Recommendations for peer review in current (strained?) climate

In this post, I will discuss challenges that arise when peer reviewing submitted articles in the current tense climate. Such climate stems from the growing recognition that we need to more openly and fully report our methods and results, avoiding questionable research practices and hence questionable conclusions. This is inspired by a recent piece wherein two authors felt unfairly accused of “nefarious practices” and also based on some of my own recent experiences peer reviewing articles.

The goal of peer review — for empirical articles at least — is to carefully evaluate research to make sure that conclusions drawn from evidence are valid (i.e., correct). This involves evaluating many different aspects of the reported research including whether correct statistical analyses were carried out, whether appropriate experimental designs were used,  and whether any confounds were unintentionally introduced, to name a few.

Another concern, which has recently received a lot more attention, is to assess the extent to which flexibility in design and/or analyses may have contributed to the reported results (Simmons et al., 2011; Gelman & Lokan, 2013). That is, if a set of data are analyzed in many different ways and such analytic multiplicity isn’t appropriately accounted for, incorrect conclusions can be drawn from the evidence due to an inflated false positive error rate (e.g., incorrectly concluding an IV had a causal effect on a DV when in fact the data are entirely consistent with what one would expect due to sampling error assuming the null is true).

Hence, a crucial task when reviewing an empirical article is to rule out that flexibility in analyses (&/or design, e.g., data collection termination rule) can account for the reported results, and hence avoid the possibility that invalid conclusions have been made. From my perspective, however, it is really important that as reviewers we do this very carefully so that authors (whose work is being reviewed) do not feel accused of intentional p-hacking or researcher misconduct.

Here’s an example to demonstrate my point. During peer-review of an article on goal-directed bias in memory judgments (at Consciousness & Cognition), O’Connor & Mill felt unfairly accused of “unconventional and nefarious practices” in analyzing their data (see here for details). We don’t have all of the details, but it looks like one of the reviewers was concerned about how exclusions were made by the authors with regard to (1) overly low sensitivity index (d’) and (2) native language requirements. This reviewer went on to say that “the authors must accept the consequences of data that might disagree with their hypotheses”. It should be clear that this reviewer was completely justified in being concerned that flexibility in the different exclusions criteria that could have been used could have lead to invalid conclusions regarding the target phenomenon (i.e., how goals can bias memory processes). However, in my opinion, the language used to express such a concern was inappropriate because it insinuated that such flexibility may have been intentionally exploited.

Another example comes from a recent paper I reviewed that reported evidence that “response effort” may moderate the impact of cleanliness priming on moral judgments (under review at Frontiers). On the surface, the evidence seemed very strong, but upon closer inspection I realized that there seemed to be quite a bit of flexibility with respect to (1) how “response effort” was operationalized across the 4 reported studies and (2) exclusion criteria used for excluding participants who exhibited “insufficient effort responding”. Concerned that such flexibility may have contributed to an inflated false positive error rate (and hence invalid conclusions), I carefully delineated these concerns and concluded my review by stating:

“In sum, the main problem is that based on the methods and results presented in the current manuscript, we cannot rule out the possibility that unintentional confirmation bias inadvertently (1) biased the operationalization of “response effort” and (2) biased the chosen exclusion criteria, which in combination represents a potential alternative explanation for the current pattern of results.”

It is important to notice that I intentionally framed my concern in terms of the fact that flexibility in analyses may have unintentionally biased the results. This is extremely crucial because most authors are probably not aware that flexibility in analyses/methods may have unduly influenced their reported results. Hence, of course they will become defensive if you insinuate that they have intentionally exploited such flexibility, when they in fact have not intentionally done so. This would be akin to insinuating that researchers intentionally confounded their experimental manipulation! The point here is that flexibility in analyses/design — just like experimental confounds — need to be ruled out, and this is necessary for valid inference regardless of whether these problems were intentionally or unintentionally introduced.

