a type-I error, but my expectations have no influence on the causal processes that produced the empirical data.  I think the practice of writing exploratory studies as if they were conducted an a priori hypothesis is considered questionable because it often requires other QRPs (e.g., excluding additional tests that didn’t work) to produce a story that is concocted to explain unexpected results.  However, if the results are presented honestly and one out of five predictor variables in a multiple-regression is significant at p < .0001, it is likely to be a replicable finding, even if it is presented with a post-hoc prediction.

In a paper, claiming that results are unaffected by demographic variables (e.g., gender) when one is actually unsure (or knows that they do).   Again, this is a relatively minor point because it only speaks about potential moderators of a reported effect.  Moderation is important, but the conclusion about the main effect remains unchanged. For example, if an effect exists for men, but not for women, it is still true that on average there is an effect.  Furthermore, a more common mistake is often to claim that gender or other factors did not moderate an effect based on an underpowered comparison of 10 men and 30 women in a study with 40 participants.  Thus, false claims about moderating variables are annoying, but not a threat to the replicability of empirical results.

Falsifying Data. I personally do not include falsifying or fabricating of data in the list of questionable research practices.  I think falsifying and fabrication of data is not a research practice. It is also something that is clearly considered fraudulent and punished when it is discovered.  In contrast, questionable research practices are tolerated in many scientific communities and there are no clear guidelines against the use of these practices.

In conclusion, the most problematic research practices that undermine the replicability of published studies are selective reporting of dependent variables, conditions, or entire studies, and optional stopping when significance is reached.  These practices make it possible to produce significant results when a study has insufficient power.  However, to achieve significance without power, the type-I error rate also increases and replicability decreases.  John et al. (2012) aptly compared these QRPs to the use of doping in sports.  I consider the R-Index a doping test for science because it reveals that researchers used these QRPs.  I hope that the R-Index will discourage the use of QRPs and increase the power and replicability of published studies.

Whether scientific organizations should ban QRPs just like sports organizations ban doping is an interesting question.  Meanwhile the R-Index can be used without draconian consequences.  Researchers can self-examine the replicability of their findings and they can examine the replicability of published results before they invest resources, time, and the future of their graduate students in research projects that fail. Granting agencies can use the R-Index to reward researchers who conduct fewer studies with replicable results rather than researchers with many studies that fail to replicate.  Finally, the R-Index can be used to track how successful current initiatives are to increase the replicability of published studies.

Further reflections on the linearity in Dr. Förster’s Data

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A previous blog examined how and why Dr. Förster’s data showed incredibly improbable linearity.

The main hypothesis was that two experimental manipulations have opposite effects on a dependent variable.

Assuming that the average effect size of a single manipulation is similar to effect sizes in social psychology, a single manipulation is expected to have an effect size of d = .5 (change by half a standard deviation). As the two manipulations are expected to have opposite effects, the mean difference between the two experimental groups should be one standard deviation (0.5 + 0.5 = 1). With N = 40, and d = 1, a study has 87% power to produce a significant effect (p < .05, two-tailed). With power of this magnitude, it would not be surprising to get significant results in 12 comparisonForsterTables (Table 1).

The R-Index for the comparison of the two experimental groups in Table is Ř = 87%
(Success Rate = 100%, Median Observed Power = 94%, Inflation Rate = 6%).

The Test of Insufficient Variance (TIVA) shows that the variance in z-scores is less than 1, but the probability of this event to occur by chance is 10%, Var(z) = .63, Chi-square (df = 11) = 17.43, p = .096.

Thus, the results for the two experimental groups are perfectly consistent with real empirical data and the large effect size could be the result of two moderately strong manipulations with opposite effects.

The problem for Dr. Förster started when he included a control condition and want to demonstrate in each study that the two experimental groups also differed significantly from the experimental group. As already pointed out in the original post, samples of 20 participants per condition do not provide sufficient power to demonstrate effect sizes of d = .5 consistently.

