06.15.17
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[61] Why p-curve excludes ps>.05

In a recent working paper, Carter et al (.pdf) proposed that one can better correct for publication bias by including not just p<.05 results, the way p-curve does, but also p>.05 results [1]. Their paper, currently under review, aimed to provide a comprehensive simulation study that compared a variety of bias-correction methods for meta-analysis.

Although the paper is well written and timely, the advice is problematic. Incorporating non-significant results into a tool designed to correct for publication bias requires one to make assumptions about how difficult it is to publish each possible non-significant result. For example, one has to make assumptions about how much more likely an author is to publish a p=.051 than a p=.076, or a p=.09 in the wrong direction than a p=.19 in the right direction, etc. If the assumptions are even slightly wrong, the tool’s performance becomes disastrous [2]

Assumptions and p>.05s
The desire to include p>.05 results in p-curve type analyses is understandable. Doing so would increase our sample sizes (of studies), rendering our estimates more precise. Moreover, we may be intrinsically interested in learning about studies that did not get to p<.05.

So why didn’t we do that when we developed p-curve? Because we wanted a tool that would work well in the real world.  We developed a good tool, because the perfect tool is unattainable.

While we know that the published literature generally does not discriminate among p<.05 results (e.g., p=.01 is not perceptibly easier to publish than is p=.02), we don’t know how much easier it is to publish some non-significant results rather than others.

The downside of p-curve focusing only on p<.05 is that p-curve can “only” tell us about the (large) subset of published results that are statistically significant. The upside is that p-curve actually works.

All p>.05 are not created equal
 The simulations reported by Carter et al. assume that all p>.05 findings are equally likely to be published: a p=.051 in the right direction is as likely to be published as a p=.051 in the wrong direction. A p=.07 in the right direction is as likely to be published as a p=.97 in the right direction. If this does not sound implausible to you, we recommend re-reading this paragraph.

Intuitively it is easy to see how getting this assumption wrong will introduce bias. “Imagine” that a p=.06 is easier to publish than is a p=.76. A tool that assumes both results are equally likely to be published will be naively impressed when it sees many more p=.06s than p=.76s, and it will fallaciously conclude there is evidential value when there isn’t any.

A calibration
We ran simulations matching one of the setups considered by Carter et al., and assessed what happens if the publishability of p>.05 results deviated from their assumptions (R Code). The black bar in the figure below shows that if their fantastical assumption were true, the tool would do well, producing a false-positive rate of 5%. The other bars show that under some (slightly) more realistic circumstances, false-positives abound.

One must exclude p>.05
It is obviously not true that all p>.05s are equally publishable. But no alternative assumption is plausible. The mechanisms that influence the publication of p>.05 results are too unknowable, complex, and unstable from paper to paper, to allow one to make sensible assumptions or generate reasonable estimates. The probability of publication depends on the research question, on the authors’ and editors’ idiosyncratic beliefs and standards, on how strong other results in the paper are, on how important the finding is for the paper’s thesis, etc.  Moreover, comparing the 2nd and 3rd bar in the graph above, we see that even minor quantitative differences in a face-valid assumption make a huge difference.

P-curve is not perfect. But it makes minor and sensible assumptions, and is robust to realistic deviations from those assumptions. Specifically, it assumes that all p<.05 are equally publishable regardless of what exact p-value they have. This captures how most researchers perceive publication bias to occur (at least in psychology). Its inferences about evidential value are robust to relatively large deviations from this assumption (e.g., if researchers start aiming for p<.045 instead of p<.05, or even p<.035, or even p<.025, p-curve analysis, as implemented in the online app (.htm), will falsely conclude there is evidential value when the null is true, no more than 5% of the time.  See our “Better P-Curves” paper (SSRN)).

Conclusion
With p-curve we can determine whether a set of p<.05 results have evidential value, and what effect we may expect in a direct replication of those studies.  Those are not the only questions you may want to ask. For example, traditional meta-analysis tools ask what is the average effect of all of the studies that one could possibly run (whatever that means; see Colada[33]), not just those you observe. P-curve does not answer that question. Then again, no existing tool does. At least not even remotely accurately.

P-curve tells you “only” this: If I were to run these statistically significant studies again, what should I expect?

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Author feedback.
We shared a draft of this post with Evan Carter, Felix Schönbrodt, Joe Hilgard and Will Gervais. We had an incredibly constructive and valuable discussion, sharing R Code back and forth and jointly editing segments of the post.

We made minor edits after posting responding to readers’ feedback. The original version is archived here .htm.

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Footnotes.

  1. When applying p-curve to estimate effect size, it is extremely similar to following the “one-parameter-selection-model” by Hedges 1984 (.pdf). [↩]
  2. Their paper is nuanced in many sections, but their recommendations are not. For example, they write in the abstract, “we generally recommend that meta-analysis of data in psychology use the three-parameter selection model.” [↩]
05.08.17
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[60] Forthcoming in JPSP: A Non-Diagnostic Audit of Psychological Research

A forthcoming article in the Journal of Personality and Social Psychology has made an effort to characterize changes in the behavior of social and personality researchers over the last decade (.pdf). In this post, we refer to it as “the JPSP article” and to the authors as “the JPSP authors.” The research team, led by Matt Motyl, uses two strategies. In the first, they simply ask a bunch of researchers how they have changed. Fewer dropped dependent variables? More preregistration? The survey is interesting and worth a serious look.

The other strategy they employ is an audit of published research from leading journals in 2003/2004 and again from 2013/2014. The authors select a set of studies and analyze them with a variety of contemporary metrics designed to assess underlying evidence. One of those metrics is p-curve, a tool the three of us developed together (see p-curve.com)  [1]. In a nutshell, p-curve analysis uses the distribution of significant p-values testing the hypotheses of interest in a set of studies to assess the evidential value of the set [2]. We were very interested to see how the JPSP authors had used it.

In any given paper, selecting the test that’s relevant for the hypothesis of interest can be difficult for two reasons. First, sometimes papers simply do not report it [3].  Second, and more commonly, when relevant tests are reported, they are surrounded by lots of other results: e.g., manipulation checks, covariates, and omnibus tests.  Because these analyses do not involve the hypothesis of interest, their results are not relevant for evaluating the evidential value of the hypothesis of interest. But p-curvers often erroneously select them anyway.  To arrive at relevant inferences about something, you have to measure that something, and not measure something else.

As we show below, the JPSP authors too often measured something else. Their results are not diagnostic of the evidential value of the surveyed papers. Selecting irrelevant tests invalidates not only conclusions from p-curve analysis, but from any analysis.

Selecting the right tests
When we first developed p-curve analysis we had some inkling that this would be a serious issue, and so we talked about p-value selection extensively in our paper (see Figure 5, SSRN), user guide (.pdf), and online app instructions (.htm). Unfortunately, authors, and reviewers, are insufficiently attentive to these decisions.

When we review papers using p-curve, about 95% of our review time is spent considering how the p-values were selected. The JPSP authors included 1,800 p-values in their paper, an extraordinary number that we cannot thoroughly review. But an evaluation of even a small number of them makes clear that the results reported in the paper are erroneous. To arrive at a diagnostic result, one would need to go back and verify or correct all 1,800 p-values. One would need to start from scratch.

The JPSP authors posted all the tests they selected (.csv). We first looked at the selection decisions they had rated as “very easy.”  The first decision we checked was wrong. So was the second. Also the third. And the 4th, the 5th, the 6th, the 7th and the 8th.  The ninth was correct.

