The 100% CI

or
Dear Sanjay

TL;DR: Publication bias is a bitch, but poor hypothesising may be worse.
Estimated reading time: 10 minutes

A few weeks ago I was listening to episode 5 of the Black Goat, flowery thoughts on my mind, when suddenly I heard Sanjay Srivastava say the following words (from minute 37:47):

And this is what I struggle with, right, with Registered Reports and this idea that we should be focusing on process and soundness and all this stuff. If there’s two papers that have equally good methods, that, before I knew the results, I would have said they were equally well-posed questions, but one reports a cure for cancer and the other reports a failed attempt to cure cancer – I’m gonna like the cure for cancer more, and I can’t escape feeling like at some point, you know, that shit matters.

First, a clarification: Sanjay does like Registered Reports (RRs)! He gave the following comment on his comment (meta Sanjay): “Looking at that quote in writing (rather than spoken) and without any context, it might sound like I’m ambivalent about RRs, but that’s not the case. I fully support the RR format and I don’t think what I said is a valid reason not to have them.” The issue is further discussed in a new Black Goat episode.

I have to admit this statement was a bit startling when I first heard it – Sanjay doesn’t like null results? But, but… publication bias! Ok, I should say that I am a bit über-anxious when it comes to this issue. I think that our collective bias against null results is one of the main causes of the replication crisis, and that makes me want everyone to embrace null results like their own children and dance in a circle around them singing Kumbaya.

But Sanjay is right of course – we all want a cure for cancer;^[1]Except for nihilists. (There’s nothing to be afraid of, Donny.) we want to find out what is true, not what isn’t. And that is why positive results will always feel more interesting and more important to us than null results. This is the root of publication bias: Every player in the publication system (readers, journal editors, reviewers, authors) is biased against null results. And every player expects every other player to be biased against null results and tries to cater for that to make progress.
Of course there are exceptions – sometimes we don’t buy a certain theory or don’t want it to be true (e.g. because it competes with our own theory). In these cases we can be biased against positive results. But overall, on average, all things being equal, I would say a general bias towards positive findings is a fair assessment of our system and ourselves, and this is what we’ll talk about today.

In this post, I will try to make the case for null results. I’m up against Sanjay Srivastava’s gut feeling, so this better be convincing. Ok, here we go: Four reasons why we should love null results.

1) We are biased against null results
Because we find positive results more important and interesting, we fall prey to motivated reasoning: We will judge studies reporting positive results to be of higher quality than studies reporting null results. We will retrospectively downgrade our impression of the methods of a paper after learning it produced null results. And we will be more motivated to find flaws in the methods, while the methods of papers reporting positive results will get an easier pass.^[2]I like the illustration of motivated reasoning by Gilovich (1991), explained here: Evidence in favour of your prior convictions will be examined taking a “Can I believe this?” stance, whereas evidence in opposition to your prior beliefs will be examined taking a “Must I believe this?” stance. The must stance typically gives evidence a much harder time to pass the test.
This means that as soon as we know the results of a study, we are no longer competent judges of the used research methods. But we know that sound methods make and break what we can learn from a study. This is why we absolutely must shield ourselves from judging papers based on or after knowing the results.
In other words: It’s ok to prefer the cancer-cure-finding RR to the non-cancer-cure-finding RR.^[3]Well… not really, though. If this leads to better outcomes for authors of positive results (fame, citations, grants), you still select for people who are willing and able to game the remaining gameable aspects of the system. But they have to be RRs, because we are guaranteed to fool ourselves if we base publication decisions on this feeling.

Reason #1: We should love null results to counter our tendency to underestimate their quality.

2) Null results are unpopular because our epistemology sucks
NB: I tried to avoid going down the epistemological and statistical rabbit holes of NHST and instead focus on the practical surface of NHST as it’s commonly used by psychologists, with all the shortcomings this entails.
This section was partly inspired by Daniël Lakens’ recent workshop in Munich, where we looked at the falsifiability of hypotheses in published papers.

I think one reason why null results are unpopular is that they don’t tell us if the hypothesis we are interested in is likely to be false or not.

The most common statistical framework in psychology is null hypothesis significance testing (NHST). We start out with a shiny new hypothesis, H_shinynew, which typically postulates an effect; a difference between conditions or a relationship between variables. But, presumably because we like it so much that we wouldn’t want it to come to any harm, we never actually test it. Instead, we set up and test a null hypothesis (H₀) of un-shiny stuff: no effect, no difference or no relationship.^[4]Better known as Gigerenzer’s “null ritual” If our test comes up significant, p < .05, we reject H₀, accept H_shinynew, and fantasise about how much ice cream we could buy from our hypothetical shiny new grant money. But what happens when p ≥ .05? P-hacking aside: When was the last time you read a paper saying “turns out we were wrong, p > .05″? NHST only tests H₀. The p-value says nothing about the probability of H_shinynew being true. A non-significant p-value means that either H₀ is true or you simply didn’t have enough power to reject it. In a Bayesian sense, data underlying a non-significant p-value can be strong evidence for the null or it can be entirely inconclusive (and everything in between).

