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Under review as a conference paper at ICLR 2027

Early Warning of Personalization Model Degradation from User Histories and Hidden States

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Abstract

Personalization encoders continually update hidden representations of evolving user interactions to guide recommendations or user-specific generation. Future quality can degrade even while recent output quality appears normal, limiting timely intervention. We ask whether user interaction history and the corresponding encoder states form a joint record that exposes warning evidence of such degradation earlier. We call this relation *Temporal State-History Matching* (TSHM). We establish conditions under which a future-quality-relevant change remains visible in the observed state component of this record while recent utility responds only weakly. We then propose `CoTRAC`, a monitoring framework in which a pluggable sentry learns a broad History-State warning and refines it through Regularity, which measures local organization of projected state motion, and Transition, which compares the latest update with a causal prediction. We evaluate dataset-specific subsets of eight sentry designs on MovieLens-1M, PENS, and Amazon Product Reviews, monitoring 13 frozen personalization host instances. Against matched recent-utility controls, History-State warning improves mean normalized area under the precision-recall curve (nAUPRC) by 0.11 on MovieLens and is higher in all 160 encoder-sentry-horizon settings. The same direction occurs in 67/80 PENS and 21/24 Amazon settings. Regularity and Transition affect event detection, warning lead, and false alarms differently, and their joint use does not systematically dominate the individual views. Source-only warnings retain 86.4% of self-warning discrimination on MovieLens and 83.6% on PENS when applied to held-out encoders. These results establish History-State evidence as a prospective warning source beyond recent utility while showing that finer structured effects are more context-dependent.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Early warning, failure prediction, sequential recommendation, user preference modeling, personalized generation, hidden-state monitoring, temporal modeling

Reviews

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1234this paper, Top 49%
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_5vrDOpenReview ↗
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2
Confidence
3
Informativeness
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Paper summary

The paper aims to identify the prediction of future utility degradation from user histories and hidden states of frozen personalization models. It introduces Temporal State-History Matching and CoTRAC, which combines a learned warning predictor with regularity and transition-based constraints. Experiments cover multiple recommendation benchmarks.

Critical strengths

a) Predicting future utility loss in frozen personalization models is a relevant problem. The MovieLens experiments show consistent improvements over learned recent-utility predictors.

b) The evaluation covers several domains and host architectures.

Critical weaknesses

a) The motivation does not clearly establish the technical challenges being resolved. The paper does address an important problem, but the challenges motivating the proposed method are not clearly identified or addressed. It does not clearly distinguish predictable preference evolution from previously unseen behavioral patterns. It also does not establish whether the learned warning remains useful when the relationship between history and degradation changes over time. Given existing research on temporal prediction and failure monitoring, the technical contribution beyond predicting future outcomes from historical features remains unclear.

b) The “matching” formulation does not establish a distinct modeling contribution. The authors call the ordered pairing of user interactions and corresponding hidden states TSHM. However, this appears to be a standard way of considering temporal observations. CoTRAC then learns to predict future utility degradation from these inputs, following a standard supervised prediction setup. Calling this record a new “matching” relation does not make it a new modeling contribution. Could the authors clarify what technical challenge TSHM resolves beyond this setup and why the proposed Regularity and Transition mechanisms are needed?

c) The theoretical result establishes local sensitivity, not earlier detection, and the visibility argument relies on the states alone. Could the authors clarify how this result supports earlier warning or the additional value of pairing interactions with states?

d) Why is there a mismatch between the History-State and utility-warning architectures on PENS, whereas MovieLens and Amazon use architecture-matched comparisons? Could these architecture differences contribute to the reported improvement?

e) The paper emphasizes the pairing of history and hidden states. However, it does not provide history-only and state-only baselines to determine whether pairing these inputs adds any predictive value.

Questions for authors

Please answer the weaknesses.

6 comments
AuthorsOpenReview ↗

Clarifying TSHM, Joint Evidence, and Prospective Warning

We thank the reviewer for recognizing this problem's importance. CoTRAC tests whether user histories and hidden states can warn of future quality loss while recent outputs still look good. We clarify what is new and also present supportive new tests, based on how consequential the concerns are.


Q1 [W-a]. Isn't this just predicting the future from past data?

