Category Archives: science

Why Frontiers Should Retract Baumeister’s Critique of Carter’s Meta-Analysis

This blog post is heavily based on one of my first blog-posts in 2014 (Schimmack, 2014).  The blog post reports a meta-analysis of ego-depletion studies that used the hand-grip paradigm.  When I first heard about the hand-grip paradigm, I thought it was stupid because there is so much between-subject variance in physical strength.  However, then I learned that it is the only paradigm that uses a pre-post design, which removes between-subject variance from the error term. This made the hand-grip paradigm the most interesting paradigm because it has the highest power to detect ego-depletion effects.  I conducted a meta-analysis of the hand-grip studies and found clear evidence of publication bias.  This finding is very damaging to the wider ego-depletion research because other studies used between-subject designs with small samples which have very low power to detect small effects.

This prediction was confirmed in meta-analyses by Carter,E.C., Kofler, L.M., Forster, D.E., and McCulloch,M.E. (2015) that revealed publication bias in ego-depletion studies with other paradigms.

The results also explain why attempts to show ego-depletion effects with within-subject designs failed (Francis et al., 2018).  Within-subject designs increase power by removing fixed between-subject variance such as physical strength.  However, given the lack of evidence with the hand-grip paradigm it is not surprising that within-subject designs also failed to show ego-depletion effects with other dependent variables in within-subject designs.  Thus, these results further suggest that ego-depletion effects are too small to be used for experimental investigations of will-power.

Of course, Roy F. Baumeister doesn’t like this conclusion because his reputation is to a large extent based on the resource model of will-power.  His response to the evidence that most of the evidence is based on questionable practices that produced illusory evidence has been to attack the critics (cf. Schimmack, 2019).

In 2016, he paid to publish a critique of Carter’s (2015) meta-analysis in Frontiers of Psychology (Cunningham & Baumeister, 2016).   In this article, the authors question the results obtained by bias-tests that reveal publication bias and suggest that there is no evidence for ego-depletion effects.

Unfortunately, Cunningham and Baumeister’s (2016) article is cited frequently as if it contained some valid scientific arguments.

For example, Christodoulou, Lac, and Moore (2017) cite the article to dismiss the results of a PEESE analysis that suggests publication bias is present and there is no evidence that infants can add and subtract. Thus, there is a real danger that meta-analysts will use Cunningham & Baumeister’s (2016) article to dismiss evidence of publication bias and to provide false evidence for claims that rest on questionable research practices.

Fact Checking Cunningham and Baumeister’s Criticisms

Cunningham and Baumeister (2016) claim that results from bias tests are difficult to interpret, but there criticism is based on false arguments and inaccurate claims.

Confusing Samples and Populations

This scientifically sounding paragraph is a load of bull. The authors claim that inferential tests require sampling from a population and raise a question about the adequacy of a sample. However, bias tests do not work this way. They are tests of the population, namely the population of all of the studies that could be retrieved that tested a common hypothesis (e.g., all handgrip studies of ego-depletion). Maybe more studies exist than are available. Maybe the results based on the available studies differ from results if all studies were available, but that is irrelevant. The question is only whether the available studies are biased or not. So, why do we even test for significance? That is a good question. The test for significance only tells us whether bias is merely a product of random chance or whether it was introduced by questionable research practices. However, even random bias is bias. If a set of studies reports only significant results, and the observed power of the studies is only 70%, there is a discrepancy. If this discrepancy is not statistically significant, there is still a discrepancy. If it is statistically significant, we are allowed to attribute it to questionable research practices such as those that Baumeister and several others admitted using.

“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.” (Roy Baumeister, personal email communication) (Schimmack, 2014).

Given the widespread use of questionable research practices in experimental social psychology, it is not surprising that bias-tests reveal bias. It is actually more surprising when these tests fail to reveal bias, which is most likely a problem of low statistical power (Renkewitz & Keiner, 2019).

Misunderstanding Power

The claims about power are not based on clearly defined constructs in statistics. Statistical power is a function of the strength of a signal (the population effect size) and the amount of noise (sampling error). Researches skills are not a part of statistical power. Results should be independent of a researcher. A researcher could of course pick procedures that maximize a signal (powerful interventions) or reduce sampling error (e.g., pre-post designs), but these factors play a role in the designing of a study. Once a study is carried out, the population effect size is what it was and the sampling error is what it was. Thus, honestly reported test statistics tell us about the signal-to-noise ratio in a study that was conducted. Skillful researchers would produce stronger test-statistics (higher t-values, F-values) than unskilled researchers. The problem for Baumeister and other ego-depletion researchers is that the t-values and F-values tend to be weak and suggest questionable research practices rather than skill produced significant results. In short, meta-analysis of test-statistics reveal whether researchers used skill or questionable research practices to produce significant results.