Recommendations

1. Always frame your concerns about flexibility in analyses/design (or any other concern) using language that focuses on the ideas rather than the authors.
2. Give the benefit of the doubt to authors and always assume that flexibility in analyses/design may have unintentionally influenced the reported results.
3. Use a standard reviewer statement that has been specifically designed to help with such matters. The statement (developed by Uri Simonsohn, Joe Simmons, Leif Nelson, Don Moore, and myself) can be used by any reviewer to request disclosure of additional methodological details, which can help assess the extent to which flexibility in analyses/design may have contributed to the reported results. Using this standard statement is another way to avoid having the authors feel as though you are insinuating they have intentionally done something questionable.

“I request that the authors add a statement to the paper confirming whether, for all experiments, they have reported all measures, conditions, data exclusions, and how they determined their sample sizes. The authors should, of course, add any additional text to ensure the statement is accurate. This is the standard reviewer disclosure request endorsed by the Center for Open Science [see http://osf.io/hadz3]. I include it in every review.”

Insufficiently open science — not theory — obstructs empirical progress!

I stumbled upon Greenwald et al.’s (1986) “Under what conditions does theory obstruct research progress” article the other day and decided to re-read it. I found it very interesting to re-read in the context of current controversies about p-hacking and replication difficulties! Very prescient indeed.

In the article, Greenwald et al. argued that theory obstructs research progress when:
1. testing theory is the central goal of research, and
2. the researcher has more faith in the correctness of the theory than in the suitability of the procedures used to test the theory.

Though I agree with their main argument (& indeed we’ve made a very similar argument here), I don’t think it’s completely correct (or at least incomplete given what we now know about modal research practices).

I want to put forward the possibility that it is insufficiently open research practices — rather than theory-confirming practices — that obstruct empirical progress! Testing theory has always involved the (precarious) goal of producing experimental results that confirm a theory-derived novel empirical predictions. Such endeavors almost always involve repeated tweaking and refinement of procedures and calibration of instruments. As long as researchers are sufficiently open about the methods used to execute their experimental tests, however, such theory-confirming practices *can* lead to empirical progress. This is the case because being open means other researchers can gauge more objectively all of the required methodological tweakings that were required to get the theory-confirming result, but is also the case because being open means using stronger methods and better thought-out experimental designs to begin with. Consequently, being more open means theory-derived empirical predictions are more open to disconfirmation (given disconfirmation requires strong methods), which actually substantially *accelerates* research progress! Don’t take my word for it, here’s what Richard Feynman had to say on the subject:

“We are trying to prove ourselves wrong as quickly as possible, because only in that way can we find progress.” (Richard Feynman)

 

Two quotes from Greenwald et al.’s article that inspired this post!

“The theory-testing approach runs smoothly enough when theoretically predicted results are obtained. However, when predictions are not confirmed, the researcher faces a predicament that can be called the disconfirmation dilemma (Greenwald & Ronis, 1981). This dilemma is resolved by the researcher’s choosing between proceeding (a) as if the theory being tested is incorrect (e.g., by reporting the disconfirming results), or (b) as if the theory is still likely to be correct. The researcher who preserves faith in the theory’s correctness will persevere at testing the theory — perhaps by conducting additional data analyses, by collecting more data, or by revising procedures and then collecting more data.” (p. 219).

“A theory-confirming researcher perseveres by modifying procedures until prediction-supporting results are obtained. Particularly if several false starts have occurred, the resulting confirmation may well depend on conditions introduced while modifying procedures in response to initial disconfirmations. However, because no systematic empirical comparison of the evolved (confirming) procedures with earlier (disconfirming) ones has been attempted, the researcher is unlikely to detect the confirmation’s dependence on the evolved details of procedure. Although the conclusions from such research need to be qualified by reference to the tried-and-abandoned procedures, those conclusions are often stated only in the more general terms of the guiding theory. Such conclusions constitute avoidable overgeneralizations.” (p. 220)

Confusion regarding scientific theory as contributor to replicability crisis?

