acceptodds
Under review as a conference paper at ICLR 2027

SafeDrift: Reliability-Audited Longitudinal Safety Evaluation of Memory-Augmented Mental-Health Agents

Abstract

Longitudinal safety evaluation of memory-augmented mental-health companion agents stacks several measurement choices (which rater scores a response, how dimension-level verdicts are aggregated, and how failures are attributed to memory) on top of the agent behavior it aims to measure. We introduce SafeDrift, an evaluation framework in which 48 clinician-reviewed personas converse over 10–15 sessions with three open-weight subject models under three memory conditions (none, rolling summary, retrieval), with every safety-critical user probe delivered verbatim-identically across all nine model–memory cells (preceding conversational histories still differ). We audit the measurement pipeline itself: a stratified 731-verdict sample is scored by the benchmark's judge, two reference LLM judges, and two human annotators. Reliability is strongly dimension-specific: referral and sycophancy fall below 0.6 under both chance-corrected agreement measures, Cohen's κ and Gwet's AC1; the annotators disagree with each other on referral (κ = 0.30), with their calibration responses indicating two distinct interpretations of the rubric; and both annotators are systematically stricter than every LLM judge on sycophancy. We then ask which substantive conclusions survive. The recognition-failure gap between the smallest and the two larger subject models (≥2.6×) replicates under all five raters; the analogous judge-derived referral gap does not. Pooled over models, memory-condition contrasts are near zero: five of six satisfy a ±10 percentage-point equivalence margin while the sixth is borderline under that margin, and no model×memory interaction is detected. Two other headline quantities depend on analysis scope: a mitigation instruction's apparent harm to one model reverses sign once exploratory dimensions are excluded, and the share of unsafe turns that flip to safe when memory is masked falls from 42–76% to 26–43% when restricted to the confirmatory safety dimensions. Longitudinal safety benchmarks should report rater-, aggregation-, and attribution-sensitivity alongside headline numbers; we release SafeDrift to make this practical.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LLM-as-a-judge, evaluation reliability, AI safety, mental health, long-term memory, longitudinal evaluation, inter-rater agreement, benchmark

Reviews

Among:
Shape:
1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_kcgSOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces SafeDrift, a framework for evaluating the longitudinal safety of memory-augmented mental-health agents. Using three models, three memory conditions, and 48 simulated personas, the authors examine how rater disagreement, score aggregation, and memory attribution affect safety conclusions. Results highlight substantial evaluation sensitivity and limited overall effects of memory.

Critical strengths
  1. The paper compares LLM judges with human annotators and identifies notable disagreements across safety dimensions, including ambiguities in the evaluation rubrics.
  2. The paper shows that changing the judge, aggregation method, or attribution criteria can lead to different safety conclusions.
Critical weaknesses
  1. The equivalence results rely heavily on pooled analyses and a ±10 percentage-point margin, with only 4 of 18 per-model comparisons meeting this criterion. The evaluation also covers just three models, with a single run per configuration, limiting the strength and generalizability of the findings.
  2. Each counterfactual response is generated only once, without a no-intervention baseline. Since generation is stochastic, FAIL-to-PASS flips may reflect sampling variability rather than the removal of memory. This makes the reported attribution rates difficult to interpret.
Questions for authors
  1. What motivates the ±10 percentage-point equivalence margin, particularly in a safety-critical setting? How should the pooled equivalence results be interpreted given the weaker per-model evidence?

  2. Could the authors provide a no-intervention baseline and repeated counterfactual samples to assess how much of the observed FAIL-to-PASS rate is due to generation variability?

  3. How stable are the main findings across different random seeds, given that each experimental configuration was evaluated only once?

3 comments
AuthorsOpenReview ↗

Response: equivalence margin, replay baseline, seeds

We thank the reviewer for these focused questions. We agree with both weaknesses and answer each question below, including what we cannot yet show.

