Tag Archives: Questionable Research Practices

Dr. R’s comment on the Official Statement by the Board of the German Psychological Association (DGPs) about the Results of the OSF-Reproducibility Project published in Science.

Thanks to social media, geography is no longer a barrier for scientific discourse. However, language is still a barrier. Fortunately, I understand German and I can respond to the official statement of the board of the German Psychological Association (DGPs), which was posted on the DGPs website (in German).

BACKGROUND

On September 1, 2015, Prof. Dr. Andrea Abele-Brehm, Prof. Dr. Mario Gollwitzer, and Prof. Dr. Fritz Strack published an official response to the results of the OSF-Replication Project – Psychology (in German) that was distributed to public media in order to correct potentially negative impressions about psychology as a science.

Numerous members of DGPs felt that this official statement did not express their views and noticed that members were not consulted about the official response of their organization. In response to this criticism, DGfP opened a moderated discussion page, where members could post their personal views (mostly in German).

On October 6, 2015, the board closed the discussion page and posted some final words (Schlussbeitrag). In this blog, I provide a critical commentary on these final words.

BOARD’S RESPONSE TO COMMENTS

The board members provide a summary of the core insights and arguments of the discussion from their (personal/official) perspective.

„Wir möchten nun die aus unserer Sicht zentralen Erkenntnisse und Argumente der unterschiedlichen Forumsbeiträge im Folgenden zusammenfassen und deutlich machen, welche vorläufigen Erkenntnisse wir im Vorstand aus ihnen ziehen.“

1. 68% success rate?

The first official statement suggested that the replication project showed that 68% of studies. This number is based on significance in a meta-analysis of the original and replication study. Critics pointed out that this approach is problematic because the replication project showed clearly that the original effect sizes were inflated (on average by 100%). Thus, the meta-analysis is biased and the 68% number is inflated.

In response to this criticism, the DGPs board states that “68% is the maximum [größtmöglich] optimistic estimate.” I think the term “biased and statistically flawed estimate” is a more accurate description of this estimate.   It is common practice to consider fail-safe-N or to correct meta-analysis for publication bias. When there is clear evidence of bias, it is unscientific to report the biased estimate. This would be like saying that the maximum optimistic estimate of global warming is that global warming does not exist. This is probably a true statement about the most optimistic estimate, but not a scientific estimate of the actual global warming that has been taking place. There is no place for optimism in science. Optimism is a bias and the aim of science is to remove bias. If DGPs wants to represent scientific psychology, the board should post what they consider the most accurate estimate of replicability in the OSF-project.

2. The widely cited 36% estimate is negative.

The board members then justify the publication of the maximally optimistic estimate as a strategy to counteract negative perceptions of psychology as a science in response to the finding that only 36% of results were replicated. The board members felt that these negative responses misrepresent the OSF-project and psychology as a scientific discipline.

„Dies wird weder dem Projekt der Open Science Collaboration noch unserer Disziplin insgesamt gerecht. Wir sollten jedoch bei der konstruktiven Bewältigung der Krise Vorreiter innerhalb der betroffenen Wissenschaften sein.“

However, reporting the dismal 36% replication rate of the OSF-replication project is not a criticism of the OSF-project. Rather, it assumes that the OSF-replication project was a rigorous and successful attempt to provide an estimate of the typical replicability of results published in top psychology journals. The outcome could have been 70% or 35%. The quality of the project does not depend on the result. The result is also not a negatively biased perception of psychology as a science. It is an objective scientific estimate of the probability that a reported significant result in a journal would produce a significant result again in a replication study.   Whether 36% is acceptable or not can be debated, but it seems problematic to post a maximally optimistic estimate to counteract negative implications of an objective estimate.

3. Is 36% replicability good or bad?

Next, the board ponders the implications of the 36% success rate. “How should we evaluate this number?” The board members do not know.  According to their official conclusion, this question is complex as divergent contributions on the discussion page suggest.

