Monday, March 5, 2018

Preregistration is a Hot Mess. And You Should Probably Do It.

There’s this episode of Family Guy where some salesman offers Peter a choice between two prizes: a boat or a mystery box. Peter can’t help himself—he reaches for the mystery box. “A boat's a boat, but a mystery box could be ANYTHING!” he says. “It could even be a boat!”

Mystery boxes are like that. Full of mystery and promise. We imagine they could be anything. We imagine them as their best selves. We imagine that they will Make Life Better, or in science, that they will Make Science Better.

Lately, I’ve been thinking a lot about what’s inside the mystery box of preregistration.

Why do I think of preregistration as a mystery box? I’ll talk about the first reason now, and come back to the second in a later post. Reason the First is that we don’t know what preregistration is or why we’re doing it. Or rather, we disagree as a field about what the term means and what the goals are, and yet we don’t even know there’s disagreement. Which means that when we talk about preregistration, we’re often talking past each other.

Here are three examples that I gave in my talk last week at SPSP.

Back in the olden days, in June 2013, Chris Chambers and colleagues published an open letter in the Guardian entitled “Trust in Science Would be Improved by Preregistration." They wrote: “By basing editorial decisions on the question and method, rather than the results, pre-registration overcomes the publication bias that blocks negative findings from the literature.” In other words, they defined preregistration as peer-review and acceptance of articles before the results are known, and they saw the major goal or benefit of preregistration as combatting publication bias.

Fast forward to December 2017: Leif Nelson and colleagues publish a blog post on “How to Properly Preregister a Study.” They define preregistration as “time-stamped documents in which researchers specify exactly how they plan to collect their data and to conduct their key confirmatory analyses,” and they explain that the goal is “to make it easy to distinguish between planned, confirmatory analyses…and unplanned exploratory analyses.” 

Then just a few weeks ago, out of curiosity, I posted the following question on PsychMAP: A researcher tweets: "A new preregistered study shows that X affects Y." What would you typically infer about this study? By far the most popular answer (currently at 114 votes, compared to the next most popular of 44) was that the main hypothesis was probably a priori (no HARKing). In other words, many psychologists seem to think preregistration means writing down your main hypothesis ahead of time, and perhaps that a primary goal is to avoid HARKing.

So if I tell you that I preregistered my study, what do I mean? And why did I do it—what was my goal?

I think we are in desperate need of a shared and precise language to talk about preregistration. Just like any other scientific construct, we’re not going to make much headway on understanding it or leveraging it if we don’t have a consensual definition of what we are talking about.

It seems to me that there are (at least) four types of preregistration, and that each one serves its own potential function or goal. These types of preregistration are not mutually exclusive, but doing any one of them doesn’t necessarily mean you’re doing the others.

Notice that I said POTENTIAL benefit or function. That’s crucial. It means that depending on how you actually implement your preregistration, you may or may not achieve the ostensible goal of that type of preregistration. Given how important these goals are for scientific progress, we need to be paying attention to how and when preregistration can be an effective tool for achieving them.

Let’s say you want to combat publication bias, so you preregister your study on AsPredicted or OSF. Who is going to be looking for your study in the future? Will they be able to find it, or might the keywords you’re using be different from the ones they would search for? Will they be able to easily find and interpret your results? Will you link to your data? If so, will a typical researcher be able to understand your data file at a glance, or did you forget to change the labels from, say, the less-than-transparent VAR1043 and 3REGS24_2?

Let’s say you have a theory that’s ready to be tested.* So you record your hypothesis ahead of time: “Stereotyping will increase with age.” But what kind of stereotypes? Measured how? The vagueness of the prediction leaves too much wiggle room for HARKing later on—and here I mean HARKing in the sense of retroactively fitting the theory to whatever results you happen to find. If you find that racial stereotypes get stronger but elderly stereotypes get weaker as people age, your vague a priori prediction leaves room for your motivated human mind to think to itself “well of course, the prediction doesn’t really make sense for stereotypes of the elderly, since the participants are themselves elderly.” Obviously, adjusting your theory in light of the data is fine if you’re theory building (e.g., asking “Do various stereotypes increase with age, and if so, when?”), but you wouldn’t want to do it and then claim that you were testing a theory-derived hypothesis in a way that allowed for the theory to be falsified. [Update: As Sanjay Srivastava pointed out in a PsychMAP discussion about this post, it's important to recognize that often, researchers wishing to provide a strong and compelling test of a theory will want to conduct a preregistration that combines elements 2 and 3—that is, specific, directional predictions about particular variables that are clearly derived from theory PLUS clear a priori constraints on researcher degrees of freedom.]

Or let’s say that want to be able to take your p-value as an indicator of the strength of evidence for your effect, in a de Grootian sense, and so you preregister a pre-analysis plan. If you write down “participants have to be paying attention,” it doesn’t clearly constrain flexibility in data analysis because there are multiple ways to decide whether participants were paying attention (e.g., passing a particular attention check vs. how long participants spent completing the survey vs. whether a participant clicked the same number for every item on a survey). If you want to avoid unintentional researcher degrees of freedom (or “HARKing” in the sense of trying out different researcher decisions and selecting only the ones that produce the desired results), you need to clearly and completely specify all possible researcher decisions in a data-independent way.**

In fact, the registered report is really the only kind of preregistration on here that’s straightforward to implement in an effective way, because much of the structure of how to do it well has been worked out by the journal and because the pieces of the preregistration are being peer reviewed.