To make matters worse, the three-group design has even less power than two independent studies because the same control group is used in a three-group comparison. When sampling error inflates the mean in the control group (e.g, true mean = 33, estimated mean = 36), it benefits the comparison for the experimental group with the lower mean, but it hurts the comparison for the experimental group with the higher mean (e.g., M = 27, M = 33, M = 39 vs. M = 27, M = 36, M = 39). When sampling error leads to an underestimation of the true mean in the control group (e.g., true mean = 33, estimated mean = 30), it benefits the comparison of the higher experimental group with the control group, but it hurts the comparison of the lower experimental group and the control group.

Thus, total power to produce significant results for both comparisons is even lower than for two independent studies.

It follows that the problem for a researcher with real data was the control group. Most studies would have produced significant results for the comparison of the two experimental groups, but failed to show significant differences between one of the experimental groups and the control group.

At this point, it is unclear how Jens Förster achieved significant results under the contested assumption that real data were collected. However, it seems most plausible that QRPs would be used to move the mean of the control group to the center so that both experimental groups show a significant difference. When this was impossible, the control group could be dropped, which may explain why 3 studies in Table 1 did not report results for a control group.

The influence of QRPs on the control group can be detected by examining the variation of means in Table 1 across the 12(9) studies. Sampling error should randomly increase or decrease means relative to the overall mean of an experimental condition. Thus, there is no reason to expect a correlation in the pattern of means. Consistent with this prediction, the means of the two experimental groups are unrelated, r(12) = .05, p = .889; r(9) = .36, p = .347. In contrast, the means of the control group are correlated with the means of the two experimental groups, r(9) = .73, r(9) = .71. If the means in the control group are the result of the unbiased means in the experimental groups, it makes sense to predict the means in the control group from the means in the two experimental groups. A regression equation shows that 77% of the variance in the means of the control group is explained by the variation in the means in the experimental groups, R = .88, F(2,6) = 10.06, p = .01.

This analysis clarifies the source of the unusual linearity in the data. Studies with n = 20 per condition have very low power to demonstrate significant differences between a control group and opposite experimental groups because sampling error in the control group is likely to move the mean of the control group too close to one of the experimental groups to produce a significant difference.

This problem of low power may lead researchers to use QRPs to move the mean of the control group to the center. The problem for users of QRPs is that this statistical boost of power leaves a trace in the data that can be detected with various bias tests. The pattern of the three means will be too linear, there will be insufficient variance in the effect sizes, p-values, and observed power in the comparisons of experimental groups and control groups, the success rate will exceed median observed power, and, as shown here, the means in the control group will be correlated with the means in the experimental group across conditions.

In a personal email Dr. Förster did not comment on the statistical analyses because his background in statistics is insufficient to follow the analyses. However, he rejected this scenario as an account for the unusual linearity in his data; “I never changed any means.” Another problem for this account of what could have happened is that dropping cases from the middle group would lower the sample size of this group, but the sample size is always close to n = 20. Moreover, oversampling and dropping of cases would be a QRP that Dr. Förster would remember and could report. Thus, I now agree with the conclusion of the LOWI commission that the data cannot be explained by using QRPs, mainly because Dr. Förster denies having used any plausible QRPs that could have produced his results.

Some readers may be confused about this conclusion because it may appear to contradict my first blog. However, my first blog merely challenged the claim by the LOWI commission that linearity cannot be explained by QRPs. I found a plausible way in which QRPs could have produced linearity, and these new analyses still suggest that secretive and selective dropping of cases from the middle group could be used to show significant contrasts. Depending on the strength of the original evidence, this use of QRPs would be consistent with the widespread use of QRPs in the field and would not be considered scientific misconduct. As Roy F. Baumeister, a prominent social psychologist put it, “this is just how the field works.” However, unlike Roy Baumeister, who explained improbable results with the use of QRPs, Dr. Förster denies any use of QRPs that could potentially explain the improbable linearity in his results.

In conclusion, the following facts have been established with sufficient certainty:
(a) the reported results are too improbable to reflect just true effects and sampling error; they are not credible.
(b) the main problem for a researcher to obtain valid results is the low power of multiple-study articles and the difficulty of demonstrating statistical differences between one control group and two opposite experimental groups.
(c) to avoid reporting non-significant results, a researcher must drop failed studies and selectively drop cases from the middle group to move the mean of the middle group to the middle.
(d) Dr. Förster denies the use of QRPs and he denies data manipulation.
Evidently, the facts do not add up.

