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Under review as a conference paper at ICLR 2027

Ninety-Nine Cents: Price-Ending Bias in Language Models Is Learned, Not Perceived

Abstract

Language models respond systematically to price endings: they are much more likely to buy a product at USD 4.99 than at USD 5.00, echoing the left-digit bias documented in human consumers. We measure this effect with a within-price placebo design that compares the 4.99 to 5.00 change with nine otherwise identical one-cent price increases that do not cross a dollar boundary. The nine placebo steps establish a baseline, isolating the additional effect at the dollar boundary. Across 683,559 cells spanning 21 models, the corrected left-digit effect is percentage points , while a matched design that removes the roundness confound by construction gives . Several experiments then probe whether the bias is perceptual (arising from digit-level processing akin to humans), or semantic (reflecting learned associations with conventional endings). Purchase probability responds to price endings with a graded pattern that favours round endings rather than dropping discretely at the dollar boundary, and the ending profile correlates with corpus frequency. Stating a fictional pricing convention in a single sentence shifts the preferred ending by percentage points, roughly ten times the native 99-cent effect. The same design applied to non-price quantities produces domain-specific patterns instead of a uniform digit effect. Rendering prices as images with progressively smaller cent digits produces a perceptual gradient reaching points, but this is entirely driven by one of 3 vision models tested. These results suggest that price-ending effects in language models resemble human left-digit bias in their functional form, but reflect learned semantic associations that can be substantially revised by in-context information.

Primary area:
interpretability and explainable AI
Keywords:
left-digit bias, language models, price endings, simulated consumers, pricing conventions

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_tyQhOpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
2(+1)
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Paper summary

The paper asks a genuinely interesting question, which is, given that LLMs appear to be significantly more likely to buy something at, e.g., $4.99 than $5.00, does this reflect a "perceptual" emphasis on the leftmost digit, or a "semantic" effect coming from the distribution of prices in the pretraining corpus?

To establish the premise, they use prompting to determine models' willingness to purchase products at various prices, looking at various one-cent increases compared to the x.99->(x+1).00 boundary, showing that there is indeed a significant "threshold"-like effect.

They use five different experiments to attempt to distinguish whether this effect is "perceptual" or "semantic". They use visual models to test the "perceptual" thesis in a visual setting. They use two attempts to disentangle a model's positive preference for round numbers with its negative aversion to whole-dollar threshold jumps. Finally they test with different prompts and different currencies. The authors argue broadly for the "semantic" explanation, i.e., that LLMs are influenced by the prevalence of prices in pretraining.

Critical strengths

The round-dollar threshold effect is very clearly and convincingly demonstrated, and is an interesting finding in its own right.

The question of whether this is "perceptual" or "semantic" is a fruitful distinction to make, and the comparisons/distinctions with human studies are fruitful.

Counting the prevalence of prices in pretraining corpora is a useful contribution.

The idea of physically varying the size of a price in a graphic is an interesting and creative approach.

Critical weaknesses

Overall, the paper is more difficult to read than it needs to be. The abstract uses language that doesn't make sense until one reads the paper; figures use language that doesn't make sense until one reads the appendix; etc.

Overall, the figures use confusing and dubious conventions. Figure 6 says "gpt-4o-mini shows a monotonic gradient", but the figure is not monotonic (it goes up from 100% to 70% then down again to 50%). Figure 7 is a linear regression using an arbitrary "roundness" score from 0-3 on the x-axis, throwing away the "0" scores (which are the vast majority of the data), and running a line from the mean "1" score through one single "2" datum to extrapolate the single "3". It's hard to take this seriously as having the level of rigor it seems to be purporting.

The prompting intervention does not seem convincing at all to me. Simply saying "retail prices in the country conventionally end in .77" breaks ecological validity, and I'm not sure that the resulting outputs are particularly meaningful. A much better approach IMO would be to use SFT to actually train the model on different price distributions.