Which brings me to the second reason why I call preregistration a mystery box: What’s inside a preregistration when it HASN’T been part of a peer reviewed registered report? Maybe not what you would assume. Stay tuned.


*Many of us don’t do a lot of theory testing, by the way—we might be collecting data to help build theory, or asking a question that’s not very theoretical but might later end up connecting speculatively to some theories in potentially interesting ways (the sort of thing you do in a General Discussion)—but we’re not working with a theory that generates specific, testable predictions yet.

**Yeah, so, we’ve been using “HARKing” to mean two things…sometimes we use it to mean changing the theory to fit the results, which hampers falsifiability, and sometimes we use it to mean reporting a result as if it’s the only one that was tested, which hampers our ability to distinguish between exploratory and confirmatory analyses. (In his 1998 article, Kerr actually talked about multiple variants of HARKing and multiple problems with it.)***

***We’ve also been using “exploratory/confirmatory” to distinguish between both exploratory vs. confirmatory PREDICTIONS (do you have a research question or a directional prediction?) and exploratory vs. confirmatory ANALYSES (are your analyses data-dependent or data-independent/selected before seeing the data).****

****Did I mention that our terminology is a hot mess?

Tuesday, January 16, 2018

You're Running out of Time

Maybe you’ve been meaning to get to it. Maybe you keep thinking, I just don’t have time right now, but soon, as soon as I submit this paper, as soon as I finish teaching this class. Maybe you’re waiting for it to blow over. Maybe it feels like a choice between work and rubbernecking to watch some kind of field-wide car crash, and you’ve been choosing to work. 

Or maybe it seems like a social psychology problem, and you’re not in that area, so it doesn’t even apply to you. In any case, business as usual. Onward and upward, publish or perish, keep on moving, nothing to see here. 

Here’s the problem, though.

You’re running out of time.

This pesky “crisis” thing? It isn’t going away.* It isn’t limited to one area of psychology, or even just psychology. It’s not something you can ignore and let other people deal with. And it isn’t even something you can put off grappling with in your own work for just another month, semester, year, two years. The alarm bells have been sounded—alarms bells about replicability, power, and publication bias—and although these concerns have been raised before and repeatedly, a plurality of scholars across scientific disciplines are finally listening and responding in a serious way

Now, it takes time to change your research practices. You have to go out and learn about the problems and proposed solutions, you have to identify which solutions make sense for your own particular research context, you have to learn new skills and create new lab policies and procedures. You have to think carefully about things like power (no, running a post-hoc power analysis to calculate observed power is not a good idea) and preregistration (like why do you want to preregister and which type of preregistration will help you accomplish your goals?), and you probably have to engage in some trial and error before you figure out the most effective approaches for your lab.

So a few years ago, when someone griped to me about seeing a researcher present a conference talk with no error bars in the graphs, I nodded sympathetically but also expressed my sense that castigating the researcher in question was premature. Things take awhile to percolate through the system. Not everybody hears about this stuff right away. It might take people awhile to go back through every talk and find every dataset and add error bars. Let’s have some patience. Let’s wait for things to percolate. Let’s give people a chance to learn, and try new things, and improve their research practices going forward, and let’s give that research time to make its slow way through the publication process and emerge into our journals.

Now, though? It’s 2018. And you’re submitting a manuscript where you interpret p = .12 on one page as “a similar trend emerged” that is consistent with your hypothesis, and on another page you use another p = .12 to conclude that “there were no differences across subsamples, so we do not investigate this variable further”…or you’re writing up a study where you draw strong conclusions from the lack of a significant difference on a behavioral outcome between 5 year olds and 7 year olds, with a grand total of 31 children per group and no discussion of the limited reliability of your measure?

Or you’re giving a talk…a new talk, about new data…and you haven’t put error bars on your graphs? And for your between-subjects interaction…for a pretty subtle effect …you collected TWENTY people per cell? And you don’t talk about power at all when you’re describing the study? Or the next study? Or the next?

Well now you’ve lost me. I’m looking out the window. I’m wondering why I’m here. Or actually, I’m wondering why YOU’RE here. Why are you here?

Are you here to science?

Well then. It’s time to pay attention.

Here is one good place to start.**

*Note, I'm not here to debate how bad the replicability crisis is. Lots of other people seem to find value in doing that, but I'm personally more interested in starting with a premise we can all agree on -- i.e., that there's always room for improvement -- and making progress on those improvements.

**And let me just emphasize that word start. I'm not saying you're out of time to finish making all improvements to your research methods and practices -- in fact, I see improving methods and practices as a process that we can incorporate into our ongoing research life, not something that really gets finished. Again, nothing is ever perfect...we can always be looking for the next step. But I do think it's time for EVERYONE to be looking for, and implementing, whatever that next step is in their own particular research context. If you find that you're still on the sidelines -- get in the game. This is not something to watch and it's not something to ignore. It's something you need to be actively engaged in.

Tuesday, November 14, 2017

Walking and Talking

I’m going to say something, and you’re not going to like it: It’s a hell of a lot easier, these days, to talk the talk than to walk the walk.

I mean this in at least three different ways.

1. Low-Cost Signals vs. High-Cost Actions
It is far easier to extol publicly the importance of changing research practices than to actually incorporate better practices in your own research. I can put together a nice rant in about ten minutes about how everyone should preregister and run highly powered studies and replicate before publishing…and while you’re at it, publish slower, prioritize quality over quantity, don't cherry-pick, and post all your data!

