Recently, Matt Motyl et al. (2017) posted a pre-print paper in which they contrasted the evidential value of several journals in two time periods (2003-2004 vs. 2013-2014). The paper sparked a lot of discussion in Facebook groups , blog posts commenting on the paper (DataColada, Dr. R), and a reply from the authors. Some of the discussion was about which effect sizes should have been coded for their analyses. As it turns out, several working groups had similar ideas to check the evidential value of journals (e.g., Leif Nelson pre-registered a very similar project here). In an act of precognition, we did a time-reversed conceptual replication of of Motyl et al.’s study already in 2015:
Anna Bittner, a former student of LMU Munich, wrote her bachelor thesis on a systematic comparison of two journals in social psychology – one with a very high impact factor (Journal of Personality and Social Psychology (JPSP), IF = 5.0 at that time), another with a very low IF (Journal of Applied Social Psychology (JASP), IF = 0.8 at that time – not to be confused with the great statistical software JASP). By coincidence (or precognition), we also chose the year 2013 for our analyses. Read her full blog post about the study below.
In a Facebook discussion about the Motyl et al. paper, Michael Inzlicht wrote: “But, is there some way to systematically test a small sample of your p-values? […] Can you randomly sample 1-2% of your p-values, checking for errors and then calculating your error rate? I have no doubt there will be some errors, but the question is what the rate is.“. As it turns out, we also did our analysis on the 2013 volume of JPSP. Anna followed the guidelines by Simonsohn et al. That means, she only selected one effect size per sample, selected the focal effect size, and wrote a detailed disclosure table. Hence, we do not think that the critique in the DataColada blog post applies to our coding scheme. The disclosure table includes quotes from the verbal hypotheses, quotes from results section, and which test statistic was selected. Hence, you can directly validate the choice of effect sizes. Furthermore, all test statistics can be entered into the p-checker app, where you get TIVA, R-Index, p-curve and more diagnostic tests (grab the JPSP test statistics & JASP test statistics).
Now we can compare two completely independently coded p-curve disclosure tables about a large set of articles. Any disagreement of course does not mean that one party is right and the other is wrong. But it will be interesting to see the amount of agreement.
Here comes Anna’s blog post about her own study. Anna Bittner is now doing her Master of Finance at the University of Melbourne.
by Anna Bittner and Felix Schönbrodt
The recent discoveries on staggeringly low replicability in psychology have come as a shock to many and led to a discussion on how to ensure better research practices are employed in the future. To this end, it is necessary to find ways to efficiently distinguish good research from bad and research that contains evidential value from such that does not.
In the past the impact factor (IF) has often been the favored indicator of a journal’s quality. To check whether a journal with a higher IF does indeed publish the “better” research in terms of evidential value, we compared two academic journals from the domain of social psychology: The Journal of Personality and Social Psychology (JPSP, Impact Factor = 5.031) and the Journal of Applied Social Psychology (JASP, Impact Factor = 0.79).
For this comparison, Anna has analysed and carefully hand-coded all studies with hypothesis tests starting in January 2013 and progressing chronologically until about 110 independent test statistics for each journal were acquired. See the full report (in German) in Anna’s bachelor thesis. These test statistics were fed into the p-checker app (Version 0.4; Schönbrodt, 2015) that analyzed them with the tools p-curve, TIVA und R-Index.
All material and raw data is available on OSF: https://osf.io/pgc86/
P-curve (Simonsohn, Nelson, & Simmons, 2014) takes a closer look at all significant p-values and plots them against their relative frequency. This results in a curve that will ideally have a lot of very small p-values (<.025) and much fewer larger p–values (>.025). Another possible shape is a flat curve, which will occur when researchers only investigate null effects and selectively publish those studies that obtained a p-value < .05 by chance. under the null hypothesis each individual p-value is equally likely and the distribution is even. P-curve allows to test whether the empirical curve is flatter than the p-curve that would be expected at any chosen power.
Please note that p-curve assumes homogeneity (McShane, Böckenholt, & Hansen, 2016). Lumping together diverse studies from a whole journal, in contrast, guarantees heterogeneity. Hence, trying to recover the true underlying effect size/power is of limited usefulness here.