The vision data are n=3, the three models disagree wildly, including in the direction of the effect, and so I'm not sure what story we are even meant to take away from them.

§4.4 claims, "Presenting the same prices in 5 formats (standard, spaced, digit-separated, ISO, spelled out in words) gives a pooled estimate of −0.26 [−3.42, 2.99]. The word rendering, which removes the digit structure entirely, gives 6.28. The profile therefore persists across representations". Consulting against Table 43, I note that +6.28 this points in the opposite direction of digitspace, plain, and spaced, which are all negative. The main text claims that a profile "persists across representations" but the data appear to say precisely the opposite.

Questions for authors

In F6, you claim that gpt-4o-mini shows a monotonic gradient, but the image appears to show the opposite. Am I misinterpreting the image?

If the word rendering in T43 is +6.28 and digitspace, plain, and spaced are all negative, then in what sense is it the case that a shared profile "persists across representations"?

2 comments
AuthorsOpenReview ↗

Reply to Reviewer tyQh [1/2]

Thank you for the close reading and the specific questions, which led to clear improvements in the revision. We answer your two questions first. Section, table, and figure numbers refer to the revised PDF.

Q1 and W2 (Figure 6). Your reading is right, and "monotonic" was the wrong word. The gpt-4o-mini estimates at 100%, 70%, 50%, and 35% cents height are −0.19, +3.31, −3.74, and −18.76. The effect concentrates at the smallest size, and the slope of a line fitted to the four estimates is 25.53 pp per unit of height [0.88, 50.45], driven by the 35% condition. The revised Section 5 reports the four values, and we also updated the Figure 6 caption.

Q2 and W5 (word rendering). We thank the reviewer for catching this inconsistency. Our earlier statement that "the profile therefore persists across representations" was too broad: the positive estimate for the word-rendered condition does not support this conclusion. We have removed the statement and revised Section 4.4 to describe the results for each representation separately, without implying a common pattern across formats (Table 19; Appendix Table 44, previously Table 43).

  • The standard format gives −2.68, a space after the dollar sign −2.31, a space between every character −3.11, and ISO notation +0.59. None is individually significant, and each format has 65 to 70 blocks, so power is limited.
  • Spacing out every character changes how the price is split into tokens, yet leaves the estimate close to that of the standard format. This argues against a tokenisation artefact, which is what the experiment was designed to test.
  • Writing the currency as a word removes the penalty at the dollar boundary: the dollar step exceeds the average within-dollar step by +1.64 pp, against −4.05 pp in the standard format, and the roundness-corrected estimate is +6.28 [0.67, 12.66]. The dollar figure changes in the same way in both formats, so a left-to-right reading account predicts the same penalty; its absence suggests that the penalty is tied to the familiar "$12.99" retail format. The corrected estimate relies on a single noisy placebo step, and each format has 65 to 70 blocks, so we present this as suggestive.

W1: readability. Thanks, we have revised the paper throughout with this in mind. The abstract now describes each design in plain words, so it can be read without the paper. Every figure caption is self-contained, and figure and table labels that used internal shorthand ("installed", "arm", "naive") now use plain descriptions. We define terms such as block, cell, and the roundness score where they first appear, and the appendix now provides the exact prompts for the non-price quantities and the stated conventions.

AuthorsOpenReview ↗

Reply to Reviewer tyQh [2/2]

W2: Figure 7 and the roundness score. Thank you for raising this concern. We clarify first that no observations with ρ=0\rho=0 were dropped: every step ends at a multiple of ten, so these endings do not occur as destinations, but they enter the analysis as starting points and through within-block detrending. On the broader concern about the roundness score, we agree that the ordinal fit relies on limited support at higher values: eight placebo steps have ρ=1\rho=1, and only one has ρ=2\rho=2, making extrapolation to ρ=3\rho=3 weakly determined. We originally used this simple specification to put the effect on a common scale across experiments, but it is not the only way we assess the effect. The earlier appendix reported a few alternative specifications. We have added another approach and made these complementary analyses more prominent in the revision.

