Our principle
We use AI to draft texts and organize material. The editorial team is responsible for every statement, every source and every score: Prof. Dr. Stephan Weibelzahl, professor of business psychology. A source named by an AI counts as unconfirmed with us until a person has checked it.
How a page is made
- Topic and search intent: Which question does the page answer? Guides (application) and concepts (terms) are kept apart so that nothing is written twice.
- Collecting sources: We start with primary sources. A book or blog counts only as a pointer to the original study.
- Draft from a template: opening, effect in brief, practical cases, ethics check, Science Corner, limits and criticism, FAQ.
- Fact check: Every source is cross-checked against a publisher or repository record (existence, authors, year, pages, DOI). Figures are read in the original. We check whether the study actually supports the statement.
- Scoring: According to the rubric, with justification. In case of doubt, the lower value applies.
- Ethics and legal check: See the code of ethics. We have legal notes reviewed by a lawyer.
- Publication with a check date.
- Review after twelve months at the latest.
Technically, the build enforces part of these rules: a page can be published only if all of its sources are marked as cross-checked.
What we found during checking
That this process is necessary is shown by how this site itself came about. In our first drafts, which came out of AI research, we corrected the following, among other things:
| Finding | Correction |
|---|---|
| Wrong journal details and DOI for Nunes and Drèze (2006) | Correct: Journal of Consumer Research, 32(4), 504–512 |
| The Zeigarnik waiter story presented as part of her experiment | It is an anecdote from the circle of Kurt Lewin |
| Rule of 100 presented as a result by Kahneman and Tversky (1979) | Prospect theory does not test discount framing. Berger (2013) coined the name |
| Left-digit figure using “2.01 versus 2.00” | That is not a 99 ending and is more expensive rather than cheaper. Thomas and Morwitz (2005) compared 3.59 with 3.60; the figure now shows that pair |
| Hull (1932) given as an observation that rats run faster closer to the goal | Hull (1932) is a theoretical paper; the running speed is a derived prediction there. Hull only tested it in a separate paper in 1934. The intended source is Hull (1934) |
| Left-digit effect explained by the dropping of right-hand digits | Anderson and Simester (2003) reject this explanation against their sales data and consider a price signal more plausible. Bizer and Schindler (2005) demonstrate the dropping only among participants with no motivation to calculate carefully. The mechanism is open |
| Currency-symbol figure with a column “without decimals” | Yang et al. (2009) tested three different formats: dollar sign, bare numeral and spelled-out currency. The figure now shows those three |
| Knutson et al. (2007) cited as evidence of insula activity at excessive prices | That is what the summary says. In the discussion the authors report that the link to the price differential was not significant (Z = −1.36) |
| Wieseke et al. (2016) given as four field experiments on sales | Only study 1 measures sales (n = 306); the other three are surveys. In the path model, round prices lower price attractiveness directly |
| Sunk-cost scenario in the Many Labs project described as replicating “consistently” | In the aggregate yes (d = 0.27), but only half of the 36 individual samples reached significance |
| Anchoring replication cited without the authors’ own correction | Klein et al. collapsed a two-step question into one step; their own follow-up test shows this enlarges the effect. None of the four anchor questions was a price |
| Anchoring on experienced B2B buyers described as “likely more weakly” | Furnham and Boo (2011) report the opposite: car dealers and estate agents anchored just as much. Their conclusion: experience does not appreciably reduce the bias |
| Described as having “no direct evidence” for pricing pages | Too absolute. The same review names a meta-analysis on reference pricing and a study on online auctions. We have not read them, but they exist |
| Fudenberg et al. (2012) rendered only as “strength varies” | Too vague. For willingness to pay — the quantity that matters for pricing pages — they found no effect at all. Their own conclusion: real, but quantitatively small |
| Concept page still said there is “no direct evidence” for pricing pages | The same absolute claim we had already corrected in the guide was still on the concept page |
| Frederick et al. (2014) rendered as the effect “often failing to appear” | Too mild. In the 27 studies with directly experienceable attributes it never once reached significance, and once ran the other way |
| Pricing tables described as especially close to lab conditions | That was our inference, not the sources’. The closest matching case — the Economist subscription — failed twice for Frederick et al., most recently with 2,003 respondents |
| Compromise effect described as stronger under pressure to justify | Simonson’s numbers support that for the attraction effect only. For the compromise effect the difference stayed below significance |
