acceptodds
Under review as a conference paper at ICLR 2027

The Gogol Effect in LLMs: Post-Completion Self-Devaluation

Abstract

Inference-time search, self-correction, and branch selection increasingly use language models to score their own intermediate generations. Such systems often treat an online score as if it were interchangeable with the score the same model would assign later. We test that assumption with a matched LIVE-REPLAY-POST protocol. LIVE records a sentence score on the original writing trajectory; REPLAY reconstructs the same visible prefix in a fresh call; POST scores the sentence after the completed output is visible. This decomposes the total retrospective shift into an IKEA-like writer-state component (R-L) and a completion-associated component (P-R). Across six models with sufficiently developed three-state data, only one has a positive mean IKEA-like shift (+2.77 points), while the other five move in the opposite direction. By contrast, four of six show positive post-completion self-devaluation, with mean P-R shifts from +3.18 to +20.06 points; one model is near zero and one moves oppositely. In the strongest case, about 88% of the total LIVE-POST change appears only after completion. We call this model-dependent pattern the Gogol effect. Separate audits show that score-level error and within-output rank stability are distinct: calibration can reduce level error but cannot repair unstable local rankings. Held-out elicitation and temperature controls preserve the main directional result. The implication is diagnostic rather than psychological: online self-scores can be useful control signals, but their temporal stability, ranking geometry, and dependence on future context must be measured rather than assumed.

Primary area:
generative models
Keywords:
large language models, self-evaluation, inference-time control, self-correction, LLM-as-a-judge, confidence calibration, state-dependent evaluation, IKEA effect, Gogol effect

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_ugTNOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
1
Read review
Paper summary

This paper studies the discrepancy between an "AI-likeliness score" a language model may assign to its generation during generation and after generation (from a retrospective viewpoint). In particular, the authors tested 3 evaluation schema: ask the model to evaluate its generation after each sentence, ask it to evaluate a completed generation one sentence at a conversation round, and finally ask it to grade all sentences in an completed response.

While the problem appears interesting, I find the problem of interesting not being well-defined and the experiment setup highly restrictive to a particular setting, which could be a good course project instead of a top-venue conference paper. Thus I recommend for rejection.

Critical strengths

None

Critical weaknesses

The phenomenon is not defined or tested with any generality. The current study is highly tied to the specific AI-likeliness setting under social media posts and specific chat templates used for interaction. The heterogeneous results also does not present a conclusive finding. Therefore I believe this paper shall be treated as an interesting standalone phenomenon presentation instead of a scientific research.

Questions for authors

None. I believe the modification required for acceptance would be substantially changing the current content of the paper.

Reviewer_TNbZOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper is interested in biases that may occur in LLM self-evaluation during (LIVE), after (POST), and during a REPLAY phase of possible generation. They liken this to the model taking on anthropomorphic characteristics such as self-attribution or a self-criticism in hindsight, defining two metrics based on the different self evaluations, whose magnitude should represent taking on these characteristics and show the metrics approximately 200 data points split across 6 models. The findings are generally mixed.

Critical strengths

The paper recognizes a potential bias in self-evaluations of models. Understanding this bias could be informative for uncertainty estimation techniques, prompting practitioners to re-consider where and how they ask for self-evaluations from AI agents.

Critical weaknesses
  • The paper is generally difficult to follow in terms of it's motivations and exact implementations (e.g., the implementation of the P,L,R scores). The main text does not contain much detail and the interpretation of the scores is largely heuristic and uses an analogy such as "IKEA-like" that doesn't make much sense to me. There is little to no analysis of the problem outside of some verbal argument and analogy.
  • The method to construct these, e.g., the replay score, appears to be heuristic and dependent on prompts without much analysis of prompt sensitivity. This could be an analysis of bias arising from a single prompt choice, rather than a true "replay" score.
  • The shear quantity of information or novel insights is severely lacking for the ICLR venue. The paper appears to present one primary results, which does not have much interesting or consistent takeaways (IMO) and relies on very limited data overall.
  • The prior work for this paper does not depend on any established theories or ideas from the literature about how bias develops (e.g., psycholinguistic theories, theories of ML for uncertainty estimation, etc.). The related works is light for a topic that has a very broad history to pull from. This contributes to the inability to draw insight from this paper, because it's scientific lineage is not very strong.
Questions for authors

I do not have any substantial questions for the authors. My view is that the content of the paper is not so difficult to understand, but the quantity and depth of the content is not substantial enough for publication at ICLR.