Specifically, Section 6 now foregrounds two estimates that require no roundness score, with their raw data shown in the revised Figure 7:

  • Matched design (E0): Two step-10 jumps both end at .00 and differ only in whether the leftmost digit changes. Their difference is −6.14 pp [−8.36, −3.86], negative in 7 of 9 models.
  • Conservative bound (core sweep): The step-10 effect minus the mean of the nine placebo effects is −2.50 pp [−3.91, −1.28]. Under the assumption that a whole-dollar ending is at least as attractive a destination as any within-dollar ending, consistent with .00 having the largest effect in the ending profile, this contrast is an upper bound on the true effect and therefore understates its magnitude when negative.

The ordinal estimate (−3.25 pp [−5.64, −0.99]) remains in Table 38 as one of five specifications, serving as a common-scale summary rather than the sole basis for our conclusion. We also report an alternative specification using the observed corpus frequency of each ending instead of the ordinal score; this yields −3.52 pp [−5.44, −1.73]. The corresponding ordinal-fit figure has been moved to Appendix C (Figure 11), with its caption clarifying the limited support at higher roundness values.

W3: The stated-convention intervention. We thank the reviewer for raising this concern. The fictional convention was intentional: using an unfamiliar ending such as .33 or .77 allowed us to test whether models would adapt their preferences to an explicitly stated pricing convention, with less influence from familiar price-ending associations. The experiment therefore tests whether ending preferences are responsive to stated conventions, rather than whether the native preference for .99 originates in training data. We have clarified this distinction in the revised Section 4.1.

Two further results help contextualise the intervention. Naming .00, a real and common price ending, moves the dollar-step estimate from −0.87 [−7.16, 7.51] to +28.71 [21.73, 36.81] (Table 28). Moreover, the change in sign across non-price domains (Table 15) and the disappearance of the penalty when currency is written as a word (Table 19) occur without any convention-setting instruction. Finally, we agree that fine-tuning on controlled price distributions would provide a more direct test of the training-data explanation and thank the reviewer for the suggestion. The revised Discussion identifies this as an important direction for future work.

W4: vision with three models. We agree with your description. The three models disagree: the slope is significant only for gpt-4o-mini (25.53 [0.88, 50.45]), the other two give −0.21 [−2.93, 2.56] and −2.74 [−18.02, 11.90], and the pooled slope has an interval that includes zero (5.65 [−2.05, 14.95]). These results support a limited conclusion: a perceptual component is detectable in one model, but the evidence does not suggest that it is a general property of vision models. We have revised Contribution 3 and Section 5 to reflect this clearly.

We hope these revisions address your concerns, and we would be glad to clarify anything further.

Reviewer_Q4d3OpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
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Paper summary

The paper raises the interesting question of whether LLMs, like humans, also exhibit a left-digit bias. The authors conduct extensive experiments and evaluations to demonstrate that this phenomenon is a “learned semantic association” rather than a “perceptual distortion.” Furthermore, they show that this behavior can be overridden within the model's context.

Critical strengths
  • The placebo experimental design is clever as it is not an approach typically utilized in the NLP field.

  • The experiments are thorough and comprehensive. The authors first establish that the effect exists and then proceed to demonstrate why it occurs.

  • The paper is transparently presented and easy to follow.

Critical weaknesses
  • The experiments do not provide sufficient evidence to conclude that the phenomenon is “not perceived,” making this assertion overclaimed. While the bias may be primarily learned, the model could simultaneously possess a digit-processing quirk. For example, in the case of societal bias, researchers have found that if models are explicitly instructed to be fair, they actually behave more fairly. In this context, is that behavior also considered 'learned' rather than 'perceived'?

  • I suggest that if this is a learned semantic association, the model's representations of 4.99 should be closer to 4.00 than to 5.00. Conducting such an embedding experiment could significantly strengthen the authors’ claims.

