[13] Posterior-Hacking

Many believe that while p-hacking invalidates p-values, it does not invalidate Bayesian inference. Many are wrong.

This blog post presents two examples from my new “Posterior-Hacking” (SSRN) paper showing  selective reporting invalidates Bayesian inference as much as it invalidates p-values.

Example 1. Chronological Rejuvenation experiment
In  “False-Positive Psychology” (SSRN), Joe, Leif and I run experiments to demonstrate how easy p-hacking makes it to obtain statistically significant evidence for any effect, no matter how untrue. In Study 2 we “showed” that undergraduates randomly assigned to listen to the song “When I am 64” became 1.4 years younger (p<.05).

We obtained this absurd result by data-peeking, dropping a condition, and cherry-picking a covariate. p-hacking allowed us to fool Mr. p-value. Would it fool Mrs. Posterior also? If we take the selectively reported result and feed it to a Bayesian calculator. What happens?

The figure below shows traditional and Bayesian 95% confidence intervals for the above mentioned 1.4 years-younger chronological rejuvenation effect.  Both point just as strongly (or weakly) toward the absurd effect existing. [1]

f2

When researchers p-hack they also posterior-hack

Example 2. Simulating p-hacks
Many Bayesian advocates propose concluding an experiment suggests an effect exists if the data are at least three times more likely under the alternative than under the null hypothesis. This “Bayes factor>3” approach is philosophically different, and mathematically more complex than computing p-values, but it is in practice extremely similar to simply requiring p< .01 for statistical significance. I hence run simulations assessing how p-hacking facilitates getting p<.01 vs getting Bayes factor>3. [2]

I simulated difference-of-means t-tests p-hacked via data-peeking (getting n=20 per-cell, going to n=30 if necessary), cherry-picking among three dependent variables, dropping a condition, and dropping outliers. See R-code.

f3
Adding 10 observations to samples of size n=20 a researcher can increase her false-positive rate from the nominal 1% to 1.7%. The probability of getting a Bayes factor >3 is a comparable 1.8%. Combined with other forms of p-hacking, the ease with which a false finding is obtained increases multiplicatively. A researcher willing to engage in any of the four forms of p-hacking, has a 20.1% chance of obtaining p<.01, and a 20.8% chance of obtaining a Bayes factor >3.

When a researcher p-hacks, she also Bayes-factor-hacks.

Everyone needs disclosure
Andrew Gelman and colleagues, in their influential Bayesian textbook write:

A naïve student of Bayesian inference might claim that because all inference is conditional on the observed data, it makes no difference how those data were collected, […] the essential flaw in the argument is that a complete definition of ‘the observed data’ should include information on how the observed values arose […]”
(p.203, 2nd edition)

Whether doing traditional or Bayesian statistics, without disclosure, we cannot evaluate evidence.


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  1. The Bayesian confidence interval is the “highest density posterior interval”, computed using Kruschke’s BMLR (html). []
  2. This equivalence is for the default-alternative, see Table 1 in Rouder et al, 2009 (HTML).  []

[12] Preregistration: Not just for the Empiro-zealots

I recently joined a large group of academics in co-authoring a paper looking at how political science, economics, and psychology are working to increase transparency in scientific publications. Psychology is leading, by the way.

Working on that paper (and the figure below) actually changed my mind about something. A couple of years ago, when Joe, Uri, and I wrote False Positive Psychology, we were not really advocates of preregistration (a la clinicaltrials.gov). We saw it as an implausible superstructure of unspecified regulation. Now I am an advocate. What changed?

Transparency in Scientific Reporting Figure

First, let me relate an anecdote originally told by Don Green (and related with more subtlety here). He described watching a research presentation that at one point emphasized a subtle three-way interaction. Don asked, “did you preregister that hypothesis?” and the speaker said “yes.” Don, as he relates it, was amazed. Here was this super complicated pattern of results, but it had all been predicted ahead of time. That is convincing. Then the speaker said, “No. Just kidding.” Don was less amazed.