Reviewer_5T2YOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

The paper asks whether an LLM's online self-score of a sentence (emitted while writing) can stand in for the score the same model would assign later. Each model writes a 5–8 sentence factual social-media post and appends a 0–100 "AI-likeness" score after each sentence (LIVE). The same sentences are re-scored in a fresh call given the text prefix through that sentence plus that call's own earlier scores (REPLAY), and again after the full text is shown with one placeholder per sentence (POST). The total shift P−L is decomposed as (R−L) + (P−R): R−L is read as an "IKEA-like" writer-state component and P−R as a "completion-associated" component the authors name the Gogol effect. On a frozen 40-prompt English set (GPT-5.5, Gemini 3.1 Pro) plus an adaptive extension to four more models (N = 8–24 prompts), R−L is positive only for Gemini (+2.77) while P−R is positive for four of six models (+3.18 to +20.06); for Gemini about 88 % of the total shift lies in P−R. Further analyses show that within-output rank reliability and level error dissociate across ten models, that four elicitation variants and a T=0 control preserve the LIVE→POST shift, and that rewriting the highest-LIVE-scored sentence is no better than rewriting a random one. A complete reproduction package (raw API responses, manifests, frozen protocols, interim adaptive looks, analysis scripts) is released

Critical strengths
  1. Unusually transparent, auditable and reproducible empirical work. Prompts, protocols and adaptive-look logs were frozen; all raw outputs (SQLite), manifests and analysis scripts are released. I re ran the package in an isolated copy and audited the runner code line by line: the three prompt templates are implemented exactly as Appendix A states; protocol failures are dropped, never imputed; the repair/ retry paths in the code left no records in the shipped database; every number that can be recomputed from the frozen outputs matches (Table 3 to the second decimal, because scikit-learn versions are unpinned). The authors are also candid about limitations (no psychological claims, survivorship, POST is not ground truth). Why consequential: the empirical observations can be trusted, and the released data are rich enough to test the paper's own interpretation — which is what my first weakness does.

  2. A practically useful warning about online self-scores, with a robust two-state result. The LIVE→POST shift is large for Gemini (+22.8 points, §5.1) and present for GPT-5.5 (+3.8, Table 1 / App. C), and it persists across held-out prompts (§5.5), four elicitation formats and T=0 (App. E). The demonstration that level error (MAE 4.2–24.5, Table 2) and within-output ranking (ρ .33–.82, Table 2) dissociate across ten models is relevant to anyone who thresholds or argmaxes self-scores in search or self-correction pipelines. Why consequential: this part of the contribution would survive even if the decomposition were dropped

Critical weaknesses
  1. The central decomposition does not identify a "completion" effect, and the authors' own data point against that interpretation. The REPLAY→POST transition changes four things at once: (a) whether later text is visible; (b) the instruction framing ("Continue the assessment" vs "The requested text has already been produced … Assess that exact completed text"); (c) single-score vs listwise scoring of all sentences; (d) score history — REPLAY sees its own previous scores, POST sees only placeholders (App. A templates; build_replay_prefix, post_messages in the released runner). §3.2 acknowledges the "retrospective prompting transition", yet the title, the named effect, the abstract ("about 88 % … appears only after completion") and the mechanism in §6 attribute P−R to completion. The released data allow a direct test. For the final sentence, the REPLAY prefix is the entire text, so P−R there cannot come from completion information. At the prompt level (experiment.sqlite3, 40 English prompts): • Gemini: last-sentence P−R = +38.2 (p = 2e-11) vs +20.1 overall and +11.5 at the first sentence; mean POST score of the last sentence 58.0 vs 34.2 for the others. • GPT-5.5: last-sentence P−R = +5.6 (p = 4e-8) vs +6.9 overall — not near zero. • The independent temperature control shows the same (Gemini +54.5 at T=0, +34.5 at T=0.7; GPT-5.5 +7.2 / +5.6). • In the 40-prompt run the per-prompt slope of P−R on the number of remaining sentences is negative for both models (Gemini −4.5 points/sentence, p ≈ 3e-7; GPT-5.5 −0.65, p ≈ 2e-5); Gemini's slope stays strongly negative in both temperature controls, GPT-5.5's is negative but not significant there. A future-context account predicts a positive slope. So the "Gogol effect", as measured, is at least largely an elicitation-format and/or score-anchoring effect — the behaviour one would expect from documented position bias in list-wise LLM judging (Shi et al., arXiv:2406.07791) and anchoring on prior scores supplied in context (Stureborg et al., arXiv:2405.01724; Kapetanovic et al., arXiv:2608.25869, contemporaneous), none of which the paper discusses. Why consequential: contributions 1–2, the 88 % figure, the mechanism paragraph and the paper's title rest on this component. Fixing it requires new format-matched conditions and most likely a re-framing of the paper, which exceeds a rebuttal-scope clarification.