“In science, the only failed experiment is one that does not lead to a conclusion.”
(Mack, 2014, p. 030101-1)

Maybe it’s just me, but I do find strong evidence for H₀ interesting. Or, if you’re not a fan of Bayesian thinking: rejecting H_shinynew with a low error rate.^[5]These two are not identical of course, but you get the idea. I assume that we don’t reject H_shinynew whenever p ≥ .05 mainly because we like it too much. But we could, and thanks to Neyman & Pearson we would know our error rate (rejecting H_shinynew when it is true): beta, more commonly known as 1-power. With 95% power, you wouldn’t even fool yourself more often when rejecting H_shinynew than when rejecting H₀.
There must be a catch, right? Of course there is. Das Leben ist kein Ponyhof, as we say in German (life isn’t a pony farm). As you know from every painful minute spent on the Sample Size Samba, power depends on effect size. With 95% power for detecting d_shinynew, you have less than 95% power for detecting anything smaller than d_shinynew. So the catch is that we must commit ourselves to defining H_shinynew more narrowly than “something going on” and think about which effect size we expect or are interested in.

I think we could gain some null-result fans back if we set up our hypothesis tests in a way that would allow us to conclude more than “H₀ could not be rejected for unknown reasons”. This would of course leave us with a lot less wiggle space to explain how our shiny new hypothesis is still true regardless of our results – in other words, we would have to start doing actual science, and science is hard.

Reason #2: Yeah, I kind of get why you wouldn’t love null results in these messy circumstances. But we could love them more if we explicitly made our alternative hypotheses falsifiable.

3) Null results come before positive results
Back to the beginning of this post: We all want to find positive results. Knowing what’s true is the end goal of this game called scientific research. But most of us agree that knowledge can only be accumulated via falsification. Due to several unfortunate hiccups of the nature of our existence and consciousness, we have no direct access to what is true and real. But we can exclude things that certainly aren’t true and real.

Imagine working on a sudoku – not an easy-peasy one from your grandma’s gossip magazines^[6]bracing myself for a shitstorm of angry grannies but one that’s challenging for your smartypants brain. For most of the fields you’ll only be able to figure out the correct number because you can exclude all other numbers. Before you finally find that one number, progress consists in ruling out another number.
Now let’s imagine science as one huge sudoku, the hardest one that ever existed. Let’s say our future depends on scientists figuring it out. And we don’t have much time. What you’d want is a) putting the smartest people of the planet on it, and b) a Google spreadsheet, because Google spreadsheets rock so that they could make use of anyone else’s progress instantly. You would want them to tell each other if they found out that a certain number does not go into a certain field.

Reason #3: We should love null results because they are our stepping stones to positive results, and although we might get lucky sometimes, we can’t just decide to skip that queue.

4) Null results are more informative
The number of true findings in the published literature depends on something significance tests can’t tell us: The base rate of true hypotheses we’re testing. If only a very small fraction of our hypotheses are true, we could always end up with more false positives than true positives (this is one of the main points of Ioannidis’ seminal 2005 paper).

When Felix Schönbrodt and Michael Zehetleitner released this great Shiny app a while ago, I remember having some vivid discussions with Felix about what the rate of true hypotheses in psychology may be. In his very nice accompanying blog post, Felix included a flowchart assuming 30% true hypotheses. At the time I found this grossly pessimistic: Surely our ability to develop hypotheses can’t be worse than a coin flip? We spent years studying psychology! We have theories! We are really smart! I honestly believed that the rate of true hypotheses we study should be at least 60%.

A few months ago, this interesting paper by Johnson, Payne, Want, Asher, & Mandal came out. They re-analysed 73 effects from the RP:P data and tried to model publication bias. I have to admit that I’m not maths-savvy enough to understand their model and judge their method,^[7]I tell myself it’s ok because this is published in the Journal of the American Statistical Association. but they estimate that over 700 hypothesis tests were run to produce these 73 significant results. They assume that power for tests of true hypotheses was 75%, and that 7% of the tested hypotheses were true. Seven percent.
Uh, umm… so not 60% then. To be fair to my naive 2015 self: this number refers to all hypothesis tests that were conducted, including p-hacking. That includes the one ANOVA main effect, the other main effect, the interaction effect, the same three tests without outliers, the same six tests with age as covariate, … and so on.

Let’s see what these numbers mean for the rates of true and false findings. If you’re anything like me, you can vaguely remember that the term “PPV” is important for this, but you can’t quite remember what it stands for and that scares you so much that you don’t even want to look at it if you’re honest… For the frightened rabbit in me and maybe in you, I’ve made a wee table to explain the PPV and its siblings NPV, FDR, and FOR.