To convey the intuition for the kinds of selection errors in the JPSP article, and to hopefully prevent other research teams from committing the same mistakes, we will share a few notable examples, categorized by the type of error. This is not an exhaustive list.

Error 1. Selecting the manipulation check
Experimenters often check to make sure that they got the manipulation right before testing its effect on the critical dependent variable. Manipulation checks are not informative about the hypothesis of interest and should not be selected. This is not controversial. For example, the authors of the JPSP article instructed their coders that “manipulation checks should not be counted.” (.pdf)

Unfortunately, the coders did not follow these instructions.

For example, from an original article that manipulated authenticity to find out if it influences subjective well-being, the authors of the JPSP article selected the manipulation check instead of the effect on well being.

Whereas the key test has a familiar p-value of .02, the manipulation check has a supernatural p-value of 10-32. P-curve sees those rather differently.

Error 2. Selecting an omnibus test.
Omnibus tests look at multiple means at once and ask “are any of these means different from any of the other means?” Psychological researchers almost never ask questions like that. Thus omnibus tests are almost never the right test to select in psychological research. The authors of the JPSP article selected about 200 of them.

Here is one example.  An original article examined satisfaction with bin Laden’s death. In particular, it tested whether Americans (vs. non-Americans), would more strongly prefer that bin Laden be killed intentionally rather than accidentally [4].

The results:

This is a textbook attenuated interaction prediction: the effect is bigger here than over there. Which interaction to select is nevertheless ambiguous: Should we collapse Germans and Pakistanis into one non-American bin? Should we include “taken to court”? Should we collapse across all forms of killings or do a separate analysis for each type? Etc. The original authors, therefore, had a large menu of potentially valid analyses to choose from, and thus so did the JPSP authors. But they chose an invalid one instead. They selected the F(10,2790)=31.41 omnibus test:

The omnibus test they selected does not test the interaction of interest. It is irrelevant for the original paper, and so it is irrelevant to use to judge the evidential value of that paper. If the original authors were wrong (so Americans and non-Americans actually felt the same way about accidental vs intentional bin Laden’s death), the omnibus test would still be significant if Pakistanis were particularly dissatisfied with the British killing bin Laden, or if the smallest American vs non-American difference was for “killed in airstrike” and the largest for “killed by British”. And so on [5].

Update 2017 12 01. We were contacted by the authors of this original article concerned that readers of this post may incorrectly conclude they themselves interpreted the omnibus test as directly testing their  hypothesis of interest. They did not, they only included the omnibus test in their paper because it is standard practice to also report it. They followed it up with planned contrasts that more directly test their hypothesis.

Error 3. Selecting the non-focal test
Often researchers interested in interactions first report a simple effect, but only the interaction tests the hypothesis of interest. First the set-up:

So there are two groups of people and for each the researchers measure pro-white bias. The comparison of the two groups is central. But, since that comparison is not the only one reported, there is room for p-curver error. The results:


Three p-values. One shows the presence of a pro-white bias in the control condition, the next shows the presence of a pro-white bias in the experimental condition, and the third compares the experimental condition to the control condition. The third one is clearly the critical test for the researchers, but the JPSP authors pulled the first one. Again, the difference is meaningful: p = .048 vs. p = .00001.

Note: we found many additional striking and consequential errors.  Describing them in easy-to-understand ways is time consuming (about 15 minutes each) but we prepared three more in a powerpoint (.pptx)

Conclusion
On the one hand, it is clear that the JPSP authors took this task very seriously. On the other hand, it is just as clear that they made many meaningful errors, and that the review process fell short of what we should expect from JPSP.

The JPSP authors draw conclusions about the status of social psychological and personality research. We are in no position to say whether their conclusions are right or wrong. But neither are they.

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Author feedback.
We shared a draft of this post on May 3rd with Matt Motyl (.htm) and Linda Skitka (.htm); we exchanged several emails, but -despite asking several times- did not receive any feedback on the post. They did draft a response, but they declined to share it with us before posting it, and chose not to post it here.

Also, just before emailing Matt about our post last week, he coincidentally emailed us. He indicated that various people had identified (different) errors in their use of p-curve analysis in their paper and asked us to help correct them. Since Matt indicated being interested in fixing such errors before the paper is officially published in JPSP, we do not discuss them here (but may do so in a future post).

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Footnotes.

  1. Furthermore, and for full disclosure, Leif is part of a project that has similar goals (https://osf.io/ngdka/). [↩]
  2. Or, if you prefer a slightly larger nutshell: P-curve is a tool which looks at the distribution of critical and significant p-values and makes an assessment of underlying evidential value. With a true null hypothesis, p-values will be distributed uniformly between 0 and .05. When the null is false (i.e., an alternative is true) then p-values will be distributed with right-skew (i.e., more 0<p<.01 than .01<p<.02 etc.). P-curve analysis involves examining the skewness of a distribution of observed p-values in order to draw inferences about the underlying evidential value: more right skewed means more evidential value; and evidential value, in turn, implies the expectation that direct replications would succeed. [↩]
  3. For example, papers often make predictions about interactions but never actually test the interaction. Nieuwenhuis et al find that of 157 papers they looked at testing interactions, only half(!) reported an interaction .pdf [↩]
  4. Here is the relevant passage from the original paper, it involves two hypothesis, the second is emphasized more and mentioned in the abstract, so we focus on it here:

    [↩]

  5. A second example of choosing the omnibus test is worth a mention, if only in a footnote. It comes from a paper by alleged fabricateur Larry Sanna. Here is a print-screen of footnote 5 in that paper. The highlighted omnibus text is the only result selected from this study.  The original authors here are very clearly stating that this is not their hypothesis of interest:
    [↩]

04.12.17
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[59] PET-PEESE Is Not Like Homeopathy

PET-PEESE is a meta-analytical tool that seeks to correct for publication bias. In a footnote in my previous post (.htm), I referred to is as the homeopathy of meta-analysis. That was unfair and inaccurate.

Unfair because, in the style of our President, I just called PET-PEESE a name instead of describing what I believed was wrong with it. I deviated from one of my rules for ‘menschplaining’ (.htm): “Don’t label, describe.”

Inaccurate because skeptics of homeopathy merely propose that it is ineffective, not harmful. But my argument is not that PET-PEESE is merely ineffective, I believe it is also harmful. It doesn’t just fail to correct for publication bias, it adds substantial bias where none exists.

note: A few hours after this blog went live, James Pustejovsky (.htm) identified a typo in the R Code which affects some results. I have already updated the code and figures below. (I archived the original post: .htm).

PET-PEESE in a NUT-SHELL
Tom Stanley (.htm), later joined by Hristos Doucouliagos, developed PET-PEESE in various papers that have each accumulated 100-400 Google cites (.pdf | .pdf). The procedure consists of running a meta-regression: a regression in which studies are the unit of analysis, with effect size as the dependent variable and its variance as the key predictor [1]. The clever insight by Stanley & Doucouliagos is that the intercept of this regression is the effect we would expect in the absence of noise, thus, our estimate of the -publication bias corrected- true effect [2].

PET-PEESE in Psychology
PET-PEESE was developed with the meta-analysis of economics papers in mind (regressions with non-standardized effects). It is possible that some of the problems identified here, considering meta-analyses of standardized effect sizes, Cohen’s d, do not extend to such settings [3].