A recommender predicts what a user may like next. In contrast, CoTRAC tests whether the recommender itself may soon perform worse, even if its recent recommendations look fine. We hence propose a monitor for an existing frozen model. The goal is not to build another recommender. On MovieLens, history–state warnings beat recent-quality warnings in 160/160 matched comparisons (Sec. 6.1).

Key takeaway: CoTRAC predicts future decline in a model's own quality. The goal is not the user's next preference.


Q2 [W-e]. Is using history and states together really better?

We predicted the same future drops using history alone, states alone, or their learned correspondence. Using both gave the best mean result across four MovieLens models:

ModelHistoryStatesBothExtra gainGain by seed (11, 23, 47)
GRU4Rec0.10210.10290.1160+0.0132+0.0107, +0.0138, +0.0150
SASRec0.05740.06880.0716+0.0028−0.0003, +0.0025, +0.0060
LRURec0.13670.21060.2201+0.0095+0.0120, +0.0074, +0.0091
Mamba4Rec0.13100.21970.2213+0.0016+0.0009, +0.0012, +0.0026

Mean nAUPRC (higher is better). New sampled warm-only tests: 3 warning architectures, 3 seeds, 4 horizons. Extra gain compares Both against States alone. Joint monitoring won 11/12 host–seed comparisons; gains are clearer for GRU4Rec and LRURec. With the warning model fixed, correct state order also beat reversed order in 124/144 comparisons.

Key takeaway: Both inputs work best on average across four models, and we observe that time order makes a difference.


Q3 [W-b]. What does TSHM add, and why R and T?

As users interact, a personalization model updates its internal picture of their interests. TSHM tracks what users did, how the model's state responded, and how the two change together. A learned correspondence helps the warning model use both, without changing the host model.

Regularity (R) asks if states change unusually. Transition (T) asks if the latest change was expected. Both make these patterns easier to use. We deliberately assigned R/T measurements to the wrong observations, keeping the trained adapters and capacity fixed. Correct pairing won 441/576 validation comparisons.

Key takeaway: TSHM monitors how interactions and states evolve together; R and T highlight useful patterns in that evolution.


Q4 [W-c]. What does the theory tell us about early warning?

Under stated conditions, the theory shows recent quality can look unchanged even when hidden states reflect a change linked to worse future quality. This explains why output-quality monitoring can miss a warning signal. Our experiments test whether learned monitors can use that signal (Sec. 3; App. D.2).

Key takeaway: While the theory explains how an earlier signal can exist, the experiments test whether it can be recognized.


Q5 [W-d]. Could PENS gains come from different warning architectures?

On MovieLens, history–state and recent-quality warning use matching architectures, and history–state wins 160/160 comparisons. Amazon also uses matched architectures. On PENS, we chose one recent-quality warning architecture using MovieLens results, then trained it on PENS. No PENS test outcomes influenced that choice. The PENS design therefore cannot explain the main MovieLens finding.

Key takeaway: The strongest evidence comes from architecture-matched comparisons, independent of the PENS choice.


Q6 [W-a]. What if user behavior changes unexpectedly?

Changing behavior is exactly why CoTRAC tracks user interactions and evolving hidden states. We test whether those changes predict future quality drops for held-out users. A change in what those warning signs mean in a new environment is a different question.

Key takeaway: CoTRAC monitors changing user behavior. Note that a new link between warning signs and outcomes requires a different test.


Overall: CoTRAC asks whether we can detect signs that a personalization model is heading toward worse performance before recent output quality reveals it. The original results show an advantage over recent-quality warning. New tests show that combining histories and states helps, and that their time order matters.

AuthorsOpenReview ↗

Gentle reminder for feedback

Dear Reviewer 5vrD,

Thank you again for your review. As the discussion period approaches its close, we wanted to gently follow up on our response and additional experiments. We have now directly addressed the main concerns raised in your review:

  • Novelty and contribution of TSHM: We clarified how CoTRAC differs from ordinary prediction. It monitors whether a personalization model's future quality may decline even while recent outputs look good. The original MovieLens experiments support this distinction in 160/160 matched comparisons.