  • The study relies on only 8 generic products, 5 personas, a US-centric framing, and a single stated-intention binary choice. While this is acceptable for mechanistic work, it means the effect is measured in a highly constrained environment. Consequently, it remains unclear whether the effect generalizes to real-world purchasing contexts.

  • The abstract's headline numbers (−3.25, −6.14) are difficult to interpret without adequate context. The contribution list (lines 59-77) describes them much more accessibly.

Questions for authors

N/A

1 comment
AuthorsOpenReview ↗

Reply to Reviewer Q4d3

We thank the reviewer for the thoughtful assessment and constructive feedback. We address each point below. All section and table references refer to the revised PDF.

W1: "not perceived" and the fairness analogy. We agree, and we have adopted your framing: the bias can be mainly learned while the model also has a digit-processing quirk, and the vision experiment shows such a component in one model. We changed the title to "… Tracks Learned Conventions", and the abstract, contribution 2, and the conclusion now say that the effect mainly reflects learned conventions. The new "Scope of the evidence" paragraph (Section 8) states that a digit-level component remains possible.

Your analogy with instructed fairness is apt. Compliance with an in-context instruction shows that a behaviour can be changed; on its own, it says little about where the behaviour came from. The revised Section 4.1 keeps the two apart: it presents the result as showing that the preference can be revised in context, and leaves the origin of the default preference to Sections 4.2 to 4.4. The case for a learned origin relies on three results beyond compliance. First, the stated convention moves the preference to an arbitrary ending (.33 or .77, each raised by more than 30 pp) and leaves the effect of the other ending small, so the response tracks which ending is named as conventional rather than a general reduction in bias. Second, in the non-price domains the equivalent step changes sign with no instruction at all (+6.18 for delivery days, −9.73 for ratings; Table 15). Third, the ending profile tracks how often each ending is posted in web text (Section 4.2).

W2: representations of prices. We thank the reviewer for this valuable suggestion. Examining internal representations would provide a useful complementary perspective on the mechanisms underlying the observed bias, and we have added this direction to the revised Discussion. We also considered how to design such an analysis to distinguish the competing explanations. A natural starting point is to compare the representations of USD 4.99, USD 4.00, and USD 5.00. However, because USD 4.99 and USD 4.00 share the leading digit (and potentially token-level features), their similarity could reflect shared numerical structure rather than left-digit truncation. We therefore suggest extending our placebo logic to representation space: comparing representational distances across the dollar boundary (USD 4.99 to USD 5.00) with those across the nine within-dollar transitions (USD 4.09 to USD 4.10, ..., USD 4.89 to USD 4.90), and examining whether prices ending in .99 cluster across dollar values, as a learned-convention account would predict. In the current behavioural data, two results play a similar role: in three-digit prices, a leading-digit change adds little beyond a tens-digit change (Table 35), and writing the currency as a word, with the same change in the dollar figure, removes the penalty at the dollar boundary (Table 19).

W3: Constrained setting. We agree that a single stated-intention choice in a controlled setting is a limitation, and the revised Limitations paragraph now makes the scope of our experiments explicit. Beyond the 8 core products, we examine 16 additional two-digit products (E0) and 8 three-digit products (E0b). We also vary personas (up to 9 per experiment), currencies (5, including the Indian rupee and Japanese yen in E4), non-price domains (5 in E3), and prompt phrasings (12 in E2). Table 39 reports the estimates for all experiments. Whether the effect carries over to real purchases involving brands, reference prices, and repeated choices remains an open question, which we now acknowledge in the revised manuscript.

W4: headline numbers in the abstract. Thanks for the suggestion. The abstract now describes each design in plain words and states what each estimate compares and how many models it covers.

Thank you again for the constructive review.