But actually thinking through how to increase the informational value of my own research, learning the set of skills necessary to do so, and practicing what I preach? Well that’s far more time-consuming, effortful, and costly.

For example. Let’s say you have a paper. It’s totally publishable, probably at a high impact journal. It reports some findings that for whatever reason, you’re not super confident about. Do you publish it? All together now: “No way!” (See? Talk is easy.)

But do you ACTUALLY decide against publishing it? Because if you do (and I have, repeatedly), your publication count and citation indices take a hit. And your coauthors’ counts and indices take a hit. And now your bean count is lower than it might otherwise be in a system that still prioritizes beans at many levels.

“Down with the beans!” you say. “Let’s change the incentive structure of science!” Awesome. Totally agree. And saying this is easy. Do you actually do it? Do you go into the faculty meeting and present a case for hiring or promoting someone WITHOUT counting any beans? And do you do this REGARDLESS of whether or not the bean count looks impressive? Because it’s tempting to only bother with the longer, harder quality conversation if the quantity isn’t there. And, if you do focus the conversation exclusively on quality, someone is likely to ask you to count the beans anyway. In fact, even if you are armed with an extensive knowledge of the quality of the candidate’s papers and a compelling case for why quality matters, you are going to have an uphill battle to convince the audience to prioritize quality over quantity—especially if those audience members come from areas of psychology that have not yet had to grapple seriously with issues of replicability and publication bias.

Or maybe you say “yes, publish that paper with the tentative findingsjust be transparent about your lack of confidence in the results! At the end of the day, publish it all…just be sure to distinguish clearly between exploratory (data-dependent) and confirmatory (data-independent) findings!” Totally agree. And again: Talk is easy. When you submit your paper, do you clearly state the exploratory nature of your findings front and center, so that even casual readers are sure to see it? If it’s not in the abstract, most people are likely to assume the results you describe are more conclusive than they actually are. But if you put it front and center, you may dramatically lower the chances that your paper gets accepted. (I haven’t tried this one yet, for exactly this reason…instead, I’ve been running pre-registered replications before trying to publish exploratory results. But again, that’s far easier to advocate than to actually do, especially when a study requires substantial resources.)

2. Superficial Shortcuts vs. Deep Thinking
It’s far easier to say you’ve met some heuristic rules about minimum sample sizes, sharing your data, or preregistering than it is to learn about and carefully think through each of these practices, what their intended consequences are, and how to actually implement them in a way that will achieve their intended consequences.

For example. I can upload my data file to the world wide internets in about 60 seconds. Whee, open data! But how open is it, really? Can other researchers easily figure out what each variable is, how the data were processed, and how the analyses were run? Clearly labeling your data and syntax, providing codebooks, making sure someone searching for data like yours will be able to find it easily--all of these things take (sometimes considerable) time and care…but without them, your “open data” is only open in theory, not practice.

Likewise, I can quickly patch together some text that loosely describes the predictions for a study I’m running and post it on OSF and call it a preregistration. But I’m unlikely to get the intended benefits of preregistration unless I understand that there are multiple kinds of preregistration, that each kind serves a different goal, and what it takes to achieve the goal in question. Likewise, I can read a tweet or Facebook post about a preregistered paper and decide to trust it (“those keywords look good, thumbs up!”), or I can go read everything critically and carefully. Equating preregistered studies with good science is easy, and we’ve done this kind of thing before (p < .05! Must be true!). Going beyond the heuristic to think critically about what was in the preregistration and what that means for how much confidence we should have in the results…that’s much harder to do.

3. Countering a Norm in Words vs. Deeds
Now, you might be thinking: It is NOT easy to talk the talk when you’re in the [career stage, institution, or environment] that I am in! And that may be very true. But of course, even here, the talk is still easier than the walk. Talking to your adviser about the merits of clearly distinguishing between data-dependent and data-independent analyses in a paper may be a challenge…but actually convincing them to agree to DO it is probably harder. Publicly stating that you’ve preregistered something may have costs if the people around you think preregistration is silly. But asking yourself why you’re preregistering—what you hope to gain (theory falsification? Type I error control?) and how to actually implement the preregistration in a way that gets you those benefits—that’s an extra layer of effort.

So what’s the point of all this talking that I’m doing right now? It’s to acknowledge that change is hard, and costly. Anyone who tells you this is easy—that there are no tradeoffs, that we just need some new simple decision rules to replace the old ones—is oversimplifying. They are talking but not walking, in the second sense above.

But this post full of talking is also meant to be a challenge to all the talkers out there, and to myself as well. Are you really (am I really) doing what you’re advocating to the fullest extent that you can? The answer is probably no. 
So: What’s the next step?

Monday, June 26, 2017

Who to Invite for Your Next Methods and Practices Symposium

Planning a symposium or panel on methods and practices in psychology? Here's a collection of top notch speakers to consider inviting.* Inspired by a recent post on PsychMAP as well as #womenalsoknowstuffnot to mention the frequency with which people ask me to recommend female speakers because they can't think of anythese are all women. So now there is no excuse for the 100% male panel on the subject. In fact, you could easily have a 100% female panel of stellar experts (and it's been done! exactly once, as far as I know). Keep in mind that many of these scholars could also be excellent contributors to special issues and handbooks on methods and practices topics.