„Im Science-Artikel wurde die relative Häufigkeit der in den Replikationsstudien statistisch bedeutsamen Effekte mit 36% angegeben. Wie ist diese Zahl zu bewerten? Wie komplex die Antwort auf diese Frage ist, machen die Forumsbeiträge von Roland Deutsch, Klaus Fiedler, Moritz Heene (s.a. Heene & Schimmack) und Frank Renkewitz deutlich.“

To help the board members to understand the number, I can give a brief explanation of replicability. Although there are several ways to define replicability, one plausible definition of replicability is to equate it with statistical power. Statistical power is the probability that a study will produce a significant result. A study with 80% power has an 80% probability to produce a significant result. For a set of 100 studies, one would expect roughly 80 significant results and 20 non-significant results. For 100 studies with 36% power, one would expect roughly 36 significant results and 64 non-significant results. If researchers would publish all studies, the percentage of published significant results would provide an unbiased estimate of the typical power of studies.   However, it is well known that significant results are more likely to be written up, submitted for publication, and accepted for publication. These reporting biases explain why psychology journals report over 90% significant results, although the actual power of studies is less than 90%.

In 1962, Jacob Cohen provided the first attempt to estimate replicability of psychological results. His analysis suggested that psychological studies have approximately 50% power. He suggested that psychologists should increase power to 80% to provide robust evidence for effects and to avoid wasting resources on studies that cannot detect small, but practically important effects. For the next 50 years, psychologists have ignored Cohen’s warning that most studies are underpowered, despite repeated reminders that there are no signs of improvement, including reminders by prominent German psychologists like Gerg Giegerenzer, director of a Max Planck Institute (Sedlmeier & Giegerenzer, 1989; Maxwell, 2004; Schimmack, 2012).

The 36% success rate for an unbiased set of 100 replication studies, suggest that the actual power of published studies in psychology journals is 36%.  The power of all studies conducted is even lower because the p < .05 selection criterion favors studies with higher power.  Does the board think 36% power is an acceptable amount of power?

4. Psychologists should improve replicability in the future

On a positive note, the board members suggest that, after careful deliberation, psychologists need to improve replicability so that it can be demonstrated in a few years that replicability has increased.

„Wir müssen nach sorgfältiger Diskussion unter unseren Mitgliedern Maßnahmen ergreifen (bei Zeitschriften, in den Instituten, bei Förderorganisationen, etc.), die die Replikationsquote im temporalen Vergleich erhöhen können.“

The board members do not mention a simple solution to the replicabilty problem that was advocated over 50 years ago by Jacob Cohen. To increase replicability, psychologists have to think about the strength of the effects that they are investigating and they have to conduct studies that have a realistic chance to distinguish these effects from variation due to random error.   This often means investing more resources (larger samples, repeated trials, etc.) in a single study.   Unfortunately, the leaders of German psychologists appear to be unaware of this important and simple solution to the replication crisis. They neither mention power as a cause of the problem, nor do they recommend increasing power to increase replicability in the future.

5. Do the Results Reveal Fraud?

The DGPs board members then discuss the possibility that the OSF-reproducibilty results reveal fraud, like the fraud committed by Stapel. The board points out that the OSF-results do not imply that psychologists commit fraud because failed replications can occur for various reasons.

„Viele Medien (und auch einige Kolleginnen und Kollegen aus unserem Fach) nennen die Befunde der Science-Studie im gleichen Atemzug mit den Betrugsskandalen, die unser Fach in den letzten Jahren erschüttert haben. Diese Assoziation ist unserer Meinung nach problematisch: sie suggeriert, die geringe Replikationsrate sei auf methodisch fragwürdiges Verhalten der Autor(inn)en der Originalstudien zurückzuführen.“

It is true that the OSF-results do not reveal fraud. However, the board members confuse fraud with questionable research practices. Fraud is defined as fabricating data that were never collected. Only one of the 100 studies in the OSF-replication project (by Jens Förster, a former student of Fritz Strack, one of the board members) is currently being investigated for fraud by the University of Amsterdam.  Despite very strong results in the original study, it failed to replicate.

The more relevant question is how much questionable research practices contributed to the results. Questionable research practices are practices where data are being collected, but statistical results are only being reported if they produce a significant result (studies, conditions, dependent variables, data points that do not produce significant results are excluded from the results that are being submitted for publication. It has been known for over 50 years that these practices produce a discrepancy between the actual power of studies and the rate of significant results that are published in psychology journals (Sterling, 1959).