Q1. The ±10 pp margin and pooled versus per-model evidence. The ±10 pp margin was not pre-specified and has no clinical derivation; the reviewer is right that it cannot carry a safety-relevant conclusion on its own. We will replace binary equivalence with the largest effect each contrast excludes (the bound of its 90% persona-cluster bootstrap CI), reported under both full-census judges so readers can apply their own margin:

Pooled contrastOriginal judge excludes effects larger thanSecond judge (gpt-4o-mini) excludes effects larger than
Recognition, summary − none5.8 pp8.9 pp
Recognition, rag − none8.7 pp5.6 pp
Referral, summary − none8.3 pp8.9 pp
Referral, rag − none7.1 pp6.9 pp
Sycophancy, summary − none9.0 pp6.8 pp
Sycophancy, rag − none9.6 ppnot excluded: +7.0 pp [0.4, 13.3]

Pooled across models, memory effects on recognition and referral larger than about 9 pp are excluded under both judges. A retrieval-related increase in sycophancy is not excluded, and the second judge estimates one. In a safety-critical setting even the excluded range may be too wide to call memory safe, and we will say so.

On per-model evidence, the reviewer is right that only 4 of 18 per-model contrasts meet ±10 pp. With 48–76 probes per cell, per-model CIs reach ±17 pp, so the data cannot exclude model-specific memory effects of 10–15 pp. The pooled result is an average across three models, not a statement about any one of them, and we will restate S2 accordingly. The model×memory interaction test detects no interaction, but at this sample size that is weak evidence of its absence.

Q2. No-intervention baseline and repeated counterfactuals. We agree this is the main gap in the attribution analysis: without a baseline, a FAIL→PASS flip after masking cannot be separated from sampling variability. The paper's own data show the risk is real. Flips concentrate in the dimension where the original judge is systematically stricter than both reference judges (86% of distress-assumption failures flip), which is what judge noise plus resampling would produce. We will add (a) a no-intervention baseline that replays the same turn with memory kept and (b) k = 5 repeated replays per turn, with and without masking, and report flip rates relative to the baseline. Until then, the masking rates should be read as an upper bound on direct, turn-level memory effects, and the revision will present them that way.

Q3. Stability across random seeds. We cannot answer this from the current data: each persona–model–condition configuration was run once, with a single seed. The persona-clustered bootstrap captures variation across personas but not across generations, so the CIs understate total uncertainty. We will state this explicitly and add repeated runs with independent seeds for the main contrasts. The largest finding, the recognition gap between llama-3.2-3b and the two larger models (23–46 pp across judges), is large relative to its CIs and unlikely to be overturned by seed variation. The memory contrasts are much closer to zero, and their stability is an open question.

We will also restructure the presentation around these points, as the reviewer found parts hard to follow.

We hope these analyses and corrections address the reviewer’s concerns, and we would be grateful if the reviewer would reconsider their assessment in light of them.

Thank you for the detailed response.

The authors have addressed W1/Q1 with additional analysis and clarified some limitations. They have also acknowledged the issues raised in W2/Q2 and Q3.

However, W1/Q1 is only partially resolved, as the per-model evidence remains limited. W2/Q2 and Q3 are still unresolved, since the authors have not provided the additional experimental results.

These missing experiments are important to the paper’s main claims. Without them, the current results are not sufficient to support the key conclusions.

Therefore, I am now more confident in my original decision to reject the paper. I will keep my rating unchanged and increase my confidence score.

We thank the reviewer for engaging with our response and for the clear statement of what remains. We agree that the per-model evidence is limited and that the no-intervention baseline, repeated counterfactual replays, and multi-seed runs are needed to support the main claims. We will run these experiments and report them in a revised version of the paper.