Here are names and institutions for potential speakers across a range of career stages. These scholars can all speak to issues that relate to our field's unfolding conversations and debates about replicability and improving research methods and practices. When possible, I've linked the name to a relevant publication as well so that you can get a sense of some of their work.

(And of course, this list is incomplete. If you or someone you know should be on it, please leave a comment with the scholar's name, position, institution, relevant speaking topics, and a link to a relevant paper if applicable!)

Samantha Anderson, PhD student, University of Notre Dame

Statistical power, replication methodology, more nuanced ways to determine the "success" of a replication study

Jojanneke Bastiaansen, Postdoc, Groningen

Citation distortion, bias in reporting 

Christina Bergmann, Max Planck Institute Nijmegen, The Netherlands

Crowd-sourced meta-analyses, open science, improving research practices in infancy research 

Dorothy Bishop, Professor, Oxford
Reproducibility, open science

Erin Buchanan, Associate Professor, Missouri State University 
Effect sizes and confidence intervals, alternatives to NHST, Bayesian statistics, statistical reporting

Katherine Button, Lecturer, University of Bath

Power estimation, replicability

Krista Byers-Heinlein, Associate Professor, Concordia University

Organizing large multi-lab collaborative studies and RRRs (she leads the ManyBabies Bilingual project, an RRR at AMPPS currently in data collection), working with hard-to-recruit/hard-to-test/hard-to-define populations (bilingual infants), and making sure the media gets your science right.

Katie Corker, Assistant Professor, Grand Valley State University
Meta-analysis, replication, perspectives on open science from teaching institutions

Angelique Cramer, Associate Professor, Tilburg University

Slow science, open science, exploratory vs. confirmatory hypothesis testing, hidden multiple-testing issues in ANOVA, replication issues in the context of psychopathology research

Alejandrina Cristia, Researcher, Ecole Normale Supérieure
Crowd-sourced meta-analyses, research practices in infancy research

Pamela Davis-Kean, Professor, University of Michigan

Large developmental data sets, replication

Elizabeth Dunn, Professor, University of British Columbia
Pre-registration, how researchers think about Bayes Factors, the NHST debate

Arianne Eason, PhD student, University of Washington

Research practices in infancy research

Ellen Evers, Assistant Professor, University of California, Berkeley

Statistical power, reliability of published work

Fernanda Ferreira, Professor, UC Davis
Open science, open access, replication, how to design appropriate replication studies when original studies involve stimuli that may be specific to certain time periods or contexts (e.g., words used in an experiment in psycholinguistics)

Jessica Flake, Postdoc, York University

Construct validation, measurement, instrument design

Susann Fiedler, Research Group Leader, Max Planck Institute for Research on Collective Goods, Bonn, Germany

Economics and ethics of science, reproducibility, publication bias, incentive structures, digital scholarship and open science

Shira Gabriel, Associate Professor, SUNY Buffalo
Editor perspective on changes in the field and implementing new ideas in journals

Kiley Hamlin, Associate Professor, University of British Columbia

How to improve methods when you study hard-to-recruit populations; personal experiences with the dangers of failing to document everything and how to prevent this problem in your own lab.

Erin Hennes, Assistant Professor, Purdue University

Simulation methods for power analysis in complex designs

Ase Innes-Ker, Senior Lecturer, Lund University
Open science, replication, peer review

Deborah Kashy, Professor, Michigan State University

Reporting practices, transparency

Melissa Kline, Postdoc, MIT

Improving practices in infancy research

Alison Ledgerwood, Associate Professor, UC Davis

Practical best practices; how to design a study to maximize what you learn from it (strategies for maximizing power, distinguishing exploratory and confirmatory research); how to learn more from exploratory analyses; promoting careful thinking across the research cycle.

Carole Lee, Associate Professor, University of Washington
Philosophy of science, peer review practices, publication guidelines

Dora Matzke, Assistant Professor, University of Amsterdam

Bayesian inference

Michelle Meyer, Assistant Professor and Associate Director, Center for Translational Bioethics and Health Care Policy at Geisinger Health System

Topics related to responsible conduct of research, research ethics, or IRBs, including ethical/policy/regulatory aspects of replication, data preservation/destruction, data sharing and secondary research uses of existing data, deidentification and reidentification, and related IRB and consent issues.

Kate Mills, Postdoc, University of Oregon 

Human neuroscience open data, multi-site collaboration

Lis Nielson, Chief, Individual Behavioral Processes Branch, Division of Behavioral and Social Research, NIH
Improving reproducibility, validity, and impact

Michèle Nuijten, PhD student, Tilberg University

Replication, publication bias, statistical errors, questionable research practices

Elizabeth Page-Gould, Associate Professor, University of Toronto

Reproducibility in meta-analysis

Jolynn Pek, Assistant Professor, York University
Quantifying uncertainties in statistical results of popular statistical models and bridging the gap between methodological developments and their application.

Cynthia Pickett, Associate Professor, UC Davis

Changing incentive structures, alternative approaches to assessing merit.

Julia Rohrer, Fellow, Deutsches Institut Für Wirtschaftsforschung, Berlin

Metascience, early career perspective on replicability issues

Caren Rotello, Professor, UMass Amherst

Measurement issues, response bias, why replicable effects may nevertheless be erroneous.

Victoria Savalei, Associate Professor, University of British Columbia

The NHST debate, how people reason about and use statistics and how this relates to the replicability crisis, how researchers use Bayes Factors.