The reference to Morey (2013) suggests that there is a valid criticism of bias tests, but that is not the case. Power-based bias tests are based on sound statistical principles that were outlined by a statistician in the journal American Statistician (Sterling, Rosenbaum, & Weinkam, 1995). Building on this work, Jerry Brunner (professor of statistics) and I published theorems that provide the basis of bias tests like TES to reveal the use of questionable research practices (Brunner & Schimmack, 2019). The real challenge for bias tests is to estimate mean power without information about the population effect sizes. In this regard, TES is extremely conservative because it relies on a meta-analysis of observed effect sizes to estimate power. These effect sizes are inflated when questionable research practices were used, which makes the test conservative. However, there is a problem with TES when effect sizes are heterogeneous. This problem is avoided by alternative bias tests like the R-Index that I used to demonstrate publication bias in the handgrip studies of ego-depletion. In sum, bias tests like the R-Index and TES are based on solid mathematical foundations and simulation studies show that they work well in detecting the use of questionable research practices.

Confusing Absence of Evidence with Evidence of Absence

PET and PEESE are extension of Eggert’s regression test of publication bias. All methods relate sample sizes (or sampling error) to effect size estimates. Questionable research practices tend to introduce a negative correlation between sample size and effect sizes or a positive correlation between sampling error and effect sizes. The reason is that significance requires a signal to noise ratio of 2:1 for t-tests or 4:1 for F-tests to produce a significant result. To achieve this ratio with more noise (smaller sample, more sampling error), the signal has to be inflated more.

The novel contribution of PET and PEESE was to use the intercept of the regression model as an effect size estimate that corrects for publication bias. This estimate needs to be interpreted in the context of the sampling error of the regression model, using a 95%CI around the point estimate.

Carter et al. (2015) found that the 95%CI often included a value of zero, which implies that the data are too weak to reject the null-hypothesis. Such non-significant results are notoriously difficult to interpret because they neither support nor refute the null-hypothesis. The main conclusion that can be drawn from this finding is that the existing data are inconclusive.

This main conclusion does not change when the number of studies is less than 20. Stanley and Doucouliagos (2014) were commenting on the trustworthiness of point estimates and confidence intervals in smaller samples. Smaller samples introduce more uncertainty and we should be cautious in the interpretation of results that suggest there is an effect because the assumptions of the model are violated. However, if the results already show that there is no evidence, small samples merely further increase uncertainty and make the existing evidence even less conclusive.

Aside from the issues regarding the interpretation of the intercept, Cunningham and Baumeister also fail to address the finding that sample sizes and effect sizes were negatively correlated. If this negative correlation is not caused by questionable research practices, it must be caused by something else. Cunningham and Baumeister fail to provide an answer to this important question.

No Evidence of Flair and Skill

Earlier Cunningham and Baumeister (2016) claimed that power depends on researchers’ skills and they argue that new investigators may be less skilled than the experts who developed paradigms like Baumeister and colleagues.

However, they then point out that Carter et al.’s (2015) examined lab as a moderator and found no difference between studies conducted by Baumeister and colleagues or other laboratories.

Thus, there is no evidence whatsoever that Baumeister and colleagues were more skillful and produced more credible evidence for ego-depletion than other laboratories. The fact that everybody got ego-depletion effects can be attributed to the widespread use of questionable research practices that made it possible to get significant results even for implausible phenomena like extrasensory perception (John et al., 2012; Schimmack, 2012). Thus, the large number of studies that support ego-depletion merely shows that everybody used questionable research practices like Baumeister did (Schimmack, 2014; Schimmack, 2016), which is also true for many other areas of research in experimental social psychology (Schimmack, 2019). Francis (2014) found that 80% of articles showed evidence that QRPs were used.

Handgrip Replicability Analysis

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

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

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

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

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

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

HandgripRindex

Conclusion

Baumeister has lost any credibility as a scientist. He is pretending to engage in a scientific dispute about the validity of ego-depletion research, but he is ignoring the most obvious evidence that has accumulated during the past decade. Social psychologists have misused the scientific method and engaged in a silly game of producing significant p-values that support their claims. Data were never used to test predictions and studies that failed to support hypotheses were not published.

“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.” (Roy Baumeister, personal email communication)

As a result, the published record lacks credibility and cannot be used to provide empirical evidence for scientific claims. Ego-depletion is a glaring example of everything that went wrong in experimental social psychology. This is not surprising because Baumeister and his students used questionable research practices more than other social psychologists (Schimmack, 2018). Now he is trying to to repress this truth, which should not surprise any psychologist familiar with motivated biases and repressive coping. However, scientific journals should not publish his pathetic attempts to dismiss criticism of his work. Cunningham and Baumeister’s article provides not a single valid scientific argument. Frontiers of Psychology should retract the article.