| DelVecchio et al. (2007) given only as a suggestion about price expectations | Too weak. The shift is demonstrated across two studies, and a third shows it in repeat choice after the promotion (44.6 versus 25.0 percent) |
| Two equally weighted mechanisms named behind the effect | The authors identify the shifted price perception as the main route: control for it and the interaction disappears |
| “Only the tyre experiment” named as the sole sample outside lecture halls | Wrong. Choi and Mattila (2014) surveyed 174 adults from an online panel |
| Sense of power in Choi and Mattila reported without noting the design | It was measured and split at the median, not induced. Only the presentation was randomly assigned |
| Freedman and Fraser’s first experiment described as a doorstep survey | It was run by telephone. Only the second experiment, with the road-safety signs, took place at the front door |
| The figure stated that hardly anyone refuses the first request | In the original about two thirds agreed; in the direct replication 10 and 18 of 30 respectively |
| Foot-in-the-door qualified only as “mainly for prosocial requests” | Too soft. For for-profit senders the effect in Dillard et al.’s (1984) meta-analysis is r = 0.02 |
| Arkes and Blumer’s theatre finding reported without its limits | The difference held only in the first half of the season, rests on 54 people and on one-tailed planned comparisons |
| “Zeigarnik’s own figure of 1.61” | That number comes from the 2025 meta-analysis, not from her paper. Zeigarnik reports 1.9 to 2.1 for her main conditions |
| Zeigarnik (1927) reported without the limits she states herself | The memory advantage disappeared with fatigue, with distraction, on the following day, and when all tasks were named in advance — the case that corresponds to a step indicator |
| Tversky and Kahneman’s (1974) wheel-of-fortune experiment given without its figures or its evidential weight | Medians of 25 and 45 percent for starting values of 10 and 65. The article is a review piece and reports neither sample size nor significance test for this experiment |
| “According to the authors, the head start needs a plausible reason” | Only when progress is counted in purchases. Counted in points it worked without a reason, and the reason did not have to be sound |
| The reply by Huber et al. (2014) rendered as a plain objection | The authors hold the boundary conditions to be real and the effect to be rare in today’s market; Huber himself found no gain for the dominating option across 586 people |
| Ovsiankina’s (1928) resumption rate given as 91 percent | Her summary does not report that figure. It gives 74 percent for interruptions by the experimenter and 100 percent for apparently accidental ones; the 91 percent is a sub-finding for cases where the work had not been seen beforehand |
| Chen, Monroe and Lou (1998) described as showing no effect, based on a secondary account | The full text shows a significant interaction for perceived savings (r = 0.17), in both directions. Only purchase intention showed no effect. The threshold at 100 was first tested by González et al. (2016) |
| Decoy effect as established (5 out of 5) | Disputed, effect score 3 |
| Progress bars: statement on fast and slow starts | An early draft said the opposite of what the meta-analysis by Villar et al. (2013) shows |
| Foot-in-the-door: replication described only as “examined again” | The direct replication found a mixed picture, see the guide |
| A price threshold attributed to Choi and Mattila (2014) | Could not be confirmed and was removed |
| Goldstein et al. (2008) described as a study run “in hotels” | Both experiments ran in the same US hotel, with the same authors. The second does not replicate the first independently |
| “75 percent” reported as a finding of the towel study | The figure came from the largest manufacturer of such signs and stood on the sign as a claim. What was measured was 44.1 percent. The authors note the gap themselves |
| The room norm presented as beating the general guest norm | It was tested against the average of the three other normative versions (49.3 versus 42.8 percent). The direct comparison with the guest norm alone (44.0 percent) is not reported as a test of its own |
| The specificity rule read as closeness to the target group | The advantage holds for the same situation, not for similar people. Gender and citizenship as reference groups mattered more to respondents and still did no better than the general norm |
| Schultz et al. (2007) presented as coming from the same year as Goldstein | It appeared a year earlier. Goldstein still cites it as a submitted manuscript |
| The evaluative mark in Schultz described only as approval | Frugal households got a happy smiley, heavy consumers a sad one. The injunctive norm was approval and disapproval |
| Boomerang and saving presented as equally solid | After four weeks the boomerang held (d = 0.59), while the saving among heavy consumers was no longer significant without the evaluative mark. The harm outlasted the benefit |