Anne Scheel, PhD student, Ludwig-Maximilians-Universität, Munich

Open science, pre-registration, replication issues from a cognitive and developmental psychology perspective, early career perspective

Linda Skitka, Professor, University of Illinois at Chicago

Empirically assessing the status of the field with respect to research practices and evidentiary value; understanding perceived barriers to implementing best practices.

Courtney Soderberg, Statistical and Methodological Consultant, Center for Open Science

Pre-registration and pre-analysis plans, sequential analysis, meta-analysis, methodological and statistical tools for improving research practices.

Jessica Sommerville, Professor, University of Washington

Research practices in infancy research.

Jehan Sparks, PhD student, UC Davis

Practical strategies for improving research practices in one's own lab (e.g., carefully distinguishing between confirmatory and exploratory analyses in a pre-analysis plan).

Barbara Spellman, Professor, University of Virginia

Big-picture perspective on where the field has been and where it’s going; what editors can do to improve the field; how to think creatively about new ideas and make them happen (e.g., RRRs at Perspectives on Psychological Science)

Sara Steegen, PhD student, University of Leuven, Belgium

Research transparency, multiverse analysis

Victoria Stodden, Associate Professor, University of Illinois at Urbana-Champaign
Enabling reproducibility in computational science, developing standards of openness for data and code sharing, big data, privacy issues, resolving legal and policy barriers to disseminating reproducible research.

Jennifer Tackett, Associate Professor, Northwestern

Replicability issues in clinical psychology and allied fields

Sho Tsuji, Postdoc, UPenn and LSCP, Paris

Crowd-sourced meta-analysis

Anna van t'Veer, Postdoc, Leiden University

Pre-registration, replication

Simine Vazire, Associate Professor, UC Davis; Co-founder, Society for the Improvement of Psychological Science (SIPS)

Replication, open science, transparency

Anna de Vries, PhD student, Groningen

Citation distortion, bias in reporting, meta-analysis

Tessa West, Associate Professor, NYU
Customized power analysis, improving inclusion in scientific discourse

Edit (6/27/17): Note that this list doesn't even try to cover the many excellent female scholars who could speak on quantitative methods more broadly—I will leave that to someone else to compile (and if you take this on, let me know and I'll link to it here!). In this list, I'm focusing on scholars who have written and/or spoken about issues like statistical power, replication, publication bias, open science, data sharing, and other topics related to core elements of the field's current conversations and debates about replicability and improving research practices (i.e., the kinds of topics covered on this syllabus). 

Thursday, June 15, 2017

Guest Post: Adjusting for Publication Bias in Meta-Analysis - A Response to Data Colada [61]

A recent blogpost on Data Colada raises the thorny but important issue of adjusting for publication bias in meta-analysis. In this guest post, three statisticians weigh in with their perspective.

Datacolada Post [61] Why p-curve excludes ps>.05
Response of Blakeley B. McShane, Ulf Böckenholt, and Karsten T. Hansen

The quick version:
Below, we offer a six-point response to the recent blogpost by Simonsohn, Simmons, Nelson (SSN) on adjusting for publication bias in meta-analysis (or click here for a PDF with figures). We disagree with many of the points raised in the blogpost for reasons discussed in our recent paper on this topic [MBH2016]. Consequently, our response focuses on clarifying and expounding upon points discussed in our paper and provides a more nuanced perspective on selection methods such as the three-parameter selection model (3PSM) and the p-curve (a one-parameter selection model (1PSM)).

We emphasize that all statistical models make assumptions, that many of these are likely to be wrong in practice, and that some of these may strongly impact the results. This is especially the case for selection methods and other meta-analytic adjustment techniques. Given this, it is a good idea to examine how results vary depending on the assumptions made (i.e., sensitivity analysis) and we encourage researchers to do precisely this by exploring a variety of approaches. We also note that it is generally good practice to use models that perform relatively well when their assumptions are violated. The 3PSM performs reasonably well in some respects when its assumptions are violated while the p-curve does not perform so well. Nonetheless, we do not view the 3PSM or any other model as a panacea capable of providing a definitive adjustment for publication bias and so we reiterate our view that selection methods—and indeed any adjustment techniques—should at best be used only for sensitivity analysis.

The full version:
Note: In the below, “statistically significant” means “statistically significant and directionally consistent” as in the Simonsohn, Simmons, Nelson (SSN) blogpost. In addition, the “p-curve” refers to the methodology discussed in SNS2014 that yields a meta-analytic effect size estimate that attempts to adjust for publication bias.(1)

Point 1: It is impossible to definitively adjust for publication bias in meta-analysis 
As stated in MBH2016, we do not view the three-parameter selection model (3PSM) or any other model as a panacea capable of providing a definitive adjustment for publication bias. Indeed, all meta-analytic adjustment techniques—whether selection methods such as the 3PSM and the p-curve or other tools such as trim-and-fill and PET-PEESE—make optimistic and rather rigid assumptions; further, the adjusted estimates are highly contingent on these assumptions. Thus, these techniques should at best be used only for sensitivity analysis.
[For more details in MBH2016, see the last sentence of the abstract; last paragraph of the introduction; point 7 in Table 1; and most especially the entire Discussion.]