References

Carter,E.C.,Kofler,L.M.,Forster,D.E.,and McCulloch,M.E. (2015).A series of meta-analytic tests of the depletion effect: Self-control does not seem to rely on a limited resource. J. Exp.Psychol.Gen. 144, 796–815. doi:10.1037/xge0000083

REPLICABILITY RANKING OF 26 PSYCHOLOGY JOURNALS

THEORETICAL BACKGROUND

Neyman & Pearson (1933) developed the theory of type-I and type-II errors in statistical hypothesis testing.

A type-I error is defined as the probability of rejecting the null-hypothesis (i.e., the effect size is zero) when the null-hypothesis is true.

A type-II error is defined as the probability of failing to reject the null-hypothesis when the null-hypothesis is false (i.e., there is an effect).

A common application of statistics is to provide empirical evidence for a theoretically predicted relationship between two variables (cause-effect or covariation). The results of an empirical study can produce two outcomes. Either the result is statistically significant or it is not statistically significant. Statistically significant results are interpreted as support for a theoretically predicted effect.

Statistically non-significant results are difficult to interpret because the prediction may be false (the null-hypothesis is true) or a type-II error occurred (the theoretical prediction is correct, but the results fail to provide sufficient evidence for it).

To avoid type-II errors, researchers can design studies that reduce the type-II error probability. The probability of avoiding a type-II error when a predicted effect exists is called power. It could also be called the probability of success because a significant result can be used to provide empirical support for a hypothesis.

Ideally researchers would want to maximize power to avoid type-II errors. However, powerful studies require more resources. Thus, researchers face a trade-off between the allocation of resources and their probability to obtain a statistically significant result.

Jacob Cohen dedicated a large portion of his career to help researchers with the task of planning studies that can produce a successful result, if the theoretical prediction is true. He suggested that researchers should plan studies to have 80% power. With 80% power, the type-II error rate is still 20%, which means that 1 out of 5 studies in which a theoretical prediction is true would fail to produce a statistically significant result.

Cohen (1962) examined the typical effect sizes in psychology and found that the typical effect size for the mean difference between two groups (e.g., men and women or experimental vs. control group) is about half-of a standard deviation. The standardized effect size measure is called Cohen’s d in his honor. Based on his review of the literature, Cohen suggested that an effect size of d = .2 is small, d = .5 moderate, and d = .8. Importantly, a statistically small effect size can have huge practical importance. Thus, these labels should not be used to make claims about the practical importance of effects. The main purpose of these labels is that researchers can better plan their studies. If researchers expect a large effect (d = .8), they need a relatively small sample to have high power. If researchers expect a small effect (d = .2), they need a large sample to have high power.   Cohen (1992) provided information about effect sizes and sample sizes for different statistical tests (chi-square, correlation, ANOVA, etc.).

Cohen (1962) conducted a meta-analysis of studies published in a prominent psychology journal. Based on the typical effect size and sample size in these studies, Cohen estimated that the average power in studies is about 60%. Importantly, this also means that the typical power to detect small effects is less than 60%. Thus, many studies in psychology have low power and a high type-II error probability. As a result, one would expect that journals often report that studies failed to support theoretical predictions. However, the success rate in psychological journals is over 90% (Sterling, 1959; Sterling, Rosenbaum, & Weinkam, 1995). There are two explanations for discrepancies between the reported success rate and the success probability (power) in psychology. One explanation is that researchers conduct multiple studies and only report successful studies. The other studies remain unreported in a proverbial file-drawer (Rosenthal, 1979). The other explanation is that researchers use questionable research practices to produce significant results in a study (John, Loewenstein, & Prelec, 2012). Both practices have undesirable consequences for the credibility and replicability of published results in psychological journals.

A simple solution to the problem would be to increase the statistical power of studies. If the power of psychological studies in psychology were over 90%, a success rate of 90% would be justified by the actual probability of obtaining significant results. However, meta-analysis and method articles have repeatedly pointed out that psychologists do not consider statistical power in the planning of their studies and that studies continue to be underpowered (Maxwell, 2004; Schimmack, 2012; Sedlmeier & Giegerenzer, 1989).

One reason for the persistent neglect of power could be that researchers have no awareness of the typical power of their studies. This could happen because observed power in a single study is an imperfect indicator of true power (Yuan & Maxwell, 2005). If a study produced a significant result, the observed power is at least 50%, even if the true power is only 30%. Even if the null-hypothesis is true, and researchers publish only type-I errors, observed power is dramatically inflated to 62%, when the true power is only 5% (the type-I error rate). Thus, Cohen’s estimate of 60% power is not very reassuring.