Ok, now we got that out of the way, let’s stick the Johnson et al. numbers into a flowchart. You see that the PPV is shockingly low: Of all significant results, only 53% are true. Wow. I must admit that even after reading Ioannidis (2005) several times, this hadn’t quite sunk in. If the 7% estimate is anywhere near the true rate, that basically means that we can flip a coin any time we see a significant result to estimate if it reflects a true effect.
But I want to draw your attention to the negative predictive value. The chance that a non-significant finding is true is 98%! Isn’t that amazing and heartening? In this scenario, null results are vastly more informative than significant results.

I know what you’re thinking: 7% is ridiculously low. Who knows what those statisticians put into their Club Mate when they calculated this? For those of you who are more like 2015 Anne and think psychologists are really smart, I plotted the PPV and NPV for different levels of power across the whole range of the true hypothesis rate, so you can pick your favourite one. I chose five levels of power: 21% (neuroscience estimate by Button et al., 2013), 75% (Johnson et al. estimate), 80% and 95% (common conventions), and 99% (upper bound of what we can reach).

The plot shows two vertical dashed lines: The left one marks 7% true hypotheses, as estimated by Johnson et al. The right one marks the intersection of PPV and NPV for 75% power: This is the point at which significant results become more informative than negative results. That happens when more than 33% of the studied hypotheses are true. So if Johnson et al. are right, we would need to up our game from 7% of true hypotheses to a whopping 33% to get to a point where significant results are as informative as null results!

This is my take-home message: We are probably in a situation where the fact that an effect is significant doesn’t tell us much about whether or not it’s real. But: Non-significant findings likely are correct most of the time – maybe even 98% of the time. Perhaps we should start to take them more seriously.

Reason #4: We should love null results because they are more likely to be true than significant results.

Especially Reason #4 has been quite eye-opening for me and thrown up a host of new questions – is there a way to increase the rate of true hypotheses we’re testing? How much of this is due to bad tests for good hypotheses? Did Johnson et al. get it right? Does it differ across subfields, and if so, in what way? Don’t we have to lower alpha to increase the PPV given this dire outlook? Or go full Bayesian? Should replications become mandatory?^[8]In the Johnson et al. scenario, two significant results in a row boost the PPV to 94%.

I have no idea if I managed to shift anyone’s gut feeling the slightest bit. But hey, I tried! Now can we do the whole Kumbaya thing please?

References
Button, K. S., Ioannidis, J. P. A., Mokrysz, C., Nosek, B. A., Flint, J., Robinson, E. S. J., & Munafò, M. R. (2013). Power failure: Why small sample size undermines the reliability of neuroscience. Nature Reviews Neuroscience, 14, 365–376.
Dawson, E., Gilovich, T., & Regan, D. T. (2002). Motivated reasoning and performance on the Wason Selection Task. Personality and Social Psychology Bulletin, 28(10), 1379–1387. doi: 10.1177/014616702236869
Gigerenzer, G. (2004). Mindless statistics. The Journal of Socio-Economics, 33, 587–606.
Gilovich, T. (1991). How we know what isn’t so: The fallibility of human reason in everyday life. New York: Free Press.
Ioannidis, J. P. A. (2005). Why most published research findings are false. PLoS Medicine, 2(8), e124. doi: 10.1371/journal.pmed.0020124
Johnson, V. E., Payne, R. D., Wang, T., Asher, A., & Mandal, S. (2017). On the reproducibility of psychological science. Journal of the American Statistical Association, 112(517), 1-10. doi: 10.1080/01621459.2016.1240079
Mack, C. (2014). In Praise of the Null Result. Journal of Micro/Nanolithography, MEMS, and MOEMS, 13(3), 030101.
Open Science Collaboration (2015). Estimating the reproducibility of psychological science. Science, 349(6251), aac4716.

TL;DR: What’s an age-effect net of all time-varying covariates?
The sound of one hand clapping.

Recently, we submitted a paper with some age trajectories of measures of individuals’ (un-)well-being. We thought of these trajectories in the most descriptive way: How do these measures change across the life course, all things considered? And really while this might not be the most interesting research question because it doesn’t directly answer why stuff happens, I’m a fan of simple descriptive studies and think they should have a place in our domain; Paul Rozin wrote a great piece on the importance of descriptive studies.

Anyway, the editor asked us to justify why we did not include any time-varying covariates (e.g. income, education, number of children, health) in our analysis of age trajectories. I thought the editor had requested an actual justification; my co-author (an economist) thought the editor just wanted to tell us that we should throw in all sorts of covariates. I felt too lazy to re-run all analyses and create new figures and tables, plus I always get a weird twitch in my left eye when somebody asks for “statistical control” without additional justification, so instead I looked into the (scientific) literature on the midlife crisis and tried to figure out how people have justified the inclusion of control variables in the analyses of age effects on well-being.^[1]Ruben, on the other hand, would probably get a twitch in his right eye if he found out I did not automate making my figures and tables.