Psychologists have started using PET-PEESE recently. For instance, in meta-analyses about religious primes (.pdf), working memory training (.htm), and personality of computer wizzes (.htm). Probably the most famous example is Carter et al.’s meta-analysis of ego depletion, published in JEP:G (.pdf).

In this post I share simulation results that suggest we should not treat PET-PEESE estimates, at least of psychological research, very seriously. It arrives at wholly invalid estimates under too many plausible circumstances. Statistical tools need to be generally valid, or at least valid under predictable circumstances. PET-PEESE, to my understanding, is neither [4].

Results
Let’s start with a baseline case for which PET-PEESE does OK: there is no publication bias, every study examines the exact same effect size, and sample sizes are distributed uniformly between n=12 and n=120 per cell. Below we see that when the true effect is d=0, PET-PEESE correctly estimates it as d̂=0, and as d gets larger, d̂ gets larger (R Code).

About 2 years ago, Will Gervais evaluated PET-PEESE in a thorough blog post (.htm) (which I have cited in papers a few times). He found that in the presence of publication bias PET-PEESE did not perform well, but that in the absence of publication bias it at least did not make things worse. The simulations depicted above are not that different from his.

Recently, however, and by happenstance, I realized that Gervais got lucky with the simulations (or I guess PET-PEESE got lucky) [5]. If we deviate slightly from some  of the specifics of the ideal scenario in any of several directions, PET-PEESE no longer performs well even in the absence of publication bias.

For example, imagine that sample sizes don’t go all the way to up n=120 per cell; instead, they go up to only n=50 per cell (as is commonly the case with lab studies) [6]:

A more surprisingly consequential assumption involves the symmetry of sample sizes across studies. Whether there are more small than large n studies, or vice versa, PET PEESE’s performance suffers quite a bit. For example, if sample sizes look like this:

then PET-PEESE looks like this:


Micro-appendix
1) It looks worse if there are more big n than small n studies (.png).
2) Even if studies have n=50 to n=120, there is noticeable bias if n is skewed across studies (.png)

It’s likely, I believe, for real meta-analyses to have skewed n distributions. e.g., this is what it looked like in that ego depletion paper (note: it plots total N, not per-cell):

So far we have assumed all studies have the exact same effect size, say all studies in the d=.4 bin are exactly d=.4. In real life different studies have different effects. For example, a meta-analysis of ego-depletion may include studies with stronger and weaker manipulations that lead to, say, d=.5 and d=.3 respectively. On average the effect may be d=.4, but it moves around. Let’s see what happens if across studies the effect size has a standard deviation of SD=.2.

Micro-appendix
3) If big n studies are more common than small ns: .png
4) If n=12 to n=120 instead of just n=50, .png

Most troubling scenario
Finally, here is what happens when there is publication bias (only observe p<.05)


Micro-appendix
With publication bias,
5) If n goes up to n=120: .png
6) If n is uniform n=12 to n=50 .png
7) If d is homogeneous, sd(d)=0 .png

It does not seem prudent to rely on PET-PEESE, in any way, for analyzing psychological research. It’s an invalid tool under too many scenarios.

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Author feedback.
Our policy is to share early drafts of our post with authors whose work we discuss. I shared this post with the creators of PET-PEESE, and also with others familiar with it: Will Gervais, Daniel Lakens, Joe Hilgard, Evan Carter, Mike McCullough and Bob Reed. Their feedback helped me identify an important error in my R Code, avoid some statements that seemed unfair, and become aware of the recent SPPS paper by Tom Stanley (see footnote 4). During this process I also learned, to my dismay, that people seem to believe -incorrectly- that p-curve is invalidated under heterogeneity of effect size. A future post will discuss this issue, impatient readers can check out our p-curve papers, especially Figure 1 in our first paper (here) and Figure S2 in our second (here), which already address it; but evidently insufficiently compellingly.

Last but not least, everyone I contacted was offered an opportunity to reply within this post. Both Tom Stanley (.pdf), and Joe Hilgard (.pdf) did.

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Footnotes.

  1. Actually, that’s just PEESE; PET uses the standard error as the predictor [↩]
  2. With PET-PEESE one runs both regressions. If PET is significant, one uses PEESE; if PET is not significant, one uses PET (!). [↩]
  3. Though a working paper by Alinaghi and Reed suggests PET-PEESE performs poorly there as well .pdf [↩]
  4. I shared an early draft of this paper with various peers, including Daniel Lakens and Stanley himself. They both pointed me to a recent paper in SPPS by Stanley (.pdf). It identifies conditions under which PET-PEESE gives bad results. The problems I identify here are different, and much more general than those identified there. Moreover, results presented here seem to directly contradict the conclusions from the SPPS paper. For instance, Stanley proposes that if the observed heterogeneity in studies is I2<80% we should trust PET-PEESE, and yet, in none of the simulations I present here, with utterly invalid results, is I2>80%; thus I would suggest to readers to not follow that advice. Stanley (.pdf) also points out that when there are 20 or fewer studies PET-PEESE should not be used; all my simulations assume 100 studies, and the results do not improve with a smaller sample of studies. [↩]
  5. In particular, when preparing Colada[58] I simulated meta-analyses where, instead of choosing sample size at random, as the funnel-plot assumes, researchers choose larger samples to study smaller effects. I found truly spectacularly poor performance by PET-PEESE, much worse that trim-and-fill. Thinking about it, I realized that if researchers do any sort of power calculations, even intuitive or based on experience, then a symmetric distributions of effect size leads to an asymmetric distributions of sample size. See this illustrative figure (R Code):

    So it seemed worth checking if asymmetry alone, even if researchers were to set sample size at random, led to worse performance for PET-PEESE. And it did. [↩]
  6. e.g., using d.f. in t-test from scraped studies as data, back in 2010, the median n in Psych Science was about 18, and around 85% of studies were n<50 [↩]
03.21.17
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[58] The Funnel Plot is Invalid Because of This Crazy Assumption: r(n,d)=0

The funnel plot is a beloved meta-analysis tool. It is typically used to answer the question of whether a set of studies exhibits publication bias. That’s a bad question because we always know the answer: it is “obviously yes.” Some researchers publish some null findings, but nobody publishes them all. It is also a bad question because the answer is inconsequential (see Colada[55]). But the focus of this post is that the funnel plot gives an invalid answer to that question. The funnel plot is a valid tool only if all researchers set sample size randomly [1].

What is the funnel plot?
The funnel plot is a scatter-plot with individual studies as dots. A study’s effect size is represented on the x-axis, and its precision is represented on the y-axis. For example, the plot below, from  a 2014 Psych Science paper (.pdf), shows a subset of studies on the cognitive advantage of bilingualism.

The key question people ask when staring at funnel plots is: Is this thing symmetric?

If we observed all studies (i.e., if there was no publication bias), then we would expect the plot to be symmetric because studies with noisier estimates (those lower on the y-axis) should spread symmetrically on either side of the more precise estimates above them. Publication bias kills the symmetry because researchers who preferentially publish significant results will be more likely to drop the imprecisely estimated effects that are close to zero (because they are p > .05), but not those far from zero (because they are p < .05). Thus, the dots in the bottom left (but not in the bottom right) will be missing.