Over the past years, Schimmack and Brunner have developed a method to estimate power for sets of studies with heterogeneous designs, sample sizes, and effect sizes. A technical report is in preparation. The basic logic of this approach is to convert results of all statistical tests into z-scores using the one-tailed p-value of a statistical test.  The z-scores provide a common metric for observed statistical results. The standard normal distribution predicts the distribution of observed z-scores for a fixed value of true power.   However, for heterogeneous sets of studies the distribution of z-scores is a mixture of standard normal distributions with different weights attached to various power values. To illustrate this method, the histograms of z-scores below show simulated data with 10,000 observations with varying levels of true power: 20% null-hypotheses being true (5% power), 20% of studies with 33% power, 20% of studies with 50% power, 20% of studies with 66% power, and 20% of studies with 80% power.

RepRankSimulation

The plot shows the distribution of absolute z-scores (there are no negative effect sizes). The plot is limited to z-scores below 6 (N = 99,985 out of 10,000). Z-scores above 6 standard deviations from zero are extremely unlikely to occur by chance. Even with a conservative estimate of effect size (lower bound of 95% confidence interval), observed power is well above 99%. Moreover, quantum physics uses Z = 5 as a criterion to claim success (e.g., discovery of Higgs-Boson Particle). Thus, Z-scores above 6 can be expected to be highly replicable effects.

Z-scores below 1.96 (the vertical dotted red line) are not significant for the standard criterion of (p < .05, two-tailed). These values are excluded from the calculation of power because these results are either not reported or not interpreted as evidence for an effect. It is still important to realize that true power of all experiments would be lower if these studies were included because many of the non-significant results are produced by studies with 33% power. These non-significant results create two problems. Researchers wasted resources on studies with inconclusive results and readers may be tempted to misinterpret these results as evidence that an effect does not exist (e.g., a drug does not have side effects) when an effect is actually present. In practice, it is difficult to estimate power for non-significant results because the size of the file-drawer is difficult to estimate.

It is possible to estimate power for any range of z-scores, but I prefer the range of z-scores from 2 (just significant) to 4. A z-score of 4 has a 95% confidence interval that ranges from 2 to 6. Thus, even if the observed effect size is inflated, there is still a high chance that a replication study would produce a significant result (Z > 2). Thus, all z-scores greater than 4 can be treated as cases with 100% power. The plot also shows that conclusions are unlikely to change by using a wider range of z-scores because most of the significant results correspond to z-scores between 2 and 4 (89%).

The typical power of studies is estimated based on the distribution of z-scores between 2 and 4. A steep decrease from left to right suggests low power. A steep increase suggests high power. If the peak (mode) of the distribution were centered over Z = 2.8, the data would conform to Cohen’s recommendation to have 80% power.

Using the known distribution of power to estimate power in the critical range gives a power estimate of 61%. A simpler model that assumes a fixed power value for all studies produces a slightly inflated estimate of 63%. Although the heterogeneous model is correct, the plot shows that the homogeneous model provides a reasonable approximation when estimates are limited to a narrow range of Z-scores. Thus, I used the homogeneous model to estimate the typical power of significant results reported in psychological journals.

DATA

The results presented below are based on an ongoing project that examines power in psychological journals (see results section for the list of journals included so far). The set of journals does not include journals that primarily publish reviews and meta-analysis or clinical and applied journals. The data analysis is limited to the years from 2009 to 2015 to provide information about the typical power in contemporary research. Results regarding historic trends will be reported in a forthcoming article.

I downloaded pdf files of all articles published in the selected journals and converted the pdf files to text files. I then extracted all t-tests and F-tests that were reported in the text of the results section searching for t(df) or F(df1,df2). All t and F statistics were converted into one-tailed p-values and then converted into z-scores.

RepRankAll

The plot above shows the results based on 218,698 t and F tests reported between 2009 and 2015 in the selected psychology journals. Unlike the simulated data, the plot shows a steep drop for z-scores just below the threshold of significance (z = 1.96). This drop is due to the tendency not to publish or report non-significant results. The heterogeneous model uses the distribution of non-significant results to estimate the size of the file-drawer (unpublished non-significant results). However, for the present purpose the size of the file-drawer is irrelevant because power is estimated only for significant results for Z-scores between 2 and 4.

The green line shows the best fitting estimate for the homogeneous model. The red curve shows fit of the heterogeneous model. The heterogeneous model is doing a much better job at fitting the long tail of highly significant results, but for the critical interval of z-scores between 2 and 4, the two models provide similar estimates of power (55% homogeneous & 53% heterogeneous model).   If the range is extended to z-scores between 2 and 6, power estimates diverge (82% homogenous, 61% heterogeneous). The plot indicates that the heterogeneous model fits the data better and that the 61% estimate is a better estimate of true power for significant results in this range. Thus, the results are in line with Cohen (1962) estimate that psychological studies average 60% power.