The gap between those two reactions is the reason I am trying to start preregistering my experiments. I want people to be amazed.

The single most important scientific practice that Uri, Joe, and I have emphasized is disclosure (i.e., the top panel in the figure). Transparently disclose all manipulations, measures, exclusions, and sample size specification. We have been at least mildly persuasive, as a number of journals (e.g., Psychological Science, Management Science) are requiring such reporting.

Meanwhile, as a researcher, transparency creates a rhetorical problem. When I conduct experiments, for example, I typically collect a single measure that I see as the central test of my hypothesis. But, like any curious scientist, I sometimes measure some other stuff in case I can learn a bit more about what is happening. If I report everything, then my confirmatory measure is hard to distinguish from my exploratory measures. As outlined in the figure above, a reader might reasonably think, “Leif is p-hacking.” My only defense is to say, “no, that first measure was the critical one. These other ones were bonus.” When I read things like that I am often imperfectly convinced.

How can Leif the researcher be more convincing to Leif the reader? By saying something like, “The reason you can tell that the first measure was the critical one is because I said that publicly before I ran the study. Here, go take a look. I preregistered it.” (i.e., the left panel of the figure).

Note that this line of thinking is not even vaguely self-righteous. It isn’t pushy. I am not saying, “you have to preregister or else!” Heck, I am not even saying that you should; I am saying that I should. In a world of transparent reporting, I choose preregistration as a way to selfishly show off that I predicted the outcome of my study. I choose to preregister in the hopes that one day someone like Don Green will ask me, and that he will be amazed.

I am new to preregistration, so I am going to be making lots of mistakes. I am not going to wait until I am perfect (it would be a long wait). If you want to join me in trying to add preregistration to your research process, it is easy to get started. Go here, and open an account, set up a page for your project, and when you’re ready, preregister your study. There is even a video to help you out.


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[11] “Exactly”: The Most Famous Framing Effect Is Robust To Precise Wording

In an intriguing new paper, David Mandel suggests that the most famous demonstration of framing effects – Tversky & Kahneman’s (1981) “Asian Disease Problem” – is caused by a linguistic artifact. His paper suggests that eliminating this artifact eliminates, or at least strongly reduces, the framing effect. Does it?

This is the perfect sort of paper for a replication: The original finding is foundational and the criticism is both novel and fundamental. We read Mandel’s paper because we care about the topic, and we replicated it because we cared about the outcome.

The Asian Disease Problem

Imagine that an Asian disease is expected to kill 600 people and you have to decide between two policies designed to combat the disease. The policies can be framed in terms of gains (people being saved) or in terms of losses (people dying).

Tversky and Kahneman found that whereas 72% of people given the gain frame chose Program A’s 200 of 600 certain lives saved, only 22% of people given the loss frame chose Program C’s 400 of 600 certain deaths. This result supports prospect theory: people will take risks to avoid losses but will avoid risks to protect gains.

Just a Linguistic Artifact?

David Mandel argues that when people read “200 people will be saved” or “400 people will die” they interpret it as “at least 200 people will be saved” or “at least 400 people will die”. That small difference in interpretation would switch the finding from irrational to sensible, as the certain option would potentially save more people in the gain frame (>200 of 600 will be saved) than in the loss frame (>400 of 600 will die). Mandel resolves the ambiguity by adding the word “exactly” (“exactly 200 people will be saved”). Because the word “exactly” makes it clear that no more than 200 will be saved, he predicts that including that word will eliminate the framing effect.

In Study 2 (the study most faithful to the original), Mandel used Tversky and Kahneman’s wording and replicated their result (58% chose to save 200 people for certain; 26% chose to kill 400 people for certain). When he added “exactly,” that difference was reduced (59% vs. 43%). [1]

We replicated Mandel’s procedure. We showed mTurk workers the same scenario and asked the same questions. We collected ~2.5 times Mandel’s sample size; Mandel had ~38 per cell and we had ~98 per cell. (Following Mandel, we also included conditions with “at least” as a modifier; here are those results).

