SIMCHI-LEVI: Behavioral Science’s Credibility Is At Risk. Replication Studies Can Help

NOTE: This blog is a repost of one originally published at the Informs blogsite ( click here). We thank David Simchi-Levi for permission to repost.

Several scientific disciplines have been conducting replication initiatives to investigate the reliability of published research results. Replication studies are particularly important in social sciences for creating and advancing the state of knowledge. Transparency plans such as data disclosure policies and pre-registration have undoubtedly improved the standards for future studies.  Replication studies help improve the level of confidence in previously-published results.

In “A Replication Study of Operations Management Experiments in Management Science” (Andrew M. Davis, Blair Flicker, Kyle Hyndman, Elena Katok, Samantha Keppler, Stephen Leider, Xiaoyang Long and Jordan D. Tong, Management Science), the authors investigate the replicability of a subset of laboratory experiments in operations management published in Management Science in 2020 and earlier to better understand the robustness, or limits, of the previously published results.

The research team, which included eight scholars from five research universities, carefully selected ten influential experimental papers in operations management based on survey-collected preferences of the operations management community more broadly. These papers covered six of the key OM topics: inventory management, supply chain contracts, queuing, forecasting, and sourcing. To control for subject-pool effects, the team conducted independent replications for each paper at two different research laboratories. The goal was to establish robust and reliable results with a statistical power of 90% at a 5% significance level.

The research team categorized replication outcomes based on p-values. When a paper’s primary hypothesis was replicated at both research sites, the team label the outcome as a “full” replication. A “partial” replication occurred when the primary hypothesis was replicated at one of the sites. And finally, when the primary hypothesis failed to replicate at either site, the authors label the outcome as a “no” replication.

Among the ten papers included in this study, six achieved full replication, two achieved partial replication, and two did not replicate. While it is encouraging to observe full replications, there is value in understanding why papers did not fully replicate. Non-replications provided interesting insights that contributed to our understanding of the research topics as well as methods.

An additional facet of the study was a survey conducted by the authors to collect predictions about the likelihood of replication of the results in papers in our study, from operations management researchers in general and specifically from OM researchers engaged in behavioral work. Interestingly, for both respondent groups, higher predictions of replication were positively associated with replication success; however, the team found that the researchers in the behavioral operations management field demonstrated more optimism about the likelihood of replication. However, overall prediction accuracy did not significantly differ between the behavioral and non-behavioral communities within operations.

This study has at least three important implications for the operations management community. First, it establishes a level of certainty about the validity, and in some cases limitations, of some of the most prominent laboratory experimental results in our field. Behavioral researchers, and those who draw on behavioral insights in analytical or empirical work, can leverage the study findings as a source of confidence about the results we tested.

Second, the study contributes interesting insights about the transferability of findings between the in-person and online data collection methods. Due to COVID-19, in some cases, the authors ran online versions of the original experiments and saw that in some cases they did indeed replicate despite the substantive differences. The COVID-19 pandemic more broadly caused an increase in online modes of data collection and remote interactions with participants, and therefore it became important to have findings that indicate when and why results can replicate across modalities and when they do not.

Third, the study initiates what we hope becomes a new norm in behavioral operations management for which this paper can serve as a foundation.  We hope that similar operations management replication projects will become prevalent in the future.  This should provide incentives for researchers to carefully document their methods in a way that will make it possible for others to replicate their results.  Additionally, a stronger norm of independently conducted replications can help disincentivize researchers from engaging in fraud as well as identify existing fraudulent data.

There are several trade-offs that need to be considered in replication studies. There have now been several replication projects in psychology, economics, and operations. Each project has taken a different approach in terms of the paper selection method, author team size and structure, the number of sites per paper, and replication type.

Some projects adopt a mechanical approach, replicating papers from specific journals within a defined timeframe, while others, select a list of papers from various journals based on an open nomination process. The replication study in the Management Science paper employed a hybrid approach, combining mechanical and selective inclusion. This allowed the research team to create a representative list of papers while also incorporating community feedback.

Replicating more papers is desirable, but it comes with increased costs and coordination challenges. Projects that replicate a larger number of papers tend to have larger, decentralized teams. In contrast, the current project formed a centralized eight-author team to ensure process consistency and coordination. The team communicated regularly and made decisions jointly, leveraging the expertise of each team member.  They also communicated with the authors of original papers throughout the replication process. For all selected papers, the original study authors shared their preferences about the hypotheses to study, shared and/or provided feedback on the materials used (software, instructions…) and the analysis, and were also given an opportunity to write responses to the replication reports.