Reviewer_ioagOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

The paper presents SafeDrift, a longitudinal safety benchmark in which 48 synthetic personas converse for 10–15 sessions with three open-weight subject models (gpt-oss-20b, qwen3.6-27b, llama-3.2-3b) under three memory conditions (none, rolling summary, retrieval), with every risk-disclosure probe delivered verbatim across all nine cells. A gpt-oss-120b judge scores each turn on four confirmatory and four exploratory dimensions (11,205 verdicts). The main contribution is an audit of the measurement pipeline: a stratified 731-verdict sample is re-rated by two reference LLM judges and two human annotators, agreement is reported per dimension with Cohen's κ and Gwet's AC1 (Table 1), and rater choice, aggregation, and attribution scope are each shown to change a headline conclusion (Table 3). The conclusions presented as surviving the audit are a rater-robust recognition gap between llama-3.2-3b and the two larger models, pooled memory contrasts equivalent to zero at ±10 pp, and no model×memory interaction. Code, verdict files, replays and annotator ratings are provided; persona scripts and transcripts are withheld pending gated release.

Critical strengths
  1. The quantitative pipeline is fully reproducible from the supplement. Every cell of Tables 1, 2, 5–14 and the counts in Figure 2 recompute exactly from runs/*/verdicts/*.jsonl, runs/*/attribution/*.jsonl, analysis/clinician_sample_{claude,gpt}.jsonl and analysis/clinician_ratings_annotator{A,B}.json (e.g. 11,205/5,625 verdicts, 921 replays, 437 distress-assumption replays flipping 86%, Table 10 vs analysis/mixed_effects_bh_main_effects.csv). The audit's numbers can therefore be trusted as computed; the remaining concerns are about provenance, not arithmetic.
  2. The audit design is well executed: byte-identical probes across cells (verified in analysis/revision/summary.txt), persona-clustered inference throughout, a pre-registered κ ≥ 0.6 gate with AC1 as a prevalence check, and an explicit refusal to make confirmatory referral claims once rubric ambiguity surfaced.
Critical weaknesses
  1. The "clinician-reviewed" and "human annotation" claims that anchor the audit are not supported by the supplement as written. The abstract and §3 state "48 clinician-reviewed personas" and Appendix I says "All 48 personas went through four rounds of clinician review"; but scripts/build_clinician_packet.py:7,16,27–30 records that rounds 1–3 by the licensed clinician covered only 14 personas (the original 10 plus acu-crs-01..04) and that round 4 was built for "34 unreviewed full-grid personas", a round the paper itself describes as "assistant-assisted". For the human annotators, the server-side saved_at stamps in analysis/clinician_ratings_annotator{A,B}.json show 583 of A's 731 ratings saved on 2026-09-21 in 4.9 h and all of B's on 2026-09-19..22, at a median of 27–30 s per turn (P25–P75 ≈ 22–37 s, no gap under 15 s) although each rated dimension carries a free-text rationale of median ≈200 (A) / ≈385 (B) characters and most turns carry several dimensions; gap length is uncorrelated with rationale length (r = −0.01 / −0.08), whereas A's August ratings on the same interface ran at a median of 275 s per turn. The "pre-rating calibration answers" (§4; Appendix B) are stored in clinician_calibration_annotator{A,B}.json with saved_at 2026-09-22, after all of A's and 714/731 of B's ratings. Because the human-reference findings (A–B referral κ = 0.30 and its "two interpretations" reading, "both annotators are systematically stricter", Table 3 row 1, Figure 3b) rest on these ratings, their provenance must be clarified before the audit can be assessed.
  2. A full-census alternative rater was computed and not reported, and two implementation facts contradict the method description. configs/full_grid.yaml:97–101 configures gpt-4o-mini as a "second full-census scorer ... on every turn (not a sample)"; runs/full-grid-v0-*/verdicts_secondary/ holds all 11,205 verdicts, and against the local judge they give κ = 0.50 (recognition), 0.55 (referral), 0.30 (sycophancy) with 1.5–1.7× higher failure rates. The paper mentions gpt-4o-mini only in the unreadable Figure 1 and states in §6 "we report every alternative we computed". Separately, Appendix M says the summarizer is "llama-3.3-70b-versatile", but configs/full_grid.yaml:76–80 and scripts/run_pilot.py:554–561 use openai/gpt-oss-120b, i.e. the judge writes the summary memory it later judges against; and runs/registry.db records llama-3.2-3b as mlx-community/Llama-3.2-3B-Instruct-4bit, a 4-bit quantised local model, undisclosed in §3 although the strongest surviving claim (S1) is a gap between that model and two full-precision API models. For a paper whose thesis is that undisclosed measurement choices move conclusions, these omissions determine my recommendation.
Questions for authors
  1. How were the 2026-09-21/22 ratings produced? Were they entered live in the rating_api.py interface, pre-written offline and pasted, or drafted with LLM assistance? What are the two annotators' professional qualifications (the text says "human annotators", Figure 1 and all file names say "clinician")?
  2. Why do both calibration files carry saved_at timestamps after the ratings, given §4/Appendix B describe them as answered before rating? Was an earlier version submitted?
  3. Please list, per persona, which review rounds it received and who performed round 4. Are 34 personas correct as "never reviewed by the independently contracted licensed clinician"?
  4. Please report the gpt-4o-mini full-census agreement (κ/AC1 per dimension) and the Table 2 / Figure 3a contrasts under that judge, and reconcile with §6's "every alternative we computed".
  5. Which summarizer model was actually used, and was llama-3.2-3b run in 4-bit? Please also state reasoning_effort (low for gpt-oss, none for qwen per harness/groq_reasoning.py) and max_tokens (768 for gpt-oss-20b vs 512) in §3.
3 comments
AuthorsOpenReview ↗

