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.

The article reported results of 10 studies with 9 z-scores being significant at p < .05 (one-tailed). The observed variance in the 10 z-scores is 0.19. Using Formula 1, the chi-square value is chi^2 (df = 9) = 1.75. Importantly, chi-square tests are usually used to test whether variance is greater than expected by chance (right tail of the distribution). The reason is that variance is not expected to be less than the variance expected by chance because it is typically assumed that a set of data is unbiased. To obtain a probability of insufficient variance, it is necessary to test the left-tail of the chi-square distribution.  The corresponding p-value for chi^2 (df = 9) = 1.75 is p = .005. Thus, there is only a 1 out of 200 probability that a random set of 10 studies would produce a variance as low as Var = .19.

This outcome cannot be attributed to publication bias because all studies were published in a single article. Thus, TIVA supports the hypothesis that the insufficient variance in Bem’s z-scores is the result of questionable research methods and that the reported effect size of d = .2 is inflated. The presence of bias does not imply that the true effect size is 0, but it does strongly suggest that the true effect size is smaller than the average effect size in a set of studies with insufficient variance.

Example 2:  

Vohs et al. (2006) published a series of studies that he results of nine experiments in which participants were reminded of money. The results appeared to show that “money brings about a self-sufficient orientation.” Francis and colleagues suggested that the reported results are too good to be true. An R-Index analysis showed an R-Index of 21, which is consistent with a model in which the null-hypothesis is true and only significant results are reported.

Because Vohs et al. (2006) conducted multiple tests in some studies, the median p-value was used for conversion into z-scores. The p-values and z-scores for the nine studies are reported in Table 2. The Figure on top of this blog illustrates the distribution of the 9 z-scores relative to the expected standard normal distribution.

Table 2

Study                    p             z          

Study 1                .026       2.23
Study 2                .050       1.96
Study 3                .046       1.99
Study 4                .039       2.06
Study 5                .021       2.99
Study 6                .040       2.06
Study 7                .026       2.23
Study 8                .023       2.28
Study 9                .006       2.73
                                                           

The variance of the 9 z-scores is .054. This is even lower than the variance in Bem’s studies. The chi^2 test shows that this variance is significantly less than expected from an unbiased set of studies, chi^2 (df = 8) = 1.12, p = .003. An unusual event like this would occur in only 1 out of 381 studies by chance alone.

In conclusion, insufficient variance in z-scores shows that it is extremely likely that the reported results overestimate the true effect size and replicability of the reported studies. This confirms earlier claims that the results in this article are too good to be true (Francis et al., 2014). However, TIVA is more powerful than the Test of Excessive Significance and can provide more conclusive evidence that questionable research practices were used to inflate effect sizes and the rate of significant results in a set of studies.

Conclusion

TIVA can be used to examine whether a set of published p-values was obtained with the help of questionable research practices. When p-values are converted into z-scores, the variance of z-scores should be greater or equal to 1. Insufficient variance suggests that questionable research practices were used to avoid publishing non-significant results; this includes simply not reporting failed studies.

At least within psychology, these questionable research practices are used frequently to compensate for low statistical power and they are not considered scientific misconduct by governing bodies of psychological science (APA, APS, SPSP). Thus, the present results do not imply scientific misconduct by Bem or Vohs, just like the use of performance enhancing drugs in sports is not illegal unless a drug is put on an anti-doping list. However, jut because a drug is not officially banned, it does not mean that the use of a drug has no negative effects on a sport and its reputation.

One limitation of TIVA is that it requires a set of studies and that variance in small sets of studies can vary considerably just by chance. Another limitation is that TIVA is not very sensitive when there is substantial heterogeneity in true non-centrality parameters. In this case, the true variance in z-scores can mask insufficient variance in random sampling error. For this reason, TIVA is best used in conjunction with other bias tests. Despite these limitations, the present examples illustrate that TIVA can be a powerful tool in the detection of questionable research practices.  Hopefully, this demonstration will lead to changes in the way researchers view questionable research practices and how the scientific community evaluates results that are statistically improbable. With rejection rates at top journals of 80% or more, one would hope that in the future editors will favor articles that report results from studies with high statistical power that obtain significant results that are caused by the predicted effect.