Reviewer_QNSaOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper examines the concept of ending price tag with $0.99 to attract consumers, so, perceptually ignoring the higher dollar value just $0.01 decimal difference. It is the central theme of this work how LLMs will react to this one-cent price difference. The results suggest that price-ending effects in language models resemble human left-digit bias in their functional form but reflect learned semantic associations that can be substantially revised by in-context information. The main claimed contribution of this paper is as follows:

1.A placebo design for isolating the dollar-boundary effect

2.Evidence for learned semantic conventions

3.A possible perceptual channel in vision

4.Identification of the roundness confound

5.Prompt sensitivity exceeds model variation

Total 13 Experiments were conducted on 21 Language models and paper reports a corrected left-digit effect of −3.25 percentage points using the placebo-based estimator and −6.14 percentage points using the matched design. The finding shows that price-ending preferences are graded that dollar boundaries. This experiment shows that LLMs mimic human like left digit bias based on learned contextual information. However, experiments require further analysis to understand the inline mechanism of the setup and robustness.

Critical strengths

a.This paper shows methodological design by distinguishing dollar-boundary effects with price ending preferences. It calculates the additional effects due to dollar boundary. This study opens new horizon to the behavioral bias in LLMs.

b.This study explains different price-ending profiles, corpus frequencies and prompt phrasing.

Critical weaknesses

a.Inconsistent claim verification: This work claim that the price ending effects are learned by LLM but it appears that it is leaned from correlation and behavioral patterns. Hence, there is some difference with title of the paper.

b.The results are highly dependent on the prompts as it varies from 0.13 to 15.94 percent points using different prompt template which shows high prompt dependence. So, it seems not to be generalized behavior.

c.In multimodal settings it is not strongly conclusive that bias is due to perception as it shows in only 1 out of 3 vision model. So, the claim between learned vs perceptual is not adequately justified.

d.Model’s actual training mixture is not similar with public corpus frequency which is one of the major flaws and it should be a drawback rather a limitation. It could lead to data leakage or some form of non-decisive while deployed in real world scenario.

e.Data repository should be more organized and self-explainable, especially the ReadMe section.

Questions for authors

a.Is there any strong evidence to support the titled claim?

b.The is a high dependency on Prompt templates, thus what is the robustness claim associated if the prompts are para-phrased?

c.Quoted “Spearman correlation is 0.333 across 30 price endings” – So what are all corpora resembles the training distributions?

d.Is the study applicable for other currencies also?

e.What will be impact on bias if the placeholder digits are increased from 2 digit to more on the left side?

3 comments
AuthorsOpenReview ↗

Reply to Reviewer QNSa [1/2]

We thank the reviewer for the thoughtful assessment and constructive feedback. We answer each point below. Section and table numbers refer to the revised PDF.

W(a) and Q(a): evidence for the title claim. We agree that the submitted title stated the conclusion more strongly than the evidence supports, and we have changed it to "… Tracks Learned Conventions" (as noted in the general response). The revised claim is that the effect mainly reflects learned conventions. It is supported by two pieces of evidence, which the new "Scope of the evidence" paragraph (Section 8) separates.

Experimental manipulations:

  • Stated convention (Section 4.1, Table 27). One sentence naming .33 as the conventional ending raises the effect of .33 from −1.46 to +36.02 pp [29.79, 42.31], while the effect of .77 remains small (+1.27). Naming .77 raises the effect of .77 to +33.02 [26.84, 38.23], while the effect of .33 remains small (+1.65). Naming .00 moves the dollar-step estimate from −0.87 [−7.16, 7.51] to +28.71 [21.73, 36.81] (Table 28).
  • Non-price domains (Section 4.3, Table 15). The equivalent step gives +6.18 for delivery days and +2.84 for calorie counts, but −9.73 for ratings and −4.97 for odometer readings. A digit-level mechanism predicts the same sign in every domain.
  • Number formats (Section 4.4, Table 19). Writing the currency as a word removes the penalty at the dollar boundary (uncorrected contrast +1.64 pp, against −4.05 pp in the standard format), although the dollar figure changes in the same way.