Response (1/2): annotation provenance and persona review

(Part 1 of 2: Q1–Q3)

We thank the reviewer for an unusually careful review. We have checked each observation against our files, and every factual point is correct. We explain what happened, report what was missing, and list the corrections we will make. We take responsibility for the errors in the manuscript.

Q1–Q2. Human annotations. Both annotators are psychologists external to the author team: one holds a PhD in psychology and is a professor of psychology; the other is a consultant clinical psychologist. Each received the 731-verdict sample as a spreadsheet, without any automated verdicts or rationales, and independently wrote a PASS/FAIL judgment and a rationale for every item. The authors then entered the returned spreadsheets into the rating interface, item by item. The saved_at timestamps therefore record data entry, not rating. This accounts for the ~30 s spacing and for the absence of any relation between that spacing and rationale length. Annotator A’s 148 entries on 3–4 August were entered directly in the interface by the annotator while piloting it. The calibration answers on the referral rubric were written by each annotator before rating and entered at the end of data entry on 22 September, which is why their timestamps follow the ratings. The revision will state that the timestamps reflect data entry. The files are named "clinician" because the interface was built for this annotation; the revision will describe both annotators by their qualifications.

Q3. Persona review. All 48 personas were reviewed. Rounds 1–3 were conducted by the consultant clinical psychologist (the clinician referred to in the paper); round 4 covered all 48 personas and was conducted by both psychologists. An AI assistant was used only to render persona files into the review-packet format; it did not perform any review. Appendix I's description of round 4 as "assistant-assisted" was unclear and invites the reading the reviewer took.

ArcPersonasRounds
Stable controlctl-stb-01, 021, 4
Stable controlctl-stb-03 – 10 (8)4
Gradual depressive escalationdep-esc-01, 021, 4
Gradual depressive escalationdep-esc-03 – 10 (8)4
Medication discontinuationmed-dsc-01, 021, 4
Medication discontinuationmed-dsc-03 – 08 (6)4
Emerging psychosispsy-emg-01, 021, 4
Emerging psychosispsy-emg-03 – 08 (6)4
Recovery with relapserec-rel-01, 021, 4
Recovery with relapserec-rel-03 – 08 (6)4
Acute-onset crisisacu-crs-01, 022, 4
Acute-onset crisisacu-crs-03, 043, 4

The 34 personas written for the full grid were not part of rounds 1–3, so the phrase "34 unreviewed full-grid personas" in scripts/build_clinician_packet.py describes their status when the round-4 packet was built. They were then reviewed in round 4 by the same clinical psychologist, together with the second psychologist. The revision will include this table and note that the two annotators had reviewed the personas, though not any model responses, before rating.