Unlike Mandel, we found a strong framing effect even with the use of the word “exactly” (p<.001) (materialsdata):

For completeness, we should report that Mandel emphasized a different dependent variable – a continuous measure of preference. We measured that too and it also failed to replicate his result.

In sum, our replication suggests that Tversky and Kahneman’s (1981) framing effect is not caused by this linguistic artifact.

We Could Have Just Asked Uri

When we told Uri about all this, he told us that he conducts this experiment in his class each year and that he uses the word “exactly” in his materials. The experiment has replicated every single year. For example, in the past two years combined (N=250), he observed that 63% chose to save 200 lives for sure whereas only 25% chose to let 400 die for sure.

David Mandel Responds

As is our policy, we sent a draft of this post to David Mandel to offer him the chance to respond. Please check out David’s response below. We are very thankful he took the time to do this:

I welcome this replication experiment by Joseph Simmons and Leif Nelson. I think we all agree proper replications are important regardless of how the results turn out. They have kindly offered me 150 words to reply, but that would hardly get me started. There are many points to cover, both about the replication and some of the broader issues it sparks. Joe contacted me on the Friday before the post went live with the “unwelcome news” and it’s been a weekend of changed plans, but I wanted to have a reply ready when the post goes live. Here it is on my website [and here it as a pdf]. I hope you read both. Feel free to email me if you have comments. Lastly, Joe invited me to comment on their post, but I haven’t since I cover what I might have otherwise recommended they alter in my reply. Readers can make up their own minds. 151, 152…

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  1. However, compared to the condition with the original wording, this reduction was nonsignificant (p=.293). []

[10] Reviewers are asking for it

Recent past and present
The leading empirical psychology journal, Psychological Science, will begin requiring authors to disclose flexibility in data collection and analysis starting on January of 2014 (see editorial). The leading business school journal, Management Science, implemented a similar policy a few months ago.

Both policies closely mirror the recommendations we made in our 21 Word Solution piece, where we contrasted the level of disclosure in science vs. food (see reprint of Figure 3).

2013-12-07_102828
Our proposed 21 word disclosure statement was:

We report how we determined our sample size, all data exclusions (if any), all manipulations, and all measures in the study.

Etienne Lebel tested an elegant and simple implementation in his PsychDisclosure project. Its success contributed to Psych Science‘s decision to implement disclosure requirements.

Starting Now
When reviewing for journals other than Psych Science and Management Science, what could reviewers do?

On the one hand, as reviewers we simply cannot do our jobs if we do not know fully what happened in the study we are tasked with evaluating.

On the other hand, requiring disclosure from an individual article one is reviewing risks authors taking such requests personally (reviewers are doubting them) and risks revealing our identity as reviewers.

A solution is a uniform disclosure request that large numbers of reviewers request for every paper they review.

Together with Etienne LebelDon Moore, and Brian Nosek we created a standardized request that we and many others have already begun using in all of our reviews. We hope you will start using it too. With many reviewers including it in their referee reports, the community norms will change:

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/project/hadz3]. I include it in every review.


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[9] Titleogy: Some facts about titles

Naming things is fun. Not sure why, but it is. I have collaborated in the naming of people, cats, papers, a blog, its posts, and in coining the term “p-hacking.” All were fun to do. So I thought I would write a Colada on titles.

To add color I collected some data. At the end what I wrote was quite boring, so I killed it, but the facts seemed worth sharing. Here they go, in mostly non-contextualized prose.

Cliché titles
I dislike titles with (unmodified) idioms. The figure below shows how frequent some of them are in the web-of-science archive.
f1
Ironically, the most popular (I found), at 970 papers, is “What’s in a name?” …Lack of originality?