Recent statistical developments have made it possible to estimate the true power of studies after correcting for publication bias.   Based on these calculations, the true power of the original studies in the OSF-project was only 50%.   Thus a large portion of the discrepancy between nearly 100% reported significant results and a replication success rate of 36% is explained by publication bias (see R-Index blogs for social psychology and cognitive psychology).

Other factors may contribute to the discrepancy between the statistical prediction that the replication success rate would be 50% and the actual success rate of 36%. Nevertheless, the lion share of the discrepancy can be explained by the questionable practice to report only evidence that supports a hypothesis that a researcher wants to support. This motivated bias undermines the very foundations of science. Unfortunately, the board ignores this implication of the OSF results.

6. What can we do?

The board members have no answer to this important question. In the past four years, numerous articles have been published that have made suggestions how psychology can improve its credibility as a science. Yet, the DPfP board seems to be unaware of these suggestions or unable to comment on these proposals.

„Damit wären wir bei der Frage, die uns als Fachgesellschaft am stärksten beschäftigt und weiter beschäftigen wird. Zum einen brauchen wir eine sorgfältige Selbstreflexion über die Bedeutung von Replikationen in unserem Fach, über die Bedeutung der neuesten Science-Studie sowie der weiteren, zurzeit noch im Druck oder in der Phase der Auswertung befindlichen Projekte des Center for Open Science (wie etwa die Many Labs-Studien) und über die Grenzen unserer Methoden und Paradigmen“

The time for more discussion has passed. After 50 years of ignoring Jacob Cohen’s recommendation to increase statistical power it is time for action. If psychologists are serious about replicability, they have to increase the power of their studies.

The board then discusses the possibility of measuring and publishing replication rates at the level of departments or individual scientists. They are not in favor of such initiatives, but they provide no argument for their position.

„Datenbanken über erfolgreiche und gescheiterte Replikationen lassen sich natürlich auch auf der Ebene von Instituten oder sogar Personen auswerten (wer hat die höchste Replikationsrate, wer die niedrigste?). Sinnvoller als solche Auswertungen sind Initiativen, wie sie zurzeit (unter anderem) an der LMU an der LMU München implementiert wurden (siehe den Beitrag von Schönbrodt und Kollegen).“

The question is why replicability should not be measured and used to evaluate researchers. If the board really valued replicability and wanted to increase replicability in a few years, wouldn’t it be helpful to have a measure of replicability and to reward departments or researchers who invest more resources in high powered studies that can produce significant results without the need to hide disconfirming evidence in file-drawers?   A measure of replicability is also needed because current quantitative measures of scientific success are one of the reasons for the replicability crisis. The most successful researchers are those who publish the most significant results, no matter how these results were obtained (with the exception of fraud). To change this unscientific practice of significance chasing, it is necessary to have an alternative indicator of scientific quality that reflects how significant results were obtained.

Conclusion

The board makes some vague concluding remarks that are not worthwhile repeating here. So let me conclude with my own remarks.

The response of the DGPs board is superficial and does not engage with the actual arguments that were exchanged on the discussion page. Moreover, it ignores some solid scientific insights into the causes of the replicability crisis and it makes no concrete suggestions how German psychologists should change their behaviors to improve the credibility of psychology as a science. Not once do they point out that the results of the OSF-project were predictable based on the well-known fact that psychological studies are underpowered and that failed studies are hidden in file-drawers.

I received my education in Germany all the way to the Ph.D at the Free University in Berlin. I had several important professors and mentors that educated me about philosophy of science and research methods (Rainer Reisenzein, Hubert Feger, Hans Westmeyer, Wolfgang Schönpflug). I was a member of DGPs for many years. I do not believe that the opinion of the board members represent a general consensus among German psychologists. I hope that many German psychologists recognize the importance of replicability and are motivated to make changes to the way psychologists conduct research.  As I am no longer a member of DGfP, I have no direct influence on it, but I hope that the next election will elect a candidate that will promote open science, transparency, and above all scientific integrity.

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R-Index predicts lower replicability of “subliminal” studies than “attribution” studies in JESP

PHP_subliminal_vs_attribution

This post compares articles in the Journal of Experimental Social Psychology that contained the keyword “subliminal” to articles that contained the word “attribution”.

PHP-curves based on t-tests and F-tests in these articles are compared.  Both sets of articles show signs of publication bias (fewer non-significant studies are reported than predicted based on post-hoc power).