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Christmas Special: R-Index of “Women Are More Likely to Wear Red or Pink at Peak Fertility”

An article in Psychological Science titled “Women Are More Likely to Wear Red or Pink at Peak Fertility” reported two studies that related women’s cycle to the color of their shirts. Study 1 (N = 100) found that women were more likely to wear red or pink shirts around the time of ovulation. Study 2 (N = 25) replicated this finding. An article in Slate magazine, “Too good to be true” questioned the credibility of the reported results. The critique led to a lively discussion about research practices, statistics, and psychological science in general.

The R-Index provides some useful information about some unresolved issues in the debate.

The main finding in Study 1 was a significant chi-square test, chi-square (1, N = 100) = 5.32, p = .021, z = 2.31, observed power 64%.

The main finding in Study 2 was a chi-square test, chi-square (1, N = 25) = 3.82, p = .051, z = 1.95, observed power 50%.

One way to look at these results is to assume that the authors planned the two studies, including sample sizes, conducted two statistical significance tests and reported the results of their planned analysis. Both tests have to produce significant results in the predicted direction at p = .05 (two-tailed) to be published in Psychological Science. The authors claim that the probability of this event to occur by chance is only 0.25% (5% * 5%). In fact, the probability is even lower because a two-tailed can be significant when the effect is opposite to the hypothesis (i.e., women are less likely to wear red at peak fertility, p < .05, two-tailed). The probability to get significant results in a theoretically predicted direction with p = .05 (two-tailed) is equivalent to a one-tailed test with p = .025 as significance criterion. The probability of this happening twice in a row is only 0.06%.  According to this scenario, the significant results in the two studies are very unlikely to be a chance finding. Thus, they provide evidence that women are more likely to wear red at peak fertility.

The R-Index takes a different perspective. The focus is on replicability of the results reported in the two studies. Replicability is defined as the long-run probability to produce significant results in exact replication studies; everything but random sampling error is constant.

The first step is to estimate replicability of each study. Replicabilty is estimated by converting p-values into observed power estimates. As shown above, observed power is estimated to be 64% in Study 1 and 50% in Study 2.   If these estimates were correct, the probability to replicate significant results in two exact replication studies would be 32%. This also implies that the chance of obtaining significant results in the original studies was only 32%. This raises the question of what researchers would do when a non-significant result is not obtained. If reporting or publication bias prevent these results from being published, published results provide an inflated estimate of replicability (100% success rate with 32% probability to be successful).

The R-Index uses the median as the best estimate of the typical power in a set of studies. Median observed power is 57%. Based on this estimate of the true power, the authors were lucky to get two significant results, when only 57% of the two studies (the expected number of significant results is 1.14 (2 * .57). The discrepancy between the success rate (100%) and the expected rate of significant results (57%) shows the inflated rate of significant results (100% – 57% = 43%). The R-Index corrects for this inflation by subtracting the inflation rate from observed power.

The R-Index is 57% – 43% = 14%.  

To interpret an R-Index of 14%, the following scenarios are helpful.

When the null-hypothesis is true and non-significant results are not reported, the R-Index is 22%. Thus, the R-Index for this pair of studies is lower than the R-Index for the null-hypothesis.

With just two studies, it is possible that researchers were just lucky to get two significant results despite a low probability of this event to occur.

For other researchers it is not important why reported results are likely to be too good to be true. For science, it is more important that the reported results can be generalized to future studies and real world situations. The main reason to publish studies in scientific journals is to provide evidence that can be replicated even in studies that are not exact replication studies, but provide sufficient opportunity for the same causal process (peak fertility influences women’s clothing choices) to be observed. With this goal in mind, a low R-Index reveals that the two studies provide rather weak evidence for the hypothesis.

In fact, only 28% of studies with an average R-Index of 43% replicated in a large test of replicability. Failed replication studies consistently tend to have an R-Index below 50%.

For this reason, Psychological Science should have rejected the article and asked the authors to provide stronger evidence for their hypothesis.

Psychological Science should also have rejected the article because the second study had only a quarter of the sample size of Study 1 (N = 25 vs. 100). Given the effect size in Study 1 and observed power of only 63% in Study 1, cutting the sample sizes by 75% reduces the probability to obtain a significant effect in Study 2 to 20%. Thus, the authors were extremely lucky to produce a significant result in Study 2. It would have been better to conduct the replication study with a sample of 150 participants to have 80% power to replicate the effect in Study 1.

Conclusion

The R-Index of “Women Are More Likely to Wear Red or Pink at Peak Fertility” is 19. This is a low value and suggests that the results will not replicate in an exact replication study. It is possible that the authors were just lucky to get two significant results. However, lucky results distort the scientific evidence and these results should not be published without a powerful replication study that does not rely on luck to produce significant results. To avoid controversies like these and to increase the credibility of published results, researchers should conduct more powerful tests of hypothesis and scientific journals should favor studies that have a high R-Index.