(Q4–Q5 follow in Part 2.)

AuthorsOpenReview ↗

Response (2/2): second full-census judge and implementation details

(Part 2 of 2: Q4–Q5)

Q4. Full-census gpt-4o-mini judge. gpt-4o-mini was run as a second judge on every turn (runs/full-grid-v0-*/verdicts_secondary/), and the manuscript does not report it. The §6 sentence "we report every alternative we computed" is therefore false as written. It was written during revision without accounting for this judge, and we withdraw it.

Agreement with the original judge (all 5,625 confirmatory verdicts):

DimensionnRawκAC1Fail, originalFail, gpt-4o-mini
Recognition60375.5%0.500.5428.5%47.1%
Referral43277.8%0.550.5729.6%49.1%
Sycophancy68463.5%0.300.2843.9%67.0%
False alarm3,90699.7%0.291.000.1%0.3%

Table 2 under gpt-4o-mini (failure %, none / summary / rag; Wilson CIs in the revision):

Dimensiongpt-oss-20bqwen3.6-27bllama-3.2-3b
Recognition43 / 46 / 3733 / 33 / 3660 / 70 / 66
Referral35 / 35 / 3833 / 29 / 3379 / 77 / 81
Sycophancy76 / 80 / 8249 / 50 / 5170 / 62 / 83

Figure 3a contrasts under gpt-4o-mini (pp, persona-cluster bootstrap 95% CI):

ContrastRecognitionReferralSycophancy
summary − none+4.5 [−0.5, 10.0]−2.1 [−10.0, 5.9]−0.9 [−7.6, 6.7]
rag − none+1.0 [−5.2, 6.6]+1.4 [−6.7, 8.0]+7.0 [0.4, 13.3]
llama − gpt-oss+22.9 [15.3, 32.2]+43.1 [30.9, 59.4]−7.9 [−15.3, −0.9]
llama − qwen+31.3 [23.1, 41.5]+47.2 [35.5, 64.2]+21.5 [11.5, 31.0]
gpt-oss − qwen+8.5 [2.9, 15.8]+4.2 [−4.8, 12.5]+29.4 [19.3, 38.6]

What changes:

  1. S1: llama-3.2-3b remains worst on recognition, but under gpt-4o-mini the gap is 1.5–1.9×, not ≥2.6×. S1 will be restated as a direction that holds under all six raters, with a rater-dependent magnitude.
  2. S2: recognition and referral memory contrasts remain small under both judges; sycophancy under retrieval does not (+7.0 pp, 95% CI excluding zero). The equivalence conclusion will be restricted to recognition and referral.
  3. Sycophancy ranking: under gpt-4o-mini, gpt-oss-20b, not llama-3.2-3b, fails most often.
  4. Table 3: gpt-4o-mini will be added as a further alternative rater; it is itself an instance of the paper's thesis.

Q5. Implementation facts.

  • Summarizer: gpt-oss-120b, the same model as the judge; Appendix M is wrong. The judge therefore wrote the summary memory it later judged against. We will correct Appendix M and list this as a confound for the summary condition.
  • llama-3.2-3b: run locally as mlx-community/Llama-3.2-3B-Instruct-4bit (4-bit). gpt-oss-20b and qwen3.6-27b were served via the Groq API, whose serving precision we cannot verify. S1 therefore compares three deployed configurations, not models at matched precision; §3 will say so.
  • Generation settings: reasoning_effort was "low" for gpt-oss models and "none" for qwen3.6-27b; max_tokens was 768 for gpt-oss-20b and 512 otherwise. §3 will state these.

The reviewer's closing point is fair: this paper argues that undisclosed measurement choices move conclusions, and it should have met that standard itself. We are grateful for the scrutiny.

We hope these analyses and corrections address the reviewer’s concerns, and we would be grateful if the reviewer would reconsider their assessment in light of them.

I appreciate the candour of this response; the per-persona table and the gpt-4o-mini analyses are what I asked for. Two things keep my assessment where it is. First, the data-entry explanation for the annotation timestamps is plausible, but it currently rests on the authors’ account alone. Since the human reference is the anchor of the audit, the original spreadsheets or their metadata should be part of the release. Second, the corrections change what the paper can claim. With the second judge, S1 weakens, the sycophancy memory and ranking results change, and the summary condition is confounded by the judge writing its own memory. The paper’s contribution is to identify which conclusions survive measurement choices, and fewer survive than the submission states. I would encourage resubmitting with these results at the centre. I am keeping my rating unchanged.

Reviewer_otdROpenReview ↗
Rating
2(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper introduces SafeDrift, a longitudinal benchmark for evaluating the safety of memory-augmented mental-health agents. It evaluates 48 clinician-reviewed personas across three models and three memory conditions, while auditing evaluator reliability, metric aggregation, and memory-based failure attribution. The results show that the recognition-failure gap between the smallest and larger models is robust across five raters, whereas the referral-failure gap is not. The paper also demonstrates that evaluation choices can change conclusions about mitigation effects and memory attribution.

Critical strengths
  1. The paper highlights the often-overlooked reliability of evaluation pipelines in longitudinal agent safety assessment, which is an important problem.

  2. linician-reviewed personas and identical scripted safety probes improve comparability across model–memory conditions, which is a thoughtful experimental design.

Critical weaknesses
  1. The memory-effect conclusions are not fully supported by the reliability audit. The paper identifies substantial disagreement among raters on referral and sycophancy, yet the primary memory-effect analysis still relies on the local judge for these dimensions. Although the authors acknowledge this limitation, the reliability audit is not fully reflected in the subsequent effect analysis. Reporting memory-condition contrasts under alternative raters on the validation subset, or separating conclusions by dimension-level reliability, would help establish which findings are robust.

  2. The memory-masking analysis captures only a limited aspect of memory's influence. The counterfactual replay removes the current memory injection while retaining the original conversation history. Consequently, it cannot capture memory effects mediated through earlier agent responses and subsequent user turns, which may be important in longitudinal settings. The single stochastic replay per case further limits interpretation of unsafe-to-safe transitions. The authors should clarify that this procedure estimates a conditional, turn-level effect rather than the overall contribution of memory to longitudinal safety failures.

  3. The equivalence conclusion is sensitive to the chosen margin. The claim that memory-condition differences are negligible relies on a ±10\pm10-pp equivalence margin, while none of the pooled contrasts meets the stricter ±5\pm5-pp margin. The rationale for the chosen margin is not sufficiently established, and model-specific estimates remain uncertain. The authors should better justify the margin and qualify the scope of the equivalence conclusion. In addition, because each persona–model–condition combination is run only once, the persona-clustered bootstrap does not capture variability across generation seeds.

Questions for authors

Refer to the weaknesses.

3 comments
AuthorsOpenReview ↗

Response: memory contrasts under a second judge, scope of masking, margin

We thank the reviewer for a careful and constructive review. We agree with all three points. Below we report new analyses run on the released data and the concrete revisions they lead to.

1. Memory conclusions should reflect the reliability audit.

We agree this was the main gap: the audit showed referral and sycophancy are rater-sensitive, yet the memory analysis used a single judge. We re-estimated every pooled memory contrast under a second full-census judge (gpt-4o-mini, run on all 11,205 turns), alongside the original judge. Persona-cluster bootstrap, 95% CIs, percentage points:

ContrastOriginal judgeSecond judge (gpt-4o-mini)
Recognition, summary − none+0.5 [−5.7, 6.9]+4.5 [−0.5, 10.0]
Recognition, rag − none−3.0 [−9.7, 3.6]+1.0 [−5.2, 6.6]
Referral, summary − none−2.1 [−9.5, 5.4]−2.1 [−10.0, 5.9]
Referral, rag − none−0.7 [−8.5, 6.8]+1.4 [−6.7, 8.0]
Sycophancy, summary − none−1.8 [−10.4, 6.5]−0.9 [−7.6, 6.7]
Sycophancy, rag − none+1.8 [−7.8, 11.3]+7.0 [0.4, 13.3]

Five of six contrasts remain small under both judges. The sixth does not: under the second judge, retrieval memory is associated with an increase in sycophancy failures of 7.0 pp, with a 95% CI excluding zero. This is the failure mode the reviewer anticipated, and it is the paper's own thesis applied to its own conclusion: a different rater changes the result. We will therefore (a) report all memory contrasts per dimension under both full-census judges, (b) restrict the "small memory effect" conclusion to recognition and referral, and (c) report the retrieval-related increase in sycophancy as a finding. We also re-estimated the contrasts on the 731-verdict validation subset under all five raters. With ~110 verdicts per memory condition the 95% CIs span about ±20 pp, so we will report that subset as underpowered for memory contrasts, not as supporting evidence.

2. Scope of memory masking.

We agree, and will make the distinction explicit. The memory-condition comparison (Table 2) estimates the total effect of memory: histories are allowed to diverge, so effects carried through earlier agent replies and later user turns are included. The masking replay estimates only a direct, turn-level effect, conditional on an unsafe turn and the realized history. We will describe it that way throughout and remove any wording that reads it as memory's overall contribution to failures. We also agree that a single stochastic replay cannot separate memory removal from sampling variability. We will add a no-intervention replay baseline (same turn, memory kept) and repeated replays, and report flip rates relative to that baseline.

3. Equivalence margin and seed variability.

The ±10 pp margin was not pre-specified, and we agree it should not carry the conclusion. We will replace binary equivalence with the largest effect each contrast excludes (the bound of its 90% CI), reported under both judges so readers can apply their own margin. Pooled, the original judge excludes effects larger than 5.8–9.6 pp on every contrast; the second judge does the same except sycophancy under retrieval. Per-model contrasts are wider (up to ±17 pp), and we will say so.

On seeds, the reviewer is right: each persona–model–condition was run once, so the persona-clustered bootstrap reflects variation across personas but not across generations. We will state this as a limitation and add repeated runs with independent seeds for the main contrasts.

We believe these changes bring the paper's claims in line with its evidence, and we are grateful for the review that prompted them.

We hope these analyses and corrections address the reviewer’s concerns, and we would be grateful if the reviewer would reconsider their assessment in light of them.

Thanks for the additional analyses. The full-census second-judge evaluation partially addresses W1. However, W3 remains insufficiently addressed: the reported confidence bounds do not adequately justify the remaining “small memory effect” claim, and the independent-seed experiments have only been proposed, with no results provided.

I am raising my rating from 1 to 2 to acknowledge the partial improvement, while maintaining my concerns about the justification and reproducibility of the memory-effect conclusions.

Thank you for raising your score and for the precise statement of what remains.

W3, the "small memory effect" claim. We agree the bounds do not support it, and we will remove it. The revised paper will state only what the intervals show:

  • Under the original judge, the pooled contrasts exclude effects larger than 5.8–9.6 pp (90% CI bounds).
  • Per-model contrasts cannot exclude effects of up to about 17 pp.
  • Under the second judge, retrieval memory is associated with a 7.0 pp increase in sycophancy failures (95% CI 0.4 to 13.3).

The conclusion becomes: no large pooled memory effect was detected for recognition or referral; pooled effects of up to about 10 pp and per-model effects of up to about 17 pp remain possible. We will make no claim of negligibility or equivalence.

Seeds. We have no multi-seed results to report within the discussion period. Until repeated runs with independent seeds are available, the abstract and limitations will describe all memory contrasts as single-run estimates whose uncertainty reflects variation across personas, not across generations.

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

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