Tag Archives: research integrity

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.

How Power Analysis Could Have Prevented the Sad Story of Dr. Förster

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[further information can be found in a follow up blog]

Background

In 2011, Dr. Förster published an article in Journal of Experimental Psychology: General. The article reported 12 studies and each study reported several hypothesis tests. The abstract reports that “In all experiments, global/local processing in 1 modality shifted to global/local processing in the other modality”.

For a while this article was just another article that reported a large number of studies that all worked and neither reviewers nor the editor who accepted the manuscript for publication found anything wrong with the reported results.

In 2012, an anonymous letter voiced suspicion that Jens Forster violated rules of scientific misconduct. The allegation led to an investigation, but as of today (January 1, 2015) there is no satisfactory account of what happened. Jens Förster maintains that he is innocent (5b. Brief von Jens Förster vom 10. September 2014) and blames the accusations about scientific misconduct on a climate of hypervigilance after the discovery of scientific misconduct by another social psychologist.

The Accusation

The accusation is based on an unusual statistical pattern in three publications. The 3 articles reported 40 experiments with 2284 participants, that is an average sample size of N = 57 participants in each experiment. The 40 experiments all had a between-subject design with three groups: one group received a manipulation design to increase scores on the dependent variable. A second group received the opposite manipulation to decrease scores on the dependent variable. And a third group served as a control condition with the expectation that the average of the group would fall in the middle of the two other groups. To demonstrate that both manipulations have an effect, both experimental groups have to show significant differences from the control group.

The accuser noticed that the reported means were unusually close to a linear trend. This means that the two experimental conditions showed markedly symmetrical deviations from the control group. For example, if one manipulation increased scores on the dependent variables by half a standard deviation (d = +.5), the other manipulation decreased scores on the dependent variable by half a standard deviation (d = -.5). Such a symmetrical pattern can be expected when the two manipulations are equally strong AND WHEN SAMPLE SIZES ARE LARGE ENOUGH TO MINIMIZE RANDOM SAMPLING ERROR. However, the sample sizes were small (n = 20 per condition, N = 60 per study). These sample sizes are not unusual and social psychologists often use n = 20 per condition to plan studies. However, these sample sizes have low power to produce consistent results across a large number of studies.

The accuser computed the statistical probability of obtaining the reported linear trend. The probability of obtaining the picture-perfect pattern of means by chance alone was incredibly small.

Based on this finding, the Dutch National Board for Research Integrity (LOWI) started an investigation of the causes for this unlikely finding. An English translation of the final report was published on retraction watch. An important question was whether the reported results could have been obtained by means of questionable research practices or whether the statistical pattern can only be explained by data manipulation. The English translation of the final report includes two relevant passages.

According to one statistical expert “QRP cannot be excluded, which in the opinion of the expert is a common, if not “prevalent” practice, in this field of science.” This would mean that Dr. Förster acted in accordance with scientific practices and that his behavior would not constitute scientific misconduct.

In response to this assessment the Complainant “extensively counters the expert’s claim that the unlikely patterns in the experiments can be explained by QRP.” This led to the decision that scientific misconduct occurred.

Four QRPs were considered.