  • History-only vs. state-only monitoring: We added direct comparisons across four models and three independent seeds. Joint monitoring achieves the highest mean performance on all four models, with positive gains in 11/12 host–seed comparisons. Correct temporal ordering also improves prediction in 124/144 comparisons.

  • Role of R/T and theoretical justification: We clarified what the theory establishes and how R/T capture different patterns in state evolution. Additional tests show that correctly matched R/T evidence improves predictions in 441/576 validation comparisons.

  • PENS comparison: We clarified the architecture-selection procedure and showed why the PENS design does not affect the original architecture-matched MovieLens findings.

We would greatly appreciate your feedback on whether the new results and clarifications address your main concerns, particularly regarding the paper's scientific contribution. We would be happy to clarify any open concerns before the discussion closes. Thank you for your time and consideration.

Thanks for the responses. I read them carefully. History-only and state-only comparisons answer my empirical question in point (e).

However, I would request that the authors address the questions as raised rather than change them. For exp. In point (a), I wanted to understand what makes it difficult to predict a decline in recommendation quality from user histories and hidden states. Q1 instead says that CoTRAC predicts whether the recommender itself may perform worse. I understood that from the paper. I also asked whether the warning still works if the relationship between history and degradation changes over time (which I believe is a more important problem when considering temporal decay). Q6 acknowledges that this remains open.

In point (b), my concern was about the method itself. What makes this a new “matching” problem? And after reading Q3, I still don’t see an answer to it.

I believe the paper needs substantial revision to clarify its main motivation and its contribution to existing research. I also hope the authors demonstrate a clear understanding of their submitted work and the relevant literature in their responses. In light of this, I am decreasing the score.

Reviewer_mTt8OpenReview ↗
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2
Confidence
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Informativeness
2
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Paper summary

The paper studies whether a user's past interactions and the internal states of frozen personalisation models can jointly help predict a drop in future task performance. They propose the CoTRAC framework that uses a History state (H) sentry to monitor past interactions, and improves it with two additional components: Regularity (R) and Transition (T). The paper also provides a theoretical result explaining when monitoring these internal states, along with recent task performance, can help detect such drops. The experiments compare this approach with methods that monitor only task performance and evaluate different model combinations, changes in downstream tasks, and the use of LLMs to predict performance issues before generation.

Critical strengths
  • Details of the method are well presented
    The paper is clearly written and defines the inputs used for causal warning, keeps the host models frozen, separates users between warning-training and test sets, and ensures that the targets and evaluation positions are matched. MovieLens and Amazon also include H/U controls with matched architectures.

  • Reporting of the limits of the method.
    I appreciate that the paper also reports negative results and discuss them, the negative absolute nAUPRC values on Amazon, actual false-alarm rates, and the cases where gains are not consistent across structured settings. It also clearly states that the theoretical result establishes conditional observability, not a guarantee of successful prediction.

Critical weaknesses
  • Contribution of the proposed method over and above existing literature is not clearly isolated
    The paper does not include controlled history-only, current-state-only, and state-trajectory-only input ablations, or temporal-order ablations with otherwise matched warning models, so there is insufficient evidence to quantify how much the joint temporal record actually contributes to the results. Further, although the authors cite prior work on confidence-based failure prediction and pre-generation state probing, they do not compare their method against these approaches. Including baselines based on causally available output-confidence features and simple hidden-state probes, trained using the same future-degradation targets and prediction horizons, would help establish the specific benefit of the proposed approach over existing methods.

  • The benefits of the structured refinements are not sufficiently established.
    The improvements from R and T are generally small, around 10−310^{-3} nAUPRC (Table 2). However, the paper specifies only seed 42 (Table 9), and its bootstrap analysis captures variation across held-out users, but they do not measure the variance due to retraining. The adapter experiment uses H's representation along with the R/T evidence, but I think there should be a H-only adapter baseline with matched model capacity that would be an apples-to-apples comparison that should clearly isolate the contribution of R/T.