The new analyses suggest that there is one simple way for Dr. Förster to show that his data have some validity. The reason is that the comparison of the two experimental groups shows an R-Index of 87%. This implies that there is nothing statistically improbable about the comparison of these data. If these reported results are based on real data, a replication study is highly likely to replicate the mean difference between the two experimental groups. With n = 20 in each cell (N = 40), it would be relatively easy to conduct a preregistered and transparent replication study. However, without further credible evidence the published data lack credible scientific evidence and it would be prudent to retract all articles that show unusual statistical patterns that cannot be explained by the author.

A Playful Way to Learn about Power, Publication Bias, and the R-Index: Simulate questionable research methods and see what happens.

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This blog introduces a simple excel spreadsheet that simulates the effect of excluding non-significant results from an unbiased set of studies.

The results in the most left column show the results for an unbiased set of 100 studies (N = 100, dropped = 0). The power value is used to compute the observed power in the 100 studies based on a normal distribution around the non-centrality parameter corresponding to the power value (e.g., power = .50, ncp = 1.96).

For an unbiased set of studies, median observed power is equivalent to the success rate (percentage of significant results) in a set of studies. For example, with 50% power, the median observed ncp is 1.96, which is equivalent to the true ncp of 1.96 that corresponds to 50% power. In this case, the success rate is 50%. As the success rate is equivalent to median observed power, there is no inflation in the success rate and the inflation rate is 0. As a result, the R-Index is equivalent to median observed power and success rate. R-Index = Median Observed Power – Inflation Rate; .50 = .50 – 0.

Moving to the right, studies with the lowest observed ncp values (equivalent to the highest p-values) are dropped in sets of 5 studies. However, you can make changes to the way results are excluded or altered to simulate questionable research practices. When non-significant studies are dropped, median observed power and success rate increase. Eventually, the success rate increases faster than median observed power, leading to a positive inflation rate. As the inflation rate is subtracted from median observed power, the R-Index starts to correct for publication bias. For example, in the example with 50% true power, median observed power is inflated to 63% by dropping 25 non-significant results. The success rate is 67%, the inflation rate is 4% and the R-Index is 59%. Thus, the R-Index still overestimates true power by 9%, but it provides a better estimate of true power than median observed power without a correction (63%).

An important special case is the scenario where all non-significant results are dropped. This scenario is automatically highlighted with orange cells for the number of studies and success rate. With 50% true power, the event occurs when 50% of the studies are dropped. In this scenario, median observed power is 76%, the success rate is 100%, inflation rate is 24% and the R-Index is 51%. These values are slightly different from more exact simulations which show 75% median observed power, 25% inflation rate and an R-Index of 50%.

The table below lists the results for different levels of true power when all non-significant results are dropped. The scenario with 5% power implies that the null-hypothesis is true, but that 5% of significant results are obtained due to sampling error alone.

True Power         MOP      IR           R-Index

5%                     66           34           32
30%                     70           30           40
50%                     75           25           50
65%                     80           20           60
80%                     87           13           73
95%                     96           04           91
Success Rate is fixed at 100%; MOP = median observed power; IR = Inflation Rate, R-Index

The results show that the R-Index tracks observed power, but it is not an unbiased estimate of true power. In real data the process that leads to bias is unknown and it is impossible to obtain an unbiased estimate of true power from a biased set of studies. This is the reason why it is important to eliminate biases in publications as much as possible. However, the R-Index provides some useful information about the true power and replicability in a biased set of studies.

Simulation R-Index [click on link to download spreadsheet]

Dr. Schnall’s R-Index

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In several blog posts, Dr. Schnall made some critical comments about attempts to replicate her work and these blogs created a heated debate about replication studies. Heated debates are typically a reflection of insufficient information. Is the Earth flat? This question created heated debates hundreds of years ago. In the age of space travel it is no longer debated. In this blog, I presented some statistical information that sheds light on the debate about the replicability of Dr. Schnall’s research.

