acceptodds
Under review as a conference paper at ICLR 2027

From Hallucinated Targets to Runaway Repetition: Termination Control in Long Structured Generation

Abstract

Long structured generation requires models to learn both what information to produce and when to terminate. Data curation evaluates item-level correctness but overlooks how supervision content shapes stopping behavior. We study this in long-document relation extraction, where task-relative hallucinated targets contain entities outside an explicit candidate list. Across Qwen3 models at 1.7B, 4B, and 8B parameters, removing these targets reduces continuous pattern repetition by 24.65–34.63 percentage points and improves extraction quality. Replacing 15% of cleaned blocks one for one with real violating blocks raises 4B repetition from 5.52% to 9.71%, preserving inputs, block counts, and termination targets. Process decomposition shows that overall repetition can rise even as local copy gain falls. On identical prefixes at natural stopping points, raw-supervision models close their lists about 32 percentage points less often, yet retain near-certain EOS execution after a forced close. A single activation pulse along the cleaned-minus-raw direction shifts closing decisions bidirectionally, exceeds equal-norm random controls, and transfers to the replacement-trained model. At natural stopping points, it also reduces subsequent repetition in the raw 4B model by 10.94 percentage points. These results trace a specific supervision defect through reuse dynamics to an internal termination control component, establishing learned stopping behavior as a criterion for structured-data quality.

Primary area:
interpretability and explainable AI
Keywords:
structured generation, repetition, termination control, supervised fine-tuning, activation intervention

Reviews

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1234this paper, Top 32%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.50 over 4 reviews, above 68% of the others.
Reviewer_4eR9OpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
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Paper summary

This paper investigates how supervised fine-tuning (SFT) target defects—specifically hallucinated entities outside the candidate set—trigger severe runaway repetition in long structured text generation. The authors demonstrate that this repetition surge is driven by impaired termination control, characterized by a sharp drop in the model's decision to emit list-closing tokens (i.e., ]), rather than an increased tendency for local copying or an inability to execute EOS tokens once closed. Through contrastive activation additions and sparse autoencoders (SAE), they identify a causal, supervision-dependent representation at layer 32 that bidirectionally steers list-closing behavior, substantially mitigating tail repetition without degrading extraction recall.

Critical strengths
  1. The paper establishes an original connection between training data curation and generation termination control, challenging the traditional view that data quality merely concerns item-level factuality. It insightfully demonstrates that constraint-violating supervision content can directly undermine the model's high-level stopping preference, proving that content defects induce behavioral breakdown even when structural tokens and EOS positions remain perfectly standard.

  2. By modeling repetition through a competing-risk survival framework that decouples reuse exposure from persistence, the authors provide a rigorous and methodologically sound analytical lens. This formulation elegantly resolves the counter-intuitive paradox of surging overall repetition despite a declining local copying tendency, offering a precise understanding of the mechanics behind runaway generation.

  3. Through shared-prefix experiments, the study cleanly separates the high-level decision to close a structured list from the mechanical execution of the EOS token, locating the failure strictly at the close-or-continue juncture. The authors then deliver compelling causal evidence through activation steering—validated by random controls, layer sweeps, and SAE feature analysis—solidly linking internal representations at specific layers to generation trajectory recovery.

Critical weaknesses
  1. Scope Limited to a Single Task and Model Family: The empirical study is conducted exclusively on Chinese document-level relation extraction using the Qwen3 model family (1.7B, 4B, 8B). While the findings are consistent across model sizes and training seeds, it remains unverified whether this phenomenon generalizes to other structured generation tasks (e.g., code generation, SQL parsing, dense JSON tool calling) or other LLM model architectures (e.g., Llama, Gemma, Mistral).

  2. Interaction with Inference-Time Constrained Decoding Unexplored: In production settings, structured output is frequently governed by constrained decoding frameworks (e.g., Outlines, Guidance, SGLang, vLLM JSON-mode). While grammar masking cannot decide semantic stopping (since both ',' and ']' are syntactically valid), discussing or empirically demonstrating how constrained decoding interacts with this internal termination defect would substantially strengthen the paper's engineering and practical impact.