  1. Improper rounding of p-values. This QRP can only be used rarely when p-values happen to be close to .05. It is correct that this QRP cannot produce highly unusual patterns in a series of replication studies. It can also be easily checked by computing exact p-values from reported test statistics.
  2. Selecting dependent variables from a set of dependent variables. The articles in question reported several experiments that used the same dependent variable. Thus, this QRP cannot explain the unusual pattern in the data.
  3. Collecting additional research data after an initial research finding revealed a non-significant result. This description of an QRP is ambiguous. Presumably it refers to optional stopping. That is, when the data trend in the right direction to continue data collection with repeated checking of p-values and stopping when the p-value is significant. This practices lead to random variation in sample sizes. However, studies in the reported articles all have more or less 20 participants per condition. Thus, optional stopping can be ruled out. However, if a condition with 20 participants does not produce a significant result, it could simply be discarded, and another condition with 20 participants could be run. With a false-positive rate of 5%, this procedure will eventually yield the desired outcome while holding sample size constant. It seems implausible that Dr. Förster conducted 20 studies to obtain a single significant result. Thus, it is even more plausible that the effect is actually there, but that studies with n = 20 per condition have low power. If power were just 30%, the effect would appear in every third study significantly, and only 60 participants were used to produce significant results in one out of three studies. The report provides insufficient information to rule out this QRP, although it is well-known that excluding failed studies is a common practice in all sciences.
  4. Selectively and secretly deleting data of participants (i.e., outliers) to arrive at significant results. The report provides no explanation how this QRP can be ruled out as an explanation. Simmons, Nelson, and Simonsohn (2011) demonstrated that conducting a study with 37 participants and then deleting data from 17 participants can contribute to a significant result when the null-hypothesis is true. However, if an actual effect is present, fewer participants need to be deleted to obtain a significant result. If the original sample size is large enough, it is always possible to delete cases to end up with a significant result. Of course, at some point selective and secretive deletion of observation is just data fabrication. Rather than making up data, actual data from participants are deleted to end up with the desired pattern of results. However, without information about the true effect size, it is difficult to determine whether an effect was present and just embellished (see Fisher’s analysis of Mendel’s famous genetics studies) or whether the null-hypothesis is true.

The English translation of the report does not contain any statements about questionable research practices from Dr. Förster. In an email communication on January 2, 2014, Dr. Förster revealed that he in fact ran multiple studies, some of which did not produce significant results, and that he only reported his best studies. He also mentioned that he openly admitted to this common practice to the commission. The English translation of the final report does not mention this fact. Thus, it remains an open question whether QRPs could have produced the unusual linearity in Dr. Förster’s studies.

A New Perspective: The Curse of Low Powered Studies

One unresolved question is why Dr. Förster would manipulate data to produce a linear pattern of means that he did not even mention in his articles. (Discover magazine).

One plausible answer is that the linear pattern is the by-product of questionable research practices to claim that two experimental groups with opposite manipulations are both significantly different from a control group. To support this claim, the articles always report contrasts of the experimental conditions and the control condition (see Table below). ForsterTable

In Table 1 the results of these critical tests are reported with subscripts next to the reported means. As the direction of the effect is theoretically determined, a one-tailed test was used. The null-hypothesis was rejected when p < .05.

Table 1 reports 9 comparisons of global processing conditions and control groups and 9 comparisons of local processing conditions with a control group; a total of 18 critical significance tests. All studies had approximately 20 participants per condition. The average effect size across the 18 studies is d = .71 (median d = .68).   An a priori power analysis with d = .7, N = 40, and significance criterion .05 (one-tailed) gives a power estimate of 69%.

An alternative approach is to compute observed power for each study and to use median observed power (MOP) as an estimate of true power. This approach is more appropriate when effect sizes vary across studies. In this case, it leads to the same conclusion, MOP = 67.

The MOP estimate of power implies that a set of 100 tests is expected to produce 67 significant results and 33 non-significant results. For a set of 18 tests, the expected values are 12.4 significant results and 5.6 non-significant results.

The actual success rate in Table 1 should be easy to infer from Table 1, but there are some inaccuracies in the subscripts. For example, Study 1a shows no significant difference between means of 38 and 31 (d = .60, but it shows a significant difference between means 31 and 27 (d = .33). Most likely the subscript for the control condition should be c not a.

Based on the reported means and standard deviations, the actual success rate with N = 40 and p < .05 (one-tailed) is 83% (15 significant and 3 non-significant results).

The actual success rate (83%) is higher than one would expect based on MOP (67%). This inflation in the success rate suggests that the reported results are biased in favor of significant results (the reasons for this bias are irrelevant for the following discussion, but it could be produced by not reporting studies with non-significant results, which would be consistent with Dr. Förster’s account ).

The R-Index was developed to correct for this bias. The R-Index subtracts the inflation rate (83% – 67% = 16%) from MOP. For the data in Table 1, the R-Index is 51% (67% – 16%).

Given the use of a between-subject design and approximately equal sample sizes in all studies, the inflation in power can be used to estimate inflation of effect sizes. A study with N = 40 and p < .05 (one-tailed) has 50% power when d = .50.