  2. The evidence for breadth and significance is thin relative to the framing. Only two models have a fixed-N decomposition. "Four of six" includes GPT-OSS (N = 8; confirmatory support rests on four fresh prompts with a one-sided t-test) and DeepSeek V4 (N = 12; pilot mean +0.35). Both were stopped at first cumulative significance, inflating their effect estimates, and the frozen protocol names a confirmatory stopping rule whereas the run used the cumulative one (FROZEN_ADAPTIVE_PROTOCOL.md and the runner default vs gogol_step4_protocol.json; App. C discloses the latter). The endpoint is a single stylistic self-judgment (perceived AI-likeness of social posts) with no human or ground-truth validation. The largest held-out cohort (24 prompts) collected no REPLAY and so tests P−L, not P−R. The lone positive IKEA-like case (Gemini R−L +2.77) does not replicate in the temperature control (−0.01 at T=0, −1.63 at T=0.7) or in two elicitation variants. The one downstream test (rewrite check) is null. Why consequential: the motivating claim about inference-time search and self-correction is not yet substantiated, so the paper's value to practitioners currently rests on the two-state warning alone.

Questions for authors

Clarifications whose answers could change my assessment:

  1. Format-matched control. On the existing 40 prompts, can you add (i) a POST-style listwise prompt applied to the prefix through sentence i, (ii) REPLAY with placeholders instead of its own earlier scores, and (iii) REPLAY at the final sentence with the "completed text" framing? If P−R remains substantial once format and score history are matched, and grows with the amount of future context, my main soundness concern is resolved and I will raise my score.
  2. How do you reconcile the completion interpretation with P−R being largest at the final sentence for Gemini (+38.2 in the main run; +54.5 at T=0) and with the negative relation between P−R and the number of remaining sentences? Please report P−R by sentence position.
  3. Can you estimate a test–retest ceiling (repeat POST and REPLAY on identical inputs at T=0.7) so that rank reliability and the small R−L values can be read against each model's own sampling noise?
  4. Please reconcile the stopping rule (confirmatory in FROZEN_ADAPTIVE_PROTOCOL.md and the runner default vs cumulative in the executed run), report all six models with CIs as the Figure 1 caption promises, and state what the confirmatory rule would have produced.
  5. The 10 Russian validation prompts were fully collected (Gemini P−R +29.4, GPT-5.5 +7.2 in replay_decomposition_summary.csv) but no results are reported — why? Were any human ratings collected with the provided templates? Suggestions (not part of my decision): test an objective endpoint (math or code verification); add a non-self control (another model's POST on the same text) to justify the "self-" in self-devaluation; reconsider the name if the format account holds. Related work the paper may wish to engage with (not required, two are contemporaneous): position bias in list-wise judging (Shi et al., arXiv:2406.07791), anchoring of LLM evaluators on prior scores (Stureborg et al., arXiv:2405.01724; Kapetanovic et al., arXiv:2608.25869), cross-mode judgment inconsistency (FairJudge, arXiv:2602.06625), and generator–evaluator self consistency (Mancoridis et al., arXiv:2606.30653), which is the closest conceptual neighbour of the LIVE vs-POST question.

Minor (not part of my decision): Figure 1 has no error bars although its caption says they appear in App. C. Table 3 shows 7 of 10 models despite "full … calibration tables" in §5.4, and its offset/affine values do not reproduce exactly under scikit-learn 1.5.0 — pin dependencies and add the main_v57 derived-vs expected comparison to reproduce_all.py. reproduce.sh aborts on CRLF checkouts; README.md fails its own checksum. App. D exclusion sentence lists "random arm" twice. Norton et al. (2012) is in the bibliography but never cited. GPT-OSS and Llama "model-specific" prompt orders are identical. Within output ρ silently excludes outputs with constant LIVE or POST vectors.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.