# Correcting bias in meta-analyses: What not to do (meta-showdown Part 1)

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*tl;dr: Publication bias and p-hacking can dramatically inflate effect size estimates in meta-analyses. Many methods have been proposed to correct for such bias and to estimate the underlying true effect. In a large simulation study, we found out which methods do not work well under which conditions, and give recommendations what*not

*to use.*

*Estimated reading time: 7 min.*

*p*-hacking inflate effect size estimates from meta-analyses. In the last years, methodologists have developed an ever growing menu of statistical approaches to correct for such overestimation. However, to date it was unclear under which conditions they perform well, and what to do if they disagree. Born out of a Twitter discussion, Evan Carter, Joe Hilgard, Will Gervais and I did a large simulation project, where we compared the performance of naive random effects meta-analysis (RE), trim-and-fill (TF),

*p*-curve,

*p*-uniform, PET, PEESE, PET-PEESE, and the three-parameter selection model (3PSM).

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**.

**Limitation of generalizability 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.**

### Never trust a naive random effects meta-analysis or trim-and-fill (unless you meta-analyze a set of registered reports)

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.

But.

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. **

### Do not use *p*-curve and *p*-uniform for effect size estimation (under heterogeneity)

As a default, heterogeneity should always be expected – even under the most controlled conditions, where many labs perform the same computer-administered experiment, a large proportion showed significant and substantial amounts of between-study heterogeneity (cf. ManyLabs 1 and 3; see also our supplementary document for more details). *p*-curve and *p*-uniform assume homogeneous effect sizes, and their performance is impacted to a large extent by heterogeneity:

As you can see, all other methods retain the nominal false positive rate, but *p*-curve and *p*-uniform go through the roof as soon as heterogeneity comes into play (see also McShane, Böckenholt, & Hansen, 2016; van Aert et al., 2016).

Under H1, heterogeneity leads to overestimation of the true effect:

(additional settings for these plots: no QRPs, no publication bias, *k* = 100 studies, true effect size = 0.5)

Note that in their presentation of *p*-curve, Simonsohn et al. (2014) emphasize that, in the presence of heterogeneity, *p*-curve is intended as an estimate of the average true effect size among the studies *submitted* to *p*-curve (see here, Supplement 2). *p*-curve may indeed yield an accurate estimate of the true effect size among the significant studies, but in our view, the goal of bias-correction in meta-analysis is to estimate the average effect of all *conducted* studies. Of course this latter estimation hinges on modeling assumptions (e.g., that the effects are normally distributed), which can be disputed, and there might be applications where indeed the underlying true effect of all significant studies is more interesting.

Furthermore, as McShane et al (2016) demonstrate, *p*-curve and *p*-uniform are constrained versions of the more general three-parameter selection model (3PSM; Iyengar & Greenhouse, 1988). The 3PSM estimates (a) the mean of the true effect, δ, (b) the heterogeneity, τ, and (c) the probability that a non-significant result enters the literature, *p*. The constraints of *p*-curve and *p*-uniform are: 100% publication bias (i.e., *p* = 0) and homogeneity (i.e., τ = 0). Hence, for the estimation of effect sizes, 3PSM seems to be a good replacement for *p*-curve and *p*-uniform, as it makes these constraints testable.

**Our recommendation: Do not use p-curve or p-uniform for effect size estimation when heterogeneity can be expected (which is nearly always the case).**

### Ignore overadjustments in the opposite direction

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. **

### Do not take it seriously if PET-PEESE does a reverse correction

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:

PET-PEESE was never 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, I see no reason for such a process.

**Our recommendation: Ignore the PET-PEESE correction if it has the wrong sign.**

### PET-PEESE sometimes overestimates, sometimes underestimates

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 safest not to use PET/PEESE at all. **

## Recommendations in a nutshell: What you should *not* use in a meta-analysis

Again, please consider the “limitations of generalizability” disclaimer above.

- When you can exclude publication bias (i.e., in the context of registered reports), do not use bias-correcting techniques. Even in the presence of some QRPs they perform worse than plain random effects meta-analysis.
- In any other setting except registered reports, expect publication bias, and do not use random effects meta-analysis or trim-and-fill. Both will give you a 100% false positive rate in typical settings, and a biased estimation.
- Under heterogeneity,
*p*-curve and*p*-uniform overestimate the underlying effect and have false positive rates >= 50% - Even if all studies entering a meta-analysis point into the same direction (e.g., all are positive), bias-correcting techniques sometimes overadjust and return a significant estimate of the
*opposite*direction. Ignore these results, set the estimate to zero, do not reject H₀. - Sometimes PET/PEESE adjust into the wrong direction (i.e., increasing the estimated true effect size)

As with any general recommendations, there might be good reasons to ignore them.

#### Additional technical recommendations

- The
*p*-uniform package (v. 0.0.2) very rarely does not provide a lower CI. In this case, ignore the estimate. - Do not run
*p*-curve or*p*-uniform on <=3 significant and directionally consistent studies. Although computationally possible, this gives hugely variable results, which are often very biased. See our supplemental material for more information and plots. - If the 3PSM method (in the implementation of McShane et al., 2016) returns an incomplete covariance matrix, ignore the result (even if a point estimate is provided).

**Now you probably ask: But what should I use? Read our preprint for an answer!**

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