  • Improved detection at the same false-alarm rate is not demonstrated.
    On Amazon at horizon 5, adding T to H increases event recall from 0.7064 to 0.7145 which is a good sign, but the realised false-alarm rate (FAR) also rises from 0.6931 to 0.7433 (Table 32, p. 63). These rates are much higher than the nominal target of 0.10. Although the authors correctly distinguish between nominal and realised FAR, I think the the results do not sufficiently establish that the method detects more failures under the same false-alarm budget. A comparison of recall and warning lead time against FAR would provide stronger evidence of practical usefulness of the proposed method.

  • Source-only reuse should include source-ensemble ablations.
    RQ3 combines rank-normalised warnings from multiple source hosts using common evaluation indices and checks whether the combined warnings can predict performance drops in a held-out host. This shows that warnings can be reused across different hosts. However, the paper does not compare this approach with similar ensembles based only on utility or interaction history. Hence, it remains unclear whether hidden-state information provides any additional benefit over these simpler inputs. Applying the same aggregation method to these baselines would help isolate this contribution. Comparing individual source-host warnings against the combined predictions would also help quantify the benefit of ensembling.

Questions for authors

Please check the weaknesses section

2 comments
AuthorsOpenReview ↗

Joint History–State Evidence, Structured Refinements, and Warning Reliability

We thank the reviewer for recognizing the careful evaluation and rigor in reporting. Our new tests address critical concerns.


Q1 [W-1]. Could simpler warning methods do just as well?

We tested recent-quality warning with simpler history alone and hidden states alone, and compared them with the proposed learned history–state correspondence on the same future quality drops. Using both history and states gave the best average result on all four MovieLens models:

ModelHistory-onlyHidden States-onlyBothExtra gainGain by seed
GRU4Rec0.10210.10290.1160+0.0132+0.0107, +0.0138, +0.0150
SASRec0.05740.06880.0716+0.0028−0.0003, +0.0025, +0.0060
LRURec0.13670.21060.2201+0.0095+0.0120, +0.0074, +0.0091
Mamba4Rec0.13100.21970.2213+0.0016+0.0009, +0.0012, +0.0026

Mean nAUPRC (higher is better); new sampled warm-only test: 3 warning architectures, 3 seeds, 4 horizons. Extra gain = Both minus States. Joint warning beat state-only in 11/12 host–seed comparisons. These tests strengthen the original 160/160 MovieLens wins over recent-quality warning. The state-only test also serves as a direct hidden-state probe for the same future outcome. Architectural simplicity was also examined across eight sentries, ranging from simpler Prefix-MLP to more elaborate temporal and risk-based designs, with 20/20 matched H/U wins per sentry (160/160 overall). The new three-sentry experiments separately isolate the contribution of history and hidden states.

Key takeaway: TSHM performs best on average across all four tested models.


Q2 [W-1]. Does the order of hidden states actually matter?

We kept the trained warning model and the states unchanged, but reversed the order of those states. The correct order gave better predictions in 124/144 comparisons, with a higher average score for every tested model. The model is using more than a collection of states - i.e., it responds to how they change over time.

Key takeaway: The sequence of hidden-state changes matters when predicting future quality drops.


Q3 [W-2]. Where do the gains from Regularity (R) and Transition (T) come from?

The original warning model already sees the hidden states. R makes unusual state changes easier to recognize, while T shows whether the latest change was expected from earlier ones. These patterns help the model decide when to adjust its warning.

We then checked whether the right measurements matter. We gave the trained model R/T measurements belonging to other observations, without changing the model, refinement adapters, or their capacity. Correct pairing led to better predictions in 441/576 validation comparisons. New three-seed tests also show that the effect depends on the host. This directly tests the value of matching structured evidence to the right observation, rather than assuming R/T always improve a warning.

Key takeaway: Correctly matched R/T measurements help the trained warning model, with the same adapter capacity.


Q4 [W-3]. Does detecting more problems simply mean more false alarms?

Not always. In Amazon, extra detections came with more false alarms, and we report both (Table 32). In new MovieLens tests, two models detected more future drops with slightly fewer false alarms. For LRURec, recall rose 27.38% → 28.24% while the false-positive rate fell 5.40% → 5.36%. For Mamba4Rec, recall rose 29.54% → 30.08% while false positives fell 5.94% → 5.88%. These results come from a separate 5%-calibrated test.

Key takeaway: Extra state-change evidence can improve detection without necessarily raising false alarms. Note that the trade-off varies by setting.