The p-curves of both JPSP and JASP were significantly right-skewed, which suggests that both journal’s output cannot be explained by pure selective publication of null effects that got significant by chance. JASP’s curve, however, had a much stronger right-skew, indicating stronger evidential value:
TIVA (Schimmack, 2014a) tests for an insufficient variance of p-values: If no p-hacking and no publication bias was present, the variance of p-values should be at least 1. An value below 1 is seen as indicator of publication bias and/or p-hacking. However, variance can and will be much larger than 1 when studies of different sample and effect sizes are included in the analysis (which was inevitably the case here). Hence, TIVA is a rather weak test of publication bias when heterogeneous studies are combined: A p-hacked set of heterogeneous effect sizes can still result in a high variance in TIVA. Publication bias and p-hacking reduce the variance, but heterogeneity and different sample sizes can increase the variance in a way that the TIVA is clearly above 1, even if all studies in the set are severely p-hacked.
As expected, neither JPSP nor JASP attained a significant TIVA result, which means the variance of p-values was not significantly smaller than 1 for either journal. Descriptively, JASP had a higher variance of 6.03 (chi2(112)=674, p=1), compared to 1.09 (chi2(111)=121, p=.759) for the JPSP. Given the huge heterogeneity of the underlying studies, a TIVA variance in JPSP close to 1 signals a strong bias. This, again, is not very surprising. We already knew before with certainty that our literature is plagued by huge publication bias.
The descriptive difference in TIVA variances can be due to less p-hacking, less publication bias, or more heterogeneity of effect sizes and sample sizes in JASP compared to JPSP. Hence, drawing firm conclusions from this numerical difference is difficult; but the much larger value in JASP can be seen as an indicator that the studies published there paint a more realistic picture.
(Note: The results here differ from the results reported in Anna’s bachelor thesis, as the underlying computation has been improved. p-checker now uses logged p-values, which allows more precision with very small p-values. Early versions of p-checker underestimated the variance when extremely low p-values were present).
Unfortunately, Motyl et al. do not report the actual variances from their TIVA test (only the test statistics), so a direct comparison of our results is not possible.
The R-Index (Schimmack, 2014b) is a tool that aims to quantify the replicability of a set of studies. It calculates the difference between median estimated power and success rate, which results in the so called inflation rate. This inflation rate is then subtracted from the median estimated power, resulting in the R-Index. Here is Uli Schimmack’s interpretation of certain R-Index values: “The R-Index is not a replicability estimate […] I consider an R-Index below 50 an F (fail). An R-Index in the 50s is a D, and an R-Index in the 60s is a C. An R-Index greater than 80 is considered an A”.
Here, again, the JASP was ahead. It obtained an R-Index of .60, whereas the JPSP landed at .49.
Both journals had success rates of around 80%, which is much higher than what would be expected with the average power and effect sizes found in psychology (Bakker, van Dijk, & Wicherts, 2012). It is known and widely accepted that journals tend to publish significant results over non-significant ones.
Motyl et al. report an R-Index of .52 for 2013-2014 for high impact journals, which is very close to our value of .49.
The comparison between JPSP and JASP revealed a better R-Index, a more realistic TIVA variance and a more right-skewed p-curve for the journal with the much lower IF. As the studies had roughly comparable sample sizes (JPSP: Md = 86, IQR: 54 – 124; JASP: Md = 114, IQR: 65 – 184), I would bet some money that more studies from JASP replicate then from JPSP.
A journal’s prestige does not protect it from research submissions that contain QRPs – contrarily it might lead to higher competition between reseachers and more pressure to submit a significant result by all means. Furthermore, higher rejection rates of a journal also leave more room for “selecting for significance”. In contrast, a journal that must publish more or less every submission it gets to fill up its issues simply does not have much room for this filter. With the currently applied tools, however, it is not possible to make a distinction between p-hacking and publication bias: they only detect patterns in test statistics that can be the result of both practices.
Bakker, M., van Dijk, A., & Wicherts, J. M. (2012). The rules of the game called psychological science. Perspectives on Psychological Science, 7(6), 543-554.