The shape of the histogram shows clear evidence of heterogeneity (the red curve fits the data better than the green curve).

The estimated power of studies with z-scores between 2 and 4 for subliminal articles is 31%.

The estimated power of studies with z-scores between 2 and 3 for attribution articles is 42%.

The R-Index for subliminal articles is 39%, whereas the R-Index for attribution articles is 49%.

The values for subliminal articles are also lower than the values for the whole set of articles in JESP.

In conclusion, these results suggest that subliminal priming studies are less replicable than other findings in social psychology and should be the target of high-powered replication studies.  These replication studies need to take into account that reported effect sizes are inflated to achieve high power.

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!

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

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.

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

It has been known for decades that published results tend to be biased (Sterling, 1959). For most of the past decades this inconvenient truth has been ignored. In the past years, there have been many suggestions and initiatives to increase the replicability of reported scientific findings (Asendorpf et al., 2013). One approach is to examine published research results for evidence of questionable research practices (see Schimmack, 2014, for a discussion of existing tests). This blog post introduces a new test of bias in reported research findings, namely the Test of Insufficient Variance (TIVA).

TIVA is applicable to any set of studies that used null-hypothesis testing to conclude that empirical data provide support for an empirical relationship and reported a significance test (p-values).

Rosenthal (1978) developed a method to combine results of several independent studies by converting p-values into z-scores. This conversion uses the well-known fact that p-values correspond to the area under the curve of a normal distribution. Rosenthal did not discuss the relation between these z-scores and power analysis. Z-scores are observed scores that should follow a normal distribution around the non-centrality parameter that determines how much power a study has to produce a significant result. In the Figure, the non-centrality parameter is 2.2. This value is slightly above a z-score of 1.96, which corresponds to a two-tailed p-value of .05. A study with a non-centrality parameter of 2.2 has 60% power.  In specific studies, the observed z-scores vary as a function of random sampling error. The standardized normal distribution predicts the distribution of observed z-scores. As observed z-scores follow the standard normal distribution, the variance of an unbiased set of z-scores is 1.  The Figure on top illustrates this with the nine purple lines, which are nine randomly generated z-scores with a variance of 1.

In a real data set the variance can be greater than 1 for two reasons. First, if the nine studies are exact replication studies with different sample sizes, larger samples will have a higher non-centrality parameter than smaller samples. This variance in the true non-centrality variances adds to the variance produced by random sampling error. Second, a set of studies that are not exact replication studies can have variance greater than 1 because the true effect sizes can vary across studies. Again, the variance in true effect sizes produces variance in the true non-centrality parameters that add to the variance produced by random sampling error.  In short, the variance is 1 in exact replication studies that also hold the sample size constant. When sample sizes and true effect sizes vary, the variance in observed z-scores is greater than 1. Thus, an unbiased set of z-scores should have a minimum variance of 1.

If the variance in z-scores is less than 1, it suggests that the set of z-scores is biased. One simple reason for insufficient variance is publication bias. If power is 50% and the non-centrality parameter matches the significance criterion of 1.96, 50% of studies that were conducted would not be significant. If these studies are omitted from the set of studies, variance decreases from 1 to .36. Another reason for insufficient variance is that researchers do not report non-significant results or used questionable research practices to inflate effect size estimates. The effect is that variance in observed z-scores is restricted.  Thus, insufficient variance in observed z-scores reveals that the reported results are biased and provide an inflated estimate of effect size and replicability.

In small sets of studies, insufficient variance may be due to chance alone. It is possible to quantify how lucky a researcher was to obtain significant results with insufficient variance. This probability is a function of two parameters: (a) the ratio of the observed variance (OV) in a sample over the population variance (i.e., 1), and (b) the number of z-scores minus 1 as the degrees of freedom (k -1).

The product of these two parameters follows a chi-square distribution with k-1 degrees of freedom.

Formula 1: Chi-square = OV * (k – 1) with k-1 degrees of freedom.

Example 1:

Bem (2011) published controversial evidence that appear to demonstrate precognition. Subsequent studies failed to replicate these results (Galak et al.,, 2012) and other bias tests show evidence that the reported results are biased Schimmack (2012). For this reason, Bem’s article provides a good test case for TIVA.

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

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

Example 2:  

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

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

Table 2

Study                    p             z          

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

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

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

Conclusion

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

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

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