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.

The power analysis shows that the pre-post design is very powerful to detect moderate to large effect sizes.   Even with a sample size of just 40 participants (20 per condition), power is 71%. If reporting bias and publication bias exclude 30% non-significant results from the evidence, observed power is inflated to 82%. The comparison of success rate (100%) and observed power (82%) leads to an estimated inflation rate of 18%) and an R-Index is 64% (82% – 18%). Thus a moderate effect size in studies with 40 or more participants is expected to produce an R-Index greater than 64%.

However, with typical sample sizes of less than 120 participants, the expected rate of significant results is less than 50%. With N = 80 and true power of 31%, the reporting of only significant results would boost the observed power to 64%. The inflation rate would be 30% and the R-Index would be 39%. In this case, the R-Index overestimates true power by 9%. Thus, an R-Index less than 50% suggests that the true effect size is small or that the null-hypothesis is true (importantly, the null-hypothesis refers to the effect in the handgrip-paradigm, not to the validity of the broader theory that it becomes more difficult to sustain effort over time).

R-Analysis

The meta-analysis included 18 effect sizes based on handgrip studies.   Two unpublished studies (Ns = 24, 37) were not included in this analysis.   Seeley & Gardner (2003)’s study was excluded because it failed to use a pre-post design, which could explain the non-significant result. The meta-analysis reported two effect sizes for this study. Thus, 4 effects were excluded and the analysis below is based on the remaining 14 studies.

All articles presented significant effects of will-power manipulations on handgrip performance. Bray et al. (2008) reported three tests; one was deemed not significant (p = .10), one marginally significant (.06), and one was significant at p = .05 (p = .01). The results from the lowest p-value were used. As a result, the success rate was 100%.

Median observed power was 63%. The inflation rate is 37% and the R-Index is 26%. An R-Index of 22% is consistent with a scenario in which the null-hypothesis is true and all reported findings are type-I errors. Thus, the R-Index supports Carter and McCullough’s (2014) conclusion that the existing evidence does not provide empirical support for the hypothesis that will-power manipulations lower performance on a measure of will-power.

The R-Index can also be used to examine whether a subset of studies provides some evidence for the will-power hypothesis, but that this evidence is masked by the noise generated by underpowered studies with small samples. Only 7 studies had samples with more than 50 participants. The R-Index for these studies remained low (20%). Only two studies had samples with 80 or more participants. The R-Index for these studies increased to 40%, which is still insufficient to estimate an unbiased effect size.

One reason for the weak results is that several studies used weak manipulations of will-power (e.g., sniffing alcohol vs. sniffing water in the control condition). The R-Index of individual studies shows two studies with strong results (R-Index > 80). One study used a physical manipulation (standing one leg). This manipulation may lower handgrip performance, but this effect may not reflect an influence on will-power. The other study used a mentally taxing (and boring) task that is not physically taxing as well, namely crossing out “e”s. This task seems promising for a replication study.

Power analysis with an effect size of d = .2 suggests that a serious empirical test of the will-power hypothesis requires a sample size of N = 300 (150 per cell) to have 80% power in a pre-post study of will-power.

 

 

Conclusion

The R-Index of 14 will-power studies with the powerful pre-post handgrip paradigm confirms Carter and McCullough’s (2014) conclusion that a meta-analysis of will-power studies (Hagger Wood, & Chatzisarantis, 2010) provided an inflated estimate of the true effect size and that the existing studies provide no empirical support for the effect of will-power manipulations on a second effortful task. The existing studies have insufficient statistical power to distinguish a true null-effect from a small effect (d = .2). Power analysis suggest that future studies should focus on strong manipulations of will-power and use sample sizes of N = 300 participants.

Limitation

This analysis examined only a small set of studies in the meta-analysis that used handgrip performance as dependent variable. Other studies may show different results, but these studies often used a simple between-subject design with small samples. This paradigm has low power to detect even moderate effect sizes. It is therefore likely that the R-Index will also confirm Carter and McCullough’s (2014) conclusion.

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).

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.