McShane, B. B., Böckenholt, U., & Hansen, K. T. (2016). Adjusting for publication bias in meta-analysis: An evaluation of selection methods and some cautionary notes. Perspectives on Psychological Science, 11, 730–749. doi:10.1177/1745691616662243
Schimmack, U. (2014b). Quantifying Statistical Research Integrity: The Replicabilty-Index.
Schimmack, U. (2014a, December 30). The Test of Insufficient Variance (TIVA): A New Tool for the Detection of Questionable Research Practices. Retrieved from https://replicationindex.wordpress.com/2014/12/30/the-test-of-insufficient-variance-tiva-a-new-tool-for-the-detection-of-questionable-research-practices/
Schimmack, U. (2015, September 15). Replicability-Ranking of 100 Social Psychology Departments [Web log post]. Retrieved from https://replicationindex.wordpress.com/2015/09/15/replicability-ranking-of-100-social-psychology-departments/
Schönbrodt, F. (2015). p-checker [Online application]. Retrieved from http://shinyapps.org/apps/p-checker/
Simonsohn, U., Nelson, L. D., & Simmons, J. P. (2014). P-curve: A key to the file-drawer. Journal of Experimental Psychology: General, 143(2), 534.
In the last year, the discussion in our field moved from “Do we have a replication crisis?” towards “Yes, we have a problem, and what can and should we change? How can be implement it?”. I think that we need both top-down changes on an institutional level, combined with bottom-up approaches, such as local Open Science Initiatives. Here, I want to present one big institutional change concerning open data.
The German Research Foundation (DFG), the largest public funder of research in Germany, updated their policy on data sharing, which can be summarized in a single sentence: Publicly funded research, including the raw data, belongs to the public. Consequently, all research data from a DFG funded project should be made open immediately, or at least a couple of months after finalization of the research project (see  and ). Furthermore, the DFG asked all scientific disciplines to develop more specific guidelines which implement these principles in their respective discipline.
The German Psychological Society (Deutsche Gesellschaft für Psychologie, DGPs) installed a working group (Andrea Abele-Brehm, Mario Gollwitzer and me) who worked for one year on such recommendations for psychology.
In the development of the document, we tried to be very inclusive and to harvest the wisdom of the crowd. A first draft (Feb 2016) was discussed for 6 weeks in an internet forum where all DGPs members could comment. Based on this discussion (and many additional personal conversations), a revised version was circulated and discussed in person with a smaller group of interested members (July 2016) and a representative of the DFG. Furthermore, we had regular contact to the “Fachkollegium Psychologie” of the DFG (i.e., the group of people which decides about funding decisions in psychology; meanwhile, the members of the Fachkollegium have changed on a rotational basis). Finally, the chair persons of all sections of the DGPs and the speakers of the young members had another possibility to comment. On September 17, the recommendations were officially adopted by the society.
I think this thorough and iterative process was very important for two reasons: First, it definitely improved the quality of the document, because we got so many great ideas and comments from the members, ironing out some inconsistencies and covering some edge cases. Second, it was important in order to get people on board. As this new open data guideline of the DFG causes a major change in the way we do our everyday scientific work, we wanted to talk to and convince as many people as possible from the early steps on. Of course not every single of the >4,000 members is equally convinced, but the topic now has considerable attention in the society.
Hence, one focus was consensus and inclusivity. At the same time, we had the goal to develop bold and forward-looking guidelines that really address the current challenges of the field, and not to settle on the lowest common denominator. For this goal, we had to find a balance between several, sometimes conflicting, values.
Research transparency ⬌ privacy rights. A first specialty of psychology is that we do not investigate rocks or electrons, but human subjects who have privacy rights. In a nutshell, privacy rights have to be respected, and in case of doubt they win over openness. But if data can be properly anonymized, there’s no problem in open sharing; one possibility to share non-anonymous research data are “scientific use files”, where access is restricted to scientists. If data cannot be shared due to privacy (or other) reasons, this has to be made transparent in the paper. (Hence, the recommendations are PRO compatible). The recommendations give clear guidance on privacy issues and gives practical advice, for example, on how to write your informed consent that you actually are able to share the data afterwards.