Point 2: Methods discussions must be grounded in the underlying statistical model
All statistical models make assumptions. Many of these are likely to be wrong in practice and some of these may strongly impact the results. This is especially the case for selection methods and other meta-analytic adjustment techniques. Therefore, grounding methods discussions in the underlying statistical model is incredibly important for clarity of both thought and communication.
SSN argue against the 3PSM assumption that, for example, a p=0.051 and p=0.190 study are equally likely to be published; we agree this is probably false in practice. The question, then, is what is the impact of this assumption and can it be relaxed? Answer: it is easily relaxed, especially with a large number of studies. We believe the p-curve assumptions that (i) effect sizes are homogenous, (ii) non-statistically significant studies are entirely uninformative (and are thus discarded), and (iii) a p=0.049 study and a p=0.001 study are equally likely to be published are also doubtful. Further, we know via Jensen’s Inequality that the homogeneity assumption can have substantial ramifications when it is false—as it is in practically all psychology research.
[For more details in MBH2016, see the Selection Methods and Modeling Considerations sections for grounding a discussion in a statistical model and the Simulation Evaluation section for the performance of the p-curve.]

Point 3: Model evaluation should focus on estimation (ideally across a variety of settings and metrics)
SSN’s simulation focuses solely on Type I error—a rather uninteresting quantity given that the null hypothesis of zero effect for all people in all times and in all places is generally implausible in psychology research (occasional exceptions like ESP notwithstanding). Indeed, we generally expect effects to be small and variable across people, times, and places. Thus, “p < 0.05 means true” dichotomous reasoning is overly simplistic and contributes to current difficulties in replication. Instead, we endorse a more holistic assessment of model performance—one that proceeds across a variety of settings and metrics and that focuses on estimation of effect sizes and the uncertainty in them. Such an evaluation reveals that the 3PSM actually performs quite well in some respects—even in SSN’s Cases 2-5 and variants thereof in which it is grossly misspecified (i.e., when its assumptions are violated; see Point 6 below).
[For more details in MBH2016, see the Simulation Design and Evaluation Metrics subsection.]

Point 4: The statistical model underlying the p-curve is identical to the model of Hedges, 1984 [H1984]
Both the p-curve and H1984 are one-parameter selection models (1PSM) that make identical statistical assumptions: effect sizes are homogenous across studies and only studies with results that are statistically significant are “published” (i.e., included in the meta-analysis). Stated another way, the statistical model underlying the two approaches is 100% identical and hence if you accept the assumptions of the p-curve you therefore accept the assumptions of H1984 and vice versa.
The only difference between the two methods is how the single effect size parameter is estimated from the data:
H1984 uses principled maximum likelihood estimation (MLE) while p-curve minimizes the Kolmogorov-Smirnov (KS) test statistic. As MLE possesses a number of mathematical optimality properties; easily generalizes to more complicated models such as the 3PSM (as well as others even more complicated); and yields likelihood values, standard errors, and confidence intervals, it falls on SSN to mathematically justify why they view the proposed KS approach to be superior to MLE for psychology data.(2)
[For more details in MBH2016, see the Early Selection Methods and p-methods subsections.]

Point 5: Simulations require empirical and mathematical grounding
For a simulation to be worthwhile (i.e., in the sense of leading to generalizable insight), the values of the simulation parameters chosen (e.g., effect sizes, sample sizes, number of studies, etc.) and the data-generating process must reflect reality reasonably well. Further still, there should ideally be mathematical justification of the results. Indeed, with sufficient mathematical justification a simulation is entirely unnecessary and can be used merely to illustrate results graphically.
The simulations in MBH2016 provide ample mathematical justification for the results based on: (i) the optimal efficiency properties of the maximum likelihood estimator (MLE; Simulation 1), (ii) the loss of efficiency resulting from discarding data (Simulation 2), and (iii) the bias which results from incorrectly assuming homogeneity as a consequence of Jensen’s Inequality (Simulation 3). We remain uncertain about the extent to which Cases 2-5 of the SSN simulations reflect reality and thus seek mathematical justification for the generalizability of the results. Nonetheless, they seem of value if viewed solely for the purpose of assessing the 3PSM model estimates when that model is misspecified.
[For more details in MBH2016, see the Simulation Evaluation section.]

Point 6: The 3PSM actually performs quite well in SSN’s simulation—even when misspecified.
Only in Case 1 of the SSN simulation is the 3PSM properly specified (and even this is not quite true as the 3PSM allows for heterogeneity but the simulation assumes homogeneity). SSN show that when the 3PSM is misspecified (Cases 2-5), its Type I error is far above the nominal α=0.05 level. We provide further results in the figures here.
• The blue bars in the left panel of Figure 1 reproduce the SSN result. We also add results for the 1PSM as estimated via KS (p-curve) and MLE (H1984). As can be seen, the Type I error of the 1PSM MLE remains calibrated at the nominal level. In the right panel, we plot estimation accuracy as measured by RMSE (i.e, the typical deviation of the estimated value from the true value). As can be seen, the 3PSM is vastly superior to the two 1PSM implementations in some cases and approximately equivalent to them in the remaining ones.
• In Figure 2, we change the effect size from zero to small (d=0.2); the 3PSM has much higher power and better estimation accuracy as compared to the two 1PSM implementations.
• In Figure 3, we return to zero effect size but add heterogeneity (τ=0.2). The 1PSM has uncalibrated Type I error for all cases while the 3PSM remains calibrated in Case 1; in terms of estimation accuracy, the 3PSM is vastly superior to the two 1PSM implementations in some cases and approximately equivalent to them in the remaining ones.(3)
• In Figure 4, we change the effect size from zero to small and add heterogeneity. The 3PSM generally has similar power and better estimation accuracy as compared to the two 1PSM implementations (indeed, only in Case 1 does the 1PSM have better power but this comes at the expense of highly inaccurate estimates). 