The Original Study

Dr. Schnall and colleagues conducted a study with 40 participants. A comparison of two groups on a dependent variable showed a significant difference, F(1,38) = 3.63. In these days, Psychological Science asked researchers to report P-Rep instead of p-values. P-rep was 90%. The interpretation of P-rep was that there is a 90% chance to find an effect with the SAME SIGN in an exact replication study with the same sample size. The conventional p-value for F(1,38) = 3.63 is p = .06, a finding that commonly is interpreted as marginally significant. The standardized effect size is d = .60, which is considered a moderate effect size. The 95% confidence interval is -.01 to 1.47.

The wide confidence interval makes it difficult to know the true effect size. A post-hoc power analysis, assuming the true effect size is d = .60 suggests that an exact replication study has a 46% chance to produce a significant results (p < .05, two-tailed). However, if the true effect size is lower, actual power is lower. For example, if the true effect size is small (d = .2), a study with N = 40 has only 9% power (that is a 9% chance) to produce a significant result.

The First Replication Study

Drs. Johnson, Cheung, and Donnellan conducted a replication study with 209 participants. Assuming the effect size in the original study is the true effect size, this replication study has 99% power. However, assuming the true effect size is only d = .2, the study has only 31% power to produce a significant result. The study produce a non-significant result, F(1, 206) = .004, p = .95. The effect size was d = .01 (in the same direction). Due to the larger sample, the confidence interval is smaller and ranges from -.26 to .28. The confidence interval includes d = 2. Thus, both studies are consistent with the hypothesis that the effect exists and that the effect size is small, d = .2.

The Second Replication Study

Dr. Huang conducted another replication study with N = 214 participants (Huang, 2004, Study 1). Based on the previous two studies, the true effect might be expected to be somewhere between -.01 and .28, which includes a small effect size of d = .20. A study with N = 214 participants has 31% power to produce a significant result. Not surprisingly, the study produce a non-significant result, t(212) = 1.22, p = .23. At the same time, the effect size fell within the confidence interval set by the previous two studies, d = .17.

A Third Replication Study

Dr. Hung conducted a replication study with N = 440 participants (Study 2). Maintaining the plausible effect size of d = .2 as the best estimate of the true effect size, the study has 55% power to produce a significant result, which means it is nearly as likely to produce a non-significant result as it is to produce a significant result, if the effect size is small (d = .2). The study failed to produce a significant result, t(438) = .042, p = 68. The effect size was d = .04 with a confidence interval ranging from -.14 to .23. Again, this confidence interval includes a small effect size of d = .2.

A Fourth Replication Study

Dr. Hung published a replication study in the supplementary materials to the article. The study again failed to demonstrate a main effect, t(434) = 0.42, p = .38. The effect size is d = .08 with a confidence interval of -.11 to .27. Again, the confidence interval is consistent with a small true effect size of d = .2. However, the study with 436 participants had only a 55% chance to produce a significant result.

If Dr. Huang had combined the two samples to conduct a more powerful study, a study with 878 participants would have 80% power to detect a small effect size of d = .2. However, the combined effect size of d = .06 for the combined samples is still not significant, t(876) = .89. The confidence interval ranges from -.07 to .19. It no longer includes d = .20, but the results are still consistent with a positive, yet small effect in the range between 0 and .20.

Conclusion

In sum, nobody has been able to replicate Schnall’s finding that a simple priming manipulation with cleanliness related words has a moderate to strong effect (d = .6) on moral judgments of hypothetical scenarios. However, all replication studies show a trend in the same direction. This suggests that the effect exists, but that the effect size is much smaller than in the original study; somewhere between 0 and .2 rather than .6.

Now there are three possible explanations for the much larger effect size in Schnall’s original study.

1. The replication studies were not exact replications and the true effect size in Schnall’s version of the experiment is stronger than in the other studies.

2. The true effect size is the same in all studies, but Dr. Schnall was lucky to observe an effect size that was three times as large as the true effect size and large enough to produce a marginally significant result.

3. It is possible that Dr. Schnall did not disclose all of the information about her original study. For example, she may have conducted additional studies that produced smaller and non-significant results and did not report these results. Importantly, this practice is common and legal and in an anonymous survey many researchers admitted using practices that produce inflated effect sizes in published studies. However, it is extremely rare for researchers to admit that these common practices explain one of their own findings and Dr. Schnall has attributed the discrepancy in effect sizes to problems with replication studies.