Q5 [W-4]. Can warnings from other models help predict drops in a new model?

We combined warnings from other trained personalization models and tested them against future quality drops in a held-out model. That model supplied no warning scores or hidden-state coordinates. The combined warnings still predicted future drops better than the event-frequency baseline: mean nAUPRC was 0.152 on MovieLens and 0.0258 on PENS, positive in 160/160 and 80/80 tested settings (Tables 37, 40). This tests whether warning information can be reused across models. Note that we do not claim that averaging is the best possible way to combine it.

Key takeaway: Warnings learned from other models remain useful for held-out models.


Overall: Our new tests show why joint history–state warning deserves attention: combining the two inputs helps, their time order matters, and correctly paired R/T evidence changes warning quality. Along with the original results, these findings support CoTRAC's central claim: a model's evolving internal evidence can reveal future quality risks that recent output quality misses.

AuthorsOpenReview ↗

Gentle reminder for feedback

Dear Reviewer mTt8,

Thank you again for your detailed review. As the discussion period approaches its end, we wanted to gently follow up on our response and additional experiments. We have now directly addressed the main concerns raised in your review:

  • Contribution beyond simpler warning methods: We added history-only, state-only, and joint-monitoring comparisons across four models and three independent seeds. Joint monitoring achieves the highest mean performance on all four models, with positive gains in 11/12 host–seed comparisons. Correct temporal ordering also improves prediction in 124/144 comparisons.

  • Role and reliability of R/T: We added three-seed evaluations and tested whether the R/T measurements must correspond to the correct observations. Correctly matched evidence performs better in 441/576 validation comparisons, with the trained models and adapter capacity unchanged.

  • Detection and false alarms: Additional experiments show that R/T can improve detection without increasing false alarms. On LRURec and Mamba4Rec, event recall improves while false-positive rates slightly decrease. We also retain the less favorable Amazon trade-offs.

  • Warning reuse across models: We clarified the source-only evaluation and the absolute results already reported in Tables 37 and 40. Warnings from other models remain informative for held-out models, with positive discrimination in all 160 MovieLens and 80 PENS comparisons.

We would greatly appreciate it if you could comment on whether these new results address your main concerns, particularly regarding the experimental evidence. We would be happy to clarify any open concerns before the discussion closes. Thank you for your time and consideration.

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

The paper formulates early warning of personalization degradation, that is, predicting a future drop in task utility while recent output quality still looks normal, and names the pairing of interaction history with the corresponding hidden state TSHM. CoTRAC attaches a pluggable sentry to a frozen host. H learns a broad warning from history and state windows, while R measures local regularity of the projected state trajectory and T measures the deviation of the newest state update from its causal prediction. R and T are trained without future labels and then applied as gated signed corrections to H. Evaluated on MovieLens-1M, PENS and Amazon Reviews with 13 frozen hosts, up to eight sentries and horizons 1, 2, 3 and 5, plus leave-one-encoder-out transfer and a pre-first-token LLM setting.

Critical strengths
  • Novelty of the problem formulation. Prospective degradation warning has not been posed as a task in its own right. The paper separates it cleanly from failure prediction, uncertainty estimation and drift detection, defines the prediction target over a future horizon rather than the current output, and specifies a monitoring interface that does not require interactions and hidden states to share a coordinate system. That last choice is what makes the formulation portable across heterogeneous personalization architectures.
  • Method design. Keeping the host encoder and task head frozen while the monitor is external and pluggable means the same framework applies to recurrent, attention-based and generative hosts without retraining any of them. The staged training order is consistent with the stated causal boundary, since the structured views are fitted from state trajectories alone and never see future utility or future degradation labels.
  • Experimental completeness. Thirteen frozen hosts across three datasets, multiple monitor architectures and four horizons give far broader coverage than is usual for internal-state probing work, and the study is extended to a change of downstream task, from recommendation to headline generation, and to a pre-generation interface on open-weight language models. The protocol also pins down what information is available at warning time and keeps the comparison against the utility baseline matched rather than merely parallel, and the authors report where the method fails to dominate as readily as where it succeeds.
Critical weaknesses
  • U sees only a scalar utility trace while H sees the full history plus a high-dimensional state window, so the clean sweep across all matched cells reflects input asymmetry rather than hidden-state content. The decisive history-only and state-only ablations are absent, and the TSHM claim rests entirely on the pairing being more informative than either part alone.

  • Because the adapter learns an arbitrary signed correction, nothing ties the RQ2 effects to the geometric meaning of R and T. A control fed an equal-dimensional random projection, or a temporally shuffled state trajectory, is needed to show that these are not simply a free residual fit.

  • nAUPRC is normalized by the event prevalence, yet the prevalence is never reported. The cross-cell means and the win counts therefore aggregate quantities that are not commensurable across hosts and horizons.

  • Amazon H nAUPRC is −0.009, which is below the prevalence reference, yet it is counted as supporting evidence. In that regime, H exceeding U only means that one uninformative ranker is less uninformative than another.

  • Source-only retention is a ratio of near-zero quantities and ranges from 27.7% to 136.9% across hosts, so its arithmetic mean of 83.6% is not a meaningful summary of transfer quality.

  • The host is frozen throughout the monitored window, so the predicted drop in nDCG or MRR may reflect exposure and popularity fluctuation in the offline log rather than degradation of the representation, which is the construct the narrative requires.

  • The separation result in Sec. 3 is a local, conditional statement whose assumptions are not given in the main text, and the paper concedes it need not hold for any particular trajectory. As presented it supports none of the empirical claims.

  • No experiment shows that acting on a warning improves downstream utility, although timely intervention is the stated motivation.

Questions for authors
  • What nAUPRC do history-only and state-only sentries achieve on the matched MovieLens cells, and what fraction of H do they recover?

  • Do the RQ2 effects persist when the adapter is fed an equal-dimensional random projection of the state window, or a temporally shuffled state trajectory?

  • What is the event prevalence for each dataset, host and horizon, and how are cells with different prevalence aggregated into the reported means and counts?

  • Can the retention ratio be replaced by a statistic that is stable near zero, with per-host transferred and self nAUPRC reported directly?

  • Since the host never changes during the monitored window, what mechanism drives the utility decline, and how is it distinguished from exposure-driven fluctuation?

  • Does triggering a simple fallback, such as non-personalized ranking or a truncated history window, on H-ranked warnings improve downstream utility relative to U-ranked or random triggering?

2 comments
AuthorsOpenReview ↗

Joint Evidence, R/T Attribution, and Evaluation Clarifications

We thank the reviewer for recognizing the novelty and breadth. Our new tests now address the core concern: do user history and hidden states together better predict future quality drops? We order our response based on the consequence of the concerns.


Q1 [W-1 / Reviewer Q1]. Is using both history and hidden states better than either alone?

We compared warnings using history alone, states alone, or their learned correspondence. All predicted the same future drops on the same test cases. Using both gave the best mean result on four MovieLens models:

ModelHistoryStatesBothExtra gain
GRU4Rec0.10210.10290.1160+0.0132
SASRec0.05740.06880.0716+0.0028
LRURec0.13670.21060.2201+0.0095
Mamba4Rec0.13100.21970.2213+0.0016

Mean nAUPRC; new sampled warm-only test: 3 warning models, 3 seeds, 4 horizons. Extra gain = Both − States. Both beat states alone in 11/12 host–seed comparisons. Correct time order beat reversed order in 124/144 comparisons. These supplement the original 160/160 wins over recent-utility warnings.

Key takeaway: The combination gives the best mean results on all four tested models.


Q2 [W-2 / Reviewer Q2]. Where do the gains from Regularity (R) and Transition (T) come from?

The warning model already sees hidden states. R makes unusual state changes explicit; T shows whether the latest change was expected. These measurements help it decide when to adjust a warning. To test whether the measurements matter, we deliberately attached R/T evidence to the wrong observations. We kept the trained model, adapters, and parameter counts unchanged. Correct pairing gave better predictions in 441/576 validation comparisons. The effect was strongest for LRURec and Mamba4Rec; gains varied by seed.

Key takeaway: Correctly matched R/T evidence helps prediction, even when the adapter and its capacity stay fixed.


Q3 [W-3 / Reviewer Q3]. Could different event frequencies make the results misleading?

Answer. Some models have more future quality drops than others. We compare both warnings on exactly the same cases and events, so adjusting for event frequency cannot change which method wins. Our averages summarize these comparisons. Note that they do not imply every setting is equally difficult. Event frequencies already appear in Tables 10, 11, and 15–17.

Key takeaway: Event frequency can affect the size of a gain, but not the winner of a head-to-head comparison.


Q4 [W-4]. What do the Amazon results show?

Amazon is difficult for both methods. History–State warning nevertheless wins 21/24 comparisons, improving mean nAUPRC from −0.023 to −0.009 and reducing probability errors (Brier, NLL, ECE). Both averages remain below the event-frequency baseline, as reported.

Key takeaway: Even where prediction is difficult, History–State warning improves on recent utility in most comparisons.


Q5 [W-5 / Reviewer Q4]. Is cross-model reuse supported only by unstable percentages?

No. We test warnings from other models against a held-out model's future drops, without using its own scores. Mean nAUPRC is 0.152 on MovieLens and 0.0258 on PENS, positive in 160/160 and 80/80 comparisons. PENS results are weaker. Tables 37 and 40 report each model's actual scores.

Key takeaway: Actual warning scores, not just retention percentages, support reuse.


Q6 [W-6 / Reviewer Q5]. Does lower quality mean the hidden state has failed?

No. CoTRAC defines degradation as a future decline in output quality, whatever its cause. Changing interests or item exposure can contribute. We would like to underline that the hidden states are warning evidence. We do not claim them to be cause of failure (Secs. 1, 3, 7).

Key takeaway: We predict whether quality will fall, without assuming why.


Q7 [W-7]. Does the theory guarantee an early alarm?

The theory identifies conditions where hidden states reflect changes linked to worse future quality while recent output quality hardly changes. This explains how a warning signal can exist. The experiments separately test predictions and alarms (Sec. 3; App. D.2).

Key takeaway: Theory explains why a signal may exist, while experiments test whether we can use it.


Q8 [W-8 / Reviewer Q6]. Must we show that acting on a warning fixes the problem?

Predicting a future decline and deciding how to prevent it are two different tasks. CoTRAC tests the warning. It is not a repair policy.

Key takeaway: Validating a warning does not require developing a repair.


Overall: The new tests strengthen the central finding: history–state monitoring provides warning evidence beyond recent utility. Event rates, transfer results, and limitations are already reported. We would like to stress that causal diagnosis and repair are separate research questions.

AuthorsOpenReview ↗

Gentle reminder for feedback

Dear Reviewer bhtr,

Thank you for your constructive review and for recognizing the novelty and breadth of our work. As the discussion period is closing in, we wanted to gently follow up on our response and additional experiments. We have now provided further evidence addressing your main concerns:

  • History-only vs. state-only monitoring: We added direct comparisons across 4 models and 3 independent seeds. Joint monitoring achieves the highest mean performance on all 4 models, with positive gains in 11/12 host–seed comparisons. Correct temporal ordering also improves prediction in 124/144 comparisons.

  • Contribution of Regularity and Transition: We tested whether the R/T measurements must belong to the correct observations. Correctly matched evidence performs better in 441/576 validation comparisons, while keeping the trained models and adapter capacity unchanged.

  • Prevalence and cross-model reuse: We clarified the matched evaluation procedure and pointed to the event-frequency tables and absolute transfer results already available in the submitted manuscript (Tables 10, 11, 15–17, 37, and 40).

We believe we have addressed your remaining concerns. We would highly appreciate your views on these new results and clarifications. Thank you again for your time and consideration.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Revised Submission

We have uploaded a revised manuscript incorporating the controlled experimental results and implementation clarifications discussed in our responses. The original problem formulation, theoretical results, and principal contributions remain unchanged. The revision includes additional RQ1 and RQ2 controls, with supporting methodological details and analyses in the appendices.

All newly added or revised content is highlighted in blue to facilitate identification of the changes, while the original manuscript content remains unchanged.

We welcome the reviewers' assessment of these additions during the remaining discussion period and would be happy to clarify any outstanding concerns.

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

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