Cat ownership, a time-varying covariate. (Pic: pixabay.com)

Whether or not life satisfaction dips in middle adulthood (somewhere between age 45-64) before rising again in older age^[2]before dipping again in a terminal decline. If you read that footnote, you’re now in the mortality salience condition of my Terror Management Theory study. has been hotly debated by psychologists and economists. There are a lot of papers out there on that subject and personally, I’m totally agnostic regarding the existence of the midlife crisis – ask me again in 20 years, if I’m not too busy driving my Porsche. But there are a lot of interesting methodological questions that arise when trying to answer this question.

A brief list of stuff I don’t want to talk about in this post, which are important nonetheless:

• the Age-Period-Cohort conundrum: In short, this requires us to make certain assumptions when we want to identify age/period/cohort effects. That’s okay though, every researcher needs to make assumptions from time to time.
• longitudinal vs. cross-sectional data: Both can have their pros and cons.
• statistical control for covariates that don’t change over time, such as gender or race, as systematic differences in the composition in the age groups can cause issues
• what we can learn from lab studies in which researchers recruit older people and then compare their performance on an arbitrary task X to the performance of their convenient undergraduate sample. How do you reasonably match 60 year old people that decided to participate in lab studies onto a younger sample of psych majors that really just want to get their freakin’ course credit?
• lots of other interesting stuff you can do with longitudinal data that is more interesting than simple descriptive trajectories

But let’s get back to the topic our editor raised: Should we control for time-varying covariates such as income, marital status, health? The logic seems straightforward: Wouldn’t we want to “purge” the relationship between age and life satisfaction from other factors?

Quite obviously, a lot of stuff changes as we age. We get older, get our degrees, start a decent job and make some money,^[3]Or, alternatively, start a blog. maybe marry and settle down or travel to an Ashram to awaken our inner goddess and spite our conservative parents or maybe just get a lot of cats.

Mount Midlife Crisis, not to be confused with Mount Doom. (Art: Hakuin Ekaku)

To control for these variables might be wrong for two distinct reasons, and I will start with the somewhat more obscure one.

First, our time-varying covariate might actually be causally affected by life satisfaction. This argument has been raised regarding the statistical control of marital status by the late Norval Glenn (2009). He simulated a data situation in which (1) life satisfaction is stable across the life course and (2) starting from 21, only the 10 happiest people marry each year. He then demonstrated that controlling for marital status will result in a spurious trajectory, that is, a pronounced decline of life satisfaction over the life course even though we know that there’s no age effect in the underlying data. If you have read this blog before and the data situation sounds somewhat familiar to you: Marital status would be one of the infamous colliders that you should not control for because if you do, I will come after you.^[4]And you should be scared because I can deliver angry rants about inapproriate treatment of third variables. I might bring cookies and hope that you have decent coffee because this might take longer. If marital status is affected by age (the older you are, the more likely you are to be married), and if satisfied people are more likely to marry, marital status becomes a collider of its two causes and should not be controlled.

The second reason is somewhat more obvious: In many cases, the time-varying covariates will mediate the effects of age on your outcome. That is probably most obvious for health: Health declines with age. Decreases in health affect life satisfaction.^[5]They obviously do, though the fact that life satisfaction remains stable until a certain age despite decreases in health has been labeled the happiness paradox. So life satisfaction might decrease with age because of declining health. Now what does it mean if we control for this potential mediator?

Well, it means that we estimate the age effect net of the parts that are mediated through health. That is not inherently nonsensical, we just have to interpret the estimate properly. For example, Andrew Oswald was cited in Vol. 30 of the Observer: “[But] encouragingly, by the time you are 70, if you are still physically fit then on average you are as happy and mentally healthy as a 20 year old.” Now this might be indeed encouraging for people who think they are taking great care of their health and predict that they will be healthy by the time they are 70; but whether it’s encouraging on average strongly depends on the average health at age 70.
For example, if we assume that only the luckiest 1% of the population will be physically fit at that age, 99% will end up unhappier than 20 year olds (whether or not 20-year-olds are very happy is a different question). That doesn’t sound very optimistic any more, does it? The lucky one percent might also be very special with respect to other characteristics such as income, and a message such as “the wealthy will be still happy at age 70, whereas the poor are wasting away because of a lack of health care” again sounds not very encouraging. For the record, I’m not claiming that this is happening, but those are all scenarios that are aligned with the simple statement that those who are physically fit at age 70 are as mentally healthy as 20 year olds.

So the estimated association has its own justification but must be interpreted carefully.^[6]Actually, there is yet another problem that has been pointed out by Felix Thoemmes in the comments section of this post. A mediator is also almost always a collider, as it is per definition caused by the independent variable of interest and (most likely) by some other factors. So you would actually have to control the backdoor paths from the mediator in turn, or else your estimate of the direct effect, whatever it reflects, will actually be biased again. Additionally, it renders the “remaining” age effect hard to interpret, so it might not be very enlightening to look at age effects net of the effects of time-varying covariates. Let’s assume you “control” all sorts stuff that happens in life as people age – marital status, education, income, number of children, maybe also number of good friends, cat ownership, changes in health, and when we are already at it, why don’t we also control for the stuff that is underlying changes in health, such as functioning of organs and cell damage? – and still find a significant age effect.