| Combining the two norms read as an amplifier | It prevents the boomerang. The extra saving among heavy consumers (1.72 against 1.22 kilowatt-hours a day) was not significant |
| Melnyk et al. (2022) announced as the work that would settle the magnitude | The mean sits at r = 0.254, but only 40 of the 250 effect sizes come from experiments. The rest are associations between a perceived norm and reported behaviour |
| The worry that norms only carry recurring routines left as an open question | Melnyk et al. test three obvious distinctions — public against private, permanent against one-off, high against low effort. None made a difference |
| Reactance presented as the best-grounded objection to a blanket informal tone | None of the 20 experiments in Rains (2013) varied the form of address or the familiarity claimed. The threat to freedom came from commanding phrasing |
| Rains (2013) read as evidence that pressure spoils the effect | The direct link between a threat to freedom and attitude is not significant there (r = 0.06). Only the indirect route through reactance is demonstrable |
| “Scarcity caused by others’ demand” treated as one pattern | It is two. The reason for the scarcity worked in Worchel et al. (1975); the announced number of other takers did not, and reversed on the price judgment |
| The cookie study reported without its limits | 134 participants in the analysis, all of them women. In the second experiment the effects appeared only among people who had not seen through the purpose; with the rest included, nothing remained. Taste was untouched |
| Lynn (1991) announced as the work that would settle the magnitude | It does settle it: r = 0.12 across 41 studies, 0.17 without five contrary ones. Reliable and small |
| Worchel and Lynn presented as two supports side by side | The cookie study is one of the 41 works in Lynn’s meta-analysis, so not an independent confirmation |
| Subtitle of Aggarwal et al. (2011) cited wrongly | Correct: A Consumer Competition Perspective |
| Quantity and time scarcity described as working by different routes | Both work by the same route: perceived competition with other buyers. A number of units produces it more strongly than a deadline |
| Aggarwal et al. (2011) invoked for online shops | The authors explicitly place online buying outside their scope, because deals are easy to compare there |
| Shi et al. (2020) presented as a review of the more recent literature | The review spans 1970 to 2017, is not a meta-analysis and gives no effect size. It covers only journals rated three or four stars on the ABS list, which excluded Lynn (1989, 1992) |
| Reasons given in terms of others’ demand recommended as the most effective form | They also count as the most liable to the suspicion of deception, because customers do not credit sellers with being able to quantify demand reliably |
| Burger (2009) presented as a replication of the paper cited here, Milgram (1963) | Burger reconstructed Experiment 5 from Milgram (1974). In the 1963 version the victim does not protest at all until 300 volts |
| Burger’s obedience rates reported as close to the original | 70 against 82.5 percent, not significantly different — but measured only up to 150 volts. The rest is an inference from Milgram’s data, not a measurement, as Burger writes himself |
| Burger’s sample reported without its pre-selection | About a third of those interested were screened out by telephone, a clinical psychologist excluded 38 percent of the remainder, plus everyone who had taken more than two psychology courses |
| Milgram read as evidence for a general authority principle | Milgram himself lists thirteen features of the experimental situation meant to carry the high obedience, among them the reputation of Yale and the complete absence of any chance to confer |
| Doliński et al. (2017) announced as a replication of the study cited here | It tests Experiment 2 from Milgram (1974), Burger tested Experiment 5, and the version cited is the one from 1963. Three related but not identical setups |
| Both replications read as confirming the full finding | Burger and Doliński both stop after the tenth of thirty buttons. How far people actually go is extrapolated in both papers, not observed |
| Doliński et al. (2017) presented without their own caveat | 72 of 80 pressed the tenth button. The authors call that a ceiling effect themselves: with eight refusals no moderating factor can be demonstrated, not even their own question about the victim’s sex |
| Trust badges at checkout presented as a question without checked research | Kim et al. (2008) and Head & Hassanein (2002) are now available in full text. In Kim the attitude towards seals correlates with trust at 0.05 and with purchase intention at 0.02; the effect score of 1 therefore rests on findings rather than on absent research |
| Trust signals justified with non-peer-reviewed practitioner research | The unsourced claim on the concept page has been replaced by Kim et al. (2008). There, perceived privacy protection, information quality and reputation explain trust; the seal does not |
| The single significant path in Kim et al. could be read as an effect | The path from the seal to perceived risk (−0.216) rests on a zero correlation of −0.03. It emerges only once other variables are partialled out and is not presented here as an effect |