The authors of this 2014 Psych Science paper concluded that publication bias is present in this literature in part based of how asymmetric the above funnel plot is (and in part on their analysis of publication outcomes of conference abstracts).

The assumption
The problem is that the predicted symmetry hinges on an assumption about how sample size is set: that there is no relationship between the effect size being studied, d, and the sample size used to study it, n. Thus, it hinges on the assumption that r(n, d) = 0.

The assumption is false if researchers use larger samples to investigate effects that are harder to detect, for example, if they increase sample size when they switch from measuring an easier-to-influence attitude to a more difficult-to-influence behavior. It is also false if researchers simply adjust sample size of future studies based on how compelling the results were in past studies. If this happens, then r(n,d)<0 [2].

Returning to the bilingualism example, that funnel plot we saw above includes quite different studies; some studied how well young adults play Simon, others at what age people got Alzheimer’s. The funnel plot above is diagnostic of publication bias only if the sample sizes researchers use to study these disparate outcomes are in no way correlated with effect size. If more difficult-to-detect effects lead to bigger samples, the funnel plot is no longer diagnostic [3].

A calibration
To get a quantitative sense of how serious the problem can be, I run some simulations (R Code).

I generated 100 studies, each with a true effect size drawn from d~N(.6,.15). Researchers don’t know the true effect size, but they guess it; I assume their guesses correlate .6 with the truth, so r(d,dguess)=.6.  Using dguess they set n for 80% power. No publication bias, all studies are reported [4].

The result: a massively asymmetric funnel plot.

That’s just one simulated meta-analysis; here is an image with 100 of them: (.png).

That funnel plot asymmetry above does not tell us “There is publication bias.”
That funnel plot asymmetry above tells us “These researchers are putting some thought into their sample sizes.”

Wait, what about trim and fill?
If you know your meta-analysis tools, you know the most famous tool to correct for publication bias is trim-and-fill, a technique that is entirely dependent on the funnel plot.  In particular, it deletes real studies (trims) and adds fabricated ones (fills), to force the funnel plot to be symmetric. Predictably, it gets it wrong. For the simulations above, where mean(d)=.6, trim-and-fill incorrectly “corrects” the point estimate downward by over 20%, to d̂=.46, because it forces symmetry onto a literature that should not have it (see R Code) [5].

Bottom line.
Stop using funnel plots to diagnose publication bias.
And stop using trim-and-fill and other procedures that rely on funnel plots to correct for publication bias.
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Authors feedback.
Our policy is to share early drafts of our post with authors whose work we discuss. This post is not about the bilingual meta-analysis paper, but it did rely on it, so I contacted the first author, Angela De Bruin. She suggested some valuable clarifications regarding her work that I attempted to incorporate (she also indicated to be interested in running p-curve analysis on follow-up work she is pursuing).

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Footnotes.

  1. By “randomly” I mean orthogonally to true effect size, so that the expected correlation between sample and effect size being zero: r(n,d)=0. [↩]
  2. The problem that asymmetric funnel plots may arise from r(d,n)<0 is mentioned in some methods papers (see e.g., Lau et al. .pdf), but is usually ignored by funnel plot users. Perhaps in part because the problem is described as a theoretical possibility, a caveat; but it is is a virtual certainty, a deal-breaker. It also doesn’t help that so many sources that explain funnel plots don’t disclose this problem, e.g., the Cochrane handbook for meta-analysis .htm. [↩]
  3. Causality can also go the other way: Given the restriction of a smaller sample, researchers may measure more obviously impacted variables. [↩]
  4. To give you a sense of what assuming r(d,dguess)=.6 implies for researchers ability to figure out the sample size they need; for the simulations described here, researchers would set sample size that’s on average off by 38%, for example, the researcher needs n=100, but she runs n=138, or runs n=62, so not super accurate R Code. [↩]
  5. This post was modified on April 7th, and October 2nd, 2017; you can see an archived copy of the original version here [↩]
02.23.17
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[57] Interactions in Logit Regressions: Why Positive May Mean Negative

Of all economics papers published this century, the 10th most cited appeared in Economics Letters , a journal with an impact factor of 0.5.  It makes an inconvenient and counterintuitive point: the sign of the estimate (b̂) of an interaction in a logit/probit regression, need not correspond to the sign of its effect on the dependent variable (Ai & Norton 2003, .pdf; 1467 cites).

That is to say, if you run a logit regression like y=logit(b1x1+b2x2+b3x1x2), and get b̂3= .5, a positive interaction estimate, it is possible (and quite likely) that for many xs, the impact of the interaction on the dependent variable is negative; that is, that as x1 gets larger, the impact of x2 on y gets smaller.

This post provides an intuition for that reversal, and discusses when it actually matters.

side note: Many economists run “linear probability models” (OLS) instead of logits, to avoid this problem. But that does not fix this problem, it just hides it. I may write about that in a future post.

Buying a house (no math)
Let’s say your decision to buy a house depends on two independent factors: (i) how much you like it (ii) how good an investment it is.

Unbounded scale. If the house decision were on an unbounded scale, say how much to pay for it, liking and investment value would remain independent. If you like the house enough to pay $200k, and in addition it would give you $50k in profits, you’d pay $250k; if the profits were $80k instead of $50k, then pay $280k. Two main effects, no interaction [1].

Bounded scale. Now consider, instead of $ paid, measuring how probable it is that you buy the house; a bounded dependent variable (0-1).  Imagine you love the house (Point C in figure below). Given that enthusiasm, a small increase or drop in how good an investment it is, doesn’t affect the probability much. If you felt lukewarm, in contrast (Point B), a moderate increase in the investment quality could make a difference. And in Point A, moderate changes again don’t matter much.

Key intuition: when the dependent variable is bounded [2], the impact of every independent variable moves it closer/further from that bound, and hence, impacts how flat the curve is, how sensitive the dependent variable it is to changes in any other variable. Every variable, then, has an interactive effect on all variables, even if they are not meaningfully related to one another and even if interaction effects are not included in the regression equation.

Mechanical vs conceptual interactions
I call interactions that arise from the non-linearity of the model, mechanical interactions, and those that arise from variables actually influencing each other, conceptual interactions.

In life, most conceptual interactions are zero: how much you like the color of the kitchen in a house does not affect how much you care about roomy closets, the natural light in the living room, or the age of the AC system. But, in logit regressions, EVERY mechanical interaction is ≠0; if you love the kitchen enough that you really want to buy the house, you are far to the right in the figure above and so all other attributes now matter less: closets, AC system and natural light all now have less detectable effects on your decision.

In a logit regression, the b̂s one estimates, only capture conceptual interactions. When one computes “marginal effects”, when one goes beyond the b̂ to ask how much the dependent variable changes as we change a predictor, one adds the mechanical interaction effect.

Ai and Norton’s point, then, is that the coefficient may be positive, b̂>0, conceptual interaction positive, but the marginal effect negative, conceptual+mechanical negative.

Let’s take this to logit land
Let
y: probability of buying the house
x1: how much you like it
x2: how good an investment it is

and,
y= logit(b1x1+b2x2)  [3]
(note: there is no interaction in the true model, no x1x2 term)

Below I plot that true model, y on x2, keeping x1 constant at x1=0 (R Code for all plots in post).


We are interested in the interaction of x1 with x2. On how x2 affects the impact of x1 on y. Let’s add a new line to the figure, keeping x1 fixed at x1=1 instead of x1=0.