[DISCLAIMER: Ideas and statements made in this blog post in no way are intended to insult or disrespect my fellow psychologists.]

In this post, I will discuss psychology’s replicability crisis from a new angle. I want to consider the possibility that confusion regarding what scientific theory is and how theory is developed may have contributed to the replicability crisis in psychology.

Scientific theories are internally consistent sets of principles that are put forward to explain various empirical phenomena. Theories compete in the scientific marketplace by being evaluated according to the following five criteria (Popper, 1959; Quine & Ullian, 1978):

1. parsimony: simpler theories involving the fewest entities are preferred to more complicated theories
2. explanatory power:  theories that can explain many empirical phenomena are preferred to theories that can only explain a few phenomena
3. predictive power: a useful theory makes new empirical predictions above and beyond extant theories
4. falsifiability: a theory must yield falsifiable predictions
5. accuracy: degree to which a theory’s empirical predictions match experimental results

It is important to explicitly point out, however, that underlying all of these considerations is the fact that before a theory can be put forward, demonstrably repeatable empirical phenomena need to exist in the first place that need to be explained! Demonstrably repeatable is understood to mean that an empirical phenomenon “can be regularly reproduced by anyone who carries out the appropriate experiment in the way prescribed” (Popper, 1959, p. 23). Put simply, scientific theories aim to explain repeatable empirical phenomena; without repeatable empirical phenomena, there is nothing to explain and hence no theories can be developed.

The idea then is that confusion regarding these points may have contributed to the current replicability crisis.  To support my point, I will briefly review some examples from the beleaguered “social priming” literature. [DISCLAIMER: I contend my argument likely also holds in other areas of experimental psychology; I’ve chosen this literature out of convenience, and hence my intention was not to pick on these specific researchers.]

For example, in a piece entitled “The Alleged Crisis and the Illusion of Exact Replication”, Stroebe and Strack (2014) state that:

“Although reproducibility of scientific findings is one of science’s defining features, the ultimate issue is the extent to which a theory has undergone strict tests and has been supported by empirical findings” (p. 60).

Stroebe and Strack seem to be saying that the most important issue (i.e., the “ultimate issue”) in evaluating scientific theory is whether the theory has been supported by empirical findings (accuracy criterion #5 from above), but at the same time downplay the reproducibility of findings as “one of science’s defining features”. This kind of position, however, doesn’t seem to fit with the considerations above whereby reproducible empirical phenomena are required before a scientific theory can even be put forward, let alone be evaluated viz-a-viz other theories.

In another example, Cesario (2014) — in the context of discussing what features of the original methodology need to be duplicated for a replication attempt to be informative — states:

“We know this only because we have relevant theories that tell us that these features should matter.” (p. 42) “Theories inform us as to which variables are important and which are unimportant (i.e., which variables can be modified from one research study to the next without consequence).” (p. 45)

Cesario seems to be saying that we can use a scientific theory to tell us which methodological features in an original study need to be duplicated to reliably observe an empirical phenomenon. Such a position would seem to be putting the cart in front of the horse, however, given that without demonstrably repeatable empirical phenomena to explain, no theory can be developed in the first place.1

A final example comes from an article by Dijksterhuis (2014, “Welcome back theory!”), who summarizes Cesario’s (2014) paper by saying:

“Cesario  draws  the  conclusion  that  although  behavioral  priming researchers  could  show  more  methodological  rigor,  the relative infancy of the theory is the main reason the field faces a problem.” (p. 74)

Dijksterhuis seems to be saying that the field of behavioral priming currently has problems with non-replications because of insufficiently developed theory. This position is again difficult to reconcile with the standard conceptualization of scientific theory. With all due respect, such a position would be akin to saying that ESP researchers have yet to document replicable ESP findings because theories of ESP are insufficiently developed!