Thus, one interpretation of the results in Table 1 is that the true effect sizes of the manipulation is d = .5, that 9 out of 18 tests should have produced a significant contrast at p < .05 (one-tailed) and that questionable research practices were used to increase the success rate from 50% to 83% (15 vs. 9 successes).

The use of questionable research practices would also explain unusual linearity in the data. Questionable research practices will increase or omit effect sizes that are insufficient to produce a significant result. With a sample size of N = 40, an effect size of d = .5 is insufficient to produce a significant result, d = .5, se = 32, t(38) = 1.58, p = .06 (one-tailed). Random sampling error that works against the hypothesis can only produce non-significant results that have to be dropped or moved upwards using questionable methods. Random error that favors the hypothesis will inflate the effect size and start producing significant results. However, random error is normally distributed around the true effect size and is more likely to produce results that are just significant (d = .8) than to produce results that are very significant (d = 1.5). Thus, the reported effect sizes will be clustered more closely around the median inflated effect size than one would expect based on an unbiased sample of effect sizes.

The clustering of effect sizes will happen for the positive effects in the global processing condition and for the negative effects in the local processing condition. As a result, the pattern of all three means will be more linear than an unbiased set of studies would predict. In a large set of studies, this bias will produce a very low p-value.

One way to test this hypothesis is to examine the variability in the reported results. The Test of Insufficient Variance (TIVA) was developed for this purpose. TIVA first converts p-values into z-scores. The variance of z-scores is known to be 1. Thus, a representative sample of z-scores should have a variance of 1, but questionable research practices lead to a reduction in variance. The probability that a set of z-scores is a representative set of z-scores can be computed with a chi-square test and chi-square is a function of the ratio of the expected and observed variance and the number of studies. For the set of studies in Table 1, the variance in z-scores is .33. The chi-square value is 54. With 17 degrees of freedom, the p-value is 0.00000917 and the odds of this event occurring by chance are 1 out of 109,056 times.

Conclusion

Previous discussions about abnormal linearity in Dr. Förster’s studies have failed to provide a satisfactory answer. An anonymous accuser claimed that the data were fabricated or manipulated, which the author vehemently denies. This blog proposes a plausible explanation of what could have [edited January 19, 2015] happened. Dr. Förster may have conducted more studies than were reported and included only studies with significant results in his articles. Slight variation in sample sizes suggests that he may also have removed a few outliers selectively to compensate for low power. Importantly, neither of these practices would imply scientific misconduct. The conclusion of the commission that scientific misconduct occurred rests on the assumption that QRPs cannot explain the unusual linearity of means, but this blog points out how selective reporting of positive results may have inadvertently produced this linear pattern of means. Thus, the present analysis support the conclusion by an independent statistical expert mentioned in the LOWI report: “QRP cannot be excluded, which in the opinion of the expert is a common, if not “prevalent” practice, in this field of science.”

How Unusual is an R-Index of 51?

The R-Index for the 18 statistical tests reported in Table 1 is 51% and TIVA confirms that the reported p-values have insufficient variance. Thus, it is highly probable that questionable research practices contributed to the results and in a personal communication Dr. Förster confirmed that additional studies with non-significant results exist. However, in response to further inquiries [see follow up blog] Dr. Förster denied having used QRPs that could explain the linearity in his data.

Nevertheless, an R-Index of 51% is not unusual and has been explained with the use of QRPs.  For example, the R-Index for a set of studies by Roy Baumeister was 49%, . and Roy Baumeister stated that QRPs were used to obtain significant results.

“We did run multiple studies, some of which did not work, and some of which worked better than others. You may think that not reporting the less successful studies is wrong, but that is how the field works.”

Sadly, it is quite common to find an R-Index of 50% or lower for prominent publications in social psychology. This is not surprising because questionable research practices were considered good practices until recently. Even at present, it is not clear whether these practices constitute scientific misconduct (see discussion in Dialogue, Newsletter of the Society for Personality and Social Psychology).

How to Avoid Similar Sad Stories in the Future

One way to avoid accusations of scientific misconduct is to conduct a priori power analyses and to conduct only studies with a realistic chance to produce a significant result when the hypothesis is correct. When random error is small, true patterns in data can emerge without the help of QRPs.