For any given investment value, say x2=0, you are more likely to buy the house if you like it more (dashed red vs solid black line). The vertical distance between lines is the impact of x1=1 vs x1=0; one can already see that around the extremes the gap is smaller, so the effect of x1 gets smaller when x2 is very big or very small.

Below I add arrows that quantify the vertical gaps at specific x2 values. For example, when x2=-2, going from x1=0 to x1=1 increases the probability of purchase by 15%, and by 23% when x2=-1 [4]

The difference across arrows captures how the impact of x1 changes as we change x2; the interaction. The bottom chart, under the brackets shows the results.  Recall there is no conceptual interaction here, model is y=x1+x2, so those interactions, +.08 and -.08 respectively, are purely mechanical.

Now: the sign reversal
So far we assumed x1 and x2 were not conceptually related. The figure below shows what happens when they are: y=logit(x1+x2+0.25x1x2). Despite the conceptual interaction being b=.25 > 0, the total effect of the interaction is negative for high values of x2 (e.g., from x2=1 to x2=2, it is -.08); the mechanical interaction dominates.


What to do about this?
Ai & Norton propose not focusing on point estimates at all, not focusing on b̂3=.25. To instead compute how much the dependent variable changes with a change of the underlying variables, the marginal effect of the interaction, the one that combines conceptual and mechanical. To do that for every data-point, and reporting the average.

In another Econ Letters paper, Greene (2010; .pdf) [5] argues averaging the interaction is kind of meaningless. He has a point, ask yourself how informative it is to tell a reader that the average interaction effect depicted above, +.11 and -.08, is +.015. He suggests plotting the marginal effect for every value instead.

But, such graphs will combine conceptual and mechanical interactions. Do we actually want to do that? It depends on whether we have a basic-research or applied-research question.

What is the research question?
Imagine a researcher examining the benefits of text-messaging parents of students who miss a homework and that the researcher is interested on whether messages are less beneficial for high GPA student (so on the interaction: message*GPA).

An applied research question may be:

How likely is a student to get an A in this class if we text message his parents when missing a homework?”

For that question, yes, we need to include the mechanical interaction to be accurate. If high GPA students were going to get an A anyway, then the text-message will not increase the probability for them. The ceiling effect is real and should be taken into account. So we need the marginal effect.

A (slightly more) basic-research question may be:

How likely is a student to get more academically involved in this class if we text message his parents when missing a homework?

Here grades are just a proxy, a proxy for involvement; if high GPA students were getting an A anyway, but thanks to the text-message will become more involved, we want to know that. We do not want the marginal effect on grades, we want the conceptual interaction, we want b̂.

In sum: When asking conceptual or basic-research questions, if b̂ and the marginal effects disagree, go with b̂.

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Authors feedback.
Our policy is to contact authors whose work we discuss, asking to suggest changes and reply within our blog if they wish. I shared a draft with Chunrong Ai & Edward Norton. Edward replied indicating he appreciated the post and suggested I tell readers about another article of his, further delving into this issue (.pdf)

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Footnotes.

  1. What really matters is linear vs non-linear scale rather that bounded vs not, but bounded provides the intuition more clearly. [↩]
  2. As mentioned before, the key is non-linear rather than bounded [↩]
  3. the logit model is y=eb1x1+b2x2/(1+e b1x1+b2x2) . [↩]
  4. percentage points, I know, but it’s a pain to write that every time. [↩]
  5. The author of that “Greene” Econ PhD econometrics textbook .htm [↩]
01.03.17
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[56] TWARKing: Test-Weighting After Results are Known

On the last class of the semester I hold a “town-hall” meeting; an open discussion about how to improve the course (content, delivery, grading, etc). I follow-up with a required online poll to “vote” on proposed changes [1].

Grading in my class is old-school. Two tests, each 40%, homeworks 20% (graded mostly on a completion 1/0 scale). The downside of this model is that those who do poorly early on, get demotivated. Also, a bit of bad lack in a test hurts a lot. During the latest town-hall the idea of having multiple quizzes and dropping the worst was popular. One problem with this model is that students can blow off a quiz entirely. After the town-hall I thought of why students loved the drop-1 idea and whether I could capture the same psychological benefit with a smaller pedagogical loss.

I came up with TWARKing: assigning test weights after results are known [2]. With TWARKing, instead of each test counting 40% for every student, whichever test an individual student did better on, gets more weight; so Julie does better in Test 1 than Test 2, then Julie’s test 1 gets 45% and test 2 35%, but Jason did better in Test 2, so Jason’s test 2 gets 45%. [3]. Dropping a quiz becomes a special case of TWARKing: worst gets 0% weight.

It polls well
I expected TWARKing to do well in the online poll but was worried students would fall prey to competition-neglect, so I wrote a long question stacking the deck against TWARKing:
question

f1

70% of student were in favor, only 15% against (N=92, only 3 students did not complete the poll).

The poll is not anonymous, so I looked at how TWARKing attitudes are correlated with actual performance.

f2

Panel A shows that students doing better like TWARking less, but the effect is not as strong as I would have expected. Students liking it 5/5 perform in the bottom 40%, those liking 2/5 are in the top 40%.

Panel B shows that students with more uneven performance do like the TWARKing more, but the effect is small and unimpressive (Spearman’s r=.21:, p=.044).

For Panel C I recomputed the final grades had TWARKing been implemented for this semester and saw how the change in ranking correlated with support of TWARKing. It did not. Maybe it was asking too much for this to work as students did not yet know their Test 2 scores.

My read is that students cannot anticipate if it will help vs. hurt them, and they generally like it all the same.

TWARKing could be pedagogically superior.
Tests serve two main roles: motivating students and measuring performance. I think TWARKing could be better on both fronts.

Better measurement. My tests tend to include insight-type questions: students either nail them or fail them. It is hard to get lucky in my tests, I think, hard to get a high score despite not knowing the material. But, easy, unfortunately, to get unlucky; to get no points on a topic you had a decent understanding of [4].  Giving more weight to the highest test is hence giving more weight to the more accurate of the two tests.  So it could improve the overall validity of the grade.  A student who gets a 90 and a 70 is, I presume, better than one getting 80 in both tests.

This reminded me of what Shugan & Mitra (2009 .pdf) label the “Anna Karenina effect” in their under-appreciated paper (11 Google cites). Their Anna Karenina effect (there are a few; each different from the other), occurs when less favorable outcomes carry less information than more favorable ones; for those situations, measures other than the average, e.g., the max, performs better for out-of-sample prediction. [5]

To get an intuition for this Anna Karenina effect: think about what contains more information, a marathon runner’s best vs worst running time? A researcher’s most vs least cited paper?

Note that one can TWARK within test, weighting the highest scored answer by each student more. I will.

Motivation. After doing very poorly in a test it must be very motivating to feel that if you study hard you can make this bad performance count less. I speculate that with TWARKing underperforming students in Test 1 are less likely to be demotivated for Test 2 (I will test this next semester, but without random assignment…).  TWARKing has the magical psychological property that the gains are very concrete, every single student gets a higher average with TWARKing than without, and they see that; the losses, in contrast, are abstract and unverifiable (you don’t see the students who benefited more than you did, leading to a net-loss in ranking).

Bottom line
Students seem to really like TWARKing.
It may make things better for measurement.
It may improve motivation.

A free happiness boost.

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Footnotes.