REPLICABILITY RANKING

The distribution of z-scores between 2 and 4 was used to estimate the average power separately for each journal. As power is the probability to obtain a significant result, this measure estimates the replicability of results published in a particular journal if researchers would reproduce the studies under identical conditions with the same sample size (exact replication). Thus, even though the selection criterion ensured that all tests produced a significant result (100% success rate), the replication rate is expected to be only about 50%, even if the replication studies successfully reproduce the conditions of the published studies. The table below shows the replicability ranking of the journals, the replicability score, and a grade. Journals are graded based on a scheme that is similar to grading schemes for undergraduate students (below 50 = F, 50-59 = E, 60-69 = D, 70-79 = C, 80-89 = B, 90+ = A).

ReplicabilityRanking

The average value in 2000-2014 is 57 (D+). The average value in 2015 is 58 (D+). The correlation for the values in 2010-2014 and those in 2015 is r = .66.   These findings show that the replicability scores are reliable and that journals differ systematically in the power of published studies.

LIMITATIONS

The main limitation of the method is that focuses on t and F-tests. The results might change when other statistics are included in the analysis. The next goal is to incorporate correlations and regression coefficients.

The second limitation is that the analysis does not discriminate between primary hypothesis tests and secondary analyses. For example, an article may find a significant main effect for gender, but the critical test is whether gender interacts with an experimental manipulation. It is possible that some journals have lower scores because they report more secondary analyses with lower power. To address this issue, it will be necessary to code articles in terms of the importance of statistical test.

The ranking for 2015 is based on the currently available data and may change when more data become available. Readers should also avoid interpreting small differences in replicability scores as these scores are likely to fluctuate. However, the strong correlation over time suggests that there are meaningful differences in the replicability and credibility of published results across journals.

CONCLUSION

This article provides objective information about the replicability of published findings in psychology journals. None of the journals reaches Cohen’s recommended level of 80% replicability. Average replicability is just about 50%. This finding is largely consistent with Cohen’s analysis of power over 50 years ago. The publication of the first replicability analysis by journal should provide an incentive to editors to increase the reputation of their journal by paying more attention to the quality of the published data. In this regard, it is noteworthy that replicability scores diverge from traditional indicators of journal prestige such as impact factors. Ideally, the impact of an empirical article should be aligned with the replicability of the empirical results. Thus, the replicability index may also help researchers to base their own research on credible results that are published in journals with a high replicability score and to avoid incredible results that are published in journals with a low replicability score. Ultimately, I can only hope that journals will start competing with each other for a top spot in the replicability rankings and as a by-product increase the replicability of published findings and the credibility of psychological science.

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

LuckyBounceTest

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

Example: Unconscious Priming Influences Behavior

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

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

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

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

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

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

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

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

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

This R-Index can be compared to several benchmarks.

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

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

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

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

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

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

Swish!

R-INDEX BULLETIN (RIB): Share the Results of your R-Index Analysis with the Scientific Community

R-Index Bulletin

The world of scientific publishing is changing rapidly and there is a growing need to share scientific information as fast and as cheap as possible.

Traditional journals with pre-publication peer-review are too slow and focussed on major ground-breaking discoveries.

Open-access journals can be expensive.

R-Index Bulletin offers a new opportunity to share results with the scientific community quickly and free of charge.

R-Index Bulletin also avoids the problems of pre-publication peer-review by moving to a post-publication peer-review process. Readers are welcome to comment on posted contributions and to post their own analyses. This process ensures that scientific disputes and their resolution are open and part of the scientific process.

For the time being, submissions can be uploaded as comments to this blog. In the future, R-Index Bulletin may develop into a free online journal.

A submission should contain a brief description of the research question (e.g., what is the R-Index of studies on X, by X, or in the journal X?), the main statistical results (median observed power, success rate, inflation rate, R-Index) and a brief discussion of the implications of the analysis. There is no page restriction and analyses of larger data sets can include moderator analysis. Inclusion of other bias tests (Egger’s regression, TIVA, P-Curve, P-Uniform) is also welcome.

If you have conducted an R-Index analysis, please submit it to R-Index Bulletin to share your findings.

Submissions can be made anonymously or with an author’s name.

Go ahead and press the “Leave a comment” or “Leave a reply” button or scroll to the bottom of the page and past your results in the “Leave a reply” box.