Patterns in the data:

  • Three-digit prices (Appendix B.14, Table 35). Relative to a step that changes only the units digit of the dollar figure, a step that also changes the tens digit gives −5.89 [−8.77, −2.94] and one that also changes the leading digit gives −6.34 [−9.79, −3.11]. A leftmost-digit account predicts that the leading digit dominates; here it adds little beyond the tens digit.
  • Corpus frequency (Section 4.2). The ending profile correlates with how often each ending is posted (Spearman 0.333 over 30 endings). This is the weakest line of evidence, and we present it as correlational.

These results leave room for a digit-level component alongside the learned convention, and the vision experiment shows one in a single model. The revised text says so.

W(b) and Q(b): prompt dependence. We agree that the size of the effect depends strongly on wording, and we report this as one of our findings (contribution 5). The direction is robust. Eleven of the 12 templates give negative estimates, 10 of them individually significant, and the remaining template gives +0.13 [−4.43, 5.36]. The pooled estimate is −8.91 [−11.04, −6.93] (Table 12). The range you quote describes the variation in size. The revision compares it with the variation across models on the same data, since all five models answered all twelve templates. Variation between templates is significant (Cochran's Q = 24.0 on 11 degrees of freedom, p = 0.013; between-template standard deviation 3.5 pp), whereas variation between models is smaller and not significant at the 5% level (Q = 8.7 on 4 degrees of freedom, p = 0.069; 2.2 pp) (Table 14). We use this to draw a practical lesson for evaluation: an estimate for a model should be reported together with its prompt (Section 8).

AuthorsOpenReview ↗

Reply to Reviewer QNSa [2/2]

W(c): vision. We agree. The vision experiment is the one place where a perceptual component appears, and only in gpt-4o-mini. The other two models show no trend (slopes −0.21 [−2.93, 2.56] and −2.74 [−18.02, 11.90]), and the pooled slope has an interval that includes zero (5.65 [−2.05, 14.95]). The revised contribution 3 and Section 5 state this scope, and it is one reason the paper now says that the effect mainly reflects learned conventions.

W(d) and Q(c): corpora and training data. We agree that public corpora are a proxy for the training data, and the revision now states this in the main discussion (the new "Scope of the evidence" paragraph, Section 8) as well as in Limitations. The training mixtures of closed models are not public, so they cannot be measured directly. We offer two reasons for using these corpora and clarify the scope of the resulting evidence. First, C4, Dolma, and RedPajama give very similar rankings of the 30 endings, with pairwise Spearman correlations of 0.968 to 0.989 (Table 30). The three share sources (Dolma and RedPajama both include C4 and Common Crawl text), so this shows consistency across large collections of web text and should not be read as three independent samples. Web crawls of this kind are a standard source of pretraining text. Second, we use these corpora solely to measure the frequency of price endings, not as inputs or evaluation material for any of the models. Thus, this analysis does not introduce leakage into the model evaluations.

W(e): repository. Thank you. The README now maps each experiment to its data file and each table and figure of the paper to the file that produces it, documents every column of the data, gives the software versions and the run time (about two minutes on a laptop, with no API key or GPU), and lists key numbers for checking a reproduction. The corpus counts are now included, so the full analysis runs offline, and a run from a fresh copy reproduces every table exactly.

Q(d): other currencies. Yes. E4 repeats the design in five currencies (Section 7, Table 17). The pooled estimate is −2.73 [−5.04, −0.15]. Four currencies give negative estimates: the US dollar −5.28 [−10.57, −0.05], the Swiss franc −4.59, the euro −4.04, and the Japanese yen −3.42. Only the US dollar is individually significant. The Indian rupee gives +3.82 [−3.09, 11.02].