  1. Like Brexit, the poll in OID290 is not binding [↩]
  2. Obviously the name is inspired by ‘HARKing’: hypothesizing after results are known.  The similarity to Twerking, in contrast, is unintentional, and, given the sincerity of the topic, probably unfortunate. [↩]
  3. I presume someone already does this , not claiming novelty [↩]
  4. Students can still get lucky if I happen to ask on a topic they prepared better for. [↩]
  5. They provide calibrations with real data in sports, academia and movie ratings. Check the paper out. [↩]
12.17.16
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[55] The file-drawer problem is unfixable, and that’s OK

The “file-drawer problem” consists of researchers not publishing their p>.05 studies (Rosenthal 1979 .pdf).
P-hacking consist of researchers not reporting their p>.05 analyses for a given study.

P-hacking is easy to stop. File-drawering nearly impossible.
Fortunately, while p-hacking is a real problem, file-drawering is not.

Consequences of p-hacking vs file-drawering
With p-hacking it’s easy to get a p<.05 [1].  Run 1 study, p-hack a bit and it will eventually “work”; whether the effect is real or not.  In “False-Positive Psychology” we showed that a bit of p-hacking gets you p<.05 with more than 60% chance (SSRN).

With file-drawering, in contrast, when there is no real effect, only 1 in 20 studies work. It’s hard to be a successful researcher with such low a success rate [2]. It’s also hard to fool oneself the effect of interest is real when 19 in 20 studies fail. There are only so many hidden moderators we can talk ourselves into. Moreover, papers typically have multiple studies. A four-study paper would require file-drawering 76 failed studies. Nuts.

File-drawering entire studies is not really a problem, which is good news, because the solution for the file-drawer is not really a solution [3].

Study registries: The non-solution to the file-drawer problem
Like genitals & generals, study registries & pre-registrations sound similar but mean different things.

A study registry is a public repository where authors report all studies they run. A pre-registration is a document authors create before running one study, to indicate how that given study will be run. Pre-registration intends to solve p-hacking. Study registries intend to solve the file-drawer problem.

Study registries sound great, until you consider what needs to happen for them to make a difference.

How the study registry is supposed to work
You are reading a paper and get to Study 1. It shows X. You put the paper down, visit the registry, search for the set of all other studies examining X or things similar to X (so maybe search by author, then by keyword, then by dependent variable, then by topic, then by manipulation), then decide which subset of the studies you found are actually relevant for the Study 1 in front of you (e.g., actually studying X, with a similarly clean design, competent enough execution, comparable manipulation and dependent variable, etc.). Then you tabulate the results of those studies found in the registry, and use the meta-analytical statistical tool of your choice  to combine those results with the one from the study still sitting in front of you.  Now you may proceed to reading Study 2.

Sorry, I probably made it sound much easier than it actually is. In real life, researchers don’t comply with registries the way they are supposed to. The studies found in the registry almost surely will lack the info you need to ‘correct’ the paper you are reading.  A year after being completed, about 90% of studies registered in ClinicalTrials.gov do not have the results uploaded to the database (NEJM, 2015 .pdf). Even for the subset of trials where posting results is ‘mandatory’  it does not happen (BMJ, 2012 .pdf), and when results are uploaded, they are often incomplete and inconsistent with the results in the published paper (Ann Int Medicine 2014 .pdf). This sounds bad, but in social science it will be way worse; in medicine the registry is legally required, for us it’s voluntary. Our registries would only include the subset of studies some social scientists choose to register (the rest remain in the file-drawer…).

Study registries in social science fall short of fixing an inconsequential problem, the file-drawer, they are burdensome to comply with, and to use.

Pre-registration: the solution to p-hacking
Fixing p-hacking is easy: authors disclose how sample size was set & all measures, conditions, and exclusions (“False Positive Psychology” SSRN). No ambiguity, no p-hacking.

For experiments, the best way to disclose is with pre-registrations.  A pre-registration consists of writing down what one wants to do before one does it. In addition to the disclosure items above, one specifies the hypothesis of interest and focal statistical analysis. The pre-registration is then appended to studies that get written-up (and file-drawered with those that don’t). Its role is to demarcate planned from unplanned analysis. One can still explore, but now readers know one was exploring.

Pre-registrations is an almost perfect fix to p-hacking, and can be extremely easy to comply with and use.

In AsPredicted it takes 5 minutes to create a pre-registration, half a minute to read it (see sample .pdf). If you pre-register and never publish the study, you can keep your AsPredicted private forever (it’s about p-hacking, not the file-drawer). Over 1000 people created AsPredicteds in 2016.

Summary
– The file-drawer is not really a problem, and study registries don’t come close to fixing it.
– P-hacking is a real problem. Easy to create and evaluate pre-registrations all but eliminate it.
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Uri’s note: post was made public by mistake when uploading the 1st draft.  I did not receive feedback from people I was planning to contact and made several edits after posting. Sorry.

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Footnotes.

  1. With p-hacking it also easy to get Bayes Factor >3; see “Posterior Hacking” http://DataColada.org/13. [↩]
  2. it’s actually 1 in 40 since usually we make directional predictions and rely on two-sided tests [↩]
  3. p-curve is a statistical remedy to the file-drawer problem and it does work .pdf [↩]
11.01.16
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[54] The 90x75x50 heuristic: Noisy & Wasteful Sample Sizes In The “Social Science Replication Project”

An impressive team of researchers is engaging in an impressive task: Replicate 21 social science experiments published in Nature and Science in 2010-2015 (.htm).

The task requires making many difficult decisions, including what sample sizes to use. The authors’ current plan is a simple rule: Set n for the replication so that it would have 90% power to detect an effect that’s 75% as large as the original effect size estimate.  If “it fails” (p>.05), try again powering for an effect 50% as big as original.

In this post I examine the statistical properties of this “90-75-50” heuristic, concluding it is probably not the best solution available. It is noisy and wasteful [1].

Noisy n.
It takes a huge sample to precisely estimate effect size (ballpark: n=3000 per cell, see DataColada[20]). Typical experiments, with much smaller ns, provide extremely noisy estimates of effect size; sample size calculations for replications, based on such estimates, are extremely noisy as well.

As a calibration let’s contrast 90-75-50 with the “Small-Telescopes” approach (.pdf), which requires replications to have 2.5 times the original sample size to ensure 80% power to accept the null. Zero noise.

The figure below illustrates. It considers an original study that was powered at 50% with a sample size of 50 per cell. What sample size will that original study recommend for the first replication (powered 90% for 75% of observed effect)? The answer is a wide distribution of sample sizes reflecting the wide distribution of effect size estimates the original could result in [2]. Again, this is the recommendation for replicating the exact same study, with the same true effect and same underlying power; the variance you see for the replication recommendation purely reflects sampling error in the original study (R Code). f1

We can think of this figure as the roulette wheel being used to set the replication’s sample size.

The average sample size recommendations of both procedures are similar: n=125 for the Small Telescopes approach vs. n=133 for 90-75-50. But the heuristic has lots of noise: the standard deviation of its recommendations is 50 observations, more than 1/3 of its average recommendation of 133 [3].

Waste
The 90-75-50 heuristic throws good money after bad, escalating commitment to studies that have already accepted the null.  Consider an original study that is false-positive with n=20. Given the distribution of (p<.05) possible original effect-size estimates, 90-75-50 will on average recommends n=67 per-cell for the first replication, and when that one fails (which it will with 97.5% chance because the original is false-positive), it will run a second replication now with n=150 participants per-cell  (R Code).