Bayesian Statistics in Small Samples: Replacing Prejudice against the Null-Hypothesis with Prejudice in Favor of the Null-Hypothesis

Matzke, Nieuwenhuis, van Rijn, Slagter, van der Molen, and Wagenmakers (2015) published the results of a preregistered adversarial collaboration. This article has been considered a model of conflict resolution among scientists.

The study examined the effect of eye-movements on memory. Drs. Nieuwenhuis and Slagter assume that horizontal eye-movements improve memory. Drs. Matzke, van Rijn, and Wagenmakers did not believe that horizontal-eye movements improve memory. That is, they assumed the null-hypothesis to be true. Van der Molen acted as a referee to resolve conflict about procedural questions (e.g., should some participants be excluded from analysis?).

The study was a between-subject design with three conditions: horizontal eye movements, vertical eye movements, and no eye movement.

The researchers collected data from 81 participants and agreed to exclude 2 participants, leaving 79 participants for analysis. As a result there were 27 or 26 participants per condition.

The hypothesis that horizontal eye-movements improve performance can be tested in several ways.

An overall F-test can compare the means of the three groups against the hypothesis that they are all equal. This test has low power because nobody predicted differences between vertical eye-movements and no eye-movements.

A second alternative is to compare the horizontal condition against the combined alternative groups. This can be done with a simple t-test. Given the directed hypothesis, a one-tailed test can be used.

Power analysis with the free software program GPower shows that this design has 21% power to reject the null-hypothesis with a small effect size (d = .2). Power for a moderate effect size (d = .5) is 68% and power for a large effect size (d = .8) is 95%.

Thus, the decisive study that was designed to solve the dispute only has adequate power (95%) to test Drs. Matzke et al.’s hypothesis d = 0 against the alternative hypothesis that d = .8. For all effect sizes between 0 and .8, the study was biased in favor of the null-hypothesis.

What does an effect size of d = .8 mean? It means that memory performance is boosted by .8 standard deviations. For example, if students take a multiple-choice exam with an average of 66% correct answers and a standard deviation of 15%, they could boost their performance by 12% points (15 * 0.8 = 12) from an average of 66% (C) to 78% (B+) by moving their eyes horizontally while thinking about a question.

The article makes no mention of power-analysis and the implicit assumption that the effect size has to be large to avoid biasing the experiment in favor of the critiques.

Instead the authors used Bayesian statistics; a type of statistics that most empirical psychologists understand even less than standard statistics. Bayesian statistics somehow magically appears to be able to draw inferences from small samples. The problem is that Bayesian statistics requires researchers to specify a clear alternative to the null-hypothesis. If the alternative is d = .8, small samples can be sufficient to decide whether an observed effect size is more consistent with d = 0 or d = .8. However, with more realistic assumptions about effect sizes, small samples are unable to reveal whether an observed effect size is more consistent with the null-hypothesis or a small to moderate effect.

Actual Results

So what where the actual results?

Condition                                          Mean     SD         

Horizontal Eye-Movements          10.88     4.32

Vertical Eye-Movements               12.96     5.89

No Eye Movements                       15.29     6.38      

The results provide no evidence for a benefit of horizontal eye movements. In a comparison of the two a priori theories (d = 0 vs. d > 0), the Bayes-Factor strongly favored the null-hypothesis. However, this does not mean that Bayesian statistics has magical powers. The reason was that the empirical data actually showed a strong effect in the opposite direction, in that participants in the no-eye-movement condition had better performance than in the horizontal-eye-movement condition (d = -.81).   A Bayes Factor for a two-tailed hypothesis or the reverse hypothesis would not have favored the null-hypothesis.

Conclusion

In conclusion, a small study surprisingly showed a mean difference in the opposite prediction than previous studies had shown. This finding is noteworthy and shows that the effects of eye-movements on memory retrieval are poorly understood. As such, the results of this study are simply one more example of the replicability crisis in psychology.

However, it is unfortunate that this study is published as a model of conflict resolution, especially as the empirical results failed to resolve the conflict. A key aspect of a decisive study is to plan a study with adequate power to detect an effect.   As such, it is essential that proponents of a theory clearly specify the effect size of their predicted effect and that the decisive experiment matches type-I and type-II error. With the common 5% Type-I error this means that a decisive experiment must have 95% power (1 – type II error). Bayesian statistics does not provide a magical solution to the problem of too much sampling error in small samples.

Bayesian statisticians may ignore power analysis because it was developed in the context of null-hypothesis testing. However, Bayesian inferences are also influenced by sample size and studies with small samples will often produce inconclusive results. Thus, it is more important that psychologists change the way they collect data than to change the way they analyze their data. It is time to allocate more resources to fewer studies with less sampling error than to waste resources on many studies with large sampling error; or as Cohen said: Less is more.

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

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

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.