But how could this happen?

I contend that such confusion regarding scientific theory has emerged due (at least in part) to the relatively weak methods used in modal research (LeBel & Peters, 2011). This includes the improper use of null hypothesis significant testing (i.e., p<.05 indicates a “reliable” finding) and an over-emphasis on conceptual rather than direct replications. Conceptual replications involve immediately following up an observed effect with a study using a different methodology, hence rendering any negative results completely ambiguous (i.e., was the different result due to the different methodology or due to the falsity of the tested hypothesis). This practice effectively shields any positive empirical findings from falsification (see here for a great blog post precisely on this point; see also Greenwald et al., 1986). Granted, once the reproducibility of a particular effect has been independently confirmed (using the original methodology), it is of course important to subsequently test whether the effect generalizes to other methods (i.e., other operationalizations of the IV and DV). However, we simply cannot skip the first step. This broadly fits with Rozin’s (2001) position that psychologists need to place much more emphasis on first reliably describing empirical phenomena, before we set out to actually test hypotheses about those phenomena.


1. That being said, Cesario should be lauded for his public stance that behavioral priming researchers need to directly replicate their own findings (using the same methodology) before publishing their findings.

 

References

Cesario, J. (2014). Priming, replication, and the hardest science. Perspectives on Psychological Science, 9, 40–48.

Dijksterhuis, A. (2014). Welcome Back Theory!. Perspectives on Psychological Science, 9(1), 72-75.

Greenwald, A. G., Pratkanis, A. R., Leippe, M. R., & Baumgardner, M. H. (1986). Under what conditions does theory obstruct research progress?. Psychological Review, 93(2), 216.

LeBel, E. P., & Peters, K. R. (2011). Fearing the future of empirical psychology: Bem’s (2011) evidence of psi as a case study of deficiencies in modal research practice. Review of General Psychology, 15,371-379

Popper, K. R. (1959). The logic of scientific discovery. New York, NY: Basic Books

Quine, W. V. O., & Ullian, J. S. (1978). The web of belief (2nd ed.). New York, NY: Random House

Rozin, P. (2001). Social psychology and science: Some lessons from Solomon Asch. Personality and Social Psychology Review, 5(1), 2-14.

Stroebe, W., & Strack, F. (2014). The alleged crisis and the illusion of exact replication. Perspectives on Psychological Science, 9, 59–71.

New replication policy at flagship social psychology journal will not be effective

The Journal of Personality and Social Psychology (JPSP) — considered social psychology’s flagship journal — recently announced their new replication policy, which officially states:

Although not a central part of its mission, the Journal of Personality and Social Psychology values replications and encourages submissions that attempt to replicate important findings previously published in social and personality psychology. Major criteria for publication of replication papers include:

    • the theoretical importance of the finding being replicated
    • the statistical power of the replication study or studies
    • the extent to which the methodology, procedure, and materials match those of the original study
    • the number and power of previous replications of the same finding
    • Novelty of theoretical or empirical contribution is not a major criterion, although evidence of moderators of a finding would be a positive factor.

Preference will be given to submissions by researchers other than the authors of the original finding, that present direct rather than conceptual replications, and that include attempts to replicate more than one study of a multi-study original publication. However, papers that do not meet these criteria will be considered as well.

Given my “pre-cognitive abilities”1, we actually submitted a replication paper to JPSP about 2 weeks *prior* to their announcement, reporting the results of two unsuccessful high-powered replication attempts of Correll’s (2008, Exp 2) 1/f noise racial bias effect. Exactly one day after the new replication policy was announced we received this rejection letter:

Your paper stands high on several of [our replication policy] criteria. You worked with the author of the original paper to duplicate materials and procedures as closely as possible, and pre-registered your data collection and analysis plans. Your studies are adequately powered. However, I have concluded that because the impact of the original Correll article has been minimal, an article aimed at replicating his findings does not have the magnitude of conceptual impact that we are looking for in the new replication section. Thus, I will decline to publish this manuscript in JPSP. To assess the impact of the Correll (2008) paper, since it is 6 years old, I turned to citation data. It has been cited 22 times (according to Web of Science) but the vast majority are journals such as Human Movement Science, Ecological Psychology, or Physics Reports, far outside our field. I have not looked at all of the citing articles, of course, but the typical citation of Correll’s work appears to be as an in-passing example of the application of dynamical systems logic. There are only two citations within social psychology. One is Correll’s 2011 JESP follow-up (which itself has been cited only twice, again by journals far outside our field). The second is an Annual Review of Psychology article on gender development (in which again Correll’s 2008 paper is cited in passing as an example of dynamical approaches). I have to conclude that Correll’s paper has had zero substantive impact in social psychology, attracting attention almost exclusively from researchers (mostly outside our field) who cite it as an example application of a specific conceptual and analytic approach. Such citations have little or nothing to do with the substance of the finding that you failed to replicate – the impact of task instructions on the PSD slope. In sum, my decision on your replication manuscript is not based on any deficiencies in your work, but on the virtually complete lack of impact of the original finding within our field.

I responded to the decision letter with the following email:

Thanks for your quick response regarding our replication manuscript (PSP-A-2014-0114). Of course it is not the outcome we had hoped for, however, we respect your decision. That being said, I would like to point out what seems to be a major discrepancy between the official policy for publication of replication papers (theoretical importance of the finding, quality of replication methods, & pre-existing replications of the finding) *and* the primary basis for rejecting our replication paper, which was that the original article had insufficient actual impact in terms of citation count. These two things are distinct and if you will be rejecting papers on the latter criteria, then your official policy should be revised to reflect this fact.

Furthermore, if you do revise your official policy in this way — whereby a major criterion for publishing replication papers is “actual impact” of original article in terms of citation count — this would mean that you could avoid publishing replication papers — no matter how high-quality — for about 85% of published articles in JPSP given the skewed distribution of article citation count whereby the vast majority of articles have minimal actual impact (Seglen, 1992). This kind of strategy would of course be a highly ineffective editorial policy if the goal is to increase the credibility and cumulative nature of empirical findings in JPSP.

To which the editor responded by saying that Corell’s (2008, Exp 2) finding was deemed “important” for methodological reasons and re-iterated that Correll’s research has had “little to no impact within our field.” More importantly, he did not address my two main concerns that their “new replication policy is (1) not well specified and (2) will not be effective in increasing the credibility of empirical findings in JPSP.”2

I responded by saying that they need — at the very least — to revise their official policy to state that they will *only* publish high-quality replication papers of theoretically important findings that have had an *actual* impact in terms of citation count. This of course means that they can avoid publishing replication papers of all recently published JPSP papers *and* the vast majority of JPSP papers that are rarely or never cited, which is simply absurd. Another curious aspect (alluded to by Lorne Campbell) is this: Can an empirical finding actually have an impact on a field if it hasn’t been independently corroborated?

 

1. Just kidding, I unfortunately do not actually have pre-cognitive abilities though it would be great if I did.
2. This is in contrast to replication policies at more reputable journals — such as Psychological Science, Journal of Experimental Social Psychology, Psychonomic Bulletin & Review, and Journal of Research in Personality — that publish high-quality replication papers of *any* findings originally published in their journal. For examples, see here and here.

Unsuccessful replications are beginnings not ends – Part II

In Part I, I argued that unsuccessful replications should more constructively be seen as scientific beginnings rather than ends. As promised, in Part II I will more concretely demonstrate this by organizing all of the available replication information for Schnall et al.’s (2008) studies using an approach being developed at CurateScience.org.