Replication studies can choose to replicate each paper at one site or multiple sites. Replicating at multiple sites helps mitigate idiosyncratic differences among labs and provides a clearer understanding of the generalizability of results. Therefore, this research team conducted a replication study for each paper at two sites.

Replication studies can opt for either exact replications, following the original protocol, or close replications, introducing some material differences while documenting them explicitly. The choice of replication type depends on the goals of the study and the interpretation of the results. Although the initial intention of the research team was to conduct exact replications, this was not always possible.  All deviations from original protocols, intentional as well as unintentional, are clearly documented.

In conclusion, this replication study in operations management provides valuable insights into the validity and transferability of experimental results. It enhances the confidence of researchers in the field and contributes to the ongoing replication movement. The research findings shed light on the intricacies of designing and conducting replication studies, addressing the trade-offs and compromises inherent in such endeavors.

We envision this study as a catalyst for future replication projects in operations management and related fields. By embracing replication and transparency, we can ensure the robustness and reliability of our research, ultimately advancing the knowledge and understanding of operations management principles and practices.

References

Andrew M. Davis, Blair Flicker, Kyle Hyndman, Elena Katok, Samantha Keppler, Stephen Leider, Xiaoyang Long and Jordan D. Tong, A Replication Study of Operations Management Experiments in Management Science. Management Science 2023 69:9, XX-XX.

For more perspective on this research, the E-i-C, David Simchi-Levi, asked two experts, Professor Colin F. Camerer(California Institute of Technology) and Professor Yan Chen(University of Michigan). Their comments are given below. Colin F. Camerer (California Institute of Technology)

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Title: Comment on “A Replication Study of Operations Management Experiments in Management Science”
camerer@caltech.edu

This comment cheerleads and historicizes the superb, action-packed paper by Davis et al (2023) replicating a carefully chosen selection of seminal behavioral operations experiments.

Almost twenty years ago, a series of seismic events began in experimental medical and social sciences, which led to a Replication Reboot in experimental social science that is still ongoing. It should continue until all the Rebooted open science practices are routine.

The first event was that Ioannidis (2005) promised to explain, as advertised in the hyperbolic title of his paper “Why Most Published Research Findings Are False”, referring to practices in medical trials.

In 2011 there were two more serious important events in experimental psychology: First, Bem (2011) published a paper in a highly-selective social psychology journal (JPSP) presenting evidence of “pre-cognitive” extrasensory perception. It was widely ridiculed—and the general claim was surely wrong (as some replication failures suggested). The JPSP defended their publication on the basis of being open-minded **[1]** and deferring to positive referee judgments. The Bem finding catalyzed concern that in some areas of experimental psychology, results that were “too cute to be true” were being published routinely. Many priming studies also failed to replicate around this time.

The second 2011 event was that Simmons et al (2011) demonstrated the idea of p-hacking—choosing specifications and subsamples iteratively until a preferred hypothesis appeared significant at a professionally-endorsed level (rigidly p<.05). (Leamer, 1978, also warned about the dangers of undisciplined “specification searches” in econometrics; his warning was often-cited but rarely followed.)

Simmons, and colleagues Simonsohn and Nelson, followed up their p-hacking bombshell with a series of papers clarifying their ideas and presenting tools (such as “p-curve”) to provide boundaries on how likely a set of studies might be exaggerated by p-hacking. By 2019 the term “p-hacking” was part of a question on the game show “Jeopardy!”.

A year later, in 2012, the research director at the Arnold Foundation, Stuart Buck, and the Arnolds themselves, became curious about whether policy evidence was really flimsy (based on highly-publicized replication failures of priming studies). Buck had seen writing from Brian Nosek about open science and he and the Arnolds communicated. The Arnold Foundation ended up investing $60 million in Open Science (see Buck 2013).

Shortly thereafter, the first multiple-study “meta-replications” appeared (Klein, 2014, a/k/a ManyLabs1; Open Science Collaboration, 2015 a/k/a RPP). The latter was the first output of the Open Science Foundation, created by Brian Nosek and Jeffrey Spies in 2013 and funded generously by the Arnold Foundation.

Those studies provided a sturdy foundation for how to do a set of replications and what can be learned. Then came two large-scale team efforts in replicating experimental economics, and then replicating general social science experiments published in high-impact Science and Nature (Camerer et al 2016, 2018). Our efforts followed the pioneering early ManyLabs and RPP work closely, except that we added prediction markets and surveys (following Dreber at al 2015). All of us are thrilled that these meta-replications have continued in different areas of experimental social science.

These historical facts help judge how quickly science—in this case, certain areas of experimental social science– is “self-correcting”. From the dramatic events of 2011 to the earliest meta-replications was only about four years. Generous private funding from the Arnold Foundation (people passionate about openness and quality of science) surely accelerated that timeline, perhaps by a factor of 2-3x.

Table 5 in this Davis et al (2023) article summarizing meta-replications shows that the first seven were not only conducted, but were published in a four-year span (2014-2018). That is amazingly fast (considering how much work goes into carefully documenting all aspects of the details and supplemental reporting, and the editorial grind). And it was done with no special centralized help from any professional organization, university, or federal funding agency. The moving forces were personal scientific contributions, Nosek and Spies creating OSF, quick writing of checks with many zeros by the Arnold Foundation, and emergence of nudges and funding from the Sloan Foundation (for Camerer et al studies, including Swedish grants to Anna Dreber and Magnus Johanneson) and then Simchi-Levi’s (2019) editorial.

About ten years later from the 2011 events, Andrew M. Davis, Blair Flicker—yes, I am spelling out all their names, not abbreviating– Kyle Hyndman, Elena Katok, Samantha Keppler, Stephen Leider, Xiaoyang Long, and Jordan D. Tong (2023) took up Simchi-Levi’s call to action. They carefully replicated ten experimental behavioral operations from studies published in Management Science.

Everyone involved deserves community thanks for putting in enormous amounts of work to produce evidence. This activity is less glamorous and career-promoting than regular kinds of innovative research. “Everyone” also includes peer scientists who made voted on which studies to replicate, and made judgments and replicability predictions in surveys. The collective effort would not be as persuasive and insightful without those peer contributions. The authors’ institutions also contributed money and resources. All this collective effort is trailblazing in extending similar meta-replication methods to a new domain. This effort also helps solidify best practices in a pipeline protocol many others can follow.

A cool feature of their approach is that peer scientists voted on which papers to replicate. The authors winnowed experimental papers down to 24, which around five in each of five substantive categories. Peer voting chose two from each category, for a total of 10 replications.

Basic results and one post-mortem

The basic results are simple to summarize: The quality of replicability varied but was generally high. A strong feature of their design is that each original finding was replicated twice, not once. Only two studies appeared to fail to replicate substantially in both replications. (Readers who aren’t interested in the nuanced details of this post-mortem should skip ahead to “Peer scientist replicability predictions are informative”.)

Let’s dig into details, as in a post-mortem, of one of the two apparent failures. It was an older paper by Ho **[2]** and Zhang (2008) about manufacturer-retail channel bargaining. It is well-known that linear pricing is inefficient because it doesn’t maximize total profit. Charging a fixed fee can fully restore efficiency (a/k/a “two-part tariff”). Ho and Zhang did the first experimental test of this theory. They were also curious about the behavioral hypothesis that retailers might encode paying a fixed fee (TPT) as a loss—if it is “mentally accounted” for as being decoupled from revenue—and balk at paying. However, if the fee is equivalently framed as a “quantity discount (QD)”, they wondered, that might reduce the loss-aversion. Their behavioral hypothesis was therefore that QD framing might be more empirically efficient than TPT.

As Ho and Zhang note in their Author Response (included in Davis et al’s supplementary material), four statistics go into the computation of overall efficiency. Three of the four statistics—wholesale and (conditional) retail prices, and the fixed fee—were strongly significantly different in the TPT and QD treatments in both the original study and the replication. Prices were lower and the fee was higher in QD. However, the difference in acceptance rates of the contracts, between the treatments, do go in opposite directions and efficiency does too.

A restriction which Davis et al used, as many others have (including our Camerer et al 2016, 2018 studies) is that only one hypothesis is tested. This is reasonable as otherwise it requires more complicated power calculations across multiple hypotheses. The efficiency prediction is what was singled out and it plainly did not replicate in magnitude or even direction. Davis et al and Ho and Zhang’s parallel discussions are in agreement about this.

A difference in protocol is that Ho and Zhang’s experiment was done on paper. Subjects had to make calculations by hand and their calculations were not checked. In the replication protocol, software was used, calculations were checked, and errors had to be corrected before subjects could proceed. The replication team noted that some subjects found this frustrating. The team also noted (as quoted in the Author Response):

“This calculation involves X + Y/(10-P) which is often not an integer. To do this calculation correctly also requires understanding order of operations, which to my great surprise it turns out that many people don’t understand. So some tried to calculate it as (X+Y)/(10-P). Even after calculating Price A correctly, they often ended up with a fraction and then had to multiply a fraction to calculate profit.”

The protocol difference and this comment make an important point: There will always be some unplanned deviations…always. The question is how well they might be anticipated and what they tell us.

This example reminds us that every experiment tests a joint hypothesis based on a long chain of behavioral elements. The chain is typically: Credibility of expected money or other reward; basic comprehension of the instructed rules; ability to make necessary calculations, whether explicitly (in the computer) or implicitly (on paper or in the brain); beliefs about what other subjects might do; a preference parameter such as the degree of loss-aversion (conditioned on a reference point); how feedback generates learning; and so on.

A good experimental design tries hard to create strong internal validity about design assumptions (such as payment credibility) and to allow thoughtful behavioral variation to identify behavioral parameters or treatment effects. (For example, Ho and Zhang recover estimates of a loss-aversion parameter, l=1.37 and 1.27 in TPT and QD.)

Sometimes “ability to make necessary calculations” is an element the experimenter wants to clamp and restrict to be true (e.g., providing a calculator) and other times it is an interesting source of behavioral variation. In this case, that “ability…” seems to have been sensitive to the experimental interface. This is a nuisance (unless, as in UI experiments, the nature of the interface is the subject of study—it wasn’t here).

This example is also a good opportunity to think about what scientists should do next in the face of a partially-failed replication. In a very few cases, a failure to replicate puts an idea or a group of scientists into a probationary period. For example, I do not think priming experiments such as many which replicated so poorly will ever recover.

In most cases, however, a partially-failed replication just means that a phenomenon is likely to be empirically sensitive to a wider range of variables than might be have been anticipated. This sensitivity should often spur more new investigation, not less.

In the case of nonlinear channel pricing, the empirical question is so interesting that mixed results of the original experiment and the replication should certainly provoke more research. As noted above, the core behavioral difference is the retailer acceptance rate of fixed-fee contracts under the TPT and QD frames. What variables cause this difference?  Given these results, this question is even more interesting than before the replication results.

Why is behavioral operations replication so solid?

The general quality of replication effects is about as good as has been seen in any of the many meta-replications in somewhat different social sciences. In the replications of Davis et al and Ozer et al (ab) the replication effect sizes are smack on the original ones (as plotted in Figure 2). Other replication effect sizes are smaller than original effects, but that is the modal result.  The relative effect size of replication compared to original data seems to generally be reliably around .60.  Replicated effects usually go in the direction show originally, but are smaller. There is some great work to be done in figuring out exactly why this replication effect shrinkage is so regular.

In my experience looking across social sciences, replication is most precarious when a dependent variable and independent variable are measured (or experimentally manipulated) with error variance, and especially when the focus of theory is an interaction. In experimental economics, theory usually produces predictions about “main effects”.

Many of the behavioral operations are also about main effects— there is a single treatment variable and a plausible intuition about the direction of its effect, often competing with another intuition that there should be no effect at all. The “bullwhip effect” in supply chains is a great illustrative example. There is a clear concept of why no such effect should occur (normatively) and why it might and seems to (behaviorally). (This example is a great gift to behavioral economics—thanks, operations researchers!– because it spotlights a kind of behavioral consequence which seems to be special to operations but might be evident in other cases once the operations example is in mind.) There is a strong intuition that providing more information could make a difference, but is difficult to know without putting people in that situation and seeing what they do whether that’s true.

This formula is what made most of the earliest behavioral economics demonstrations so effective. Typically we were pitting one conventionally-believed convenient assumption—e.g., people discount exponentially, players in games are in equilibrium, people are selfish, people see through framing differences—against a plausible alternative.

Altmejd et al (2019) used LASSO methods to create a long list of features of both original studies and replication samples, to then predict from about 150 actual replications, what features of studies predicted replicability best (including prediction market forecasts). The LASSO “shrinks” features with weak predictive power to have zero coefficients (to limit false positives).

One of the important findings is that replication is less likely when the hypothesized effect is an interaction term rather than a main effect. Interactions are hard to detect when there is measurement error in both of two variables which are hypothesized to interact. Happily, behavioral operations seems to be in a start-up period in which main effects are still quite interesting. Interactions are part of human nature too, but identifying them requires larger high-quality samples and science which can confidently point to some plausible interactions and ignore others.

Publishing replications: Many » 1

People often say that pure replication of a single previous study is not professionally rewarding (it can even make enemies) and is hard to publish. I think that’s generally true. Replicating one study raises a question that is difficult for the replicator to answer: Why did you choose this studyto spend your time replicating? A single-study replication also cannot answer the most fundamental questions the profession would like to know about—such as “Does replicability failure casts possible fault on an author team or on a chosen topic that is hard to replicate?”

What we have learned in general science from the RPP and ManyLabs replications, and efforts like our own and this one in Management Science, is that meta-replicating a group of studies is a whole different enterprise. It is more useful and persuasive. It renders the question “Why replicate this particular study?” irrelevant and clearly answers the question “What does this tell us in general about studies on this topic?”. It is especially persuasive using the method the authors did here, which was to survey peer scientists about what they would most like to see replicated.

Furthermore, in our modern experience (post-2010) some funders—not necessarily all, but enough to supply enough resources—and many journals, are actually receptive to publishing these meta-replications. All sensible editors are open to publishing replication—they realize how important it is—but they would rather not have to adjudicate how to decide which of many one-study replications to publish. Editor Simchi-Levi’s editorial (2019) is an important demonstration of an active call from an editor of a prestigious journal.

Peer scientist replicability predictions are informative

In Davis et al (2023) peer scientist predictions of replicability were substantially correlated with actual predictability. There is also a small ingroup-optimism bias, in which peers most expert in behavioral operations predicted higher replication rates than non-experts, by about .08. However, both groups were about equally accurate when predictions are matched to actual replication outcomes. This is an important finding because it implies that in gathering accurate peer predictions, the peer group can be defined rather broadly. It does not have to be scientists closely expert with the style or scope of experiments.

Peer accuracy in predicting replicability raises a fundamental question about the nature of peer review and may suggest a simple improvement.

Suppose that referees are, to some extent, including guessed p(replication) as an input to their judgment of whether a paper should be published. And suppose there are observable features Xp of a refereed paper p—sample size, p-values, whether tested hypotheses are interactions, etc.—which both referees can easily see, and can also be seen in the post-refereeing process after papers are published.

Simple principles of rational forecasting imply that even if the features Xp are associated with replicability in the unconditional sample of papers reviewed, those features should not be associated with actually replicability of papers that are accepted, because referee selection will largely erase their predictive power.

Think of the simplest example of sample size N. Suppose a referee knows that there is a function p(replication|N) which is increasing in N. If she rejects papers with perceived low replicability, according to that function, then the set of accepted papers will not have replicability which is closely associated with N.  The association was erased by referee selection.

However, it is a strong and reliable fact that actual replicability, based on observable characteristics of published papers, is somewhat predictable from peer judgments (surveys or more sophisticated prediction markets) and from simple observables like p-values and sample sizes. Altmejd et al (2019) found binary classification around 70% (where 50% is random and 100% is perfect). Most other studies, include Davis et al, also found a positive correlation between replication predictions and actual replication. In a working paper studying 36 PNAS experimental paper, Holtzmeister et al (in prep) find a very strong association between prediction-market predictions and actual replication. From 36 experiments published recently in PNAS, from the bottom 12 (judged as least likely to replicate by prediction markets), ten of 12 did not replicate at all.

There is no way around a hard truth here: In different fields, implicit referee and editorial decisions are choosing to publish studies for which replicability failures are substantially predictable, based on data the referees and editors had. The predictability increment is also not a small effect, it is substantial.

What can we do that is better? A few years ago, I proposed to a private foundation a pilot test where some submitted papers would be randomly “audited” by gathering peer predictions and then actually replicating the paper while it was being reviewed. The foundation liked the idea but was not willing to pay for a pilot unless we figured out who would pay for replications and investigator time if such a system were made permanent. We did not do the pilot. It is still worth a try.

What can we do better moving forward?

These results show that the quality of behavioral operations experiments, in terms of choice of theories, methods and sampling designed to create replicability, is solid. No area of social science has shown uniformly better replicability and some areas of psychology are clearly worse.

There is much to admire in Davis et al’s carefully-worded conclusion. I’ll mostly just quote and endorse some of their advice.

Suppose you are an active researcher, perhaps newer and not too burdened by old pre-Open Science bad habits. What should you be sure to do, to ensure your results are easy to replicate and likely to replicate?

**Design for a generic subject pool.**Whomever your starting subject pool is, somebody somewhere might want to replicate your experiment as exactly as possible, including written or oral instructions and user interface. It could be in a foreign country (so you want instructions to be faithfully translateable), with higher or lower literacy groups, with younger students or aging seniors, etc. You should want replication to be easy and to design for likely robustness.

I was taught by the great experimental economist Charlie Plott. Charlie obsessed over writing clear, plain instructions. For example, he avoided the term “probability”; instead, he would always describe a relative frequency of chance events that subjects could actually see. In many early experiments we also used his trick—a bingo cage of numbered balls which generated relative frequencies.

The simplicity of his instructions is now even more important as something to strive for, because online experiments, and the ability to do experiments in many countries and with people of many ages, requires the most culturally- and age-robust instructions.

Design for an online future: This advice is, of course, closely related to the above. Davis et al were harshly confronted with this because, during pandemic shutdown of many in-lab experiments they had to do a lot more online, even when the original experiments being replicated had not originally been online.

“Design for an open science future” is another desirable goal. In Camerer et al (2016) we had to entirely recreate software that was obsolete just to done study. The Davis et al replication project also created some de novo software.

Software degrades. If you create or use software for your experiments, the more customized, local, and poorly supported your software is, the more likely it will not be useable ___ years later (fill in the blank, 2, 3, 5).

Let’s end on a positive note. The Reproducibility Reboot is well underway, has been successful, and has been embraced by funders, journal editors, and energetic scientists willing to spend their valuable time on this enterprise. Korbmacher et al (2023) is a superb and thorough recent review. There is much to celebrate. We are like a patient going to the doctor, hoping for the best, but hearing that we need to put in more walking steps and eat healthier for or selves and our science to live longer. In five or twenty years, all of us will look back with some pride at the improvement in open science methods going on right now, of which this terrific behavioral operations project is an example.

[1]** As the saying goes “Keep your minds open—but not so open that your brains fall out.”**

**[2]** Disclosure: Teck-Hua Ho was a PhD student at Wharton when I was on the faculty there and we later wrote many papers together. Juan-juan Zhang was his advisee at Berkeley.

References

Altmejd A, Dreber A, Forsell E, Huber J, Imai T, et al. (2019) Predicting the replicability of social science lab experiments. PLOS ONE 14(12): e0225826.  https://doi.org/10.1371/journal.pone.0225826

Buck, Stuart. Metascience since 2012: A personal history. https://forum.effectivealtruism.org/posts/zyrfPkX6apFoDCQsh/metascience-since-2012-a-personal-history

Camerer CF, Dreber A, Forsell E, Ho TH, Huber J, Johannesson M, Kirchler M, et al. (2016) Evaluating replicability of laboratory experiments in economics. Science 351(6280):1433–1436.

Camerer CF, Dreber A, Holzmeister F, Ho T-H, Huber J, Johannesson M, Kirchler M, et al. (2018) Evaluating the replicability of social science experiments in Nature and Science between 2010 and 2015. Nature Hum. Behav. 2:637–644.

Simchi-Levi D (2019) Management science: From the editor, January 2020. Management Sci. 66(1):1–4.

Dreber A, Pfeiffer T, Almenberg J, Isaksson S, Wilson B, Chen Y, Nosek BA, et al. (2015) Using prediction markets to estimate the reproducibility of scientific research. Nature 112(50):15343–15347.

Klein R, Ratliff K, Vianello M, Adams R Jr, Bahn´ık S, Bernstein M, Bocian K, et al. (2014) Data from investigating variation in replicability: A “many labs” replication project. J. Open Psych. Data 2(1):e4.

Korbmacher, M., Azevedo, F., Pennington, C.R. et al. The replication crisis has led to positive structural, procedural, and community changes. Commun Psychol 1, 3 (2023).

Leamer, Edward. 1978. Specification Searches: Ad Hoc Inference with Nonexperimental Data. Wiley

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

Simmons, J.P.,Nelson,L.D.,& Simonsohn,U.(2011). False-positive psychology: Undisclosed flexibility in data collection and analysis allows presenting anything as significant. Psychological Science, 22, 1359–1366.

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Yan Chen (University of Michigan)

TitleThe Emerging Science of Replication

yanchen@umich.edu

**Background.**Replications in the social and management sciences are essential for ensuring the reliability and progress of scientific knowledge. By replicating a study, researchers can assess whether the original results are consistent and trustworthy. This is crucial for building a robust body of knowledge. Furthermore, replications can help identify the conditions under which a phenomenon does or does not occur, thus honing theories and rendering them more precise and practical in real-world contexts. If a finding is consistently replicated, it becomes more likely to be accepted as a reliable part of the scientific understanding.

Over the past decade, the issue of empirical replicability in social science research has received a great deal of attention. Prominent examples include the Reproducibility Project: Psychology (Open Science Collaboration 2015), the Experimental Economics Replication Project (Camerer et al. 2016), and the Social Sciences Replication Project (Camerer et al. 2018). In particular, this discussion has focused on the degree of success in replicating laboratory experiments, the interpretation when a study fails to be replicated (Gilbert et al. 2016), the development of recommendations on how to approach a replication study (Shrout and Rodgers 2018), and best practices in replication (Chen et al. 2021).

This is an exciting time when the scientific community is converging on a set of principles for the emerging science of replication. Davis et al.(forthcoming) make significant contributions towards our shared understanding of these principles.

**Summary.**Davis et al. (forthcoming) present the first large-scale replication study in the area of operations management published in Management Science prior to 2020. Using a two-stage paper selection process including inputs from the research community, the authors identify ten prominent experimental operations management papers published in this journal. For each paper, they conduct high-powered (90% to detect the original effect size at the 5% significance level) replication study of the main results across at least two locations using original materials. Due to lab closures during the COVID-19 pandemic, this study also tests replicability in multiple modalities (in-person and online). Of these ten papers, six achieve full replication (at both sites), two achieve partial replication (at one site), and two do not replicate. In the discussion section, the authors share their insights on the tradeoffs and compromises in designing and implementing an ambitious replication study, which contribute to the emerging science of replication.

**Comments.**Compared to prior replication studies, this study has several distinct characteristics. First, this study contains independent replications across two locations, whereas the three prominent earlier replication studies contain one location for each original study (Open Science Collaboration 2015, Camerer et al. 2016, 2018). A multi-site replication helps determine whether a set of findings hold across diverse subject pools and cultural contexts, and enhance the robustness of the findings. Second, this study tests replicability in multiple modalities (in-person and online), whereas most of previous replication projects contain one modality. While replicating individual choice experiments online was unexpected due to the lab closure during the pandemic, it does teach us that it is important to “design for an online future.”

For researchers conducting lab and field experiments, in addition to design for an on- line future, we should “design for a generic subject pool.” How might researchers of original experiments design for a generic subject pool? In lab experiments, we could aim at collecting data from distinct subject pools. For example, in the classic centipede game experiment (McKelvey and Palfrey 1992), researchers recruited subjects from Caltech and Pasadena City College, two subject pools with different average analytical abilities. In a recent field experiment on a ride-sharing platform (Ye *et al.*2022), researchers conducted the same field experiment across three cities of distinct size, competitiveness and culture. These multi-site design helps define the boundaries of each finding.

While this and previous replication studies use classical null hypothesis significance testing to evaluate replication results, we note that several studies have proposed that repli- cations take a Bayesian approach. Verhagen and Wagenmakers (2014) explore various Bayesian tests and demonstrate how previous studies and replications alter established knowledge through the Bayesian approach. When addressing how the field should con- sider failed replications, Earp and Trafimow (2015) consider the Bayesian approach and how failed replications affect the confidence of original findings.

McShane and Gal (2016) propose “a more holistic and integrative view of evidence that includes consideration of prior and related evidence, the type of problem being evaluated, the quality of the data, the effect size, and other considerations.” They warn that null hypothesis significance testing leads to dichotomous rather than continuous interpretations of evidence. Future replications might consider both the classical and Bayesian approaches to evaluate replication results.

References

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