Data reuse ⬌ right of first usage. A second balance concerns an optimal reuse of data on the one hand, and the right of first usage of the original authors. In the discussion phase during the development of the recommendations, several people expressed the fear of “research parasites”, who “steal” the data from hard-working scientists. A very common gut feeling is: “The data belong to me”. But, as we are publicly funded researchers with publicly funded research projects, the answer is quite clear: the data belong to the public. There is no copyright on raw data. On the other hand, we also need incentives for original researchers to generate data in the first place. Data generators of course have the right of first usage, and the recommendations allow to extend this right by an embargo of 5 more years (see below). But at the end of the day, publicly funded research data belongs to the public, and everybody can reuse it. If data are open by default, a guideline also must discuss and define how data reuse should be handled. Our recommendations make suggestions in which cases a co-authorship should be offered to the data providers and in which cases this is not necessary.
Verification ⬌ fair treatment of original authors. Finally, research should be verifiable, but with a fair treatment of the original authors. The guidelines say that whenever a reanalysis of a data set is going to be published (and that also includes blog posts or presentations), the original authors have to be informed about this. They cannot prevent the reanalysis, but they have the chance to react to it.
We distinguish two types of data sharing:
Type 1 data sharing means that all raw data should be openly shared that is necessary to reproduce the results reported in a paper. Hence, this can be only a subset of all available variables in the full data set: The subset which is needed to reproduce these specific results. The primary data are an essential part of an empirical publication, and a paper without that simply is not complete.
Type 2 data sharing refers to the release of the full data set of a funded research project. The DGPs recommendations claim that after the end of a DFG-funded
project all data – even data which has not yet been used for publications – should be made open. Unpublished null results, or additional, exploratory variables now have to chance to see the light and to be reused by other researchers. Experience tells that not all planned papers have been written after the official end date of a project. Therefore, the recommendations allow that the right of first usage can be extended with an embargo period of up to 5 years, where the (so far unpublished) data do not have to be made public. The embargo option only applies to data that has not yet been used for publications. Hence, typically an embargo cannot be applied to Type 1 data sharing.
To summarize, I think these recommendations are the most complete, practical, and specific guidelines for data sharing in psychology to date. (Of course much more details are in the recommendations themselves). They fully embrace openness, transparency and scientific integrity. Furthermore, they do not proclaim detached ethical principles, but give very practical guidance on how to actually implement data sharing in psychology.
What are the next steps? The president of the DGPs, Prof. Conny Antoni, and the secretary Prof. Mario Gollwitzer already contacted other psychological societies (APA, APS, EAPP, EASP, EFPA, SIPS, SESP, SPSP) and introduced our recommendations. The Board of Scientific Affairs of EFPA – the European Federation of Psychologists’ Associations – already expressed its appreciation of the recommendations and will post them on their website. Furthermore, it will discuss them in an invited symposium on the European Congress of Psychology in Amsterdam this year. A mid-term goal will also be to check compatibility with existing other guidelines and to think about a harmonization of several guidelines within psychology.
As other scientific disciplines in Germany also work on their specific implementations of the DFG guidelines, it will be interesting to see whether there are common lines (although there certainly will be persisting and necessary differences between the requirements of the fields). Finally, we are in contact with the new Fachkollegium at the DFG, with the goal to see how the recommendations can and should be used in the process of funding decisions.
If your field also implements such recommendations/guidelines, don’t hesitate to contact us.
Schönbrodt, F., Gollwitzer, M., & Abele-Brehm, A. (2017). Der Umgang mit Forschungsdaten im Fach Psychologie: Konkretisierung der DFG-Leitlinien. Psychologische Rundschau, 68, 20–35. doi:10.1026/0033-3042/a000341. [PDF German][PDF English]
(English translation by Malte Elson, Johannes Breuer, and Zoe Magraw-Mickelson)
by Angelika Stefan & Felix Schönbrodt
This is the second part of “Two meanings of priors”. The first part explained a first meaning – “priors as subjective probabilities of models”. While the first meaning of priors refers to a global appraisal of existing hypotheses, the second meaning of priors refers to specific assumptions which are needed in the process of hypothesis building. The two kinds of priors have in common that they are both specified before concrete data are available. However, as it will hopefully become evident from the following blog post, they differ significantly from each other and should be distinguished clearly during data analysis.