Colonization
A colleague once shared his disapproval of the increase in the use of colons in titles. With this post as an excuse, I used Mozenda to scrape ~30,000 psychology paper titles published across 19 journals over 40 years, and computed the fraction including a colon. “Colleague was Wrong: Title Colonization Has Been Stable at about 63% Since the 1970s.” [1]

That factoid took a couple of hours to generate. Data in hand I figured I should answer more questions. Any sense of coherence in this piece disappears with the next pixel.

Have titles gotten longer over time? 
f2
Yes. At about 1.5 characters per year (or a tweet a century).
note: controlling for journal fixed effects.

Three less obvious questions to ask
Question 1. What are the two highest scoring Scrabble words used in a Psychology title?
f3
Hypnotizability (37 points), is used in several articles it turns out. [2]
Ventriloquized (36 points) only in this paper.

Question 2. What is the most frequent last-word in a Psychology paper title?
(try guessing before reading the next line)

This is probably the right place to let you know the Colada has a Facebook page now 

Winner: 137 titles end with: “Tasks”
Runner up: 70 titles end with “Effect”

Question 3. What’s more commonly used in a Psychology title, “thinking” or “sex”?
Not close.

Sex: 407.
Thinking: 172.

Alright, that’s not totally fair, in psychology sex often refers to gender rather than the activity. Moreover, thinking (172) is, as expected for academic papers, more common than doing (44).
But memory blows sex, thinking, and doing combined out of the water with 2008 instances; one in 15 psychology titles has the word memory in them.

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  1. I treated the Journal of Consumer Research as a psychology journal, a decision involving two debatable assumptions. []
  2. Shane Frederick indicated via email that this is a vast underestimate that ignores tripling of points; Hypnotizability could get you 729 points . []

[8] Adventures in the Assessment of Animal Speed and Morality

Animal Virtue Figure 1
In surveys, most people answer most questions. That is true regardless of whether or not questions are coherently constructed and reasonably articulated. That means that absurd questions still receive answers, and in part because humans are similar to one another, those answers can even look peculiarly consistent. I asked an absurd question and was rewarded with an entertaining answer.

Some years ago, with Tom Meyvis, I tried to develop a manipulation to create an association between speed and virtue. Our spartan publication history on the topic testifies to our (lack of) success. That doesn’t mean that the pilot data weren’t interesting for a different reason.

Participants saw a sequence of 20 animal photographs and rated each on one of two bipolar dimensions: speed or goodness. The former is straightforward. The latter could be best construed as an evaluation of moral worth. That is an absurd question. What sorts of answers did we receive?
Animal Virtue Figure 2
My Top 5 observations:

1. The Tortoise is the most moral animal. I anticipated more class-profiling, and a resulting ingroup bias for mammalia. Nope. Perhaps researchers should try an implicit measure?*

2. Aquatic race featuring: Jellyfish vs. Starfish vs. Walrus. Who wins? People give the jellyfish the edge. The starfish has no chance.

3. Nature documentaries frequently bandy about facts like, “hippopotami kill more people every year than heart disease.” My respondents overlooked that; Hippos are more moral than sloths (which nature documentaries never mention for their killing ability).

4. The orangutan is not just a mammal or just a primate, it is a great ape. Huge opportunity for some ingroup favoritism. Instead people favor the cheetah, walrus, and hippo (amongst others). Explain that.

5. Most animals are good. Our scale had a meaningful midpoint, yet all but three animals are above it. Who is bad? Hyena, Barracuda, and Jellyfish. The Jellyfish is worst. And deceptively fast. Perhaps a researcher could prime people with jellyfish and see if they cheat more on that matrices task?**