From the “Small Telescopes” paper (.pdf) we know that if 2.5 times the original (n=20) were run in the first replication, n=50,  we already would have an 80% chance to accept the null. So in the vast majority of cases, when replicating it with n=67, we will already have accepted the null; why throw another n=150 at it? That dramatic explosion of sample size for false-positive original findings is about the same for any original n, such that:

False-positive original findings lead to replications with about 12 times as many subjects per-cell when relying on 90-75-50. 

If the false-positive original was p-hacked, it’s worse. The original p-value will be close to p=.05, meaning a smaller estimated original effect size and hence even larger replication sample size. For instance, if the false-positive original got p=.049, 90-75-50 will trigger replications with 14 times the original sample size (R Code).

Rejecting the null
So far we have focused on power and wasted observations for accepting the null. What if the null is false? The figure below shows power for rejecting the null. We see that if the original study had even mediocre power, say 40%, the gains of going beyond 2.5 times the original are modest. The Small Telescopes approach provides reasonable power to accept and also to reject the null (R Code).

f3c

Better solution.
Given the purpose (and budget) of this replication effort, the Small-Telescopes recommendation could be increased to 3.5n instead of 2.5n, giving nearly 90% power to accept the null [4].

The Small Telescopes approach requires fewer participants overall than 90-75-50 does, is unaffected by statistical noise, and it paves the way to a much needed “Do we accept the null?” mindset to interpreting ‘failed’ replications.

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Author feedback.
Our policy is to contact authors whose work we discuss, asking to suggest changes and reply within our blog if they wish. I shared a draft with several of the authors behind the Social Science Replication Project and discussed it with a few them. They helped me clarify the depiction of their sample-size selection heuristic, prompted me to drop a discussion I had involving biased power estimates for the replications, and prompted me -indirectly- to add the entire calculations and discussions involving waste that’s included in the post you just read. Their response was prompt and valuable.

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Footnotes.

  1. The data-peeking involved in the 2nd replication inflates false-positives a bit, from 5% to about 7%, but since replications involve directional predictions, if they use two-sided tests, it’s fine. [↩]
  2. The calculations behind the figure work as follows. One begins with the true effect size, the one giving the original sample 50% power. Then one computes how likely each possible significant effect size estimate is, that is, the distribution of possible effect size estimates for the original (this comes straight from the non-central distribution). Then one computes for each effect size estimate, the sample size recommendation for the replication that the 90-75-50 heuristic would result in, that is, one based on an effect 75% as big as the estimate, and since we know how likely each estimate is, we know how likely each recommendation is, and that’s what’s plotted. [↩]
  3. How noisy the 90-75-50 heuristic recommendation is depends primarily on the power of the original study and not the specific sample and effect sizes behind such power. If the original study has 50% power, the SD of the recommendation over the average recommendation is ~37% (e.g., 50/133) whether the original had n=50, n=200 or n=500. If underlying power is 80%, the ratio is ~46% for those same three sample sizes. See Section (5) in the R Code [↩]
  4. Could also do the test half-way, after 1.75n, ending study if already conclusive; using a slightly stricter p-value cutoff to maintain desired false-positive rates; hi there @lakens [↩]
09.30.16
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[53] What I Want Our Field To Prioritize

When I was a sophomore in college, I read a book by Carl Sagan called The Demon-Haunted World. By the time I finished it, I understood the difference between what is scientifically true and what is not. It was not obvious to me at the time: If a hypothesis is true, then you can use it to predict the future. If a hypothesis is false, then you can’t. Replicable findings are true precisely because you can predict that they will replicate. Non-replicable findings are not true precisely because you can’t. Truth is replicability. This lesson changed my life. I decided to try to become a scientist.

Although this lesson inspired me to pursue a career as a psychological scientist, for a long time I didn’t let it affect how I actually pursued that career. For example, during graduate school Leif Nelson and I investigated the hypothesis that people strive for outcomes that resemble their initials. For example, we set out to show that (not: test whether) people with an A or B initial get better grades than people with a C or D initial. After many attempts (we ran many analyses and we ran many studies), we found enough “evidence” for this hypothesis, and we published the findings in Psychological Science. At the time, we believed the findings and this felt like a success. Now we both recognize it as a failure.

The findings in that paper are not true. Yes, if you run the exact analyses we report on our same datasets, you will find significant effects. But they are not true because they would not replicate under specifiable conditions. History is about what happened. Science is about what happens next. And what happens next is that initials don’t affect your grades.

Inspired by discussions with Leif, I eventually (in 2010) reflected on what I was doing for a living, and I finally remembered that at some fundamental level a scientist’s #1 job is to differentiate what is true/replicable from what is not. This simple realization forever changed the way I conduct and evaluate research, and it is the driving force behind my desire for a more replicable science. If you accept this premise, then life as a scientist becomes much easier and more straightforward. A few things naturally follow.

First, it means that replicability is not merely a consideration, but the most important consideration. Of course I also care about whether findings are novel or interesting or important or generalizable, or whether the authors of an experiment are interpreting their findings correctly. But none of those considerations matter if the finding is not replicable. Imagine I claim that eating Funyuns® cures cancer. This hypothesis is novel and interesting and important, but those facts don’t matter if it is untrue. Concerns about replicability must trump all other concerns. If there is no replicability, there is no finding, and if there is no finding, there is no point assessing whether it is novel, interesting, or important. [1] Thus, more than any other attribute, journal editors and reviewers should use attributes that are diagnostic of replicability (e.g., statistical power and p-values) as a basis for rejecting papers. (Thank you, Simine Vazire, for taking steps in this direction at SPPS <.pdf>). [2]

Second, it means that the best way to prevent others from questioning the integrity of your research is to publish findings that you know to be replicable under specifiable conditions. You should be able to predict that if you do exactly X, then you will get Y. Your method section should be a recipe for getting an effect, specifying exactly which ingredients are sufficient to produce it. Of course, the best way to know that your finding replicates is to replicate it yourself (and/or to tie your hands by pre-registering your exact key analysis). This is what I now do (particularly after I obtain a p > .01 result), and I sleep a lot better because of it.

Third, it means that if someone fails to replicate your past work, you have two options. You can either demonstrate that the finding does replicate under specifiable/pre-registered conditions or you can politely tip your cap to the replicators for discovering that one of your published findings is not likely to be true. If you believe that your finding is replicable but don’t have the resources to run the replication, then you can pursue a third option: Specify the exact conditions under which you predict that your effect will emerge. This allows others with more resources to test that prediction. If you can’t specify testable circumstances under which your effect will emerge, then you can’t use your finding to predict the future, and, thus, you can’t say that it is true.

Andrew Meyer and his colleagues recently published several highly powered failures to reliably replicate my and Leif’s finding (.pdf; see Study 13) that disfluent fonts change how people predict sporting events (.pdf; see Table A6). We stand by the central claims of our paper, as we have replicated the main findings many times. But Meyer et al. showed that we should not  – and thus we do not – stand by the findings of Study 13. Their evidence that it doesn’t consistently replicate (20 games; 12,449 participants) is much better than our evidence that it does (2 games; 181 participants), and we can look back on our results and see that they are not convincing (most notably, p = .03). As a result, all we can do is to acknowledge that the finding is unlikely to be true. Meyer et al.’s paper wasn’t happy news, of course, but accepting their results was so much less stressful than mounting a protracted, evidence-less defense of a finding that we are not confident would replicate. Having gone that route before, I can tell you that this one was about a million times less emotionally punishing, in addition to being more scientific. It is a comfort to know that I will no longer defend my own work in that way. I’ll either show you’re wrong, or I’ll acknowledge that you’re right.