What does that mean? Well, it means that you haven’t included all time-varying covariates that are relevant to life satisfaction because age effects must necessarily be mediated through something. The sheer passing of time only has effects because stuff happens in that time.
The “stuff” might be all sorts of things, and we might be inclined to consider that stuff more or less psychologically meaningful. For example, we might not consider changes in marital status or physical health to be “genuinely psychological”, so we might decide to control for these things to arrive at a purely psychological age effect. Such a “purely psychological” age effect might then be driven by e.g. people’s attitude towards the world. For example, people might get more optimistic and thus more satisfied controlling for other life circumstances. But I would again be careful with those interpretations, because of the collider problem outlined before and because of the somewhat arbitrary distinction between physical changes and social role changes as opposed to psychological changes.

In other words: what you should or shouldn’t control for always depends on your research question. If you study living things and control for life, don’t be surprised if your results seem a bit dull.

April Fool’s Post 2017

“The pursuit of knowledge is, I think, mainly actuated by love of power. And so are all advances in scientific technique.”
― Bertrand Russell

Today on the 100% CI we have to stop the jokes for a moment. Today, we will talk about being disappointed by your idols, about science criticism being taken too far. Here, we reveal how Dr. Andrew Gelman, the prominent statistician and statistics blogger, abused his power.

We do not make this accusation lightly, but our discoveries leave no other conclusion: In his skepticism of psychological science, Dr. Gelman lost sight of right and wrong. What follows is a summary of the evidence we obtained.

This March the four of us visited the Applied Statistics Center at Columbia University for a brief workshop on Stan, the probabilistic programming language. We were excited about this opportunity to learn from one of our personal heroes.

The course, however, did not live up to our expectations. Frequently, Dr. Gelman would interrupt the course with diatribes against psychological science. On the second-to-last afternoon, we were supposed to write our first Stan code in a silent study session. We were left alone in the Gelman lab and our minds wandered. Our attention was drawn to a particularly large file drawer that turned out to be unlocked. What we discovered can only be described as profoundly shocking:

Inside were literally dozens of study reports on Power Posing. At first glance, this did not seem particularly strange as Dr. Gelman is known to write frequently about this phenomenon on his blog.

But this particular file drawer problem was different: The lab log revealed that Dr Gelman was desperate to obtain evidence against the phenomenon – and failed repeatedly. Initially, he invested enormous resources to run experiments with extraordinary four digit sample sizes to “nail the coffin shut on Power Pose”, as a hand-written note on an early report reads. The data painted a very clear picture, and it was not to his liking. As it dawned on him that, contrary to his personal convictions, Power Posing might be a real phenomenon, he began to stack the deck.

Instead of simple self-reports, he tried manifest behavioral observations and even field studies where the effect was expected to vanish. Power Pose prevailed. He deliberately reduced study samples to the absurdly low numbers often criticized on his very own blog. But even in his last attempts with 1-β almost equal to ɑ: Power Pose prevailed. As more and more evidence in favor of Power Posing was gathered, the research became… sloppy. Conditions were dropped, outliers removed, moderators randomly added, and, yes, even p-values were rounded up. Much to Dr. Gelman’s frustration, Power Pose prevailed. He was *unable* to collect data in favor of the null hypothesis.

He thought he had one final Bayesian trick up his sleeve: By hiring a skilled hypnotist he manipulated his priors, his own beliefs (!) in Power Posing. But even with these inhumane levels of disbelief, the posterior always indicated beyond a doubt: Power Pose prevailed. It was almost like the data were trying to tell him something – but Dr. Gelman had forgotten how to listen to evidence a long time ago.

In a recent publication, Simmons and Simonsohn analyzed the evidential value of the published literature on Power Posing. The centerpiece of their research is a p-curve (figure below, left graph) on the basis of which they “conclusively reject the null hypothesis that the sample of existing studies examines a detectable effect.” Had Dr. Gelman not hidden his findings in a file drawer, Simmons and Simonsohn’s conclusions would have been dramatically different (right graph).

Initially, we couldn’t believe that he would go this far just to win an argument. We were sure there must have been some innocuous explanation – yet we also did not want to confront him with our suspicions right away. We wanted to catch him red-handed.

Thus, we decided to infiltrate one of his studies, which he was covertly advertising under the obvious pseudonym Mr. Dean Wangle. He administered the study wearing a fake moustache and a ridiculous French beret, but his voice is unmistakeable. Below is a video of an experimental session that we were able to record with a hidden camera. The footage is very tough to watch.

Combined, the evidence leaves only one conclusion: Andrew Gelman betrayed science in his war on power posing.

So… what is media psychology anyway?

Does playing violent video games increase aggression?^[1]No, but violent video game research kinda does. What makes advertisements persuasive?^[2]David Hasselhoff, obvs. Are 5%25%75% of the population addicted to social media?^[3]It’s almost like humans have a fundamental need for social interactions. Who are these people that watch porn?^[4]Literally everyone everywhere Why do we enjoy cat videos so much?^[5]WHY???