  3. Practical Application of the Intervention: The activation pulse intervention is tested at oracle/pre-selected prefix boundaries (natural stops, early points, pre-reuse points). The paper does not propose an online, automated trigger mechanism to deploy this steering vector dynamically during arbitrary open-ended decoding, which slightly restricts its utility as an inference-time mitigation tool.

Questions for authors

Q1: Clarification on Grammar/Constrained Decoding: In real-world deployment of structured JSON extraction, constrained decoding engines enforce schema adherence. When both continuing (e.g., generating {,) and closing (generating ]) are grammatically valid tokens, does constrained decoding alter the relative stop margin between raw and cleaned models, or does it leave the supervision-induced gap intact?

Q2: Generalizability across Model Families: Have the authors observed similar termination degradation and stop-margin collapse on non-Qwen architectures (e.g., Llama-3 or Mistral) when trained on constraint-violating structured targets?

Q3: Deployment of Activation Steering: The single-pulse intervention effectively reduces tail repetition when applied at natural stopping points. Could the authors clarify how one might automatically detect or calibrate the intervention point during continuous runtime decoding without access to reference stopping ground truth?

4 comments

We sincerely thank Reviewer 4eR9 for a thoughtful and encouraging review. We are grateful that the reviewer recognizes "an original connection between training data curation and generation termination control" that challenges "the traditional view that data quality merely concerns item-level factuality"; finds the competing-risk framework "a rigorous and methodologically sound analytical lens" that "elegantly resolves the counter-intuitive paradox" of rising repetition with declining local copying; and considers the shared-prefix and steering results "compelling causal evidence". We also thank the reviewer for rating the soundness without substantive concerns. The three questions concern generality and deployment, and we answer each with a new experiment (new Appendix P, in blue).

Q2 / W1: other model families

We repeated the 4B pipeline with Gemma3-4B-it, using the same supervision files and SFT recipe and Gemma's recommended decoding (T = 1.0, top-p 0.95, top-k 64), just as Qwen3 used its own (App. P.1). The termination degradation and stop-margin collapse reproduce:

  • Raw supervision raises continuous pattern repetition from 1.59% to 8.74% (+7.14 [6.20, 8.11]; 5.5-fold, vs. 5.9-fold for Qwen3-4B), lowers entity-pair F1 by 3.92 [3.58, 4.23] points, and raises generated out-of-candidate blocks from 4.8% to 30.4%.
  • OBR 15% raises repetition by 2.57 [1.94, 3.21] points while changing mean output length by only 121 tokens (+2.7%), ruling out length even more cleanly than in Qwen3.
  • Both exposure (+0.047 [0.038, 0.055]) and persistence (+0.025 [0.018, 0.033]) increase, and gap stopping falls from 21.75% to 10.30%.
  • On identical prefixes, the raw model closes less often at natural stops (14.0% → 7.8%, −6.25 [−8.14, −4.52]), with first-token stop margins lower by 1.05, 1.06, and 1.25 nats at natural-stop, early, and pre-reuse anchors. OBR shifts the natural-stop margin by −0.37 [−0.50, −0.26] nats (Qwen3-4B: −0.33). After a forced close, EOS probability stays ≥ 0.999998 for every model and anchor role.

Absolute rates are lower for Gemma under its own decoding, so we compare paired differences. One observation is family-specific: fine-tuning on cleaned data lowers Gemma repetition relative to the untuned model, so the untuned-to-cleaned observation of §4.4 applies to Qwen3. Among other structured tasks, JSON tool calling is the closest analogue (a list whose elements must come from a closed set given in the input), and we leave it to future work.