| Widely quoted sales figures for trust seals taken over unchecked | The figure of more than 66 percent additional sales in López Jiménez et al. (2021) comes from a survey of 127 retailers who already carry a seal, not from buyers. The work is therefore listed as a market source, not as evidence |
| Hasan (2016) checked and not included | The paper measures no trust seals but perceived irritation among 93 students after an aborted purchase; it adds no evidence to the questions these pages ask |
| Credibility research presented as inconsistent throughout | Pornpitakpan (2004) records that almost all studies of the main effect find the credible source superior and that contrary findings are “few”. What is inconsistent are the interactions, not the main effect |
| Expert voices recommended without contraindications | Three situations are documented in which the less credible source is superior: a positive existing attitude to the brand, the customer’s own experience of the product, and a claim that runs against the sender’s own interests |
| The sender effect presented without its relation to evidence | Where the message contained supporting evidence, high- and low-credibility senders were equally persuasive. Unfamiliar evidence helped only the low-credibility source |
| Expert voices recommended across all product types | For packaged everyday goods neither expert nor celebrity did anything; there the typical consumer was the most effective sender (Friedman & Friedman, 1979) |
| Five decades of findings read as findings about the same thing | The factor analyses of the construct are considered open to attack, and the factors found changed over the years. Pornpitakpan herself calls them unresolved and includes studies of both kinds |
| Amos et al. (2008) presented as general support for expert voices | The paper measures celebrity endorsers. The largest value is negative information about the person (r = −0.62); trustworthiness (0.46) beats expertise (0.38), and performance in the celebrity’s own field correlates at practically zero |
| The mean r values in Amos et al. read as weighted figures | The authors put a note under their table saying these are unweighted values; the test was run on weighted ranks. The most striking value rests on about eight of the 266 effect sizes |
| Celebrity effect sizes carried over to a German-language market | Outside the US they came out less than half as large (0.19 against 0.45), and among non-students about half as large (0.25 against 0.49) |
| The factor of 2 attributed to Kahneman and Tversky (1979) | The 1979 paper gives no number. The factor comes from Tversky and Kahneman (1991) and rests on mug experiments ($7.12 against $3.12); the authors themselves advise reading that estimate with caution |
| Prospect theory reported without its data basis | Hypothetical bets answered on questionnaires by students and faculty, usually 66 to 95 people per problem. The authors name the limits of that method themselves |
| Gal and Rucker’s objection reported as a mere matter of interpretation | It is methodological: the endowment effect vanished with the same sample and the same stimuli once keeping was an active choice too — 41 against 18 percent became 26 against 26 |
| The criticism of loss aversion dated to 2018 | Gal and Rucker trace it back to Gal (2006). 2018 is the year it was widely noticed in consumer psychology, not the year it arose |
| Loss framing in copy recommended without the meta-analysis on it | In O’Keefe and Jensen (2007), reported by Gal and Rucker, loss framing was significantly superior in no application area across 93 studies — and inferior for prevention messages |
| The size of loss aversion left open | Brown et al. (2024) collect 607 estimates from 150 papers: mean 1.96 (1.82 to 2.10), median of the raw values 1.69, range 0.04 to 23.46. 93.9 percent of the estimates lie above 1 |
| The much-quoted 2.25 attributed to the 1991 paper | It comes from Tversky and Kahneman (1992): 25 graduate students, unincentivised lottery choices, only the median reported. Brown and colleagues judge it pitched too high |
| Gal and Rucker’s objection left standing as an open dispute | Mrkva et al. (2020) defuse it for choices under risk: at least ten papers offer a choice between two lotteries, neither of which is the status quo — and people are loss averse there too |
| A factor of about 2 assumed for small amounts as well | In Mrkva et al.’s German-speaking sample it was 1.12 (1.07 to 1.17) for bets of €6, and between 1.8 and 2.7 for the same 360 people’s trading tasks |
| The coefficient from decision research carried over to brand choice | Neumann and Böckenholt (2014), reported by Brown and colleagues, find 1.49 rather than 1.96 for consumer brand choice |
| Loss aversion treated as a property of all buyers | It varies systematically: stronger with age (d between 0.11 and 0.20), weaker with product knowledge — and attribute by attribute, with d = −0.53 for the interaction |
| Loss framing in copy carried at effect score 3 | Downgraded to 2. As attribute framing it stands at d = 0.26, and in O’Keefe and Jensen there is no application area where it is significantly superior |