Why are Stereotype-Threat Effects on Women’s Math Performance Difficult to Replicate?

Updated on May 19, 2016
– corrected mistake in calculation of p-value for TIVA

A Replicability Analysis of Spencer, Steele, and Quinn’s seminal article on stereotype threat effects on gender differences in math performance.

Background

In a seminal article, Spencer, Steele, and Quinn (1999) proposed the concept of stereotype threat. They argued that women may experience stereotype-threat during math tests and that stereotype threat can interfere with their performance on math tests.

The original study reported three experiments.

STUDY 1

Study 1 had 56 participants (28 male and 28 female undergraduate students). The main aim was to demonstrate that stereotype-threat influences performance on difficult, but not on easy math problems.

A 2 x 2 mixed model ANOVA with sex and difficulty produced the following results.

Main effect for sex, F(1, 52) = 3.99, p = .051 (reported as p = .05), z = 1.96, observed power = 50%.

Interaction between sex and difficulty, F(1, 52) = 5.34 , p = .025, z = 2.24, observed power = 61%.

The low observed power suggests that sampling error contributed to the significant results. Assuming observed power is a reliable estimate of true power, the chance of obtaining significant results in both studies would only be 31%. Moreover, if the true power is in the range between 50% and 80% power, there is only a 32% chance that observed power to fall into this range. The chance that both observed power values fall into this range is only 10%.

Median observed power is 56%. The success rate is 100%. Thus, the success rate is inflated by 44 percentage points (100% – 56%).

The R-Index for these two results is low, Ř = 12 (56 – 44).

Empirical evidence shows that studies with low R-Indices often fail to replicate in exact replication studies.

It is even more problematic that Study 1 was supposed to demonstrate just the basic phenomenon that women perform worse on math problems than men and that the following studies were designed to move this pre-existing gender difference around with an experimental manipulation. If the actual phenomenon is in doubt, it is unlikely that experimental manipulations of the phenomenon will be successful.

STUDY 2

The main purpose of Study 2 was to demonstrate that gender differences in math performance would disappear when the test is described as gender neutral.

Study 2 recruited 54 students (30 women, 24 men). This small sample size is problematic for several reasons. Power analysis of Study 1 suggested that the authors were lucky to obtain significant results. If power is 50%, there is a 50% chance that an exact replication study with the same sample size will produce a non-significant result. Another problem is that sample sizes need to increase to demonstrate that the gender difference in math performance can be influenced experimentally.

The data were not analyzed according to this research plan because the second test was so difficult that nobody was able to solve these math problems. However, rather than repeating the experiment with a better selection of math problems, the results for the first math test were reported.

As there was no repeated performance by the two participants, this is a 2 x 2 between-subject design that crosses sex and treat-manipulation. With a total sample size of 54 students, the n per cell is 13.

The main effect for sex was significant, F(1, 50) = 5.66, p = .021, z = 2.30, observed power = 63%.

The interaction was also significant, F(1, 50) = 4.18, p = .046, z = 1.99, observed power = 51%.

Once more, median observed power is just 57%, yet the success rate is 100%. Thus, the success rate is inflated by 43% and the R-Index is low, Ř = 14%, suggesting that an exact replication study will not produce significant results.

STUDY 3

Studies 1 and 2 used highly selective samples (women in the top 10% in math performance). Study 3 aimed to replicate the results of Study 2 in a less selective sample. One might expect that stereotype-threat has a weaker effect on math performance in this sample because stereotype threat can undermine performance when ability is high, but anxiety is not a factor in performance when ability is low. Thus, Study 3 is expected to yield a weaker effect and a larger sample size would be needed to demonstrate the effect. However, sample size was approximately the same as in Study 2 (36 women, 31 men).

The ANOVA showed a main effect of sex on math performance, F(1, 63) = 6.44, p = .014, z = 2.47, observed power = 69%.

The ANOVA also showed a significant interaction between sex and stereotype-threat-assurance, F(1, 63) = 4.78, p = .033, z = 2.14, observed power = 57%.

Once more, the R-Index is low, Ř = 26 (MOP = 63%, Success Rate = 100%, Inflation Rate = 37%).

Combined Analysis

The three studies reported six statistical tests. The R-Index for the combined analysis is low Ř = 18 (MOP = 59%, Success Rate = 100%, Inflation Rate = 41%).

The probability of this event to occur by chance can be assessed with the Test of Insufficient Variance (TIVA). TIVA tests the hypothesis that the variance in p-values, converted into z-scores, is less than 1. A variance of one is expected in a set of exact replication studies with fixed true power. Less variance suggests that the z-scores are not a representative sample of independent test scores.   The variance of the six z-scores is low, Var(z) = .04, p < .001,  1 / 1309.