These are the typical research questions media psychologists are concerned with. Broadly, media psychology describes and explains human behavior, cognition, and affect with regards to the use and effects of media and technology. Thus, it’s a hybrid discipline that borrows heavily from social, cognitive, and educational psychology in both its theoretical approaches and empirical traditions. The difference between a social psychologist and a media psychologist that both study video game effects is that the former publishes their findings in JPSP while the latter designs “What Twilight character are you?” self-tests^[6]TEAM EDWARD FTW! for perezhilton.com to avoid starving. And so it goes.

New is always better

A number of media psychologists is interested in improving psychology’s research practices and quality of evidence. Under the editorial oversight of Nicole Krämer, the Journal of Media Psychology (JMP), the discipline’s flagship^[7]By “flagship” I mean one of two journals nominally dedicated to this research topic, the other being Media Psychology. It’s basically one of those People’s Front of Judea vs. Judean People’s Front situations. journal, not only signed the Transparency and Openness Promotion Guidelines, it has also become one of roughly fifty journals that offer the Registered Reports format.

To promote preregistration in general and the new submission format at JMP in particular, the journal launched a fully preregistered Special Issue on “Technology and Human Behavior” dedicated exclusively to empirical work that employs these practices. Andy Przybylski^[8]Who, for reasons I can’t fathom, prefers being referred to as a “motivational researcher” and I were fortunate enough to be the guest editors of this issue.

The papers in this issue are nothing short of amazing – do take a look at them even if it is outside of your usual area of interest. All materials, data, analysis scripts, reviews, and editorial letters are available here. I hope that these contributions will serve as an inspiration and model for other (media) researchers, and encourage scientists studying media to preregister designs and share their data and materials openly.

Media Psychology BC^[9]Before Chambers

If you already suspected that in all this interdisciplinary higgledy-piggledy, media psychology did not only inherit its parent disciplines’ merits, but also some of their flaws, you’re probably^[10]unerring-absolute-100%-pinpoint-unequivocally-no-ifs-and-buts-dead-on-the-money correct. Fortunately, Nicole was kind enough to allot our special issue editorial more space than usual in order to report a meta-scientific analysis of the journal’s past and to illustrate how some of the new practices can ameliorate the evidential value of research. For this reason, we surveyed a) availability of data, b) errors in the reporting of statistical analyses, and c) sample sizes and statistical power of all 147 studies in N = 146 original research articles published in JMP between volume 20/1, when it became an English-language publication, and volume 28/2 (the most recent issue at the time this analysis was planned). This blog post is a summary of the analyses in our editorial, which — including its underlying raw data, analysis code, and code book — is publicly available at https://osf.io/5cvkr/.

Availability of Data and Materials

Historically the availability of research data in psychology has been poor. Our sample of JMP publications suggests that media psychology is no exception to this, as we were not able to identify a single publication reporting a link to research data in a public repository or the journal’s supplementary materials.

Statistical Reporting Errors

A recent study by Nuijten et al. (2015) indicates a high rate of reporting errors in reported Null Hypothesis Significance Tests (NHSTs) in psychological research reports. To make sure such inconsistencies were avoided for our special issue, we validated all accepted research reports with statcheck 1.2.2, a package for the statistical programming language R that works like a spellchecker for NHSTs by automatically extracting reported statistics from documents and recomputing^[11]p-values are recomputed from the reported test statistics and degrees of freedom. Thus, for the purpose of recomputation, it is assumed that test statistics and degrees of freedom are correctly reported, and that any inconsistency is caused by errors in the reporting of p-values. The actual inconsistencies, however, can just as well be caused by errors in the reporting of test statistics and/or degrees of freedom. p-values.

For our own analyses, we scanned all n_emp = 131 JMP publications reporting data from at least one empirical study (147 studies in total) with statcheck to obtain an estimate for the reporting error rate in JMP. Statcheck extracted a total of 1036 NHSTs reported in n_nhst = 98 articles. Forty-one publications (41.8% of n_nhst) reported at least one inconsistent NHST (max = 21), i.e. reported test statistics and degrees of freedom did not match reported p-values. Sixteen publications (16.3% of n_nhst) reported at least one grossly inconsistent NHST (max = 4), i.e. the reported p-value is < .05 while the recomputed p-value is > .05, or vice-versa. Thus, a substantial proportion of publications in JMP seem to contain inaccurately reported statistical analyses, of which some might affect the conclusions drawn from them (see Figure 1).