| The self-reference effect carried without an effect size | Symons and Johnson (1997): d = 0.50 across 129 effect sizes — 0.65 against semantic processing, 0.35 against reference to another person, 0.20 against an intimate other |
| Rogers et al. (1977) reported without its sample size | 32 people in the first experiment, 27 in the second. In the second the rest of the depth hierarchy collapsed; the authors note that their group procedure typically fails to replicate it |
| Self-reference presented as a lever for product copy | For nouns it stands at d = 0.03 against reference to another person, at 0.16 against a desirability question, and at 0.02 when a memory test is expected — none of the three distinguishable from zero |
| “Self-referencing” treated as a single term | In the marketing literature it often denotes meta-advertising that points at itself. Iyer and Mallika (2023) run both under one name, which is why we did not include that work |
| Loss aversion in decisions carried at effect score 3 | Raised to 4 once Brown et al. (607 estimates) and Mrkva et al. (17,720 respondents) had been read: 93.9 percent of the estimates lie above 1, and the status-quo objection does not bite for choices under risk |
| Endowment effect and free trials carried at effect score 3 | Lowered to 2: Mrkva et al. themselves concede the endowment effect can be explained without loss aversion — by aversion to bad deals, to selling on unfavourable terms, or by plain feelings of ownership |
| Packard et al. (2018) carried as a single study | It is six studies: field data from 1,277 customer-service emails linked to purchases over the following 90 days, plus lab experiments with more than 1,600 participants |
| Which pronoun works in customer contacts was not stated | Only the agent’s own first person (β = 1,245.76, p < .001). “We” (p = .18) and “you” (p = .33) show no effect |
| Direct address of the customer assumed to work | It is a solid null finding: the authors tried four times to overturn it, and a Bayesian analysis across five tests puts the null more than a hundred times more likely than an effect |
| Addressing the customer treated as harmless throughout | Where the customer is made the actor rather than the recipient, satisfaction and purchase intentions fall from 4.88 to 4.41. In the field data this applied to about a quarter of all uses of “you” |
| Burnkrant and Unnava (1995) reported as a general amplifier | On Packard and colleagues’ account, self-reference worked there only under four simultaneous conditions: low involvement, strong and positive arguments, no competing stimuli, moderate volume |
| Reactance carried without a note on its measurability | Rodrigues et al. (2019) state that it is practically impossible to establish whether reactance is occurring; they consider the corresponding manipulation check unusable |
| Burnkrant and Unnava (1995) cited as evidence that self-reference hurts with weak arguments | Weak arguments do not appear in the paper; both experiments used strong ones throughout. That finding belongs to Burnkrant and Unnava (1989) and says something different: there, strong and weak arguments did not differ at all under low self-referencing |
| The tipping point of direct address misnamed | It is not argument strength that reverses the effect but a second amplifier in the same copy: a relevant product picture removed the advantage (4.70 against 4.59), rhetorical questions reversed it (5.90 to 5.43) |
| Packard’s summary of Burnkrant adopted unchecked | Two of the four conditions named there are not in the paper that way: the volume of address was never varied, and argument strength belongs to the 1989 paper |
| The advertising study carried without its sample size | 61 and 75 students, a single invented product. The authors themselves call for testing on samples more representative of the advertiser’s target market |
| Self-referencing through direct address carried at effect 3 and transfer 2 | Lowered to 2 and 1: with nouns the effect is d = 0.03, against a desirability question 0.16, and rhetorical questions reverse it |
| Pronouns in service contacts carried at effect score 2 | Raised to 3, after the justification for the cap — a single study — proved false |
| The evaluative mark presented as a reliable safeguard against the boomerang | It holds for the 287 households in Schultz et al. (2007). At scale, consumption still rose among politically conservative households above the norm (Costa & Kahn, 2013) |
| The role of the referent group tied to Goldstein et al. (2008) alone | The 2018 retrospective names identification with the referent group as the factor that decides between effect and reversal at scale |
| Bickman (1974) cited as evidence that a uniform produces more compliance | Only the guard’s uniform worked. The milkman’s did not differ from plain clothes — Bickman himself: the power lies in the type of uniform, not in its mere presence |
| Bickman’s legitimacy reading carried over unexamined | It is an argument by elimination, not a measurement. His own two questionnaire studies find the guard neither more legitimate nor more obeyed |