Correction: I initially reported, “A chi-square test shows that the probability of this event is less than 1 out of 1,000,000,000,000,000, chi-square (df = 5) = 105.”

I made a mistake in the computation of the probability. When I developed TIVA, I confused the numerator and denominator in the test. I was thrilled that the test was so powerful and happy to report the result in bold, but it is incorrect. A small sample of six z-scores cannot produce such low p-values.

Conclusion

The replicability analysis of Spencer, Steele, and Quinn (1999) suggests that the original data provided inflated estimates of effect sizes and replicability. Thus, the R-Index predicts that exact replication studies would fail to replicate the effect.

Meta-Analysis

A forthcoming article in the Journal of School Psychology reports the results of a meta-analysis of stereotype-threat studies in applied school settings (Flore & Wicherts, 2014). The meta-analysis was based on 47 comparisons of girls with stereotype threat versus girls without stereotype threat. The abstract concludes that stereotype threat in this population is a statistically reliable, but small effect (d = .22). However, the authors also noted signs of publication bias. As publication bias inflates effect sizes, the true effect size is likely to be even smaller than the uncorrected estimate of .22.

The article also reports that the after a correction for bias, using the trim-and-fill method, the estimated effect size is d = .07 and not significantly different from zero. Thus, the meta-analysis reveals that there is no replicable evidence for stereotype-threat effects on schoolgirls’ math performance. The meta-analysis also implies that any true effect of stereotype threat is likely to be small (d < .2). With a true effect size of d = .2, the original studies by Steel et al. (1999) and most replication studies had insufficient power to demonstrate stereotype threat effects, even if the effect exists. A priori power analysis with d = .2 would suggest that 788 participants are needed to have an 80% chance to obtain a significant result if the true effect is d = .2. Thus, future research on this topic is futile unless statistical power is increased by increasing sample sizes or by using more powerful designs that can demonstrate small effects in smaller samples.

One possibility is that the existing studies vary in quality and that good studies showed the effect reliably, whereas bad studies failed to show the effect. To test this hypothesis, it is possible to select studies from a meta-analysis with the goal to maximize the R-Index. The best chance to obtain a high R-Index is to focus on studies with large sample sizes because statistical power increases with sample size. However, the table below shows that there are only 8 studies with more than 100 participants and the success rate in these studies is 13% (1 out of 8), which is consistent with the median observed power in these studies 12%.

R-IndexStereotypeThreatMetaAnalysis

It is also possible to select studies that produced significant results (z > 1.96). Of course, this set of studies is biased, but the R-Index corrects for bias. If these studies were successful because they had sufficient power to demonstrate effects, the R-Index would be greater than 50%. However, the R-Index is only 49%.

CONCLUSION

In conclusion, a replicability analysis with the R-Index shows that stereotype-threat is an elusive phenomenon. Even large replication studies with hundreds of participants were unable to provide evidence for an effect that appeared to be a robust effect in the original article. The R-Index of the meta-analysis by Flore and Wicherts corroborates concerns that the importance of stereotype-threat as an explanation for gender differences in math performance has been exaggerated. Similarly, Ganley, Mingle, Ryan, Ryan, and Vasilyeva (2013) found no evidence for stereotype threat effects in studies with 931 students and suggested that “these results raise the possibility that stereotype threat may not be the cause of gender differences in mathematics performance prior to college.” (p 1995).

The main novel contribution of this post is to reveal that this disappointing outcome was predicted on the basis of the empirical results reported in the original article by Spencer et al. (1999). The article suggested that stereotype threat is a pervasive phenomenon that explains gender differences in math performance. However, The R-Index and the insufficient variance in statistical results suggest that the reported results were biased and, overestimated the effect size of stereotype threat. The R-Index corrects for this bias and correctly predicts that replication studies will often result in non-significant results. The meta-analysis confirms this prediction.

In sum, the main conclusions that one can draw from 15 years of stereotype-threat research is that (a) the real reasons for gender differences in math performance are still unknown, (b) resources have been wasted in the pursuit of a negligible factor that may contribute to gender differences in math performance under very specific circumstances, and (c) that the R-Index could have prevented the irrational exuberance about stereotype-threat as a simple solution to an important social issue.

In a personal communication Dr. Spencer suggested that studies not included in the meta-analysis might produce different results. I suggested that Dr. Spencer provides a list of studies that provide empirical support for the hypothesis. A year later, Dr. Spencer has not provided any new evidence that provides credible evidence for stereotype-effects.  At present, the existing evidence suggests that published studies provide inflated estimates of the replicability and importance of the effect.

This blog also provides further evidence that male and female psychologists could benefit from a better education in statistics and research methods to avoid wasting resources in the pursuit of false-positive results.

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

[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.