Q1 / W2: constrained decoding

Constrained decoding leaves the supervision-induced gap intact. A grammar mask only removes tokens; at a block boundary both the close and the continue token are grammatical, so the stop margin is unchanged. We verified this with xgrammar on all shared-prefix anchors: under a JSON schema of the target format, both decision tokens are allowed at all 256 (4B) and 255 (8B) reachable anchors, so the natural-stop raw − cleaned margin gap remains −1.98 [−2.20, −1.77] nats at 4B and −1.88 [−2.09, −1.68] at 8B. In generation with vLLM structured outputs (4B, 1,106 records × 2 seeds):

Raw modelRepetitionContext limitOOC blocksRaw − cleaned repetition
No constraint33.6%22.5%26.5%+28.07 [25.77, 30.47]
JSON schema32.2%20.8%27.9%+27.22 [25.00, 29.57]
Schema + candidate enum29.6%18.8%0.0%+24.14 [21.93, 26.18]

Restricting source and target to each record's candidate list removes every out-of-candidate block and closes the triple-F1 gap (−1.14 → −0.06), yet 86% of the repetition gap remains (29.6% vs. 5.5%). Constrained decoding fixes what is written, not when to stop, which is why we locate the defect in learned termination.

Q3 / W3: online deployment without reference stopping points

The intervention point does not require ground truth. Our anchors are complete-block boundaries, where the next token either closes or continues the list, and these can be detected from the partial JSON during decoding; "natural stop" is only a post-hoc label. We therefore applied the closing shift online at every boundary after the fourth block (App. P.3). We use its logit form because the recalibrated control shows that the direction acts at the decision point as a closing shift of about 1.5 nats (App. P.2). β = 1.5 is that measured shift and β = 2 the raw − cleaned natural-stop margin gap; neither was tuned on generation outcomes. Over all 1,106 records (two seeds):

  • Raw model: repetition 33.63% → 17.99% / 15.01% (−15.64 [−17.86, −13.43] / −18.63 [−20.71, −16.50]); context-limit endings 22.51% → 4.70% / 3.16%; pair F1 +1.38 [0.71, 2.00] / +1.65 [1.03, 2.25], with pair precision unchanged. This removes 56–66% of the raw − cleaned repetition gap and 84–92% of the context-limit gap.
  • Cleaned model: pair F1 unchanged (−0.20 [−0.75, 0.38] / +0.09 [−0.45, 0.64]), so the shift can be applied without knowing in advance whether a model has the defect.
  • No truncation: at early anchors, where margins lie far below the decision, no condition produces a close.

We also thank the reviewer for the note on the single pulse. With a larger sample, its effect at natural stops is smaller than the 16-anchor estimate (see our response to Reviewer qBAk), which is why acting at every boundary is the deployable form.

We sincerely thank the reviewer again for these insightful questions, which reflect a deep understanding of how structured generation is deployed in practice. They led us to experiments that substantially strengthen the paper’s generality and practical value. A second model family, Gemma3-4B-it, reproduces the termination degradation and the stop-margin gap. Constrained decoding removes out-of-candidate content but leaves most of the termination gap intact. An online closing shift at every block boundary, which needs no reference stopping points, removes most of the excess repetition and context-limit endings without loss of F1. We hope these results address the reviewer’s concerns, and we would welcome any further discussion or suggestions. If the reviewer finds the additions convincing, we would be grateful if this could be reflected in the final assessment. Thank you again for your encouraging and constructive review.

Dear Reviewer 4eR9,

Thank you again for your valuable comments on our paper. As the author-reviewer discussion period ends today, we would like to kindly check whether our response has addressed your concerns. Thanks again for your time and help in improving the quality of this paper.

Best regards, The authors

Thank the authors for the response. Most of my concerns have been addressed, and I have decided to maintain my original score of weak acceptance.