In order to know how well evidence supports a hypothesis compared to another hypothesis, one must know the concrete specifications of each hypothesis. For example, in the tea tasting experiment, each hypothesis was characterized by a specific probability (e.g., the success rate of exactly 0.5 in HFisher of the previous blog post). What might sound trivial at first – deciding on the concrete specifications of a hypothesis – is in fact one of the major challenges when doing Bayesian statistics. Scientific theories are often imprecise, resulting in more than one plausible way to derive a hypothesis. With deciding upon one specific hypothesis, often new auxiliary assumptions are made. These assumptions, which are needed in order to specify a hypothesis adequately, are called “priors” as well. They influence the formulation and interpretation of the likelihood (which gives you the plausibility of data under a specific hypothesis). We will illustrate this in an example.
A food company conducts market research in a large German city. They know from a recent representative enquiry by the German Federal Statistical Office that Germans spend on average 4.50 € for their lunch (standard deviation: 0.60 €). Now they want to know if the inhabitants of one specific city spend more money for their lunch compared to the German average. They expect lunch expenses to be especially high in this city because of the generally high living costs. In a traditional testing procedure in inferential statistics the food company would formulate two hypotheses to test their assumption: a null and an alternative hypothesis: H0: µ ≤ 4.50 and H1: µ > 4.50.
In Bayesian hypothesis testing, the formulation of the hypotheses has to be more precise than this. We need precise hypotheses as a basis for the likelihood functions which assign probability values to possible states of reality. The traditional formulation, µ > 4.50, is too vague for that purpose: Is any lunch cost above 4.50€ a priori equally likely? Is it plausible that a lunch costs 1,000,000€ on average? Probably not. Not every state of reality is, a priori, equally plausible. “Models connect theory to data“ (Rouder, Morey, & Wagenmakers, 2016), and a model that predicts everything predicts nothing.
As Bayesian statisticians we therefore must ask ourselves: Which values are more plausible given that our hypotheses are true? Of course, our knowledge differs from case to case in this point. Sometimes, we may be able to commit to a very small range of plausible values or even to a single value (in this case, we would call the respecting hypothesis a “point hypothesis”). Theories in physics sometimes predict a single state of reality: “If this theory is true, then the mass of a Chicks boson is exactly 1.52324E-16 gr”.
More often, however, our knowledge about plausible values under a certain theory might be less precise, leading to a wider range of plausible values. Hence, the prior in the second sense defines the probability of a parameter value given a hypothesis, p(θ | H1).
Let us come back to the food company example. Their null hypothesis might be that there is no difference between the city in the focus of their research project and the German average. Hence, the null hypothesis predicts an average lunch cost of 4.50€. With the alternative hypothesis, it becomes slightly more complex. They assume that average lunch expenses in the city should be higher than the German average, so the most plausible value under the alternative hypothesis should be higher than 4.5. However, they may deem it very improbable that the mean lunch expenses are more than two standard deviations higher than the German average (so, for example, it should be very improbable that someone spends more than, say, 10 EUR for lunch even in the expensive city). With this knowledge, they can put most plausibility on values in a range from 4.5 to 5.7 (4.5 + 2 standard deviations). They could further specify their hypothesis by claiming that the most plausible value should be 5.1, i.e., one standard deviation higher than the German average. The elements of these verbal descriptions of the alternative hypothesis can be summarized in a truncated normal distribution that is centered over 5.1 and truncated at 4.5 (as the directional hypothesis does not predict values in the opposite direction).
With this model specification, the researchers would place 13% of the probability mass on values larger than 2SD of the general population (i.e., > 5.7).
Making it even more complex, they could quantify their uncertainty about the most plausible value (i.e., the maximum of the density distribution) by assigning another distribution to it. For example, they could build a normal distribution around it, with a mean of 5.1 and a standard deviation of 0.3. This would imply that in their opinion, 5.1 is the “most plausible most plausible value” but that values between 4.8 and 5.4 are also potential candidates for the most plausible value.