| Brehm’s book called irreplaceable because no secondary source carried its data | Wrong. Miron and Brehm (2006) report the film experiment from the book, written up by Brehm himself |
| Reactance as a personality trait carried without qualification | All three common scales are held to be psychometrically questionable; Miron and Brehm consider the trait reading of little value, and one finding even reverses the expectation |
| Reactance presented as rising with pressure | Brehm corrects this himself: it depends on the difficulty of restoring the freedom and falls to zero once the freedom is lost for good |
| Goal gradient and Ovsiankina carried at effect score 4 | Lowered to 3. Both rest on a mixed replication record, which under rule 3 allows at most 3 |
| Evaluability and compromise effect carried at effect score 3 | Lowered to 2. Both rest on a single study without replication, which under rule 2 allows at most 2 |
| Brehm’s correction on the difficulty of restoration presented as settled | Too confident. Steindl et al. (2015) list the question explicitly as open. What has support is the related distinction from Laurin et al. (2012): the unavoidable is rationalised, the avoidable produces reactance |
| The injunctive norm’s protection against the boomerang carried as a single finding of Schultz (2007) | Cialdini et al. (1990) show the same in experiment 4 with swept litter. The score stays at 2, because Cialdini co-authored both papers |
| The specificity rule called “the least independently tested part of the field” | Out of date. Bohner and Schlüter (2014) replicated it directly in two German hotels. In study 1 the same-room advantage reversed significantly (78.0 against 85.6 percent, p = .017) |
| Normative messages presented as more effective than a standard environmental appeal | Not supported in Germany: 81.9 against 83.7 percent (no difference), and in the second study the environmental appeal was actually superior (93.3 against 76.5 percent) |
| Georgescu and Herman (2020) checked and not taken up | The paper measures intentions, not behaviour, across 340 students in a quota sample; its “social norm” is a single yes/no question asking respondents whether they attribute their own behaviour to it. A null result from self-report about one’s own motives is not evidence against the effect |
| Han, Lee and Kim (2018) checked and not taken up | The paper does not measure social norms at all. It models moral obligation as an alternative to them and collects intentions through an online panel; it can contribute nothing to the question of whether normative messages work |
| Social proof carried at effect score 4 with an unchecked replication record | The replication record is set to mixed and the score lowered to 3. The direct replication by Bohner and Schlüter (2014) failed on two of three points; rule 3 then allows at most 3 |
| Specific reference group carried at effect score 2 | Lowered to 1. Level 1 here does not mean “no research” but “research exists and finds practically nothing” — and after the German replication that is the situation |
| Processing fluency said we had read no replication study | Out of date. Bornstein (1989) pools 208 effect sizes on the repetition effect (r = .26); Meyer et al. (2015) and Sirota et al. (2021) show across 18 studies that the disfluency offshoot of the same theory does not exist (g = −.01) |
| The effect score of 3 for processing fluency justified by the missing meta-analysis | Only half right now. A meta-analysis has been checked, but it concerns repetition and liking, not prices. The score stays at 3; the justification is made precise |
| Added: three moderators that limit the transfer to prices | For paintings and drawings Bornstein finds no effect (r = −.03), nor for uniform repetition (r = −.02), and consciously perceived stimuli work more weakly than unconscious ones (.34 against .53) |
| Pain of paying and mental accounting said we had read no replication study | Out of date. Schomburgk et al. (2024) pool 392 effect sizes on cashless payment (g = .135); Li and Feldman (2025) re-ran all 17 problems from Thaler (1999) pre-registered (11 supported, 3 mixed, 3 failed) |
| Decoupling and payment transparency presented as load-bearing mechanisms | Neither works on its own (p = .57 and p = .12). Only their combination does — and for buy-now-pay-later the effect reverses (ḡ = −.35) |
| The “pennies-a-day” framing carried as an unverified reading lead | Checked since Li and Feldman (2025) and, at d = .61, the strongest single finding in their paper. The other two reading leads remain unverified |
| Topical accounts (calculator and jacket) reported without qualification | The pre-registered repetition failed: 11 against 7 percent instead of 68 against 29 (p = .066) |
| Processing fluency, pain of paying and mental accounting carried with an unchecked replication record | All three set to mixed. In each case the main finding holds while partial predictions fail; the effect scores stay at 3 |
| Berger’s Contagious (2013) carried as a source for discount framing | Removed. The book names the Rule of 100 but does not test it; under rule 5 books do not count as evidence. Berger remains named in the text as the one who coined the term |