Caution is advised when speculating about the causes of the inconsistencies. Many of them are probably clerical errors that do not alter the inferences or conclusions in any way.^[13]For example, in 20 cases the authors reported p = .000, which is mathematically impossible (for each of these p_recomputed < .001). Other inconsistencies might be explained by authors not declaring that their tests were one-tailed (which is relevant for their interpretation). However, with some concern, we observe it is unlikely to be the only cause, as in 19 out of 23 cases the reported p-values were equal to or smaller than .05 while the recomputed p-values were larger than .05, whereas the opposite pattern was observed in only four cases. Indeed, if incorrectly reported p-values resulted merely from clerical errors, we would expect inconsistencies in both directions to occur at approximately equal frequencies.

All of these inconsistencies can easily be detected using the freely available R package statcheck or, for those who do not use R, in your browser via www.statcheck.io.

Sample Sizes and Statistical Power

High statistical power is paramount in order to reliably detect true effects in a sample and, thus, to correctly reject the null hypothesis when it is false. Further, low power reduces the confidence that a statistically significant result actually reflects a true effect. A generally low-powered field is more likely to yield unreliable estimates of effect sizes and low reproducibility of results. We are not aware of any previous attempts to estimate average power in media psychology.

Strategy 1: Reported power analyses. One obvious strategy for estimating average statistical power is to examine the reported power analyses in empirical research articles. Searching all papers for the word “power” yielded 20 hits and just one of these was an article that reported an a priori determined sample size.^[14]In the 19 remaining articles power is mentioned, for example, to either demonstrate observed or post-hoc power (which is redundant with reported NHSTs), to suggest larger samples should be used in future research, or to explain why an observed nonsignificant “trend” would in fact be significant had the statistical power been higher.

Strategy 2: Analyze power given sample sizes. Another strategy is to examine the power for different effect sizes given the average sample size (S) found in the literature. The median sample size in JMP is 139 with a considerable range across all experiments and surveys (see Table 1). As in other fields, surveys tend to have healthy sample sizes apt to reliably detect medium to large relationships between variables.

For experiments (including quasi-experiments), the outlook is a bit different. With a median sample size per condition/cell of 30.67, the average power of experiments published in JMP to detect small differences between conditions (d = .20) is 12%, 49% for medium effects (d = .50), and 87% for large effects (d = .80). Even when assuming that the average effect examined in the media psychological literature could be as large as those in social psychology (d = .43), our results indicate that the chance that an experiment published in JMP will detect them is 38%, worse than flipping a coin.^[15]An operation that would be considerably less expensive.

Table 1. Sample sizes and power of studies published in JMP volumes 20/1 to 28/2.
n = Number of published studies; MD_S = Median sample size; MD_s/cell = Median sample size per condition; 1-ß_r=.1/d=.2 / 1-ß_r=.3/d=.5 / 1-ß_r=.5/d=.8 = Power to detect small/medium/large bivariate relationships/differences between conditions.
For between-subjects, mixed designs, and total we assumed independent t-tests. For within-subjects designs we assumed dependent t-tests. All tests two-tailed, α = .05. Power analyses were conducted with the R package pwr 1.20

Feeling the Future of Media Psychology

The above observations could lead readers to believe that we are concerned about the quality of publications in JMP in particular. If anything, the opposite is true, as this journal recently committed itself to a number of changes in its publishing practices to promote open, reproducible, high-quality research. These analyses are simply another step in a phase of sincere self-reflection. Thus, we would like these findings, troubling as they are, to be taken not as a verdict, but as an opportunity for researchers, journals, and organizations to reflect similarly on their own practices and hence improve the field as a whole.

One key area which could be improved in response to these challenges is how researchers create, test, and refine psychological theories used to study media. Like other psychology subfields, media psychology is characterized by frequent emergence of new theories which purport to explain phenomena of interest.^[16]As James Anderson recently put it in a very clever paper (as usual): “Someone entering the field in 2014 would have to learn 295 new theories the following year.” This generativity may, in part, be a consequence of the fuzzy boundaries between exploratory and confirmatory modes of social sciences research.

Both modes of research – confirming hypotheses and exploring uncharted territory – benefit from preregistration. Drawing this distinction helps the reader determine which hypotheses carefully test ideas derived from theory and previous empirical studies, and it liberates exploratory research from the pressure to present an artificial hypothesis-testing narrative.

As technology experts, media psychology researchers are well positioned to use and study new tools that shape our science. A range of new web-based platforms have been built by scientists and engineers at the Center for Open Science, including their flagship, the OSF, and preprint services like PsyArXiv. Designed to work with scientists’ existing research flows, these tools can help prevent data loss due to hardware malfunctions, misplacement,^[17]Including mindless grad students and hungry dogs or relocations of researchers, while enabling scientists to claim more credit by allowing others to use and cite their materials, protocols, and data. A public repository for media psychology research materials is already in place.

Like psychological science as a whole, media psychology faces a pressing credibility gap. Unlike some other areas of psychological inquiry,^[18]such as meta science however, media research — whether concerning the Internet, video games, or film — speaks directly to everyday life in the modern world. It affects how the public forms their perceptions of media effects, and how professional groups and governmental bodies make policies and recommendations. In part because it is key to professional policy, empirical findings disseminated to caregivers, practitioners, and educators should be built on an empirical foundation with sufficient rigor.