What you can notice in the example about the development of hypotheses is that the market researchers have to make auxiliary assumptions on top of their original hypothesis (which was H1: µ > 4.5). If possible, these prior plausibilities should be informed by theory or by previous empirical data. Specifying alternative hypothesis in this way may seem to be an unnecessary burden compared to traditional hypothesis testing where these extra assumptions seemingly are not necessary. Except that they are necessary. Without going into detail in this blog post, we recommend to read Rouder et al.’s (2016a) “Is there a free lunch in inference?“, with the bottom line that principled and rational inference needs specified alternative hypotheses. (For example, in Neyman-Pearson testing, you also need to specify a precise alternative hypothesis that refers to the “smallest effect size of interest”)
Furthermore, readers might object: “Researchers rarely have enough background knowledge to specify models that predict data“. Rouder et al. (2016b) argue that this critique is overstated, as (1) with proper elicitation, researchers often know much more than they initially think, (2) default models can be a starting point if really no information is available, and (3) several models can be explored without penalty.
A question that may come to your mind soon after you understood the difference between the two kinds of priors is: If they both are called “priors”, do they depend on each other in some way? Does the formulation of your “personal prior plausibility of a hypothesis” (like the skeptical observer’s prior on Mrs. Bristol’s tea tasting abilities) influence the specification of your model (like the hypothesis specification in the second example) or vice versa?
The straightforward answer to this question is “no, they don’t”. This can be easily illustrated in a case where the prior conviction of a researcher runs against the hypothesis he or she wants to test. The food company in the second example has sophisticatedly determined the likelihood of the two hypotheses (H0 and H1), which they want to pit against each other. They are probably considerably convinced that the specification of the alternative hypothesis describes reality better than the specification of the null hypothesis. In a simplified form, their prior odds (i.e., priors in the first sense) can be described as a ratio like 10:1. This would mean that they deem the alternative hypothesis ten times as likely as the null hypothesis. However, another food company, may have prior odds of 3:5 while conducting the same test (i.e., using the same prior plausibilities of model parameters). This shows that priors in the first sense are independent of priors in the second sense. Priors in the first sense change with different personal convictions while priors in the second sense remain constant. Similarly, prior beliefs can change after seeing the data – the formulation of the model (i.e., what a theory predicts) stays the same. (As long as the theory, from which the model specification is derived, does not change. In an estimation context, the model parameters are updated by the data.)
The term “prior” has two meanings in the context of Bayesian hypothesis testing. The first one, usually applied in Bayes factor analysis, is equivalent to a prior subjective probability of a hypothesis (“how plausible do you deem a hypothesis compared to another hypothesis before seeing the data”). The second meaning refers to the assumptions made in the specification of the model of the hypotheses which are needed to derive the likelihood function. These two meanings of the term “prior” have to be distinguished clearly during data analysis, especially as they do not depend on each other in any way. Some researchers (e.g., Dienes, 2016) therefore suggest to call only priors in the first sense “priors” and speak about “specification of the model” when referring to the second meaning.
Dienes, Z. (2011). Bayesian versus orthodox statistics: Which side are you on?. Perspectives On Psychological Science, 6(3), 274-290. http://doi:10.1177/1745691611406920
Dienes, Z. (2016). How Bayes factors change scientific practice. Journal Of Mathematical Psychology, 7278-89. http://doi:10.1016/j.jmp.2015.10.003
Lindley, D. V. (1993). The analysis of experimental data: The appreciation of tea and wine. Teaching Statistics, 15(1), 22-25. http://dx.doi.org/10.1111/j.1467-9639.1993.tb00252.x
Rouder, J. N., Morey, R. D., Verhagen, J., Province, J. M., & Wagenmakers, E. J. (2016a). Is there a free lunch in inference? Topics in Cognitive Science, 8, 520–547. http://doi.org/10.1111/tops.12214
Rouder, J. N., Morey, R. D., & Wagenmakers, E. J. (2016b). The Interplay between Subjectivity, Statistical Practice, and Psychological Science. Collabra, 2(1), 6–12. http://doi.org/10.1525/collabra.28
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