CurateScience.org aims to accelerate the growth of cumulative knowledge by organizing information about replication results and allowing constructive comments by the community of scientists regarding the careful interpretation of replication results. Links to available data, syntax files, and experimental materials will also be organized. The web platform aims to be a one-stop shop to locate, add, and modify such information and also facilitate constructive discussions and new scholarship of published research findings. (The kinds of heated debates currently happening regarding Schnall et al.’s studies that makes science so exciting — well, minus the ad hominem attacks!)

Below is a screenshot of the organized replication results for the Schnall et al. (2008) studies, including links to available data files, forest plot graph of the effect size confidence intervals, and aggregated list of relevant blog posts and tweets.

cs-schnalletal-screenshot

As can be seen, there are actually 4 additional direct replications in addition to Johnson et al.’s (2014) special issue direct replications. As mentioned in Part I, two “successful” direct replications have been reported for Schnall et al.’s Study 1. However, as can readily be seen, these two studies were under-powered (@60%) to detect the original d=-.60 effect size and both effect size CIs include zero. Consequently, it would be inappropriate to characterize these studies as “successful” (the < .05 p-values reported on PsychFileDrawer.org were one-tailed tests). That being said, these studies should not be ignored given they contribute additional evidence that should count toward one’s overall evaluation of the evidence for the claim that cleanliness priming influences moral judgments.

Unsuccessful replications should also be viewed as beginnings given that virtually all replicators make their data publicly available for verification and re-analysis (one of Curate Science’s focus). Hence, any interested researcher can download the data and re-analyze it from a different theoretical perspective and potentially gain new insights into the discrepant results. Data availability also plays an important role in interpreting replication results, especially in the case the results have not been peer-reviewed. That is, one should put more weight into replication results whose conclusions can be verified via re-analysis than replication results that do not have available data.

Organizing replication results in this situation makes it clear that virtually all of the replication efforts have targeted Schnall et al.’s Study 1. Only one direct replication is so far available for Shnall et al.’s Study 2. Though this replication study used a much larger sample and was pre-registered (hence more weight should be given to its results), it is not the case that the final verdict has been spoken. Our confidence in Study 2’s original results should decrease to some extent (assuming the replication results can be reproduced from the raw data), however, more evidence would be needed to further decrease our confidence.

And even in the event of subsequent negative results from high-powered direct replications (for either of Schnall et al.’s studies), it would still be possible that cleanliness priming can influence moral judgments using more accurate instruments or using more advanced designs (e.g., highly-repeated within-person designs). CurateScience.org aims to facilitate constructive discussions and theoretical debates of these kinds to accelerate the growth of cumulative knowledge in psychology/neuroscience (and beyond). Unsuccessful replications are beginnings, not ends.

Unsuccessful replications are beginnings not ends – Part I

Recently, there has been lots of controversy brewing around the so called “replication movement” in psychology. This controversy reached new heights this past week in response to Johnson, Cheung, & Donnellen’s (2014) “failed” replications of Schnall, Benton, & Harvey’s (2008) cleanliness priming on moral judgment finding. Exchanges have spiraled out of control, with unprofessional and overly personal comments uttered. For example, an original author accusing replicators of engaging in “replication bullying” and a “status quo supporter” calling (young) replicators “assholes” and “shameless little bullies”.

In this post, I want to try and bring back the conversation to substantive scientific issues regarding the crucial importance of direct replications and will argue that direct replications should be viewed as constructive rather than destructive. But first a quick clarification regarding the peripheral issue of the term “replication bullying.”

The National Center Against Bullying defines bullying as: “Bullying is when someone with more power repeatedly and intentionally causes hurt or harm to another person who feel helpless to respond.” 