| The framing effect rested on Many Labs and one re-appraisal | Extended with Li and Feldman (2025): the gain–loss asymmetry is confirmed under pre-registration (84 against 44 percent, Cramer’s V = .41). Topical account-keeping from the same 1981 paper, by contrast, failed |
| The figure d = .26 for attribute framing was carried at second hand | Piñón and Gambara (2005) is now in hand. The figure holds, but 27 percent of the 30 effect sizes point the other way, and across the psychology papers the mean is −.25 |
| Tversky and Kahneman (1981) counted as a pure questionnaire study | The full text shows that on three of the ten problems one participant in ten played for real money, and the authors state that the effects are not eliminated by monetary incentives |
| Macé (2012) was carried as a checked field source | Only the abstract and introduction are available (pages 115–116). What they support has been added and marked as such; the analysis itself remains unverified |
| Piñón and Gambara (2005) carried a DOI that was not theirs | The identifier 10.1027/2151-2604/a000321 belongs to Steiger and Kühberger (2018) and slipped when the new source was inserted. It now sits with the right title again |
| On the German social proof page, Goldstein, Cialdini and Griskevicius (2008) were called “the only meta-analysis” among the works cited there | It is a field study in a single hotel. The meta-analyses on that page are Melnyk et al. (2022) and Bergquist et al. (2019). The sentence now reads “the most-cited single study in this field”, which is what the English version had said all along |
| Macé (2012) has been available in full since 9 November 2026 | The decisive figure does not appear in the abstract: of 43,144 estimated elasticities, 72.4 percent are not significant and 8.7 percent are negative. The median effect of +10.5 percent is carried by the top quarter |
| Inferred from the introduction that most stores were already in the diminishing range | The full text supports the inference with its own figures: 53.6 percent observed practice, optimum at 50 to 60 percent in three of four categories. The statement now rests on Macé’s simulation rather than on an extrapolation |
| Kühberger (1998) was the one source in the list without a full text | Removed. The paper could not be obtained, and every figure attributed to it comes from the re-appraisal by Steiger and Kühberger (2018) anyway. The text now names the re-appraisal as the origin. With that, every source on the site has been read in full |
| Evaluability rested on the original 1996 paper | Four further full texts checked. The result: the hypothesis holds only halfway. That the easy-to-place attribute carries the judgment without a comparison is confirmed repeatedly; that the ranking flips under comparison missed significance in Sher and McKenzie (2014) and failed in one of two studies in Vonasch et al. (2023) |
| The reversals were presented as an evaluation error | Sher and McKenzie (2014) explain the same data as a sensible inference from incomplete market knowledge: in their second experiment the ranking does not flip under any information state. The page now calls the finding a reversal of evaluation, not of preference |
| The compromise effect page stated that “there is no replication study of this pattern — neither a successful one nor a failed one” | Untrue. Neumann, Böckenholt and Sinha (2016) pool 142 experimental comparisons. The same boilerplate also stood on the evaluability page and has been removed there too. What was true is that we had checked none |
| The compromise effect was presented as a pull toward the middle | The meta-analysis separates two things: that the middle option is chosen more often is established; that an added tier raises its absolute sales is not — the mean sits at −0.17 and is not significant. In Simonson and Tversky (1992) the third tier moves sales not toward the middle but from the cheap option to the expensive one |
| The experiments were described as hypothetical across the board | Simonson and Tversky used product samples and catalogue photographs, and several studies paid out. Real shop data are still missing, but “hypothetical” was too sweeping |
| Social proof carried Bergquist et al. (2019) as its one unchecked source | Now evaluated in full text. It supplies a distinction the previous text did not have: norms spoken as a message work at d = 0.18 across 57 experiments, norms read off the surroundings at d = 0.59 across 27. Everything a shop can word falls into the lower row |
| The social proof guide carried a duplicated sentence and a wrong source count | The reference to Cialdini et al. (1990) was doubled in both languages, and the Schultz et al. (2018) retrospective was called “the most useful of the seven sources” — the guide carries nine. Both fixed |
| The limits of Macé’s analysis were not stated | Added: 9.2 percent of items drop out because their price always ends in 9 — so on the case of a shop priced “.99” throughout, the paper says nothing. The data are from 1989 to 1994 |
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