The R-Index of Simmons et al.’s 21 Word Solution

Simmons, Nelson, and Simonsohn (2011) demonstrated how researchers can omit inconvenient details from research reports. For example, researchers may have omitted to mention a manipulation that failed to produce a theoretically predicted effect. Such questionable practices have the undesirable consequence that reported results are difficult to replicate. Simons et al. (2011, 2012) proposed a simple solution to this problem. Researchers who are not engaging in questionable research practices could report that they did not engage in these practices. In contrast, researchers who used questionable research practices would have to lie or honestly report that they engaged in these practices. Simons et al. (2012) proposed a simple 21 statement and encouraged researchers to include it in their manuscripts.

“We report how we determined our sample size, all data exclusions (if any), all manipulations, and all measures in the study.”

A search in WebofScience in June 2014 retrieved 326 articles that cited Simons et al. (2011). To examine the effectiveness of this solution to the replication crisis, a set of articles was selected that reported original research results and claimed that they adhered to Simons et al.’s standards. The sample size was determined by the rules to sample a minimum of 10 articles and a minimum of 20 studies. The R-Index is based on 11 articles with 21 studies.

The average R-Index for the set of 11 articles is 75%. There are 6 articles with an R-Index greater than 90%, suggesting that these studies had very high statistical power to produce statistically significant results.

To interpret this outcome it is helpful to use the following comparison standards.

When true power is 50% and all non-significant results are deleted to inflate the success rate to 100%, the R-Index is 50%.

A set of 18 multiple study articles in the prestigious journal science had only 1 article with an R-Index over 90% and 13 articles with an R-Index below 50%.

Conclusion

The average R-Index of original research articles that cite Simmons et al.’s (2011) article is fairly high and close to the ideal of 80%. This shows that some researchers are reporting results that are likely to replicate and that these researchers use the Simmons et al. reference to signal their research integrity. It is notable that the average number of studies in these 11 articles is about two studies. None of these articles reported four or more studies and six articles reported a single study. This observation highlights the fact that it is easier to produce replicable results when resources are used for a single study with high statistical power rather than wasting resources on several underpowered studies that either fail or require luck and questionable research practices to produce statistically significant results (Schimmack, 2012).

Although it is encouraging that some researchers are now including a statement that they did not engage in questionable research practices, the number of articles that contain these statements is still low. Only 10 articles in the journal Psychological Science that published Simmons et al.’s article make a reference to Simmons et al. and none of these cited it for the purpose of declaring that the authors complied with Simmons et al.’s recommendations. At present, it is therefore unclear how much researchers have changed their practices or not.

The R-Index provides an alternative approach to examine whether reported results are credible and replicable. Studies with high statistical power and honest reporting of non-significant results are more likely to replicate. The R-Index is easy to compute. Editors could ask authors to compute the R-Index for submitted manuscript. Reviewers can compute the R-Index during their review. Editors can use the R-Index to decide, which manuscripts gets accepted and ask authors to include the R-Index in publications. Most important, readers can compute the R-Index to examine whether they can trust a set of published results.

The R-Index for 18 Multiple Study Articles in Science (Francis et al., 2014)

“Only when the tide goes out do you discover who has been swimming naked.”  Warren Buffet (Value Investor).

 

 

Francis, Tanzman, and Matthews (2014) examined the credibility of psychological articles published in the prestigious journal Science. They focused on articles that contained four or more articles because (a) the statistical test that they has insufficient power for smaller sets of studies and (b) the authors assume that it is only meaningful to focus on studies that are published within a single article.

They found 26 articles published between 2006 and 2012. Eight articles could not be analyzed with their method.

The remaining 18 articles had a 100% success rate. That is, they never reported that a statistical hypothesis test failed to produce a significant result. Francis et al. computed the probability of this outcome for each article. When the probability was less than 10%, they made the recommendation to be skeptical about the validity of the theoretical claims.

For example, a researcher may conduct five studies with 80% power. As expected, one of the five studies produced a non-significant result. It is rational to assume that this finding is a type-II error as the Type-II error should occur in 1 out of 5 studies. The scientist decides not to include the non-significant result. In this case, there is bias, the average effect size across the four significant studies is slightly inflated, but the empirical results do support empirical claims.

If, however, the null-hypothesis is true and a researcher conducts many statistical tests and reports only significant results, demonstrating excessive significant results would also reveal that the reported results provide no empirical support for the theoretical claims in this article.

The problem with Francis et al.’s approach is that it does not clearly distinguish between these two scenarios.