According to this definition, it is very clear that publishing failed replications of original research findings does not come close to meeting the criteria for bullying. Replicators have no intention to harm the original researcher(s), but rather have the intention to add new evidence regarding the robustness of a published finding. This is a normal part of science and is actually the most important feature of the scientific method, which ensures an empirical literature is self-correcting and cumulative. Of course the original authors may claim that their reputation might be harmed by the publication of fair and high-quality replication studies that do not corroborate their original findings. However, this is an unavoidable reality of engaging in scientific endeavors. Science involves highly complex and technically challenging activities. When a new empirical finding is added to the pool of existing ideas, there will always be a risk that competent independent researchers may not be able to corroborate the original findings.

That being said, science entails the careful calibration of beliefs about how our world works. Scientific beliefs are carefully calibrated to the totality of the evidence available for a certain claim. This involves a graded continuum between (1) high confidence in a belief when strong evidence is continually found to support a certain claim and (2) strong doubt in a belief when weak evidence is repeatedly found. In between these two poles, exists a graded continuum where one may have low to moderate confidence in a belief until more high-quality evidence is produced.

For example, in the Schnall et al. situation, Johnson et al.’s have reported two unsuccessful direct replications for each of the two studies originally reported by Schnall et al. However, two *successful* direct replications of Schnall et al.’s Study 1 also have been reported by completely independent researchers.  These “successful” direct replications, however, were both severely under-powered to detect the original effect size. Notwithstanding this limitation, these studies nonetheless should be considered in carefully calibrating one’s belief regarding the claim that cleanliness priming can reduce the severity of moral judgments. Furthermore, future research would need to be executed to understand these discrepant results. Finally, even in the absence of the successful direct replications, Johnson et al.’s two high-quality direct replications does not indicate that the idea that cleanliness priming reduces severity of moral judgments is perpetually wrong. The idea might indeed have some truth to it under a different set of operationalizations and/or in different contexts. The challenge is to identify those operationalizations and contexts whereby the phenomenon yields replicable results. Unsuccessful replications are beginnings, not ends.

In the second part of this post, I will more concretely demonstrate how unsuccessful replications are beginnings by organizing all of the replication information for the Schnall et al.’s (2008) studies using an approach being developed at CurateScience.org.

A simpler and more intuitive publication bias index?

At this past SPSP, Uri Simonsohn gave a talk on new ways of thinking about statistical power. From this new perspective, you first determine how large a sample size you can afford for a particular project. Then, you can determine the minimum effect size that can reliably detected (i.e., 95% power) for that sample size (e.g., d_min = .73 can be reliably detected with n=50/cell). I believe that this approach is a much more productive way of thinking about power for several reasons, one being that it substantially enhances the interpretation of null results. For instance, you can conclude (assuming integrity of methods and measurement instruments) that the effect you’re studying is unlikely to be the size of the minimum effect size reliably detectable for your sample size (or else you would have detect it). That being said, it is still possible the effect exists but is much smaller in magnitude, which would require a much larger sample size to reliably detect.

In this post, I use the core ideas from this new approach to come up with a simpler and more intuitive way of gauging publication bias for extant empirical studies.

The idea is simple. If a study reports an observed effect size smaller than the minimum effect size reliably detectable for the sample size used, then the study likely suffers from publication bias and should be interpreted with caution. The further away the observed effect size is from the minimally detectable effect size, the larger the bias. Let’s look at some concrete examples.

Zhong & Liljenquist’s (2006) Study 1 on the “Macbeth effect” found a d=.53 using n=30/cell. At this sample size, however, only effect sizes as large as d=.95 (or greater) are reliably detectable with 95% power. On the other hand, Tversky & Kahneman’s (1981) Framing effect study found a d=1.13 using n=153/cell. At that sample size, effect sizes as small as d=.41 are reliably detectable. See Table below for other examples:
minimum effect size

The new bias index can be calculated as follows:  minimum effect size - bias-equation

(And note we’d want to calculate a 95% C.I. around the bias estimate, given that bias estimates should be more precise for larger Ns all else being equal.)

To shed more light on the value of this simpler publication bias index, in the near future I will calculate these for studies where replicability information exists and test empirically whether the index predicts lower likelihood of replication.