Reviewer_vSQrOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
2
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Paper summary

In Chinese document-level relation extraction, models generate lists of relations among entities from a specified candidate list. This paper investigates whether training targets containing relations with entities outside this list make models more likely to repeat earlier relations and less likely to end the list. The authors first compare models trained on data that retain or remove these violating relations. Since removing relations also shortens the training targets, they introduce one-for-one relation-block replacement, preserving inputs, relation counts, and termination-label counts while approximately matching token lengths, to distinguish the effects of supervision content from changes in target length. They then analyze how the reuse of earlier relations develops into continuous repetition and compare models’ tendencies to close the list when continuing from the same partial output. They also test whether an activation intervention at that decision point can change the probability of closure. The authors report that these supervision defects can increase repetition and reduce list-closing frequency, while models remain able to produce an end-of-sequence token after a forced list closure.

Critical strengths
  1. The authors include a useful control for the changes in target length caused by data cleaning. Simply removing violating relations shortens the training answers, making it difficult to determine whether changes in repetition arise from cleaner content or shorter targets. The replacement experiment instead exchanges valid relation blocks for violating ones one for one, keeping the inputs, relation counts, and termination-label counts unchanged while approximately matching token lengths. With 15% replacement, repetition increases by 4.19 and 5.07 percentage points across two 4B training seeds relative to their cleaned-data baselines. This provides more direct evidence that the violating relations contribute to repetitive generation.

  2. The authors distinguish between choosing to close the relation list and ending the response after the list is closed. Given the same document and the same unfinished list, models trained on data containing violating relations are less likely to close the list than models trained on cleaned data. Once a valid list ending is supplied, both groups assign a near-certain probability to the end-of-sequence token. This comparison helps identify which part of the stopping process differs between the models.

Critical weaknesses
  1. In my judgment, the paper's central problem is a narrow, constructed case study of limited scientific value. The authors first define relation blocks with out-of-candidate endpoints as a supervision defect and then construct raw, cleaned, and OBR supervision around that definition. The experimental design therefore operationalizes the authors' problem definition rather than providing independent evidence that the problem matters. The paper does not report the defect's prevalence in existing datasets or real annotation workflows, its downstream impact, or an independent rationale for treating this particular inconsistency as an important research problem. The controlled comparisons can establish a local effect, but they do not show that the problem itself is prevalent, consequential, or general enough to justify the paper's broader contribution claim. The evaluation is also limited to one task, the Qwen3 family, a fixed decoding configuration, and full-continuation interventions at 4B only. In my view, this is a carefully instrumented study of a self-defined phenomenon, not a demonstrated answer to a scientifically important question; the authors should either provide independent evidence of prevalence and impact or explicitly frame the work as a controlled case study and narrow its claims.

  2. The paper's mechanistic framing does not establish a scientifically meaningful mechanism. The authors decompose behavior in their constructed setting into increasingly specialized quantities and interventions, but these analyses measure and redescribe the phenomenon they defined rather than identifying a mechanism that is independent of that construction. Changing a local stopping decision or showing that an activation direction is associated with closing behavior supports only local associations; it does not show that the proposed mechanism explains the importance of the self-defined defect or how it would generalize. The problem is therefore not a lack of analyses. Additional diagnostics of the same kind would continue to describe the same constructed phenomenon rather than establish a substantive mechanism. The elaboration creates an impression of depth without changing the nature of the evidence. The paper should state what it means by a mechanism and what evidence would establish one beyond local behavioral associations.

  3. The manuscript is exhaustive but lacks argumentative hierarchy, which makes the central contribution difficult to assess. The underlying claim is simple: out-of-candidate supervision increases repetition and reduces list closure. Yet the paper surrounds it with competing-risk decomposition, exposure/persistence, multiple anchor types, activation directions, random-direction controls, SAE readings, and extensive appendix analyses without establishing which results are primary evidence, which are supporting diagnostics, and which assumptions the conclusions depend on. The resulting completeness is enumerative rather than selective: it demonstrates effort but obscures the question, evidence chain, and limitations. At present, the manuscript reads as a collection of analyses rather than a deliberately prioritized argument. The authors should reorganize the paper around the central claim and a small number of decisive comparisons, move ancillary diagnostics to the appendix, state clearly what is new and what remains uncertain, and remove material that does not advance the argument.