The R-Index addresses this problem. It provides quantitative information about the replicability of a set of studies. Like Francis et al., the R-Index is based on the observed power of individual statistical tests (see Schimmack, 2012, for details), but the next steps are different. Francis et al. multiply observed power estimates. This approach is only meaningful for sets of studies that reported only significant results. The R-Index can be computed for studies that reported significant and non-significant results. Here are the steps:

Compute median observed power for all theoretically important statistical tests from a single study; then compute the median of these medians. This median estimates the median true power of a set of studies.

Compute the rate of significant results for the same set of statistical tests; then average the rates across the same set of studies. This average estimates the reported success rate for a set of studies.

Median observed power and average success rate are both estimates of true power or replicability of a set of studies. Without bias, these two estimates should converge as the number of studies increase.

If the success rate is higher than median observed power, it suggests that the reported results provide an inflated picture of the true effect size and replicability of a phenomenon.

The R-Index uses the difference between success rate and median observed power to correct the inflated estimate of replicability by subtracting the inflation rate (success rate – median observed power) from the median observed power.

R-Index = Median Observed Power – (Success rate – Median Observed Power)

The R-Index is a quantitative index, where higher values suggest a higher probability that an exact replication study will be successful and it avoids simple dichotomous decisions. Nevertheless, it can be useful to provide some broad categories that distinguish different levels of replicability.

An R-Index of more than 80% is consistent with true power of 80%, even when some results are omitted. I chose 80% as a boundary because Jacob Cohen advised researchers that they should plan studies with 80% power. Many undergraduates learn this basic fact about power and falsely assume that researchers are following a rule that is mentioned in introductory statistics.

An R-Index between 50% and 80% suggests that the reported results support an empirical phenomenon, but that power was less than ideal. Most important, this also implies that these studies make it difficult to distinguish non-significant results and type-II errors. For example, two tests with 50% power are likely to produce one significant result and one non-significant result. Researches are tempted to interpret the significant one and to ignore the non-significant one. However, in a replication study the opposite pattern is just as likely to occur.

An R-Index between25% and 50% raises doubts about the empirical support for the conclusions. The reason is that an R-Index of 22% can be obtained when the null-hypothesis is true and all non-significant results are omitted. In this case, observed power is inflated from 5% to 61%. With a 100% success rate, the inflation rate is 39%, and the R-Index is 22% (61% – 39% = 22%).

An R-Index below 20% suggest that researchers used questionable research methods (importantly, these method are questionable but widely accepted in many research communities and not considered to be ethical misconduct) to obtain results that are statistically significant (e.g., systematically deleting outliers until p < .05).

Table 1 list Francis et al.’s results and the R-Index. Studies are arranged in order of the R-Index.  Only 1 study is in the exemplary category with an R-Index greater than 80%.
4 studies have an R-Index between 50% and 80%.
8 studies have an R-Index in the range between 20% and 50%.
5 studies have an R-Index below 20%.

There are good reasons why researchers should not conduct studies with less than 50% power.  However, 13 of the 18 studies have an R-Index below 50%, which suggests that the true power in these studies was less than 50%.

Conclusion

The R-Index provides an alternative approach to Francis’s TES to examine the credibility of a set of published studies. Whereas Francis concluded that 15 out of 18 articles show bias that invalidates the theoretical claims of the original article, the R-Index provides quantitative information about the replicability of reported results.

The R-Index does not provide a simple answer about the validity of published findings, but in many cases the R-Index raises concerns about the strength of the empirical evidence and reveals that editorial decisions failed to take replicability into account.

The R-Index provides a simple tool for editors and reviewers to increase the credibility of published results and to increase the replicability of published findings. Editors and reviewers can compute, or ask authors who submit manuscripts to compute, the R-Index and use this information in their editorial decision. There is no clear criterion value, but a higher R-Index is better and moderate R-values should be justified by other criteria (e.g., uniqueness of sample).

The R-Index can be used to examine whether editors continue to accept articles with low replicability or are committed to the publication of empirical results that are credible and replicable.

Do it yourself: R-Index Spreadsheet and Manual is now available.

Science is self-correcting, but it often takes too long.

A spreadsheet to compute the R-Index and a manual that shows how to use the spreadsheet is now available on the www.r-index.org website. Researchers from all fields of science that use statistics are welcome to use the R-Index to examine the statistical integrity of published research findings. A high R-Index suggests that a set of studies reported results that are likely to replicate in an EXACT replication study with high statistical power. A low R-Index suggests that published results may be biased and that published results may not replicate. Researchers can share the results of their R-Index analyses by submitting the completed spreadsheets to www.r-index.org and the results will be posted anonymously. Results and spreadsheets will be openly accessible.