In sum, the 3PSM actually performs quite well compared to the two 1PSM implementations—particularly when the focus is on estimation accuracy as is proper; this is especially encouraging given that the 1PSM is correctly specified in all five cases of Figures 1-2 while the 3PSM is only correctly specified in Case 1 of the figures. Although these results favor the 3PSM relative to the two 1PSM implementations, we reiterate our view that selection methods—and indeed any adjustment techniques—should at best be used only for sensitivity analysis.

(1) The same authors have developed a distinct methodology also labelled p-curve that attempts to detect questionable research practices. This note does not comment on that methodology.
(2) Both MLE and KS are asymptotically consistent and thus asymptotically equivalent for the statistical model specified here. Consequently, any justification will likely hinge on small sample properties which can be mathematically intractable for this class of models. Justifications based on robustness to model specification are not germane here because if a different specification deemed more appropriate, the model would be re-specified according to this more appropriate specification and that model estimated.
(3) A careful reading of SNS2014 reveals that the p-curve is not meant to estimate the population average effect size. As shown here and in MBH2016, it cannot as no 1PSM can. This is important because we believe that the heterogeneous effect sizes (i.e., τ > 0) are the norm in psychology research.

[H1984] Hedges, L. V. (1984). Estimation of effect size under nonrandom sampling: The effects of censoring studies yielding statistically insignificant mean differences. Journal of Educational and Behavioral Statistics, 9, 61–85.

[MBH2016] McShane, B.B., Böckenholt, U., and Hansen, K.T. (2016), “Adjusting for Publication Bias in Metaanalysis: An Evaluation of Selection Methods and Some Cautionary Notes.” Perspectives on Psychological Science, 11(5), 730-749.

[SNS2014] Simonsohn,U., Nelson, L.D. and Simmons, J.P. (2014) “p-Curve and Effect Size: Correcting for Publication Bias Using Only Significant Result”, Psychological Science, 2014, Vol.9(6), 666-681.

Monday, April 17, 2017

Everything is F*cking Nuanced: The Syllabus

Psych 342: Everything is Fucking Nuanced
Prof. Alison Ledgerwood
Class meetings: Ongoing, forever

A common theme in discussions about replicability and improving research practices across scientific disciplines has been debating whether or not science (or a specific scientific discipline) is “in crisis.” The implicit logic seems to be that we have to first establish that there is a crisis before research practices can begin to improve, or conversely, that research practices need not change if there is not a crisis. This debate can be interesting, but it also risks missing the point. Science is hard, reality is messy, and doing research well requires constantly pushing ourselves and our field to recognize where there is room for improvement in our methods and practices.

We can debate how big the sense of crisis should be till the cows come home. But the fact is, whether you personally prefer to describe the current state of affairs as “science in shambles” or “science working as it should,” we have a unique opportunity right now to improve our methods and practices simply because (a) there is always room for improvement and (b) we are paying far more attention to several key problems than we were in the past (when many of the same issues were raised and then all too often ignored; e.g., Cohen, 1992; Greenwald, 1975; Maxwell, 2004; Rosenthal, 1979).

In this class, we will move beyond splashy headlines like “Why most published research findings are false,” “Everything is fucked,”* and “Psychology is in crisis over whether it’s in crisis” to consider the less attention-grabbing but far more important question of Where do we go from here? Along the way, we will learn that the problems we face are both challenging and nuanced, and that they require careful and nuanced solutions.

Week 1 - Introduction to the F*cking Nuance: How we got here, and the single most important lesson we can learn going forward
Spellman, B. A. (2015). A short (personal) future history of Revolution 2.0. Perspectives on Psychological Science, 10, 886-899.

Ledgerwood, A. (2016). Introduction to the special section on improving research practices: Thinking deeply across the research cycle. Perspectives on Psychological Science, 11, 661-663.


Week 2: Estimating Replicability is F*cking Nuanced

Open Science Collaboration (2015). Estimating the reproducibility of psychological science. Science, 349(6251), aac4716.

Etz, A., & Vandekerckhove, J. (2016). A Bayesian Perspective on the Reproducibility Project: Psychology. PLoS ONE 11(2): e0149794. 

Stanley, D. J., & Spence, J. R. (2014). Expectations for replications: Are yours realistic? Perspectives on Psychological Science, 9, 305-318.

Anderson, S. F., & Maxwell, S. E. (2016). There’s more than one way to conduct a replication study: Beyond statistical significance. Psychological Methods, 21, 1.

Week 3: Power is F*cking Nuanced

Maxwell, S. E. (2004). The persistence of underpowered studies in psychological research: Causes, consequences, and remedies. Psychological Methods, 9, 147-163.

Button, K. S., Ioannidis, J. P., Mokrysz, C., Nosek, B. A., Flint, J., Robinson, E. S., & Munafò, M. R. (2013). Power failure: why small sample size undermines the reliability of neuroscience. Nature Reviews Neuroscience, 14, 365-376.

Perugini, M., Gallucci, M., & Costantini, G. (2014). Safeguard power as a protection against imprecise power estimates. Perspectives on Psychological Science, 9, 319-332.

McShane, B. B., & Böckenholt, U. (2014). You cannot step into the same river twice: When power analyses are optimistic. Perspectives on Psychological Science, 9, 612-625.