Dr. Schnall’s Replicability Index

Based on Dr. Schnall’s original study it is impossible to say which of these explanations accounts for her results. However, additional evidence makes it possible to test the third hypothesis that Dr. Schnall knows more than she was reporting in her article. The reason is that luck does not repeat itself. If Dr. Schnall was just lucky, other studies by her should have failed because Lady Luck is only on your side half the time. If, however, disconfirming evidence is systematically excluded from a manuscript, the rate of successful studies is higher than the observed statistical power in published studies (Schimmack, 2012).

To test this hypothesis, I downloaded Dr. Schnall’s 10 most cited articles (in Web of Science, July, 2014). These 10 articles contained 23 independent studies. For each study, I computed the median observed power of statistical tests that tested a theoretically important hypothesis. I also calculated the success rate for each study. The average success rate was 91% (ranging from 45% to 100%, median = 100%). The median observed power was 61%. The inflation rate is 30% (91%-61%). Importantly, observed power is an inflated estimate of replicability when the success rate is inflated. I created the replicability index (R-index) to take this inflation into account. The R-Index subtracts the inflation rate from observed median power.

Dr. Schnall’s R-Index is 31% (61% – 30%).

What does an R-Index of 31% mean? Here are some comparisons that can help to interpret the Index.

Imagine the null-hypothesis is always true, and a researcher publishes only type-I errors. In this case, observed power is 61% and the success rate is 100%. The R-Index is 22%.

Dr. Baumeister admitted that his publications select studies that report the most favorable results. His R-Index is 49%.

The Open Science Framework conducted replication studies of psychological studies published in 2008. A set of 25 completed studies in November 2014 had an R-Index of 43%. The actual rate of successful replications was 28%.

Given this comparison standards, it is hardly surprising that one of Dr. Schnall’s study did not replicate even when the sample size and power of replication studies were considerably higher.

Conclusion

Dr. Schnall’s R-Index suggests that the omission of failed studies provides the most parsimonious explanation for the discrepancy between Dr. Schnall’s original effect size and effect sizes in the replication studies.

Importantly, the selective reporting of favorable results was and still is an accepted practice in psychology. It is a statistical fact that these practices reduce the replicability of published results. So why do failed replication studies that are entirely predictable create so much heated debate? Why does Dr. Schnall fear that her reputation is tarnished when a replication study reveals that her effect sizes were inflated? The reason is that psychologists are collectively motivated to exaggerate the importance and robustness of empirical results. Replication studies break with the code to maintain an image that psychology is a successful science that produces stunning novel insights. Nobody was supposed to test whether published findings are actually true.

However, Bem (2011) let the cat out of the bag and there is no turning back. Many researchers have recognized that the public is losing trust in science. To regain trust, science has to be transparent and empirical findings have to be replicable. The R-Index can be used to show that researchers reported all the evidence and that significant results are based on true effect sizes rather than gambling with sampling error.

In this new world of transparency, researchers still need to publish significant results. Fortunately, there is a simple and honest way to do so that was proposed by Jacob Cohen over 50 years ago. Conduct a power analysis and invest resources only in studies that have high statistical power. If your expertise led you to make a correct prediction, the force of the true effect size will be with you and you do not have to rely on Lady Luck or witchcraft to get a significant result.

P.S. I nearly forgot to comment on Dr. Huang’s moderator effects. Dr. Huang claims that the effect of the cleanliness manipulation depends on how much effort participants exert on the priming task.

First, as noted above, no moderator hypothesis is needed because all studies are consistent with a true effect size in the range between 0 and .2.

Second, Dr. Huang found significant interaction effects in two studies. In Study 2, the effect was F(1,438) = 6.05, p = .014, observed power = 69%. In Study 2a, the effect was F(1,434) = 7.53, p = .006, observed power = 78%. The R-Index for these two studies is 74% – 26% = 48%.   I am waiting for an open science replication with 95% power before I believe in the moderator effect.

Third, even if the moderator effect exists, it doesn’t explain Dr. Schnall’s main effect of d = .6.