Q(e): more digits on the left. Two experiments address this. E0 uses two-digit prices. Holding the destination ending at .00, a dollar step that changes the leftmost digit (19.99 to 20.00) differs from one that does not (12.99 to 13.00) by −6.14 pp [−8.36, −3.86] (Section 6). E0b uses three-digit prices (Appendix B.14). Relative to a step that changes only the units digit (214.99 to 215.00), a step that also changes the tens digit (219.99 to 220.00) gives −5.89 [−8.77, −2.94], and a leading-digit change (199.99 to 200.00) gives −6.34 [−9.79, −3.11]. The effect therefore persists with more digits, and the leading digit adds little beyond the tens digit, which fits a convention account better than a leftmost-digit account. Scaling all prices by 100 gives −3.64 [−5.95, −1.95] across 12 blocks (Appendix B.3).

We hope these revisions address your concerns, and we would be glad to clarify anything further.

Overall, I acknowledge that the authors have made efforts to improve the paper and address the feedback. Nevertheless, I feel that the concerns regarding the interpretation of the central findings and their generalizability are still relevant. Therefore, I would prefer to maintain my original assessment.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response to all reviewers and the area chair

We thank the reviewers for careful and constructive reviews. While the reviews recognised the potential of our approach and findings, they also identified areas where we could make our claims more precise. We have addressed these concerns through revisions to the manuscript, as detailed below. The revision collects no new data: every new number comes from re-analysing the panels released with the submission, and the updated analysis code is in the anonymised repository.

Title. Following Reviewers QNSa and Q4d3, we have changed the title from "Ninety-Nine Cents: Price-Ending Bias in Language Models Is Learned, Not Perceived" to "Ninety-Nine Cents: Price-Ending Bias in Language Models Tracks Learned Conventions". The evidence shows a dominant learned component, and the vision experiment shows a perceptual component in one model, so the previously submitted title stated the conclusion more strongly than the evidence supports.

Main changes.

  1. Headline estimates (abstract, Section 6, new Figure 7). The abstract and Section 6 now report two estimates that need no model of roundness: the matched design (E0), −6.14 pp [−8.36, −3.86] across 9 models, and a conservative bound from the core sweep, −2.50 pp [−3.91, −1.28] across 15 models. The conservative bound is step 10 minus the mean placebo step. If a whole dollar is at least as attractive a destination as any within-dollar ending, its expectation lies at or above the true effect, so it can only understate a negative effect. The ordinal roundness correction (−3.25 [−5.64, −0.99]) remains as a common scale for comparing experiments. (tyQh, Q4d3)
  2. Scope of the claims (abstract, contributions, Section 4.1, new "Scope of the evidence" paragraph in Section 8). The revision separates experimental manipulations from correlational evidence, describes the corpus counts as a proxy for training data, and states that a digit-level component remains possible alongside the learned convention. (QNSa, Q4d3)
  3. Vision (Section 5, Figure 6). The description of the gpt-4o-mini results is revised, and all four estimates and all three model slopes are reported. (tyQh, QNSa)
  4. Number formats (Section 4.4). Rewritten to state what Table 19 shows. (tyQh)
  5. Prompt phrasing (Section 7, new Table 14). The variation across templates is now compared with the variation across models on the same data. (QNSa)
  6. Readability. The abstract can now be read without the paper: it describes each design in plain words and states what each estimate compares. Every figure caption is self-contained, internal labels in figures and tables (such as "installed" and "arm") are replaced with plain descriptions, and each term is defined where it first appears. (Q4d3, tyQh)
  7. Limitations (Section 8). The coverage of products, personas, and currencies is stated with counts. (Q4d3)
  8. Repository. The README maps every experiment to its data and to the tables and figures it produces, and documents the data columns. The corpus counts are now included, so the full analysis runs offline. (QNSa)

Clarifications. The revision also tightens several descriptions: the vision results for gpt-4o-mini (Section 5), the results across number formats (Section 4.4), the summary of the prompt-phrasing results (Section 7), and the contrast between step 10 and the largest placebo step (Appendix C), which tends to overstate the effect and is no longer presented as a bound. All core-sweep intervals now come from a single set of bootstrap resamples, so they agree across tables. The table of models in Appendix A now lists, for each model, the experiments it appears in.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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