social psychology’s crisis of confidence

A recent NYT Magazine article has prompted colleagues and friends alike to ask me, what’s going on in your discipline? Perhaps you’ve heard that there’s a “crisis” in social psychology. It’s been covered prominently–e.g.,  NYT, AtlanticSlateWikipedia. This essay is my attempt at explaining.

Introduction

The present crisis in social psychology can be traced to two highly publicized events in 2010 and 2011—publication of impossible findings using accepted methods of rigorous psychological science (Bem, 2011; Simmons, Nelson, & Simonsohn, 2011), and cases of fraud, notably Diederick Stapel (Finkel, Eastwick, & Reis, 2015; Yong, 2012). These events prompted numerous special issues on methodological rigor, replication, and transparency (e.g., Ledgerwood, 2016; Stangor & Lemay, 2016), large-scale efforts to replicate findings in flagship journals (Open Science Collaboration, 2015), and ominous commentaries from leaders of the field (e.g., Kahneman (2012), “I see a train wreck looming”). The current crisis echoes that of prior decades (Elms, 1975; Gergen, 1973; McGuire, 1973), but has notable differences (Hales, 2016; Spellman, 2014). First, I discuss how common research practices undermine our ability to make valid inferences. Second, I elaborate on why the field is grappling with these issues, and how the current crisis differs from those of the past. I conclude with recommendations for moving forward.

Common (and “Questionable”) Practices

Many research practices in social psychology (e.g., selectively reporting a subset of measures used) have long been recognized as “questionable” because they increase false inferences (e.g., Greenwald, 1975; Rosenthal, 1979). Yet, these practices remain surprisingly common (John, Loewenstein, & Prelec, 2012), due to perverse incentives, norms, or lack of awareness (Nosek, Spies, & Motyl, 2012). Many questionable practices are justifiable sometimes (particularly when reported transparently), though all of them increase the likelihood of false inferences (Nosek et al., 2012 for review). Here, I focus on the practice I see as most central to the current crisis.

The principle common research practice to the present crisis is opaque and misleading reporting of researcher degrees of freedom (Simmons et al., 2011). Researcher degrees of freedom are the set of possible methodological and statistical decisions in the research process. For example, should outliers be excluded? Which items should be used? It is rare, and sometimes impractical, to have a priori predictions about how to make all, or even most, of these decisions. Thus, it is common practice to explore alternatives after seeing data. In a given dataset, slightly different alternatives can lead to vastly different conclusions, and there may be no objective justification for taking one alternative over another (Gelman & Loken, 2013). For example, imagine a test that is non-significant when data are log-transformed, and significant when they are truncated. These two approaches may be equally justified for skewed data. However, we often rationalize in favor of alternatives that meet our expectations, in this case, statistical confirmation of our hypothesis (John et al., 2012). There are many other biases that lead us to favor positive alternatives (e.g., motivated reasoning or hindsight bias). Recall Richard Feynman’s advice to Caltech’s class of 1974, in science “the first principle is that you must not fool yourself – and you are the easiest person to fool.”

Furthermore, bias-prone decisions compound to exacerbate false inferences, even when decisions are seemly bias-free. By way of analogy, imagine the research process is a garden of forking paths. Each fork in the path represents a decision (e.g., truncating data), which eventually leads to an outlet (representing the conclusion). The long and winding path taken through this labyrinth may be justified by scientific logic at each juncture. However, because there are so many junctures, it is improbable that any two scientists (or even the same scientist a year from now) would take the same path through the garden. Deviation at a single fork can lead to disparate outlets, because new decisions are informed by data that were altered by previous decisions (Gelman & Loken, 2013). This is how 29 research teams can examine the same dataset with the same hypothesis, and come to 29 different conclusions (Silberzahn et al., 2017). When decisions are not determined a priori, they are inevitably guided by data and biases that influence the validity of inferences.

Research degrees of freedom increase the likelihood of false inferences, however they do not intrinsically undermine scientific progress. Nonetheless, it is not only common practice to maintain flexibility in design and analysis (Gardner, Lidz, & Hartwig, 2005; Ioannidis, 2005), it is also common to publish results as if only a single path was explored, or even as if a single path was predetermined (Begley & Ellis, 2012; Bem, 2003; Giner-Sorolla, 2012). Such presentation makes it challenging to distinguish between confirmatory (more reliable) and exploratory (more tentative) research. Without reliable representation of the current evidence, it is difficult to determine the degree to which an effect is understood and valid, as well as where to place future research efforts. The regularity of many researcher degrees of freedom accompanied by opaque or misleading reporting is central to the current crisis.

Why we are Reeling

Social psychology is grappling with a crisis (again), because formerly theoretical concerns about replicability (Elms, 1975; Gergen, 1973; McGuire, 1973), have been made tangible by empirical findings (Bem, 2011; Simmons et al., 2011) and fraud (e.g., Stapel)—both of which received considerable attention beyond ivory towers. A Google News search of “replication crisis and social psychology” reveals over 7,000 articles in the last few years including prominent outlets such as NYT, BBC, and WSJ. Scholars agree that outright fraud is a problem, but a rare one, and thus, not a primary concern. In contrast, questionable research practices are concerning because they are so common (John et al., 2012) and can result in impossible findings (Simmons et al., 2011). Many point to Daryl Bem’s (2011) paper on “precognition” as the catalyst of the present crisis. The paper, published in JPSP, appears to show that people have extrasensory perception. The distinguished Lee Ross, who served as peer reviewer, said of it, “clearly by the normal rules that we [used] in evaluating research, we would accept this paper… The level of proof here was ordinary. I mean that positively as well as negatively. I mean it was exactly the kind of conventional psychology analysis that [one often sees], with the same failings and concerns that most research has” (Engber, May 2017). Bem empirically arrived at an improbable conclusion (ESP exists) using common practices for entry into our flagship journal. This prompted Simmons and colleagues (2011) to use the same common practices to conduct an experiment that came to an impossible conclusion (that listening to certain songs can change the listeners’ age). These events led many social psychologists to question common practices, and revisit theoretical concerns of the past.

This Time is Different

The current crisis echoes that of prior decades (Gergen, 1973; McGuire, 1973), even centuries (Allport, 1968; Schlenker, 1974), in that it is concerned with replicability (Stangor & Lemay, 2016)—and rightfully so. The transparent communication of methods that enables scientific knowledge to be reproduced is the defining principle of the scientific method, and perhaps the only quality separating scientific belief from other beliefs (Nosek et al., 2012; Kuhn, 1962; Lakatos, 1978; Popper, 1934). Just as replicability is a sign of a functioning science, so too may be the perpetual self-conscious grappling with claims for scientific status. Psychologists and philosophers of science have long debated the scientific status of social psychology (Schlenker, 1974). In fact, such self-critical angst can be traced to the historical origin of the discipline when we differentiated ourselves from philosophy (Danziger, 1990). Yet, there are notable differences between the “crisis of confidence” in the 1970s (Elms, 1975), and that of today.

First, the former crisis was largely characterized by concerns about external validity, whereas today’s crisis in primarily concerned with threats to statistical conclusion validity (Hales, 2016). For example, McGuire (1967, 1973) worried that our focus on the “ingenious stage manager” of the laboratory produces conditions that render null results meaningless and positive result banal, while at the same time being unlikely to replicate outside the laboratory. Another example is found in Gergen (1973), who argued that social psychological effects are hopelessly dependent on the historical and cultural context in which they are tested, and thus impossible to generalize to principles in a traditional scientific sense.

In contrast, today’s crisis is concerned with the validity of statistical conclusions drawn from an experiment (Hales, 2016). Instead of asking, “does the effect generalize?” We are now asking, “does the effect exist at all?” In the previous crisis, Mook (1983) famously argued in defense of external validity. Laboratory experimentation need only concern itself with “what can happen” (as opposed to “what does happen”). It is the theory tested by a particular experiment that generalizes, not the experiment itself. A compelling defense, however, the assertion rests on the validity of statistical conclusions. The contemporary crisis is grappling with the assertion that common practices not only demonstrate “what can happen,” but that they can be used to show that “anything can happen.” If anything can happen in our laboratories, what differentiates our science from science fiction?

A second way in which the current crisis is different is related to changes in technology and demographics (Spellman, 2014). Technological changes are eliminating space concerns, and increasing speed and transparency of communication. One consequence of which is that people who fail to replicate research can more readily share that information, and see that they are not alone. Thus, it is easier to be critical of the finding itself rather than assume a methodological mistake was made (McGuire, 1973). Similarly, increases in diversity of the field have precipitated more critical questioning of the status quo. In brief, today’s crisis has elements of a social revolution that were missing from prior crises (Spellman, 2014). These factors will fuel a more persistent push for change this time around.

Recommendations

I conclude with recommended changes to improve confidence in our science. In fear of presumption, I follow McGuire (1973) in submitting my suggestions as koans—full of paradox and caveat; they are intended to be at once provocative and banal.

Koan 1:“Does a person who practices with great devotion still fall into cause and effect?…No, such a person doesn’t.”

Preregister

In 2000, the National Heart Lung and Blood Institute (NHLBI) initiated a policy requiring all funded pharmaceutical trials to prospectively register outcomes in an uneditable database, ClinicalTrials.gov. After the policy went into effect, the prevalence of positive results reported in NHLBI-funded trials dropped from 57% to 8% (Kaplan & Irvin, 2015). Preregistration improves confidence in published findings because it reduced selective reporting. More broadly, preregistration makes researcher degrees of freedom more apparent, reduces opaque and misleading reporting (Nosek, Ebersole, DeHaven, & Mellor, 2017), and allows us to better distinguish between confirmatory and exploratory research (Nosek et al., 2012).

Koan 2: “Having our cake and eating it too.”

Explore Small, Confirm Big

There is growing recognition that “small sample sizes hurt the field in many ways” (Stangor & Lemay, 2016), because it undermines both statistical confidence and the perception of rigor (Button et al., 2013). However, there is a trade-off to reckon with—it is resource expensive and unreasonable to test all hypotheses with large samples (Baumeister, 2016). We can have our cake and eat it too if we instead explore new questions with small samples to determine which are worth putting to larger confirmatory tests (Sakaluk, 2016). True, so long as we call a spade a spade. Small-N studies should leave the reader with the impression that the effect is tentative and exploratory, and then attempt to confirm “big” (Baumeister, 2016; Dovidio, 2016). Though, there is disagreement over implementation. Should there be separate journals for small-exploratory and large-confirmatory studies (Baumeister, 2016)? Should those studies appear in sequence in the same paper (Stangor & Lemay, 2016), or in different sections of the same journal (Dovidio, 2016)? My contention is that any of these approaches will be better than the status quo, so long as “truth in advertising” is maintained.

Koan 3:“He who pays the piper calls the tune.”

Gatekeepers and Replicators

Editors and reviewers tacitly agree that replicability is foundational to confidence and scientific progress, yet few journals incentivize replication. A recent study found that, of 1151 psychology journals reviewed, only 3% explicitly stated that they accept replications (4.3% of 93 social psychology journals; Martin & Clarke, 2017). If researchers could be assured that replications get published, more would be conducted. However, what makes for a constructive replication is widely debated. A promising approach is to test hypotheses as exactly as possible, while simultaneously testing new conditions that refine and generalize (Hüffmeier, 2016). Publishers must provide carrots to replicate, preregister, increase sample size, etcetera, or, as Nosek and colleagues suggest (2012), let us do away with them. Make publishing trivial and engage in post-publication peer review, they say. This allows researchers to decide when content is worth publishing and shifts the priority of evaluators to methodological, theoretical, and practical significance, and away from apparent statistical significance. Registered reports prompt a similar shift by enabling results-blind peer review (Munafò et al., 2017). Publishers could act as managers of peer review, focusing solely on bolstering confidence and rigor in the process, instead of also engaging in dissemination, marketing, and archiving. This is a worthy and feasible objective in the internet age (Nosek et al., 2012).

Koan 4: “What is the way? …An open-eyed man falling into the well.”

Transparency

The ultimate solution to our confidence dilemma is openness (Nosek et al., 2012). Make more information from our studies available. Preregistration helps make the research plan transparent, but the field would also benefit from changing norms around sharing and archiving data, materials, and workflows (Simonsohn, 2013; Wicherts, Bakker, & Molenaar, 2011; Wicherts, Borsboom, Kats, & Molenaar, 2006). More transparency not only addresses fabrication, it also enables verification, correction, and aggregation of knowledge—all of which bolster confidence in (and progress of) science. There is concern that greater transparency unveils the messy complexity and conflicting evidence of our science. That it enables science deniers and other malevolent critics in their efforts to mislead the public. To this I say, “fools believe and liars lie,” regardless of truth or access. In my admittedly optimistic view, earnestly open presentation wins confidence in the long run. For example, scientists who concede failures, explore reasons for failure, or are transparent in their publication of failures (as opposed to denying their validity, hiding them, or not acting) are perceived as more able and ethical (Ebersole, Axt, & Nosek, 2016). Scientists overestimate the negative consequences of a failed replications and transparent reporting (Fetterman & Sassenberg, 2015).

Conclusion

The present crisis is not entirely new, but it has critical difference. If we can use common research practice to find the impossible, where does that leave our science? I venture that these koan may move us to embrace our science not as history entirely (Gergen, 1973) but perhaps as evidence-based history. So too, in the style of Rozin (2001), may we start to embrace the exploratory and narrative nature of our present science. Perhaps then, we will again find our confidence.

References (click here)

 

Advertisements

come say hi at SPSP – coffee, sugar, and climate change – open and reproducible science

This week, at the society for personality and social psychology’s annual convention, I’m speaking in a symposium, rethinking health behavior change. I will talk about a study in which we* tested strategies to help people reduce the amount of sweetener added to their daily coffee (ideally without reducing enjoyment of it**). I’m also presenting a poster on how people talk to others about making behavioral changes that affect the environment.

One thing that excites me about these studies–they represent my first (admittedly clumsy) attempts at being completely reproducible and open with my science. Datasets, R analysis scripts, hypotheses, and all other study materials are publicly available***, and were preregistered****.

Openness and reproducibility in science fascinate me—both as a topic of research and as a guiding principle for my own research. Since starting graduate school, I have preregistered (nearly) all of my studies and have been working toward making the entire process transparent. I’ve also been learning how to write reproducible code in R. It has been challenging… you know, for the obvious reasons… misaligned incentives, human fallibility, complexity, and time. BUT, I’ve learned a lot (i think*****), and it has made me a better scientist (i think******). If nothing else, I can now make these cool graphs (below) for conference talks (and next time I won’t have to spend way too much time trying to make them look pretty*******).

Psych friends, come say hi at SPSP. Here’s the time and location for my talk and poster (and related scripts and files, here and here). Or, let’s just get a drink.

*me, Traci Mann, and Tim (our coffee connoisseur collaborator).

**that’s the hard part… sugar is yummy.

*** public project pages for the “coffee study” and “social message framing study” (the one climate change).

****an uneditable public archive of the study plan that is time-stamped prior to collecting (or looking at) data.

*****i welcome feedback and comments (particular on my R code). let me know if you find errors or have suggestions for improvement.

******hard to test empirically. though I’m pretty darn sure reproducibility and openness make Science better.

*******the beauty of reproducible code.

Sneak peek at SPSP presentation figures.

coffee

^Here’s the code (viewable in any web browser).

image-1-16-17-at-3-03-pm

^Here’s the code.

p.s. HT to Simine Vazire whose blog inspired the above footnote style. #usefulbloghack.

What Do We Want our Scientific Discourse to Look Like?

I was recently quoted in an article appearing in the Observer, a publication of Association for Psychological Science. In the article Alison Ledgerwood quotes from a diverse set of voices in psychology on the topic of scientific discourse in part in response to Susan Fiske’s piece in the Observer. Fiske takes issue with methodological critics of psychological science (who she referred to as “methodological terrorists” in an earlier draft circulated online). Her article promoted many responses (see here) and a call led by Ledgerwood to write a more diverse (and less status-driven) article for the Observer on the topic. True to form, Alison quoted my writing fairly, and elegantly brought together many other contributions.

Here, I provide my small contribution in its entirety.

We would serve each other, and science as a whole, better if we treated critique and communication of science as an open and humble process of discovery and improvement. To this end, I would like to see our scientific discourse focus more on methodology and evidence. This is easier said than done. Criticisms of the science are often construed as criticisms of the scientist. Even when we, as scientists, appreciate the criticism and recognize its scientific value, it still evokes concerns that others will lose trust in us and in our research. It is no wonder people are distressed by methodological criticism. However, focusing our discourse on methodology and evidence, with more awareness of how tone and context influence others’ perceptions of the scientist whose work is under the microscope, will help ensure healthy development of our science. Second, I would like to see an increase in open and humble scientific discourse. Openness may make our mistakes and shortcomings more apparent, and it may make it easier for others to critique our work, but it will surely improve our science. If we simultaneously place more value on humble communication, I expect criticisms will feel less personal and be easier to swallow as well. Finally, as a graduate student, I feel vulnerable publicly stating my thoughts on criticism and openness in science, which speaks to the climate of our discourse. It is essential that we have a communication environment in which graduate students, post-docs, and junior faculty from all backgrounds are rewarded for humbly and openly presenting methodologically sound ideas, research, and criticisms.

Meehl on theory testing, never gets old.

The position of Popper and the neo-Popperians is that we do not “induce” scientific theories by some kind of straightforward upward seepage from the clearly observed facts, nor do we “confirm” theories as the Vienna positivists supposed. All we can do is to subject theories—including the wildest and “unsupported” armchair conjectures (for a Popperian, completely kosher)’— to grave danger of refutation…

A theory is corroborated to the extent that we have subjected it to such risky tests; the more dangerous tests it has survived, the better corroborated it is. If I tell you that Meehl’s theory of climate predicts that it will rain sometime next April, and this turns out to be the case, you will not be much impressed with my “predictive success.” Nor will you be impressed if I predict more rain in April than in May, even showing three asterisks (for p < .001) in my t-test table! If I predict from my theory that it will rain on 7 of the 30 days of April, and it rains on exactly 7, you might perk up your ears a bit, but still you would be inclined to think of this as a “lucky coincidence.” But suppose that I specify which 7 days in April it will rain and ring the bell; then you will start getting seriously interested in Meehl’s meteorological conjectures. Finally, if I tell you that on April 4th it will rain 1.7 inches (.66 cm), and on April 9th, 2.3 inches (.90 cm) and so forth, and get seven of these correct within reasonable tolerance, you will begin to think that Meehl’s theory must have a lot going for it. You may believe that Meehl’s theory of the weather, like all theories, is, when taken literally, false, since probably all theories are false in the eyes of God, but you will at least say, to use Popper’s language, that it is beginning to look as if Meehl’s theory has considerable verisimilitude, that is, “truth-like-ness.”

Meehl, P. E. (1978). Theoretical risks and tabular asterisks: The slow progress of soft psychology. Journal of Consulting and Clinical Psychology, 46, 806–834. doi:10.1037//0022-006X.46.4.806

Can Theory Change What it is a Theory About?

In Beyond Freedom and Dignity B.F. Skinner writes, “no theory changes what it is a theory about; man remains what he has always been.” By this Skinner means that the underlying rules or processes that guide human behavior are constant, and that knowledge of these processes does not change their nature. However, throughout the social psychological literature we see suggestions of just the opposite—knowledge of a psychological process can change the psychological process. For example, Schmader (2010) provides evidence that simply teaching people about stereotype threat may “inoculate them against its effects.” The theory of social identity threat postulates that people are sensitive to contexts that threaten their identity, and when such a situation is detected people engage in ruminative conflict that can distract them enough to undermine their performance in that setting. Schmader is claiming that giving people knowledge of psychological processes predicted by theory changes the processes that unfold. This point raises several important questions: what is a psychological theory? Does psychological theory describe stable processes in the Skinnerian sense? Can we think of psychological theory in the same way that we think about theories of say physics or biology? If we believe theory must have some element of stability (e.g., if we believe light traveled at the same speed in the middle ages as it does today), and that theories exist out side of and are independent from our knowledge of their existence (e.g. the theory of special and general relativity existed before Einstein identified them, and his discovery did not change their quality), then can we classify social psychological theories as theories? My sense is no. Or maybe we need to modify our definition of what qualifies as a theory. Or perhaps our definition of stability in the processes that underlie phenomena and our belief that observation is independent from underlying processes needs modification.

References

Schmader, T. (2010). Stereotype Threat Deconstructed. Current Directions in Psychological Science, 19, 14–18. doi:10.1177/0963721409359292

 

 

a thought on personal record keeping

The weight of what has gone undocumented can be burdensome. If you are like me, you may find the struggle to find a balance between experiencing and recording life taxing. However, I believe the record keeping process holds the potential to enrich what has been lived and release the pressure of experience, the pressure to hold onto memories. Writing relieves the mental strain required to remember, clearing the way for fuller experience of the current moment. But too much record keeping is like watching the sun set over the Taj Mahal through a video camera–You’re so busy recording what’s happening that you fail to truly experience the happening. Writing about past experiences is never an act of transcription nor is it an act independent of the present. The act recreates the memory, it attempts to reflect what was felt, and in doing so it reshapes your present moment.

 

impression management and open science

I love this Charles H. Cooley (1902, p. 320) quote on how self-presentational concerns have institutional and professional forms (including in science, gasp!)

If we never tried to seem a little better than we are, how could we improve or “train ourselves from the outside inward?” And the same impulse to show the world a better or idealized aspect of ourselves finds an organized expression in the various professions and classes, each of which has to some extent a cant or pose, which its members assume unconsciously, for the most part, but which has the effect of a conspiracy to work upon the credulity of the rest of the world. There is a cant not only of theology and of philanthropy, but also of law, medicine, teaching, even of science—perhaps especially of science, just now, since the more a particular kind of merit is recognized and admired, the more it is likely to be assumed by the unworthy.

The unveiling of fraudulent research among highly acclaimed scientists along with the advent of new computing and archiving technologies has driven a recent (depending on how you measure it) push from within the scientific community for more “open” practices. The debate around open science and reluctance in adopting its practices are rarely discussed in terms of interpersonal processes. However, discussions of open science are discussions about the presentation of scientific research to other scientists and the public. I think the relevance of impression management processes to calls for more openness in science is an area worth exploring in more detail. I’d like to write more on this, please post in the comments if you know of anyone who has written on this topic.

References

Coole, C.H. (1902). Human nature and the social order. New York, NY: C. Scribner’s sons.