We are, on balance, optimistic that media psychologists can meet these challenges and lead the way for psychologists in other areas. This special issue and the registered reports submission track present an important step in this direction and we thank the JMP editorial board, our expert reviewers, and of course, the dedicated researchers who devoted their limited resources to this effort.

The promise of building an empirically-based understanding of how we use, shape, and are shaped by technology is an alluring one. We firmly believe that incremental steps taken towards scientific transparency and empirical rigor will help us realize this potential.

If you read this entire post, there’s a 97% chance you’re on Team Edward.

(this post was jointly written by Malte & Anne; in a perfect metaphor for academia, WordPress doesn’t know how to handle multiple authors)

We believe in scientific openness and transparency, and consider unrestricted access to data underlying publications indispensable. Therefore, we^[1]Not just the authors of this post, but all four of us. signed the Peer Reviewers’ Openness (PRO) Initiative, a commitment to only offer comprehensive review for or recommend the publication of a manuscript if the authors make their data and materials publicly available, unless they provide compelling reasons^[2]The data-hungry dog of a former grad student whose name you forgot is not a compelling reason. why they cannot do so (e.g. ethical or legal restrictions).

As reviewers, we enthusiastically support PRO and its values.
Also as reviewers, we think PRO can be a pain in the arse.

Ok, not really. But advocating good scientific practice (like data sharing) during peer review can result in a dilemma.

This is how it’s supposed to work: 1) You accept an invitation for review. 2) Before submitting your review, you ask the editor to relay a request to the authors to share their data and materials (unless they have already done so). 3) If authors agree – fantastic. If authors decline and refuse to provide a sensible rationale why their data cannot be shared – you reject the paper. Simple.
So far, so PRO. But here’s where it gets hairy: What happens when the action editor handling the paper refuses to relay the request for data, or even demands that such a request is removed from the written review?

Here is a reply Anne recently got from an editor after a repeated^[3]The editor apologised for overlooking the first email – most likely an honest mistake. Talk to Chris Chambers if you want to hear a few stories about the funny tendency of uncomfortable emails to get lost in the post. PRO request:

“We do not have these requirements in our instructions to authors, so we can not ask for this without discussing with our other editors and associate editors. Also, these would need to involve the publication team. For now, we can relieve you of the reviewing duties, since you seem to feel strongly about your position.
Let me know if this is how we should proceed so we do not delay the review process further for the authors.”

Much like judicial originalists insist on interpreting the US constitution literally as it was written by a bunch of old white dudes more than two centuries ago, editors will sometimes cite existing editorial guidelines by which authors obligate themselves to share data on request, but only after a paper has been published, which has got to be the “Don’t worry, I use protection” argument of academia.^[4]We picked a heterosexual male perspective here but we’re open to suggestions for other lewd examples. Also, we know that this system simply does. not. work.

As reviewers, it is our duty to evaluate submitted research reports, and data are not just an optional part of empirical research – they are the empirical research (the German Psychological Society agrees!). You wouldn’t accept a research report based on the promise that “theory and hypotheses are available on request”, right?^[5]Except when reviewing for Cyberpsychology.

PRO sets “data or it didn’t happen” as a new minimum standard for scientific publications. As a consequence, comprehensive review should only be offered for papers that meet this minimum standard. The technically correct^[6]The best kind of being correct. application of the PRO philosophy for the particular case of the Unimpressed Editor is straightforward: When they decide – on behalf of the authors! – that data should or will not be shared, the principled consequence is to withdraw the offer to review the submission. As they say, PRO before the status quo.

Withdrawing from the process, however, decreases the chance that the data will be made publicly accessible, and thus runs counter to PRO’s ideals. As we say in German, “Operation gelungen, Patient tot” – surgery successful, patient deceased.

Adhering strictly to PRO would work great if everybody participated: The pressure on non-compliant journals would become too heavy. Then again, if everybody already participated, PRO wouldn’t be a thing. In the world of February 2017, editors can just appoint the next best reviewer^[7]Withdrawing from review might still have an impact in the absence of a major boycott by causing the editors additional hassle and delaying the review process – then again, this latter part would unfairly harm the authors, too. who might simply not care about open data – and couldn’t you push for a better outcome if you kept your foot in the door? Then again, if all PRO signatories eroded the initiative’s values that way, the day of reaching the critical mass for a significant boycott would never come.

A major concern here is that the authors are never given the chance to consider the request although they might be receptive to the arguments presented. If increased rates of data sharing is the ultimate goal, what is more effective: boycotting journals that actively suppress such demands by invited reviewers, or loosening up the demands and merely suggest that data should be shared so at least the gist of it gets through?

There are two very different ways to respond to such editorial decisions, and we feel torn because each seems to betray the values of open, valuable, proper scientific research. You ask: What is the best strategy in the long run? Door in the face! Foot in the door! Help, I’m trapped in a revolving door! We would really like to hear your thoughts on this!