Another important lesson from this story is to reduce the number of statistical tests as much as possible. Table 1 reported 18 statistical tests with the aim to demonstrate significance in each test. Even with a liberal criterion of .1 (one-tailed), it is highly unlikely that so many significant tests will produce positive results. Thus, a non-significant result is likely to emerge and researchers should think ahead of time how they would deal with non-significant results.

For the data in Table 1, Dr. Förster could have reported the means of 9 small studies without significance tests and conduct significance tests only once for the pattern in all 9 studies. With a total sample size of 360 participants (9 * 40), this test would have 90% power even if the effect size is only d = .35. With 90% power, the total power to obtain significant differences from the control condition for both manipulations would be 81%. Thus, the same amount of resources that were used for the controversial findings could have been used to conduct a powerful empirical test of theoretical predictions without the need to hide inconclusive, non-significant results in studies with low power.

Jacob Cohen has been trying to teach psychologists the importance of statistical power for decades and psychologists stubbornly ignored his valuable contribution to research methodology until he died in 1998. Methodologists have been mystified by the refusal of psychologists to increase power in their studies (Maxwell, 2004).

One explanation is that small samples provided a huge incentive. A non-significant result can be discarded with little cost of resources, whereas a significant result can be published and have the additional benefit of an inflated effect size, which allows boosting the importance of published results.

The R-Index was developed to balance the incentive structure towards studies with high power. A low R-Index reveals that a researcher is reporting biased results that will be difficult to replicate by other researchers. The R-Index reveals this inconvenient truth and lowers excitement about incredible results that are indeed incredible. The R-Index can also be used by researchers to control their own excitement about results that are mostly due to sampling error and to curb the excitement of eager research assistants that may be motivated to bias results to please a professor.

Curbed excitement does not mean that the R-Index makes science less exciting. Indeed, it will be exciting when social psychologists start reporting credible results about social behavior that boost a high R-Index because for a true scientist nothing is more exciting than the truth.

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.

The Replicability-Index (R-Index): Quantifying Research Integrity

Post-Hoc Power, r-index, R-Index4Science, Replicability, Research Integrity, science, , , ,

ANNIVERSARY POST.  Slightly edited version of first R-Index Blog on December 1, 2014.

In a now infamous article, Bem (2011) produced 9 (out of 10) statistically significant results that appeared to show time-reversed causality.  Not surprisingly, subsequent studies failed to replicate this finding.  Although Bem never admitted it, it is likely that he used questionable research practices to produce his results. That is, he did not just run 10 studies and found 9 significant results. He may have dropped failed studies, deleted outliers, etc.  It is well-known among scientists (but not lay people) that researchers routinely use these questionable practices to produce results that advance their careers.  Think, doping for scientists.

I have developed a statistical index that tracks whether published results were obtained by conducting a series of studies with a good chance of producing a positive result (high statistical power) or whether researchers used questionable research practices.  The R-Index is a function of the observed power in a set of studies. More power means that results are likely to replicate in a replication attempt.  The second component of the R-index is the discrepancy between observed power and the rate of significant results. 100 studies with 80% power should produce, on average, 80% significant results. If observed power is 80% and the success rate is 100%, questionable research practices were used to obtain more significant results than the data justify.  In this case, the actual power is less than 80% because questionable research practices inflate observed power. The R-index subtracts the discrepancy (in this case 20% too many significant results) from observed power to adjust for the inflation.  For example, if observed power is 80% and success rate is 100%, the discrepancy is 20% and the R-index is 60%.

In a paper, I show that the R-index predicts success in empirical replication studies.

The R-index also sheds light on the recent controversy about failed replications in psychology (repligate) between replicators and “replihaters.”   Replicators sometimes imply that failed replications are to be expected because original studies used small samples with surprisingly large effects, possibly due to the use of questionable research practices. Replihaters counter that replicators are incompetent researchers who are motivated to produce failed studies.  The R-Index makes it possible to evaluate these claims objectively and scientifically.  It shows that the rampant use of questionable research practices in original studies makes it extremely likely that replication studies will fail.  Replihaters should take note that questionable research practices can be detected and that many failed replications are predicted by low statistical power in original articles.