Previous investigations typically looked only at publication bias or questionable research practices QRPs (but not both), used non-representative study-level sample sizes, or only compared few bias-correcting techniques, but not all of them. Our goal was to simulate a research literature that is as realistic as possible for psychology. In order to simulate several research environments, we fully crossed five experimental factors: (1) the true underlying effect, δ (0, 0.2, 0.5, 0.8); (2) between-study heterogeneity, τ (0, 0.2, 0.4); (3) the number of studies in the meta-analytic sample, k (10, 30, 60, 100); (4) the percentage of studies in the meta-analytic sample produced under publication bias (0%, 60%, 90%); and (5) the use of QRPs in the literature that produced the meta-analytic sample (none, medium, high).
This blog post summarizes some insights from our study, internally called “meta-showdown”. Check out the preprint; and the interactive app metaExplorer. The fully reproducible and reusable simulation code is on Github, and more information is on OSF.
In this blog post, I will highlight some lessons that we learned during the project, primarily focusing on what not do to when performing a meta-analysis.
Constraints on Generality disclaimer: These recommendations apply to typical sample sizes, effect sizes, and heterogeneities in psychology; other research literatures might have different settings and therefore a different performance of the methods. Furthermore, the recommendations rely on the modeling assumptions of our simulation. We went a long way to make them as realistic as possible, but other assumptions could lead to other results.
If studies have no publication bias, nothing can beat plain old random effects meta-analysis: it has the highest power, the least bias, and the highest efficiency compared to all other methods. Even in the presence of some (though not extreme) QRPs, naive RE performs better than all other methods. When can we expect no publication bias? If (and, in my opinion only if) we meta-analyze a set of registered reports.
In any other setting except registered reports, a consequential amount of publication bias must be expected. In the field of psychology/psychiatry, more than 90% of all published hypothesis tests are significant (Fanelli, 2011) despite the average power being estimated as around 35% (Bakker, van Dijk, & Wicherts, 2012) – the gap points towards a huge publication bias. In the presence of publication bias, naive random effects meta-analysis and trim-and-fill have false positive rates approaching 100%:
More thoughts about trim-and-fill’s inability to recover δ=0 are in Joe Hilgard’s blog post. (Note: this insight is not really new and has been shown multiple times before, for example by Moreno et al., 2009, and Simonsohn, Nelson, and Simmons, 2014).
Our recommendation: Never trust meta-analyses based on naive random effects and trim-and-fill, unless you can rule out publication bias. Results from previously published meta-analyses based on these methods should be treated with a lot of skepticism.
Update 2017/06/09: We had a productive exchange with Uri Simonsohn and Joe Simmons concerning what should be estimated in a meta-analysis with heterogeneity. Traditionally, meta-analysts have tried to arrive at techniques that recover the true average effect of all conducted studies (AEA – average effect of all studies). Simonsohn et al (2014) propose estimating a different magnitude; the average effect of the studies one observes, rather than of all studies (AEO – average effect of observed studies). See Simonsohn et al (2014), the associated Supplementary Material 2, and also this blog post for arguments why they think this is a more useful quantity to estimate.
Hence, an investigation of the topic can be done on two levels: A) What is the more appropriate estimand (AEA or AEO?), and B) Under what conditions are estimators able to recover the respective true value with the least bias and least variance?
Instead of updating the section of the current blog post in the light of our discussion, I decided to cut it out and to move the topic to a future blog post. Likewise, one part of our manuscript’s revision will be a more detailed discussion about excatly these differences.
I archived the previous version of the blog post here.
Many bias-correcting methods are driven by QRPs – the more QRPs, the stronger the downward correction. However, this effect can get so strong, that methods overadjust into the opposite direction, even if all studies in the meta-analysis are of the same sign:
Note: You need to set the option “Keep negative estimates” to get this plot.
Our recommendation: Ignore bias-corrected results that go into the opposite direction; set the estimate to zero, do not reject H₀.
Typical small-study effects (e.g., by p-hacking or publication bias) induce a negative correlation between sample size and effect size – the smaller the sample, the larger the observed effect size. PET-PEESE aims to correct for that relationship. In the absence of bias and QRPs, however, random fluctuations can lead to a positive correlation between sample size and effect size, which leads to a PET and PEESE slope of the unintended sign. Without publication bias, this reversal of the slope actually happens quite often.
See for example the next figure. The true effect size is zero (red dot), naive random effects meta-analysis slightly overestimates the true effect (see black dotted triangle), but PET and PEESE massively overadjust towards more positive effects:
As far as I know, PET-PEESE is typically not intended to correct in the reverse direction. An underlying biasing process would have to systematically remove small studies that show a significant result with larger effect sizes, and keep small studies with non-significant results. In the current incentive structure of psychological research, I see no reason for such a process, unless researchers are motivated to show that a (maybe politically controversial) effect does not exist.
Our recommendation: Ignore the PET-PEESE correction if it has the wrong sign, unless there are good reasons for an untypical selection process.
A bias can be more easily accepted if it always is conservative – then one could conclude: “This method might miss some true effects, but if it indicates an effect, we can be quite confident that it really exists”. Depending on the conditions (i.e., how much publication bias, how much QRPs, etc.), however, PET/PEESE sometimes shows huge overestimation and sometimes huge underestimation.
For example, with no publication bias, some heterogeneity (τ=0.2), and severe QRPs, PET/PEESE underestimates the true effect of δ = 0.5:
In contrast, if no effect exists in reality, but strong publication bias, large heterogeneity and no QRPs, PET/PEESE overestimates at lot:
In fact, the distribution of PET/PEESE estimates looks virtually identical for these two examples, although the underlying true effect is δ = 0.5 in the upper plot and δ = 0 in the lower plot. Furthermore, note the huge spread of PET/PEESE estimates (the error bars visualize the 95% quantiles of all simulated replications): Any single PET/PEESE estimate can be very far off.
Our recommendation: As one cannot know the condition of reality, it is probably safest not to use PET/PEESE at all.
Again, please consider the “Constraints on Generality” disclaimer above.
As with any general recommendations, there might be good reasons to ignore them.
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.
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