Fourth, it means advocating for policies and actions that enhance the replicability of our science. I believe that the #1 job of the peer review process is to assess whether a finding is replicable, and that we can all do this better if we know exactly what the authors did in their study, and if we have access to their materials and data. I also believe that every scientist has a conflict of interest – we almost always want the evidence to come out one way rather than another – and that those conflicts of interest lead even the best of us to analyze our data in a way that makes us more likely to draw our preferred conclusions. I still catch myself p-hacking analyses that I did not pre-register. Thus, I am in favor of policies and actions that make it harder/impossible for us to do that, including incentives for pre-registration, the move toward including exact replications in published papers, and the use of methods for checking that our statistical analyses are accurate and that our results are unlikely to have been p-hacked (e.g., because the study was highly powered).

I am writing all of this because it’s hard to resolve a conflict when you don’t know what the other side wants. I honestly don’t know what those who are resistant to change want, but at least now they know what I want. I want to be in a field that prioritizes replicability over everything else. Maybe those who are resistant to change believe this too, and their resistance is about the means (e.g., public criticism) rather than the ends. Or maybe they don’t believe this, and think that concerns about replicability should take a back seat to something else. It would be helpful for those who are resistant to change to articulate their position. What do you want our field to prioritize, and why?

  1. I sometimes come across the argument that a focus on replicability will increase false-negatives. I don’t think that is true. If a field falsely believes that Funyuns will cure cancer, then the time and money that may have been spent discovering true cures will instead be spent studying the Funyun Hypothesis. True things aren’t discovered when resources are allocated to studying false things. In this way, false-positives cause false-negatives. [↩]
  2. At this point I should mention that although I am an Associate Editor at SPPS, what I write here does not reflect journal policy. [↩]
09.26.16
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[52] Menschplaining: Three Ideas for Civil Criticism

As bloggers, commentators, reviewers, and editors, we often criticize the work of fellow academics. In this post I share three ideas to be more civil and persuasive when doing so.

But first: should we comment publicly in the first place?
One of the best known social psychologist, Susan Fiske (.htm), last week circulated a draft of an invited opinion piece (.pdf), where she called academics who critically discuss published research in social media and blogs a long list of names including ‘self-appointed data police’ [1].

I think data-journalist is a more accurate metaphor than is data-police. Like journalists and unlike police officers, (academic) bloggers don’t have physical nor legal powers, they merely exercise free-speech sharing analyses and non-binding opinions that are valued by the people who choose to read them (in contrast, we are not free to ignore the police). Like journalists’, bloggers’ power hinges on being interesting, right, and persuasive.

Importantly, unlike journalists, most academic bloggers have similar training in the subject matter as the original authors whose work they discuss, and they inhabit their social and professional circles as well.  So bloggers are elite journalists: more qualified and better incentivized to be right [2].

Notorious vs influential
Bloggers and other commentators, as Susan Fiske reminds us, can fall in the temptation of getting more attention by acting out, say using colorful language to make unsubstantiated and vague accusations. But the consequences are internalized.

Acting out ends up hurting commentators more than those commented on. Being loud makes you notorious, not influential (think Ann Coulter). Moreover, when you have a good argument, acting out is counterproductive, it distracts from it.  You become less persuasive. Only those who already agree with you will respond to your writing. Academics who make a living within academia have no incentive to be notorious.

Despite the incentives to be civil, there is certainly room in public discussions for greater civility. If the president of APS had asked me to write a non-peer-reviewed article on this topic, I would have skipped the name-calling and gotten to the following three ideas.

Idea 1. Don’t label, describe
It is tempting to label the arguments we critique, saying about them things like ‘faulty logic,’ ‘invalid analyses,’ ‘unwarranted conclusions.’ These terms sound specific, but are ultimately empty phrases that cannot be evaluated by readers. When we label, all we are really saying is “Listen, I am so upset about this, I am ready to throw some colorful terms around.”

An example from my own (peer-reviewed & published) writing makes me cringe every time:
“Their rebuttal is similarly lacking in diligence. The specific empirical concerns it raised are contradicted by evidence, logic, or both.”
What a douche.

Rather than vague but powerfully sounding labels, “lacking diligence”, “contradicted by evidence,” it is better to describe the rationale for those labels. What additional analyses should have they run, and how do they contradict their conclusions? I should’ve written:
“The rebuttal identifies individual examples that intuitively suggest my analyses were too conservative, but, on the one hand, closer examination shows the examples are not actually conservative, and on the other, the removal of those examples leaves the results unchanged.”

Now readers know what to look for to decide if they agree with me. Labels becomes redundant, we can drop them.

Idea 2. Don’t speculate about motives
We often assume our counterparts have bad intentions. A hidden agenda, an ulterior nefarious motive. They do this because they are powerful, if not then because they are powerless. For instance, I once wrote
“They then, perhaps disingenuously, argued that…” Jerk.

Two problems with speculating about motives. First, it is delusional to think we know why someone did something by just seeing what they did, especially if it is in our interest to believe their intentions are not benign.  We don’t know why people do what they do, and it is too easy to assume they do so for reasons that would make us happier or holier.  Second, intentions are irrelevant. If someone publishes a critique of p-curve because they hate Joe’s, Leif’s and/or my guts, all that matters is if they are right or wrong, so when discussing the critique, all we should focus on is whether it is right or wrong.

Idea 3. Reach out
Probably the single thing that has helped me improve the most in the civility department consists of our policy in this blog: contacting authors whose work we discuss before making things public. It is amazing how much it helps, both after receiving the feedback, addressing things that tick people off that we would have never guessed, and before, anticipating remarks that may be irritating, and dropping them.

I obviously cannot do this as a reviewer or editor, in those cases I still apply Ideas 1 & 2. Also, as a heuristic check on tone, I imagine I am going to dinner with the authors and their parents that night.

Summary.
1) I disagree with the substance of Susan Fiske’s piece. Academics discussing research in blogs and social media are elite data-journalists playing an indispensable role in modern science: disseminating knowledge, detecting and correcting errors, and facilitating open discussions.
2) I object its tone, calling colleagues terrorists, among many other things, increases the notoriety of our writing, but reduces its influence. (It’s also disrespectful).
3) I shared three ideas to improve civility in public discourse: Don’t label, don’t infer motives, and reach out.

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Author feedback.
I shared a draft of this post with Susan Fiske who suggested I make clear the document that circulated was a draft which she will revise before publication. I edited the writing to reflect this.

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Footnotes.

  1. Her piece included the following terms to describe bloggers or their actions: (1) Mob, (2) Online vigilantes, (3) Self-appointed data police, (4) Personal ferocity, (5) crashing people, (6) Unmoderated attacks, (7) Unaccountable bullies, (8) Adversarial viciousness, (9) Methodological terrorists, (10) Dangerous minority, (11) Destructo-critics, (12) They attack the person (oops), (13) Self-appointed critics. [↩]
  2. and less interesting, and worse at writing, and with less exciting social lives, but with more stable jobs. [↩]