Questions for authors
  1. What evidence establishes sufficient prevalence and practical impact for this problem beyond the authors' own data construction pipeline? Given that the experiments cover only one model family and full-continuation interventions are tested only on the 4B model, what scientific insights do the results establish that are important enough to justify the contribution?

  2. What new insights do the existing analyses provide into why violating training targets leads to sustained repetition? Being able to change whether a model ends the list does not directly explain how violating supervision causes sustained repetition. What evidence connects the two and supports a mechanistic explanation that goes beyond describing the phenomenon?

4 comments

We thank the reviewer for the time spent on our paper and for recognizing the replacement control and the separation of closing from EOS execution as strengths. We first address significance (W1, Q1), then mechanism and organization (W2, W3, Q2).

W1 / Q1: Is this a constructed, narrow problem?

(1) The problem is established in the literature, not constructed by us. Fine-tuning extraction models on LLM-generated annotations is standard practice (UniversalNER, ICLR 2024; GoLLIE, ICLR 2024). LLM annotators are documented to violate exactly the constraint we study: in DocGNRE (Li et al., EMNLP 2023), GPT-3.5 and GPT-4 were instructed to use only the given entity list and still produced triples with entities outside it, which had to be filtered afterwards; GenRES (Jiang et al., NAACL 2024) reports that prompting LLMs with a fixed set of entities or relations induces hallucination. Our raw supervision is the output of such a workflow (teacher LLMs including Qwen3-235B-A22B; App. H), and the constraint is part of the task input itself (each input supplies the candidate list, §3.1). We constructed only the standard filtered set and OBR, the control the reviewer calls useful. In our raw data, 24.94% of target blocks (194,407 / 779,398) violate the constraint, and 97.27% of records contain at least one violation. None are mere case or whitespace variants: 58.0% of violating endpoints are entirely new strings. The violation rate rises from 12.6% in the first tenth of a list to 32.1% in the last tenth, so the teacher keeps inventing relations exactly where a list should end.

(2) The problem is general and consequential. It arises whenever an LLM generates long structured supervision under an input-defined closed set, such as entity lists, schemas, or tool inventories. The consequences are large. At 4B, raw supervision more than doubles mean output length (4,734 → 11,001 tokens), sends 21.06% of responses to the 32k context limit (cleaned: 1.14%), lowers JSON completeness from 98.73% to 78.68%, and lowers pair F1 at every scale (Table 1). Replacing only 15% of blocks, with all termination targets intact, nearly doubles repetition (5.52% → 9.71%). The effect is not specific to Qwen3 or to one decoding setting: Gemma3-4B-it reproduces it (repetition +7.14 [6.20, 8.11]; OBR +2.57 [1.94, 3.21]; lower stop margins at every anchor role; App. P.1), and the raw − cleaned repetition gap remains significant under greedy decoding (+43.9 pts), without presence penalty (+37.2), and at T = 1.0 (+7.0), all intervals excluding zero. If left unaddressed, the defect cannot be removed at inference time: constraining outputs to the candidate list eliminates every out-of-candidate block, yet 86% of the repetition gap remains (see our response to 4eR9).

(3) What the study contributes. Recent top-venue work shows that supervision content shapes behavior beyond item correctness: EOS decisions in multimodal models (Yue et al., ACL 2024), hallucination after learning new facts (Gekhman et al., EMNLP 2024), and broad behavior after narrow fine-tuning (Betley et al., ICML 2025). Repetition, meanwhile, has mainly been studied through decoding and internal copying components (Li et al., NeurIPS 2023; Hiraoka & Inui, NAACL 2025; Yao et al., Findings of ACL 2025). Following that line, we show that a specific, checkable data defect changes when models stop. This yields (i) a criterion for structured-data curation beyond item correctness, namely the stopping behavior a dataset induces; (ii) a diagnosis that separates choosing to close from executing EOS, so practitioners know where to act; and (iii) an effective inference-time remedy. