78  Research Credibility and Integrity

Peer review (Chapter 77) screens manuscripts one at a time. This chapter is about what that screen missed, and how the field found out. Over roughly a decade, psychology, economics, and the quantitative social sciences, marketing among them, went through a period of self-examination usually called the credibility revolution or the replication crisis, during which they reconsidered how much of their published record they actually believed. The data-and-code policies and data editors described in Section 77.12 are its operational residue. So are preregistration, registered reports, and the forensic re-analysis of published results.

The history matters to three readers. An author needs it because the failure modes it documented (undisclosed analytic flexibility, small samples, results that hinge on one defensible specification among many) are now the first things a referee looks for. A referee needs it because it supplies the specific checklist of failure modes to screen for, and because several of the underlying statistical questions remain unsettled, so a referee cannot demand adherence to any one camp. A reader needs it because most of the ways a literature goes wrong involve no misconduct at all: of the forty-seven controversies indexed at the end of this chapter, one concerns fabricated data.

The chapter begins with the evidence that the literature was less reliable than assumed and the reforms that evidence motivated (Section 78.1). It then turns to the statistical-significance debates the crisis reopened (Section 78.2), to the forensic methods and integrity cases that data transparency made possible (Section 78.3), and to marketing’s own best-documented credibility episode, which involved no fabrication (Section 78.4). It closes with how the field argues in public (Section 78.5), a tour of marketing’s recurring methodological disagreements that says where each now stands (Section 78.6), and an index of the controversies documented throughout the book (Section 78.7). The newest of these disputes, whether language models should be built into peer review, concerns the review process itself and is treated there (Section 77.13).

78.1 The Replication and Credibility Crisis

The intellectual spark is usually credited to Simmons, Nelson, and Simonsohn (2011), False-Positive Psychology, which showed by simulation and live demonstration that exploiting researcher degrees of freedom, the undisclosed choices about exclusions, conditions, covariates, and stopping rules that every analysis involves, can manufacture statistically significant support for essentially any hypothesis, driving the false-positive rate far above the nominal five percent even when no effect exists. The authors proposed disclosure remedies (the well-known “twenty-one-word solution”). Gelman and Loken (2014) sharpened the point with the metaphor of the garden of forking paths: a researcher need not consciously run many analyses to inflate error rates, because the single analysis actually run is contingent on the data observed, so the p-value is uninterpretable without a pre-specified plan. The disagreement here is not about whether the mechanism is real (it provably is) but about how much of the published literature it has actually contaminated and how aggressively the field should respond, a distinction worth preserving when a reviewer raises the concern.

Controversy: the paper that broke psychology’s confidence in itself

The credibility revolution has a specific trigger, and it is worth knowing, because the logic that produced it applies unchanged to marketing. The field’s standard methods were used correctly, by a respected researcher, at a top journal, to demonstrate something almost nobody believed.

2011 — the paper. Bem (2011) publishes Feeling the Future in the Journal of Personality and Social Psychology, reporting nine experiments in which participants appear to be influenced by stimuli presented after their responses. The methods are conventional. The statistics are conventional. Eight of the nine studies reach significance.

2011 — the response, in the same issue. Wagenmakers et al. (2011) reply that the correct inference is not that precognition exists but that the field’s standard analytic practice is broken: exploratory analysis presented as confirmatory, and p-values interpreted without regard to the prior implausibility of the hypothesis. Their argument generalizes immediately—if these methods produce this result, what are they producing everywhere else?

2012 — the replications fail. Ritchie, Wiseman, and French (2012) report three unsuccessful attempts to replicate the retroactive-recall effect. Notably, they had difficulty placing the paper: journals that had published the original were not obviously in the business of publishing failures to replicate it, which became an argument about publication incentives in its own right.

Why this is in a marketing book. Bem’s paper is the field’s cleanest natural experiment on its own methods, precisely because the hypothesis was one nobody wanted to accept. When a method yields a conclusion the field is prepared to believe, the method is not tested. Every reform in this chapter—preregistration, registered reports, disclosure standards, data posting—descends from a community concluding that the conventional pipeline could manufacture support for anything. Marketing runs the same pipeline on hypotheses that are entirely plausible, which is a harder case to audit, not an easier one.

The empirical question, how replicable is the literature, was addressed by large coordinated projects. The Open Science Collaboration (2015) replicated 100 psychology studies and found that roughly one-third to one-half met various replication criteria, with replication effect sizes about half the size of the originals. Camerer et al. (2018) replicated social-science experiments published in Nature and Science and successfully reproduced about thirteen of twenty-one, again with attenuated effects. The picture is worse where independent observations are expensive. In experimental asset markets the unit of analysis is the market, not the trader, so a study with 160 traders in ten-trader markets has sixteen observations. Huber et al. (2026) ran preregistered replications of 17 results from four prominent studies in the American Economic Review, Journal of Finance, Review of Financial Studies, and Review of Finance, collecting 166 new markets with 1,544 participants; one of the originals, on self-control, had rested on eight markets per condition. Each primary test was sized for 90 percent power to detect two-thirds of the original effect. Only 3 of the 14 results originally reported as significant replicated, and in the working-paper version the average replication effect was 2.9 percent of the original (Huber et al. 2024). Induced excitement, depleted self-control, and the share of female traders all failed to predict bubbles, with point estimates of the wrong sign. Two findings survived: cognitive reflection, fluid intelligence, and theory of mind predicted trading earnings (though the latter two at roughly 60 and 40 percent of their original size), and experience roughly halved the bubble measures when the same traders traded a second market. The working paper also notes that some of the original treatment comparisons were run in separate sessions instead of being randomized within a session. A referee reading a market-level experiment should therefore check two things: how many markets per arm there are, and whether treatments were assigned within a session. A non-replication is ambiguous, however: it can mean the original was a false positive, or that the replication differed in some hidden but consequential way. The Many Labs projects (Klein et al. 2014, 2018) addressed this by running identical protocols across many sites, finding that most effects were robust across samples while a minority varied, evidence that contextual heterogeneity is real but does not by itself account for most non-replications. Figure 78.1 arranges these landmarks. The honest synthesis, which a reviewer can state as genuine convergence rather than as one camp’s opinion, is that replication rates sit materially below 100 percent and effect sizes shrink on replication, while the mix of causes remains debated.

Archival replication looks different, and a recent strategy case shows what it can and cannot deliver. Bettis, Helfat, and Shaver (2016) distinguish a narrow replication, which reruns the original design on the original sample and is mainly confirmatory, from a quasi-replication, which keeps the design but changes the sample to test robustness or generalizability. Kofford, Lewis, and Melancon (2026) do both for Flammer (2013), an event study of investor reactions to environmental news, and then extend it. The narrow replication recovers the original average reactions almost exactly. The quasi-replication adds a decade and finds the same time trends in decade means. The regression version of the trend test went less well. The authors could not exactly reproduce Flammer’s coefficients, which they attribute to differences in how the control variables were built, and in their extended sample the trend was significant for eco-friendly events but not for eco-harmful ones (Kofford, Melancon, and Lewis 2025). They also attribute small differences in average returns to CRSP’s corrections of historical data, so even a database the whole field shares is not fixed over time. A referee reading an archival replication should ask which tables were reproduced and which were not, and whether the data vintage is reported. Section 26.7.5 works through the case, including an arithmetic audit of its tables.

Controversy: how bad is the replication rate? A fight about the number itself

The headline finding that roughly a third to a half of psychology studies replicated became one of the most cited results in social science, and it was contested directly, in Science, by four senior researchers. The exchange is short—both pieces occupy the same page—and unusually instructive, because it is a disagreement about statistical method conducted over a statistic about statistical method.

2015 — the estimate. Open Science Collaboration (2015) report the Reproducibility Project: Psychology, replicating 100 studies with the original authors’ materials.

March 2016 — the challenge. Gilbert et al. (2016) argue the project systematically understated replicability: that many replications differed from the originals in ways likely to matter, that the sampling of studies was not representative, and that the statistical criteria used to declare a replication failed were themselves biased toward failure. Their conclusion is that the data are consistent with a much higher reproducibility rate than reported.

March 2016 — the response, same page. Anderson et al. (2016), writing for 44 members of the collaboration, reply that the critique’s own assumptions are optimistic, that its preferred benchmark relies on a subset of studies chosen in a way that favors the conclusion, and that the original estimate stands.

How a referee should hold this. The prudent position is not to pick a number. It is to notice what both sides concede: replication rates are below 100 percent, replication effect sizes are systematically smaller than originals, and the causes—false positives, hidden moderators, methodological drift between original and replication—cannot be separated from the aggregate statistics alone. That is enough to justify every reform in this chapter without needing to settle whether the true figure is 40 percent or 60. Beware of anyone who quotes one figure as settled, in either direction.

flowchart LR
    A[2011<br/>False-Positive<br/>Psychology] --> B[2014<br/>Garden of<br/>forking paths]
    B --> C[2015<br/>Open Science<br/>Collaboration]
    C --> D[2014-18<br/>Many Labs<br/>1 and 2]
    D --> E[2017<br/>Reproducibility<br/>manifesto]
    E --> F[2018+<br/>Preregistration &<br/>registered reports]
Figure 78.1: A timeline of the credibility revolution. The diagnostic work (forking paths, false positives) precedes the large replication audits, which in turn motivate the institutional reforms (preregistration, registered reports, open-data mandates) that now shape the review process.

78.1.1 Preregistration and Registered Reports

If selective reporting and forking paths are the disease, preregistration (committing to hypotheses and analyses before seeing the data) and registered reports (peer review of the design before results are known, with in-principle acceptance) are the leading proposed cures (Nosek et al. 2018; Munafò et al. 2017). Registered reports relocate the review process itself: the referee evaluates the question and the design rather than the result, which removes the incentive to reverse-engineer a clean story from a messy dataset. Early outcome evidence is encouraging; Soderberg et al. (2021) found that registered reports scored higher on rigor and quality dimensions than comparison papers. The mature position is not that preregistration is mandatory for all work but that it disciplines confirmatory inference without displacing exploratory analysis, provided the exploratory portion is labeled honestly. The journal-level counterpart is the Transparency and Openness Promotion (TOP) framework (Nosek et al. 2015), which the data-deposit norms described in Section 77.12 instantiate.

78.2 Statistical-Significance Debates

The crisis reopened a foundational and still-unresolved argument about statistical significance itself. The American Statistical Association took the unusual step of issuing a formal statement (Wasserstein and Lazar 2016) clarifying what a p-value is not: it is not the probability that the null hypothesis is true, and statistical significance is not practical importance. There is broad agreement on these negative claims and continued disagreement on what, if anything, should replace null-hypothesis significance testing; the ASA’s own follow-up (Wasserstein, Schirm, and Lazar 2019) surveyed the options and pointedly declined to endorse a single replacement.

Three reform proposals now compete, and a referee should recognize them as live rather than settled. The redefine camp (Benjamin et al. 2018) proposes lowering the default threshold for new discoveries from .05 to .005, treating the interval between as merely suggestive. The justify camp (Lakens et al. 2018) replies that no single threshold fits all contexts and that researchers should transparently justify the alpha they adopt given the costs of each kind of error. The abandon camp (Amrhein, Greenland, and McShane 2019; McShane et al. 2019), the last of which is led in part by a marketing and statistics scholar, argues for retiring the dichotomous significant-versus-not verdict entirely and treating p-values as one continuous piece of evidence among many. Table 78.1 summarizes the three positions. The accurate summary for the book is near-universal agreement that a bright-line p < .05 is misused, alongside genuine disagreement on the remedy.

Table 78.1: Three competing responses to the misuse of statistical significance. The field has not converged on a winner.
Position Core proposal Representative work
Redefine Lower the default discovery threshold to .005; .005–.05 is “suggestive” Benjamin et al. (2018)
Justify No universal threshold; justify alpha from error costs and study goals Lakens et al. (2018)
Abandon Retire the significant/not-significant dichotomy; treat p as continuous evidence Amrhein, Greenland, and McShane (2019); McShane et al. (2019)
Controversy: the significance wars, in order

Table 78.1 states the three positions; the sequence in which they arrived explains why none of them won, and a referee who knows the order will read a methods section differently.

2016 — the professional body intervenes. The American Statistical Association issues a formal statement on p-values (Wasserstein and Lazar 2016). This is unusual: scholarly societies do not normally rule on how to interpret a statistic. The statement is almost entirely negative—six principles about what a p-value is not—and it deliberately stops short of prescribing a replacement.

2018 — a threshold is proposed, and immediately contested. Benjamin et al. (2018), with a large multidisciplinary author list, propose lowering the default discovery threshold to .005. Lakens et al. (2018) reply, with an author list of comparable size and overlapping fields, that no universal threshold can be right and that researchers should justify alpha from the error costs of the specific decision. Two large coalitions of methodologists, publishing near-simultaneously, reaching opposite conclusions from the same premise that .05 is misused.

2019 — a third camp says the question is wrong. Amrhein, Greenland, and McShane (2019) and McShane et al. (2019) argue for retiring the dichotomy entirely. The same year, the ASA’s own follow-up (Wasserstein, Schirm, and Lazar 2019) surveys the options and pointedly declines to endorse one.

How to use this at the desk. The disagreement is real, so a referee cannot demand adherence to any one camp. What all three positions share is a rejection of the bright line applied mechanically, and that shared ground is enough to support a concrete request: report effect sizes with intervals, state the inferential threshold and why it was chosen, and do not describe a result as absent because it failed to cross .05. Those are compatible with redefine, justify, and abandon alike—which is why they are the requests worth making.

Running underneath this is the longer-standing Bayesian versus frequentist question: whether to quantify evidence with p-values and confidence intervals or with posterior probabilities and Bayes factors. The Bayesian side (Rouder et al. 2009; Wagenmakers et al. 2018) emphasizes that Bayes factors can quantify evidence for a null hypothesis and sidestep several p-value pathologies, while the frequentist-reform side is well represented by the ASA materials above. Modern practice increasingly treats the two as complementary and reports both; the chapters on Bayesian modeling develop the machinery a reviewer would check.

78.3 Forensic Data Analysis and Integrity

Data transparency did more than let reviewers regenerate reported numbers; it enabled a class of forensic methods that probe published results for arithmetic and statistical impossibilities, and it made possible the independent re-analyses associated with the blog Data Colada. The methods matter more than any individual case, so we lead with the toolkit, summarized in Table 78.2.

Table 78.2: The forensic toolkit for screening published quantitative results. SPRITE, a related raw-data reconstruction method, circulates as a preprint and is cited here by lineage to GRIM rather than by a fabricated identifier.
Tool What it checks Source
p-curve Whether a set of significant findings reflects a real effect or selective reporting, from the distribution of significant p-values Simonsohn, Nelson, and Simmons (2014)
Specification-curve / multiverse Runs and displays all defensible analytic choices rather than one, exposing fragility Steegen et al. (2016); Simonsohn, Simmons, and Nelson (2020)
GRIM Whether a reported mean is arithmetically possible given the sample size and integer responses Brown and Heathers (2017)
Excess-uniformity checks Whether improbable similarity across conditions signals fabricated data Simonsohn (2013)

P-curve (Simonsohn, Nelson, and Simmons 2014) infers whether a body of significant findings reflects a genuine effect or selective reporting by examining the shape of the distribution of significant p-values. Specification-curve or multiverse analysis (Steegen et al. 2016; Simonsohn, Simmons, and Nelson 2020) formalizes running and reporting all reasonable analytic specifications rather than a single favored one, so a reader can see whether a result depends on a particular defensible choice. GRIM (Brown and Heathers 2017) performs a deceptively simple arithmetic check: given a sample size and integer-valued responses, only certain means are possible, and a reported mean that is not on that list signals an error. And Simonsohn (2013) showed that excessive uniformity or improbable similarity across conditions can reveal fabricated data from the statistics alone, an argument for routine data posting. These are exactly the checks a transparency package now lets a referee, or a later reader, perform.

The remainder of this section describes a small number of prominent integrity cases. It does so in a deliberately measured, court-reporter register: every factual claim is anchored only to public records, namely retraction notices, official investigation outcomes, and dated published analyses. Where matters remain contested or are the subject of litigation, that is stated as such, and no allegation is asserted as settled fact. The pedagogical point is what the forensic methods and data transparency can reveal, not a verdict on any person.

Consider first the field-experiment literature on honesty pledges. A 2012 article in PNAS (Shu et al. 2012) reported that signing an honesty declaration before rather than after reporting information reduced dishonesty, using auto-insurance mileage data among other studies. In 2020 a registered set of replications co-authored by several of the original authors did not reproduce the effect (Kristal et al. 2020). In 2021, Data Colada published a post (post number 98, dated August 2021) reporting anomalies in the field-experiment data underlying the 2012 paper, and PNAS subsequently published a retraction of the article (Proceedings of the National Academy of Sciences 2021). The accurate public-record summary is therefore: the 2012 article was retracted in 2021; a replication by several of the original authors had failed to reproduce the effect; and an independent analysis reported anomalies in the underlying field data. Public reporting has attributed the questioned data to a particular source, but because responsibility is contested and related matters have touched litigation, the book assigns no blame.

A second sequence concerns several papers co-authored by one researcher. A 2015 article in Psychological Science (Gino, Kouchaki, and Galinsky 2015) was retracted in 2023, a fact recorded in the journal’s published retraction notice (Psychological Science 2023). In 2023 Data Colada published a four-part series (“Data Falsificada,” posts 109 through 112) reporting anomalies across several co-authored papers; the relevant institution conducted an internal investigation, and several papers were retracted. Defamation litigation related to these allegations has been reported in public sources, and elements remain contested. The book states only that the matter has been the subject of litigation and that the allegations remain contested, without characterizing the merits. The durable lesson for a reviewer is structural rather than personal: arithmetic checks like GRIM, distributional checks like p-curve, and above all the routine posting of raw data are what make independent verification possible, which is precisely why the transparency requirements in Section 77.12 have teeth.

Controversy: the retraction wave, 2021–2023

The credibility revolution reached marketing’s own journals as retractions rather than as debate. Only the public record is described here: what the journals published, and when. Nothing below characterizes any person’s conduct, and where responsibility has been contested or litigated, the book takes no position (see the two sequences above).

Journal of Marketing Research published three separate retraction notices during 2022.1 The Journal of Consumer Research retracted Super Size Me: Product Size as a Signal of Status in 2023 (Journal of Consumer Research 2023), and issued an unusually dense run of errata and corrigenda across 2021 and 2022.

Two observations for a reviewer. First, the volume of errata is as informative as the retractions: a correction notice is what a journal issues when something is wrong but the finding survives, and a sudden cluster of them indicates that people started checking. Second, none of this machinery is triggered by peer review, which had already passed on every one of these papers. It is triggered by post-publication scrutiny of data that authors were, increasingly, required to post. That is the argument for the transparency requirements in Section 77.12 stated as an outcome rather than a principle.

78.4 A Marketing Case Without Fabrication

Both integrity sequences in Section 78.3 turn on questioned data, and both were resolved—to the extent they were resolved—by retraction. That is the vivid failure mode, and it is not the common one. Marketing’s own best-documented episode involves no allegation of fabricated data, no retraction, and no misconduct finding, and it is arguably the more instructive case for exactly that reason.

The claim was that portfolios formed on customer-satisfaction scores earn abnormal stock returns (Fornell et al. 2006; Aksoy et al. 2008; Fornell, Morgeson, and Hult 2016b). Five independent teams failed to reproduce it: Jacobson and Mizik (2009b) and Jacobson and Mizik (2009a) located the effect in a handful of technology firms, Ittner, Larcker, and Taylor (2009) found nothing under standard multifactor asset-pricing tests, O’Sullivan, Hutchinson, and O’Connell (2009) found nothing after standard risk adjustment, and Bell, Ledoit, and Wolf (2014) reopened how the portfolios should be formed at all. When the argument returned to the Journal of Marketing in 2016, the journal published the critiques in the same issue as the claim (Kumar 2016; Sorescu and Sorescu 2016; Bharadwaj and Mitra 2016; Fornell, Morgeson, and Hult 2016a). Two of those commentaries report that they could not evaluate the result at all, because the trading strategy on which it rested had not been disclosed. The strategy was productized as a publicly traded fund launched weeks after publication, so the claim has since accumulated a decade of live out-of-sample record. Section 4.6.1 assembles the full record; Section 4.6.3 supplies the meta-analytic magnitudes against which the headline should have been read.

Several features of this episode are worth a reviewer’s attention. Nothing in it required anyone to fabricate anything: an undisclosed estimator, a threshold chosen without justification, and a sample window that happened to contain an unusual era are sufficient on their own. The published exchange, which looks like the system working, is also what allowed the dispute to close without resolution—printing both sides substitutes the appearance of adjudication for adjudication itself. And the affirmative and null results are asymmetrically distributed across research groups, which is information a reader should weigh and a citation count will not reveal.

The episode also shows where financial-interest information actually surfaced. The fund’s SEC registration statement discloses that its adviser was also its index provider and that a named individual—the creator of the underlying measure and an author of the studies establishing its predictive power—held a controlling interest in both the adviser and the index organization (Section 4.6.1 quotes the filing). Securities regulation compelled that disclosure to investors, and it is public. Whether an equivalent statement would reach a reader of the journal articles depends on a journal’s disclosure policy, and marketing has historically asked less here than medicine does. The reviewer’s question is the one the submission form may not pose: does any author hold a financial position that gains value if this specific result is believed, and would a reader be able to find that out? As elsewhere in this chapter, the book asserts no verdict on any person’s conduct; the public record consists of the published papers, the published commentaries, and a fund’s reported performance, and it is sufficient for the methodological point. The remedies are the ones this chapter has already argued for: disclosed estimation procedures, preregistered portfolio-formation rules, and out-of-sample tests as a condition of publication rather than an afterthought.

78.5 How the Field Argues in Public

The satisfaction episode is unusual in scale but not in kind. Marketing conducts a surprising amount of its quality control in the open, through a genre most readers never encounter because it sits in the back pages: the published comment, the rejoinder, and the erratum. A doctoral student who has never read one should, because this is where the field’s methodological standards are actually set—not in editorials about rigor, but in specific people telling specific people that a specific equation is wrong, under their own names, permanently, with a DOI.

Controversy: duelling in the back pages of Marketing Science

Three sequences, each a matched pair or triad published by the journal itself. As elsewhere in this chapter, the account states what was published and when; the substance of who is right is left to the papers.

A commentary, answered in one page. Amaldoss and He (2013) publish Pricing Prototypical Products in 2013. Twelve years later S. Li, Pu, and Zheng (2025) publish a commentary disputing the result, and Amaldoss and He (2025) answer in a rejoinder whose title is itself the disagreement stated as a question—Can a Prototypical Product Be Priced Lower Than a Nonprototypical Product? The rejoinder occupies a single page (page 728). Note the interval: a published analytical result sat for over a decade before anyone put a challenge to it in print.

An erratum on somebody else’s model. Shulman, Cunha, and Saint Clair (2015) publish Consumer Uncertainty and Purchase Decision Reversals in 2015. In 2025 the journal publishes He and Li (2025)—an erratum, written not by the original authors but by two unaffiliated researchers, and titled, in the journal’s own table of contents, Erratum on “Purchase Decision Reversals” Model by Shulman et al. (2015). The original authors reply on the following page (Shulman, Cunha, and Saint Clair 2025). This genre is worth pausing on: it is a third party formally entering the record to state that a published model contains an error, a correction mechanism most fields have no established route for at all.

The same pattern in JMR. Bumbaca, Misra, and Rossi (2020) publish a distributed MCMC method for Bayesian hierarchical models in 2020. Braun (2024) revisits it in a commentary four years later; Bumbaca, Misra, and Rossi (2025) reply the following year. Again the reply runs two pages.

Three structural features recur. The lag between claim and challenge is measured in years, sometimes more than a decade, because writing a comment is unrewarded work. The rejoinder is nearly always shorter than the commentary, and often a single page. And the journal publishes both and moves on, without adjudicating—the same feature visible in Section 78.4, where an unresolved dispute was closed by printing both sides. A reader who wants to know which party was right must still do the work themselves.

78.6 A Tour of Marketing’s Methodological Debates

Marketing research spans an unusually wide methodological range, and several long-running debates recur often enough that an author, a referee, or a reader should be able to frame each one fairly, recognizing both the contribution and its standard critique rather than mechanically penalizing a method some camp dislikes. Each debate below is stated neutrally in a few sentences and forwarded to the chapter where it properly lives; the home chapters develop them in full.

Framing a debate neutrally is not the same as treating every question as open. Some of these disputes have been decided by a proof or by a large body of evidence, and presenting them as matters of camp would teach the wrong lesson. Each entry therefore ends with a note on where it stands, using four labels:

  • Settled. The point in dispute is a mathematical or identification result. What remains is practice, not truth.
  • Settled within limits. The evidence decides the question for the settings studied; whether it carries over to others is open.
  • Converged in practice. The camps still disagree in principle but now agree on what a careful study does.
  • Open. Neither the evidence nor the concepts decide it yet.

Some entries add a sentence labeled Our read: the book’s own assessment, resting on the evidence cited beside it. The book offers no such assessments about people; the integrity cases earlier in the chapter are reported from the public record only. Table 78.3 at the end of the tour collects the labels, together with a request a referee can make whichever side the authors take.

Structural versus reduced-form modeling. Should a study estimate the primitives of a behavioral or economic model (structural), enabling counterfactual and welfare simulation, or prioritize clean identification of a specific causal effect through design and quasi-experiment (reduced-form)? The economics credibility revolution (Angrist and Pischke 2010) sharpened design-based inference, while structural advocates (Chintagunta et al. 2006) argue structural models answer policy questions reduced-form cannot, with internal cautions on both sides about weak instruments (Rossi 2014) and undisciplined structural assumptions (Mazzeo et al. 2006). The causal-inference and structural-modeling chapters develop the trade-off.

Where it stands: converged in practice. The two programs now read more as complements than as rivals. A structural model can be checked against an experiment held out of its estimation, as Todd and Wolpin (2006) did with a randomized school-subsidy program, and the internal cautions on both sides are about the same thing: identification. What remains is a choice of question rather than a disagreement about evidence. A counterfactual outside the observed range of policy needs a model; a single causal effect inside it usually does not. Our read: choose by the question, and hold both kinds of paper to the same standard for saying which variation identifies each estimate.

Formative versus reflective measurement. In reflective measurement the latent construct causes its indicators; in formative measurement the indicators compose the construct, so dropping one changes its meaning, and misspecifying the direction biases structural estimates (Bollen and Lennox 1991; Jarvis, MacKenzie, and Podsakoff 2003; Diamantopoulos, Riefler, and Roth 2008). A skeptical strand questions whether formative “constructs” are latent variables at all and proposes content-validity-first alternatives (Rossiter 2002). This debate is developed where constructs and variables are distinguished (Chapter 3) and in the measurement-scales chapter.

Where it stands: open. No dataset can settle whether indicators cause a construct or compose it, so the core dispute is conceptual. Part of it is technical, though. A formative block is identified only when the construct also sends paths to other variables, so its estimated meaning shifts with whichever outcomes the model includes (Diamantopoulos, Riefler, and Roth 2008; Howell, Breivik, and Wilcox 2007). Howell, Breivik, and Wilcox (2007) call this interpretational confounding and advise reflective measurement wherever possible; Edwards (2011) argues that the aims of formative measurement can be met with reflective models; Diamantopoulos, Riefler, and Roth (2008) set out how to specify and estimate formative models properly. Our read: when a measure is defined by its components, call it an index, report its weights, and let reflectively measured outcomes carry the structural claims.

The PLS-SEM controversy. Partial Least Squares path modeling is popular in some marketing subfields and distrusted in others; critics argue it lacks a true latent-variable model and yields biased estimates with unreliable fit heuristics (Rönkkö and Evermann 2013), while proponents reply that the critiques target outdated versions and that PLS suits prediction-oriented, formative, and small-sample work (Henseler et al. 2014). This is an unusually clean critique-plus-rejoinder exchange in one journal, developed in the structural-models chapter.

Where it stands: settled in part. The original technical complaint has been conceded. Classic PLS estimates are inconsistent when constructs are reflective, which is why consistent PLS (PLSc) was introduced to correct them (Dijkstra and Henseler 2015). Whether a composite-based model suits theory testing at all remains open. Rönkkö et al. (2016) argue that PLS amounts to regression on weighted scale scores, and report that the editors of the Journal of Operations Management had announced that research using it was likely to be desk-rejected. Our read: for reflective constructs use covariance-based SEM or PLSc, and reserve composite PLS for indexes or for prediction, and say which one is in use.

Measuring advertising returns. Can observational attribution methods recover the causal effect of advertising on sales, or are large randomized experiments effectively required? Evidence that ad effects are tiny relative to sales variance (Lewis and Rao 2015), that brand-keyword paid search delivered near-zero incremental value in a large field experiment (Blake, Nosko, and Tadelis 2015), and that observational methods diverge substantially from experimental benchmarks (Gordon et al. 2019) pushes toward experiments for incrementality, while attribution modeling (H. (Alice). Li and Kannan 2014; Berman 2018) remains useful for allocation under stated assumptions. The advertising and causal-inference chapters develop the convergence.

Where it stands: settled within limits. For measuring incrementality, the experimental benchmark has won on the evidence. In large sets of Facebook experiments (663 in the later study), observational estimators, including double machine learning given more than 5,000 user-level features, missed the experimental lifts by large and variable margins (Gordon et al. 2019; Gordon, Moakler, and Zettelmeyer 2023). The limit is the scope of any single experimental null. On Bing, brand-keyword ads raised a brand’s clicks by 1 to 4 percent when no competitor bid on its name, and defensive brand advertising earned a strongly positive return when competitors did (Simonov, Nosko, and Rao 2018). So the eBay result does not show that brand search never pays. Whether calibrated media-mix models can close the gap without experiments is open.

The nudge-effectiveness debate. How large and reliable are choice-architecture “nudge” effects in aggregate? A 2021 meta-analysis reported a moderate positive average effect (Mertens et al. 2022), while reanalyses argued that the effect is not distinguishable from zero once publication bias is modeled (Maier et al. 2022) and that heterogeneity precludes expecting uniform effects (Szaszi et al. 2022). This is as much a dispute about meta-analytic method as about nudges, and it is developed in the nudges chapter.

Where it stands: settled within limits. The strongest evidence came from outside the meta-analytic exchange. DellaVigna and Linos (2022) assembled 126 trials covering 23 million people, including every trial run by two large U.S. nudge units, and found an average take-up effect of 1.4 percentage points at scale, against 8.7 points in nudge trials published in academic journals. Selective publication, made worse by low power, explains about 70 percent of the gap. The average published effect is therefore inflated, while the at-scale effect is small and clearly non-zero for this class of government take-up nudges. Whether the same holds for other kinds of nudge, and whether an average is the right quantity given the heterogeneity Szaszi et al. (2022) emphasize, is open.

Mediation-analysis critiques. Bootstrap and Baron-Kenny-style mediation from observational designs is ubiquitous in consumer research, but critics argue that without experimental manipulation of the mediator a mediation claim is causally unidentified (Bullock, Green, and Ha 2010), while a constructive-reform position urges better practice (manipulated mediators, moderation-of-process, sensitivity analysis) rather than abandonment (Pieters 2017). The causal-inference chapter develops the identification requirements.

Where it stands: settled. The identification point is a theorem, not a camp. Randomizing the treatment does not randomize the mediator, so an indirect effect is identified only under sequential ignorability, an assumption the study’s own data cannot test (Imai, Keele, and Yamamoto 2010). What remains is practice: how often a consumer study reports the sensitivity analysis or the manipulated mediator that the theorem calls for.

The common-method-bias debate. When predictor and outcome come from the same respondent at one time, shared method can inflate observed correlations; one position catalogs this as a serious, pervasive threat requiring design and statistical remedies (Podsakoff et al. 2003), while another argues the blanket assumption is overstated and that some popular post-hoc corrections do more harm than good (Spector 2006). The surveys and measurement-scales chapters develop the practical safeguards.

Where it stands: converged in practice. The later reviews pair statistical controls with procedural remedies at the design stage, such as taking the predictor and the criterion from different sources, at different times, or in different response formats (Podsakoff, MacKenzie, and Podsakoff 2012; MacKenzie and Podsakoff 2012). The measurement-scales chapter explains why the widely reported Harman single-factor test is not one of the useful statistical controls (Chapter 39). How large the bias is in a typical study remains disputed (Spector 2006).

Online-panel and MTurk data quality. Crowdsourced samples democratized data collection but raised concerns about non-naivete, inattentive responding, and bots; early validations argued the data are reliable and diverse (Buhrmester, Kwang, and Gosling 2011; Paolacci and Chandler 2014), later work documented worker non-naivete (Chandler, Mueller, and Paolacci 2014), and a recent exchange disputes whether alarming invalid-response rates reflect inherent platform failure (Webb and Tangney 2022) or remediable design and screening choices (Keith and McKay 2024). The surveys and data chapters develop the concrete safeguards (attention checks, geolocation and bot screening, preregistered exclusion rules).

Where it stands: settled within limits. The decline in quality is documented, not anecdotal. Validity failures on MTurk rose sharply around 2018 (Chmielewski and Kucker 2020; Kennedy et al. 2021), and head-to-head comparisons place Prolific and CloudResearch well ahead of MTurk on most quality measures (Douglas, Ewell, and Brauer 2023; Peer et al. 2022). Screening on response-validity indicators recovers much of the loss (Chmielewski and Kucker 2020), which is the substance of Keith and McKay (2024)’s position. The open part is a moving target: each platform’s quality changes from year to year, so a published comparison ages quickly.

Endogeneity correction without instruments. When no credible instrument exists, can a distributional assumption stand in for one? Park and Gupta (2012) proposed modeling the joint distribution of an endogenous regressor and the structural error with a Gaussian copula, so that identification comes from the regressor’s non-normality rather than from an exclusion restriction, and the method spread quickly because instruments are scarce. Simulation studies then found a fundamental bias in models with an intercept, which describes almost every applied model, along with low power in smaller samples (Becker, Proksch, and Ringle 2022), and showed that performance deteriorates quickly when assumptions that cannot be tested are violated (Eckert and Hohberger 2023). Refinements followed: a panel version with fixed effects (Haschka 2022), an adjusted estimator that reduces the finite-sample bias (Liengaard et al. 2025), and a two-stage approach that tolerates normally distributed endogenous regressors and correlation between endogenous and exogenous regressors (Yang, Qian, and Xie 2025). Instrumental variables are developed in Section 44.6, and the endogeneity problem in choice models in Section 59.12.

Where it stands: settled in part. The original estimator’s limits have been documented by independent simulations and are the starting point of every refinement since (Becker, Proksch, and Ringle 2022; Eckert and Hohberger 2023; Liengaard et al. 2025; Yang, Qian, and Xie 2025). Whether the refinements make the approach a primary identification strategy, rather than a check, is open: they keep the Gaussian copula’s assumed dependence between regressor and error (Yang, Qian, and Xie 2025), and some of the approach’s assumptions cannot be tested (Eckert and Hohberger 2023). Our read: report a copula correction beside a design-based estimate rather than in place of one, together with the evidence of non-normality it relies on.

Laboratory experiments and external validity. Must a theory test resemble the market it is about? Calder, Phillips, and Tybout (1981) distinguished two kinds of generalization, applying a specific effect and applying a general theory, and argued that whether student subjects and laboratory settings are appropriate depends on which of the two a study claims. Lynch (1982) replied that the handling of unmanipulated background factors governs how useful an experiment’s results are, and the exchange continued through three more replies in the same journal (Calder, Phillips, and Tybout 1982, 1983; Lynch 1983). Later work moved the argument toward evidence and practice. Effect sizes from student samples differ from those of adult samples in both direction and magnitude, with no systematic pattern (Peterson 2001), and Morales, Amir, and Lee (2017) map when realistic manipulations and measures of actual behavior are worth their cost. The field-experiments seminar takes up external validity and scaling (Section 61.13), and the consumer-behavior seminar the related question of what counts as consumer research (Section 63.2.1).

Where it stands: open. The disagreement in principle was never resolved, but it is easier to act on than it looks. Our read: a paper should state which kind of generalization it claims. A theory test can defend a convenient sample on Calder and colleagues’ grounds, but a claim that an effect will appear in a market needs a sample and setting from that market, and Peterson (2001) show why a student result is no substitute.

Single-item versus multi-item measures. Does every construct need several items? Bergkvist and Rossiter (2007) found that single-item measures of attitude toward the ad and toward the brand predicted as well as multi-item scales, and concluded that constructs made of a concrete object and a concrete attribute should be measured with one item, in line with the C-OAR-SE procedure cited above. Diamantopoulos et al. (2012) replied with a simulation in which, under most conditions met in practice, multi-item scales predict clearly better and single items match them only under narrow conditions; Bergkvist (2015) answered that appropriate single-item measures are here to stay. Reliability and validity are developed in the measurement-scales chapter (Section 39.4).

Where it stands: open. Both positions allow single items under some conditions and disagree about how common those conditions are, which Diamantopoulos et al. (2012) find narrow even for concrete constructs. Our read: a single item needs an argument that its construct is concrete, and a paper using one should show predictive or convergent validity directly, since a single item yields no internal-consistency estimate.

Median splits and mean-centering. Two habits of moderation analysis in consumer research drew formal exchanges. Iacobucci et al. (2015b) argued from simulations that a median split of a continuous predictor can be as good as the continuous variable and is sometimes preferable for parsimony. Two commentaries in the same issue disagreed: Rucker, McShane, and Preacher (2015) recommended that regression on the continuous variable remain the normative procedure, and McClelland et al. (2015) reported technical errors in the simulations and concluded that median splits bring no real benefit while costing power and adding false positives. The original authors’ rebuttal confined their claim to independent variables that are uncorrelated (Iacobucci et al. 2015a). The second habit, mean-centering to reduce collinearity in moderated regression, was examined analytically by Echambadi and Hess (2007), and Iacobucci et al. (2016) distinguished the correlation between a variable and its own product term, which centering reduces, from collinearity in the model as a whole, which it does not. The power cost of discarding information is taken up with sample size in Section 40.7.7.

Where it stands: mean-centering settled; median splits converged in practice. Echambadi and Hess (2007) prove that centering changes neither the precision of any estimate, simple and interaction effects included, nor \(R^2\), so centering is a choice about how to interpret lower-order coefficients and does nothing for collinearity. For median splits, even the defense now covers only uncorrelated predictors, and the continuous alternative costs nothing: a regression with spotlight tests at focal values, or a floodlight range of significance, answers the same question (Spiller et al. 2013).

Language-model respondents. Can a large language model stand in for survey or experimental participants? Argyle et al. (2023) showed that persona-prompted models reproduce subgroup response patterns in aggregate. In marketing, GPT-3.5’s survey answers were consistent with downward-sloping demand and gave willingness-to-pay estimates of realistic magnitude (Brand, Israeli, and Ngwe 2024), and later studies tested models as substitutes or supplements in perceptual analysis and preference measurement (P. Li et al. 2024; Goli and Singh 2024). Critics document compressed variance and answers that swing with prompt wording and model version (Bisbee et al. 2024), and argue that substituting models for members of identity groups misportrays and flattens those groups (Wang, Morgenstern, and Dickerson 2025). Calibrating model outputs against human benchmarks is the newest response (Leng, Sang, and Agarwal 2026). The surveys chapter develops the method and its cautions (Section 40.4.4).

Where it stands: open. The models change faster than the evaluations, so a verdict on any one model ages quickly. Our read, as stated in Section 40.4.4 following Sarstedt et al. (2024): silicon samples belong upstream, in pretesting items and piloting designs, and not in the data that adjudicates a claim about people.

Table 78.3: Where each debate in the tour stands, and a request a referee can make without taking a side.
Debate Where it stands A request every side can accept
Structural vs. reduced-form Converged in practice Say which variation identifies each key estimate
Formative vs. reflective Open Justify the measurement direction; name the outcomes that identify a formative block
PLS-SEM Settled in part State whether constructs are composites or common factors; use a consistent estimator for the latter
Advertising returns Settled within limits Validate observational attribution against an experiment, or bound its error
Nudge effectiveness Settled within limits Power the study for at-scale effects, not published ones
Observational mediation Settled Report a sensitivity analysis for sequential ignorability, or manipulate the mediator
Common method bias Converged in practice Describe how predictor and criterion were separated by design
Online-panel quality Settled within limits Preregister exclusion rules; report screening results by platform
Copula endogeneity correction Settled in part Report the regressor’s non-normality and the estimate without the correction
Lab experiments and external validity Open State whether the claim is an effect application or a theory application
Single- vs. multi-item measures Open Argue that the construct is concrete; show validity directly
Median splits and mean-centering Centering settled; splits converged in practice Report the continuous-variable analysis alongside any split
Language-model respondents Open Benchmark synthetic responses against human data, variances as well as means

78.7 An Index of the Book’s Documented Controversies

The first eight debates above, and many episodes not on that list, are developed somewhere in this book as a Controversy callout: a dated, chronological account of what was published, by whom, and in what order, with every claim traceable to a cited source. The five added after them are treated as methods in their home chapters rather than as narrated episodes, so they are not indexed here. Table 78.4 is the index. It is worth reading straight through at least once, because the recurring structural features—the years-long lag before anyone writes a comment, the reply that is shorter than the attack, the journal that prints both sides and adjudicates nothing—say more about how the field actually self-corrects than any single dispute does.

Table 78.4: Controversies internal to marketing, with the chapter that develops each and the kind of breakdown it illustrates.
Controversy Chapter What kind of failure
Common method bias: how much does it matter? Chapter 3 Target article, two adjacent commentaries
The satisfaction anomaly, 1994–2026 Section 4.6.1 Unreplicated claim, undisclosed estimator
Net Promoter: the one number Chapter 4 Practitioner claim, disconfirmed and adopted anyway
SERVQUAL vs. SERVPERF Section 6.3 Measure that lost the argument and kept the users
Advertising returns without an experiment Chapter 14 Commercially load-bearing method, weak identification
The constructive format (IJRM 31(1)) Chapter 14 Two teams, mutual commentaries, same issue
How big is a nudge? Chapter 20 Meta-analysis vs. two reanalyses, one year
Formative constructs: are they constructs? Chapter 39 Ontological, so no dataset resolves it
PLS-SEM and what counts as a latent variable Section 39.2.5 Critique and reply, same journal
Is MTurk broken, or is your screening? Section 40.4 Attribution: platform failure or study design
Structural vs. reduced-form Section 38.1 Two camps answering different questions
Observational mediation Section 44.9 Ubiquitous procedure, untestable assumption
Distributed MCMC for hierarchical Bayes Section 45.1.7 Methods claim, challenge, short reply
Duelling in the back pages Section 78.5 Comment, erratum on another team’s model, rejoinder
The retraction wave, 2021–2023 Section 78.3 Post-publication scrutiny, not peer review
What is consumer research? Section 63.2.1 A schism about what counts as a contribution
Money priming, across four papers Section 63.2.12 Vote counting is not evidence aggregation
Too many options, and the jam study Chapter 13 A vivid effect that turned out conditional
Is there a reservation price to measure? Chapter 41 The construct the instrument presumes
Can you estimate a Bass model pre-peak? Chapter 28 In-sample fit is not forecasting ability
Does differentiation do anything? Section 12.3 A tradition that disputes the chapter’s premise
Does the machinery beat a rule of thumb? Chapter 17 Benchmark against the naive alternative
The EDLP experiment that went the wrong way Chapter 21 A sound mechanism, the wrong policy inference
Which reference-price model is right? Section 21.5 A construct whose operationalization never converged
Do loyalty programs create loyalty? Chapter 16 Evidence that looks the same either way
Does the recovery paradox happen? Section 22.6 A regularity that holds only under conditions
Is service-dominant logic a theory? Chapter 22 A lens is not a warrant
Contracts and trust: substitutes or complements? Section 66.3 One construct, two dimensions, opposite signs
The long tail, and what recommenders did to it Chapter 13 Two links in the chain run opposite ways
Who fakes reviews, and detecting it Chapter 13 Identifying a deliberately concealed behavior
The externalities a platform does not price Chapter 70 Optimizing your own sides misses the rest

Marketing does not generate its methods from scratch, and it did not generate its methodological crisis from scratch either. Sixteen further episodes, imported from the neighbouring fields, are narrated where the relevant method is taught, because a marketing student inherits these arguments along with the tools.

Table 78.5: Controversies imported from the fields marketing borrows its theory and methods from.
Controversy Field Chapter Why it matters here
The paper that broke psychology’s confidence Psychology Section 78.1 The trigger for every reform in this chapter
How bad is the replication rate? Psychology Section 78.1 A fight about the statistic everyone quotes
Ego depletion at scale Psychology Section 63.2.8 A generative paradigm, tested properly
The spreadsheet that moved fiscal policy Economics Chapter 33 Why the pipeline must be code, not cells
The fast-food minimum-wage study Economics Section 44.1.2 Where design-based disputes actually end up
Can matching recover an experimental answer? Economics Section 44.1.3 The attribution question, thirty years earlier
Efficient markets, and the Nobel that split Finance Chapter 26 The assumption every event study rests on
The finance anomaly audit Finance Section 26.9.1 The base rate for any “X predicts returns” claim
The significance wars, in order Statistics Section 78.2 Three camps, none of which won
The two cultures Statistics Section 69.1 Prediction and inference are different jobs
Is the resource-based view a theory? Management Chapter 26 The tautology risk in any asset argument
How much does industry matter? Management Section 10.3 Variance decompositions are not assumption-free
An issue on whether to retire one model Info. systems Chapter 28 What happens when a model becomes infrastructure
Do accounting numbers mean what we assume? Accounting Section 32.1.4 Every Compustat control rests on this
The bullwhip effect, and measuring it Operations Section 66.2 A real mechanism need not dominate the data
Fighting fire with fire Management / IS Section 77.13 The dispute is about peer review itself

The distribution across both tables is the point. Of forty-seven narrated episodes, exactly one concerns fabricated data. The rest are undisclosed procedures, untestable assumptions, category errors about what a measure is, a formula error in a spreadsheet, claims that outran their evidence, and disagreements that were printed and then left unresolved. Those are the failure modes a referee will actually encounter, and none of them is caught by asking whether the authors are honest.

One further pattern is visible only when the two tables are read together. The economics cases (Section 44.1.3 and Chapter 14) reach the same conclusion about observational versus experimental estimates from completely separate literatures three decades apart, and the psychology cases explain why marketing’s own reforms took the shape they did. A student who reads only the marketing column will mistake local history for the whole argument.

78.8 Key Takeaways

  • Exploiting researcher degrees of freedom, or simply following a garden of forking paths, can manufacture significant support for an effect that does not exist (Simmons, Nelson, and Simonsohn 2011; Gelman and Loken 2014). The live dispute is how much of the literature this has contaminated, not whether the mechanism is real.
  • Large coordinated replications find replication rates materially below 100 percent and replication effect sizes well below the originals (Figure 78.1). The exact rate is contested, and the causes (false positives, hidden moderators, drift between original and replication) cannot be separated from the aggregate statistics.
  • Where independent observations are expensive, count the units per arm and check whether treatments were randomized within a session. In an archival replication, ask which tables were reproduced and whether the data vintage is reported.
  • Preregistration and registered reports discipline confirmatory inference without displacing exploratory analysis, provided the exploratory part is labeled as such.
  • There is near-universal agreement that a mechanical p < .05 line is misused, and three competing remedies (Table 78.1). The requests compatible with all three are effect sizes with intervals, a stated and justified threshold, and no claim that an effect is absent because it missed significance.
  • Forensic tools (Table 78.2) and posted raw data are what make independent verification possible. Integrity cases are described here only from public records, without verdicts on any person.
  • Marketing’s best-documented credibility episode involved no fabrication. An undisclosed estimator, an unjustified threshold, and a favorable sample window were sufficient (Section 78.4), and the financial-interest question it raises is one a submission form may not ask.
  • The field corrects itself through comments, errata, and rejoinders that arrive years late, run shorter than the challenge, and are printed without adjudication (Section 78.5).
  • Marketing’s methodological debates are not all equally open (Table 78.3). Two are settled by proof (mediation identification and mean-centering), several are settled by evidence within stated limits, and four remain open in principle: formative measurement, the external validity of laboratory experiments, single-item measures, and language-model respondents. A referee should treat the settled points as settled and, on the open ones, ask only for what every side accepts.
  • Across the forty-seven controversies indexed in Table 78.4 and Table 78.5, the failure modes a reader will actually meet are undisclosed procedures, untestable assumptions, category errors about measures, and claims that outran their evidence.

78.9 Further Reading

The diagnosis is best read in its original form: Simmons, Nelson, and Simonsohn (2011) on researcher degrees of freedom and Gelman and Loken (2014) on forking paths, followed by the replication evidence in Open Science Collaboration (2015) and Camerer et al. (2018). Munafò et al. (2017) and Nosek et al. (2018) set out the reform agenda, and Wasserstein, Schirm, and Lazar (2019) surveys the post-significance options without choosing among them. For the economics side of the revolution, which reorganized empirical work around research design rather than replication, start with Angrist and Pischke (2010) and continue in Chapter 44. The review-side machinery that implements these reforms, from data editors to the referee’s own validity requests, is in Chapter 77.

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  1. Journal of Marketing Research retraction notices, doi:10.1177/00222437221101398, doi:10.1177/00222437221139856, and doi:10.1177/00222437221149006. The notices are cited here only as evidence that the retractions occurred.↩︎