Week 4: Selecting an Optimal Research Strategy is F*cking Nuanced

Finkel, E. J., Eastwick, P. W., & Reis, H. T. (2017). Replicability and other features of a high-quality science: Toward a balanced and empirical approach. Journal of Personality and Social Psychology, 113, 244-253.

Miller, J., & Ulrich, R. (2016). Optimizing research payoff. Perspectives on Psychological Science, 11, 664-691.

Week 5: Interpreting Results from Individual Studies is F*cking Nuanced

De Groot, A. D. (2014). The meaning of “significance” for different types of research [translated and annotated by Eric-Jan Wagenmakers, Denny Borsboom, Josine Verhagen, Rogier Kievit, Marjan Bakker, Angelique Cramer, Dora Matzke, Don Mellenbergh, and Han LJ van der Maas]. Acta psychologica, 148, 188-194.

Schönbrodt, F. D., & Perugini, M. (2013). At what sample size do correlations stabilize? Journal of Research in Personality, 47, 609-612. 

Ledgerwood, A., Soderberg, C. K., & Sparks, J. (2017). Designing a study to maximize informational value. In J. Plucker & M. Makel (Eds.), Toward a more perfect psychology: Improving trust, accuracy, and transparency in research (pp. 33-58). Washington, DC: American Psychological Association. (See section on “Distinguishing Exploratory and Confirmatory Analyses.”)

Week 6: Maximizing What We Learn from Exploratory (Data-Dependent) Analyses is F*cking Nuanced

Steegen, S., Tuerlinckx, F., Gelman, A., & Vanpaemel, W. (2016). Increasing transparency through a multiverse analysis. Perspectives on Psychological Science, 11, 702-712.

Sagarin, B. J., Ambler, J. K., & Lee, E. M. (2014). An ethical approach to peeking at data. Perspectives on Psychological Science, 9, 293-304.

Wang, Y., Sparks, J., Gonzales, J., Hess, Y. D., & Ledgerwood, A. (2017). Using independent covariates in experimental designs: Quantifying the trade-off between power boost and Type I error inflation. Journal of Experimental Social Psychology, 72, 118-124.


Week 7: The Role of Direct, Systematic, and Conceptual Replications is F*cking Nuanced

Pashler, H., & Harris, C. R. (2012). Is the replicability crisis overblown? Three arguments examined. Perspectives on Psychological Science, 7, 531-536.

Roediger, H. L. (2012). Psychology’s woes and a partial cure: The value of replication. APS Observer, 25, 9.

Fabrigar, L. R., & Wegener, D. T. (2016). Conceptualizing and evaluating the replication of research results. Journal of Experimental Social Psychology, 66, 68-80.

Crandall, C. S., & Sherman, J. W. (2016). On the scientific superiority of conceptual replications for scientific progress. Journal of Experimental Social Psychology, 66, 93-99.

Week 8: Thinking Cumulatively about Evidence is F*cking Nuanced 

Braver, S. L., Thoemmes, F. J., & Rosenthal, R. (2014). Continuously cumulating meta-analysis and replicability. Perspectives on Psychological Science, 9, 333-342.

Tsuji, S., Bergmann, C., & Cristia, A. (2014). Community-augmented meta-analyses: Toward cumulative data assessment. Perspectives on Psychological Science, 9, 661-665.

McShane, B.B. and Böckenholt, U. (2017). Single paper meta-analysis: Benefits for study summary, theory-testing, and replicability. Journal of Consumer Research, 43, 1048-1063.

Week 9: Dealing with Publication Bias in Meta-Analysis is F*cking Nuanced

Inzlicht, M., Gervais, W., & Berkman, E. (September 11, 2015). Bias-Correction Techniques Alone Cannot Determine Whether Ego Depletion is Different from Zero: Commentary on Carter, Kofler, Forster, & McCullough, 2015.

McShane, B.B., Böckenholt, U., and Hansen, K.T. (2016). Adjusting for publication bias in meta-analysis: An evaluation of selection methods and some cautionary notes. Perspectives on Psychological Science, 11, 730-749.

Week 10: Incentive Structures Need Some F*cking Nuance

Maner, J. K. (2014). Let’s put our money where our mouth is: If authors are to change their ways, reviewers (and editors) must change with them. Perspectives on Psychological Science, 9, 343-351. 

Tullett, A. M. (2015). In search of true things worth knowing: Considerations for a new article prototype. Social and Personality Psychology Compass 9: 188–201.

Nosek, B. A., Spies, J. R., & Motyl, M. (2012). Scientific utopia: II. Restructuring incentives and practices to promote truth over publishability. Perspectives on Psychological Science, 7, 615-631.

Pickett, C. (2017, April 12). Let's Look at the Big Picture: A System-Level Approach to Assessing Scholarly Merit. Retrieved from

Week 11: Keep Reading...

*Note that in contrast to the other two headlines mentioned here,

Sanjay’s Everything is Fucked” title is obviously intentionally hyperbolic for comedic effect. He goes on to write: “What does it mean, in science, for something to be fucked? …In this class we will go a step further and say that something is fucked if it presents hard conceptual challenges to which implementable, real-world solutions for working scientists are either not available or routinely ignored in practice.” His post, as well as the other two articles noted here, raise important issues in thoughtful ways. But if you just focus on the titles, as many people have, you might find yourself sliding into a polarizing argument about how bad things are or aren’t. And this polarizing argument can distract us from the more pressing question of how do we get better, right now, starting today.