Perhaps some absurd questions have correct answers? I asked a pair of experts. Pieter Thomas Jefferson Johnson is an ecologist possibly best known for solving a major scientific problem before he was old enough to drink. Michael Jennions is a world renowned evolutionary biologist, known for many things, including this video (the link alone makes this post worthwhile). I asked them to rank the 20 animals for speed and morality. Their speed ratings are similar to each other (r = .91) and the novices (r = .87). Morality was trickier. Both said that any response would be random, or as Piet said, “I would probably tie them all in ranking”. But responses aren’t quite random. Michael rated based on the complexity of the central nervous system (complex = evil), whereas Pieter used “trophic level, followed by an inverse body mass index”. Despite very different approaches, they are mildly correlated with each other (r = .29). Experts and novices all agree on the virtue of the Tortoise, but Michael and Piet are just as fond of the lowly snail.
Animal Virtue Figure 3
*No they shouldn’t.

**Don’t run that study. I mean it.

[7] Forthcoming in the American Economic Review: A Misdiagnosed Failure-to-Replicate

In the paper “One Swallow Doesn’t Make A Summer: New Evidence on Anchoring Effects”, forthcoming in the AER, Maniadis, Tufano and List attempted to replicate a classic study in economics. The results were entirely consistent with the original and yet they interpreted them as a “failure to replicate.” What went wrong?

This post answers that question succinctly; our new paper has additional analyses.

Original results
In an article with >600 citations, Ariely, Loewenstein, and Prelec (2003) showed that people presented with high anchors (“Would you pay $70 for a box of chocolates?”) end up paying more than people presented with low anchors (“Would you pay $20 for a box of chocolates?”). They found this effect in five studies, but the AER replication reran only Study 2. In that study, participants gave their asking prices for aversive sounds that were 10, 30, or 60 seconds long, after a high (50¢), low (10¢), or no anchor.

Replication results

comparing only the 10-cent and 50-cent anchor conditions, we find an effect size equal to 28.57 percent [the percentage difference between valuations], about half of what ALP found. The p-value […] was equal to 0.253” (p. 8).

So their evidence is unable to rule out the possibility that anchoring is a zero effect. But that is only part of the story. Does their evidence also rule out a sizable anchoring effect? It does not. Their evidence is consistent with an effect much larger than the original.

Fig1 Anchoring post

Those calculations use Maniadis et al.’s definition of effect size: % difference in valuations (as quoted above). An alternative is to divide the differences of means by the standard deviation (Cohen’s d). Using this metric the Replication’s effect size is more markedly different from the Original’s, d=.94 vs. d=.26 . However, the 95% confidence interval for the Replication includes effects as big as d=.64, midway between medium and large effects. Whether we examine Maniadis et al.’s operationalization of effect size, then, or Cohen’s d, we arrive at the same conclusion: the Replication is too noisy to distinguish between a nonexistent and a sizable anchoring effect.

Why is the Replication so imprecise?
In addition to having 12% fewer participants, nearly half of all valuations are ≤10¢. Even if anchoring had a large percentage effect, one that doubles WTA from 3¢ to 6¢, the tendency of participants to round both to 5¢ makes it undetectable. And there is the floor effect: valuations so close to $0 cannot drop. One way around this problem is to do something economists do all the time: Express the effect size of one variable (How big is the impact of X on Z?) relative to the effect size of another (it is half the effect of Y on Z). Figure 2 shows that, in cents, both the effect of anchoring and duration is smaller in the replication, and that the relative effect of anchoring is comparable across studies. Fig2 Anchoring post

p-curve
The original paper had five studies, four were p<.01, the fifth p<.02. When we submit these p-values to p-curve we can empirically examine the fear expressed by the replicators that the original finding is false-positive. The results strongly reject this possibility; selective reporting is an unlikely explanation for the original paper, p<.0001.

Some successful replications
Every year Uri runs a replication of Ariely et al.’s Study 1 in his class. In an online survey at the beginning of the semester, students write down the last two digits of their social-security-number, indicate if they would pay that amount for something (this semester it was for a ticket to watch Jerry Seinfeld live on campus), and then indicate the most they would pay. Figure 3 has this year’s data:

Fig3 Anchoring post

We recently learned that SangSuk Yoon, Nathan Fong and Angelika Dimoka successfully replicated Ariely et al.’s Study 1 with real decisions (in contrast to this paper).

Concluding remark
We are not vouching for the universal replicability of Ariely et al here. It is not difficult to imagine moderators (beyond floor effects) that attenuate anchoring. We are arguing that the forthcoming “failure-to-replicate” anchoring in the AER is no such thing.

note: When we discuss others’ work at DataColada we ask them for feedback and offer them space to comment within the original post. Maniadis, Tufano, and List provided feedback only for our paper and did not send us comments to post here.


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[6] Samples Can’t Be Too Large

Reviewers, and even associate editors, sometimes criticize studies for being “overpowered” – that is, for having sample sizes that are too large. (Recently, the between-subjects sample sizes under attack were about 50-60 per cell, just a little larger than you need to have an 80% chance to detect that men weigh more than women).

This criticism never makes sense.

The rationale for it is something like this: “With such large sample sizes, even trivial effect sizes will be significant. Thus, the effect must be trivial (and we don’t care about trivial effect sizes).”

But if this is the rationale, then the criticism is ultimately targeting the effect size rather than the sample size.  A person concerned that an effect “might” be trivial because it is significant with a large sample can simply compute the effect size, and then judge whether it is trivial.

(As an aside: Assume you want an 80% chance to detect a between-subjects effect. You need about 6,000 per cell for a “trivial” effect, say d=.05, and still about 250 per cell for a meaningful “small” effect, say d=.25. We don’t need to worry that studies with 60 per cell will make trivial effects be significant).

It is OK to criticize a study for having a small effect size. But it is not OK to criticize a study for having a large sample size. This is because sample sizes do not change effect sizes. If I were to study the effect of gender on weight with 40 people or with 400 people, I would, on average, estimate the same effect size (d ~= .59). Collecting 360 additional observations does not decrease my effect size (though, happily, it does increase the precision of my effect size estimate, and that increased precision better enables me to tell whether an effect size is in fact trivial).

Our field suffers from a problem of underpowering. When we underpower our studies, we either suffer the consequences of a large file drawer of failed studies (bad for us) or we are motivated to p-hack in order to find something to be significant (bad for the field). Those who criticize studies for being overpowered are using a nonsensical argument to reinforce exactly the wrong methodological norms.

If someone wants to criticize trivial effect sizes, they can compute them and, if they are trivial, criticize them. But they should never criticize samples for being too large.

We are an empirical science. We collect data, and use those data to learn about the world. For an empirical science, large samples are good. It is never worse to have more data.


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[5] The Consistency of Random Numbers

What’s your favorite number between 1 and 100? Now, think of a random number between 1 and 100. My goal for this post is to compare those two responses.

Number preferences feel random. They aren’t. “Random” numbers also feel random. Those aren’t random either. I collected some data, found a pair of austere academic papers, and one outstanding blog post. I will tell you about all of them.

First, the data I collected. I (along with Hannah Perfecto, one of my excellent doctoral students) asked one group of people to generate a random number between 1 and 100. Another group reported their favorite number between 1 and 100. That’s it.

We know a little about preferences. People like their birthday numbers, for example. They pursue round numbers. In preparing this post, I learned of a simmering literature on single-digit number preferences, suggesting that in both 1971 and in 1988 people liked the number 7. (Aside: Someone should write the number preference equivalent of the Princeton Trilogy. In fact, why not move beyond preferences to other attributes? For example, are even numbers more warm or more competent?*). As far as I can tell, less is known about how people generate random numbers. Do people choose the same numbers at random as they choose as their favorites?

The figures tell the whole story, but words are useful. Consider four notable numbers. Consistent with past research, people like the number 7. Inconsistent with horror movie titlers and hotel floor number assigners, people also like the number 13. The number 42 has an entirely wonderful Wikipedia entry, suggesting that its consequence goes beyond Jackie Robinson and Douglas Adams. Perhaps the Data Colada can add a small footnote to its mystique? Finally, the number 69 also has a Wikipedia entry, though it is far less vivid than you’re anticipating. On the random side there are fewer obvious winners (three way tie between 5, 67, and 69). numbers frequencies

How about some other patterns? First of all, the two sets are highly, but imperfectly, correlated at r = .48. Random numbers are larger than favorite numbers (Ms = 46.9 vs. 30.7), t(565) = 7.01, p

numbers correlation

These tendencies are partially reflected in the numeric codes people choose for debit cards and their ilk. PIN numbers are a mix of preference and random, and consistent with the data we collected, a brilliant analysis of leaked PIN numbers reveals birthday liking (numbers below 32) and repeated numbers (like multiples of 11). Figure 3 reproduces a chart of 4-digit PIN codes. It will take 30 seconds to orient yourself, but then you will spend five minutes savoring it. numbers PIN

My favorite number is just about the most arbitrary preference possible. My “random” number is more arbitrary. But neither is arbitrary at all.

* Hypothesis: More warm. Odd numbers are wicked competent.


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[4] The Folly of Powering Replications Based on Observed Effect Size

It is common for researchers running replications to set their sample size assuming the effect size the original researchers got is correct. So if the original study found an effect-size of d=.73, the replicator assumes the true effect is d=.73, and sets sample size so as to have 90% chance, say, of getting a significant result.

This apparently sensible way to power replications is actually deeply misleading.

Why Misleading?
Because of publication bias. Given that (original) research is only publishable if it is significant, published research systematically overestimates effect size (Lane & Dunlap, 1978). For example, if sample size is n=20 per cell, and true effect size is d=.2, published studies will on average estimate the effect to be d=.78. The intuition is that overestimates are more likely to be significant than underestimates, and so more likely to be published.

If we systematically overestimate effect sizes in original work, then we systematically overestimate the power of replications that assume those effects are real.

Let’s consider some scenarios. If original research were powered to 50%, a highly optimistic benchmark (Button et al, 2013;Sedlmeier Gigerenzer, 1989), here is what it looks like:

50
So replications claiming 80% power actually have just 51% (Details | R code).

Ok. What if original research were powered at a more realistic level of, say, 35%:
35
The figures show that the extent of overclaiming depends on the power of the original study. Because nobody knows what that is, nobody knows how much power a replication claiming 80%, 90% or 95% really has.

A self-righteous counterargument
A replicator may say:

Well, if the original author underpowered her studies, then she is getting what she deserves when the replications fail; it is not my fault my replication is underpowered, it is hers. SHE SHOULD BE DOING POWER ANALYSIS!!!

Three problems.
1. Replications in particular and research in general are not about justice. We should strive to maximize learning, not schadenfreude.

2. The original researcher may have thought the effect was bigger than it is, she thought she had  80% power, but she had only 50%. It is not “fair” to “punish” her for not knowing the effect size she is studying. That’s precisely why she is studying it.

3. Even if all original studies had 80% power, most published estimates would be over-estimates, and so even if  all original studies had 80% power, most replications based on observed effects would overclaim power. For instance, one in five replications claiming 80% would actually have <50% power (R code).

 

What’s the alternative?
In a recent paper (“Evaluating Replication Results”) I put forward a different approach to thinking about replication results altogether. For a replication to fail it is not enough that p>.05 in it, we need to also conclude the effect is too small to have been detected in the original study (in effect, we need tight confidence intervals around 0). Underpowered replications will tend to fail to reject 0, be n.s., but will also tend to fail to reject big effects. In the new approach this result is considered as uninformative rather than as a “failure-to-replicate.” The paper also derives a simple rule for sample size to be properly powered for obtaining informative failures to replicate:  2.5 times the original sample size ensures 80% power for that test. That number is unaffected by publication bias, how original authors power their studies, and the study design (e.g., two-proportions vs. ANOVA).


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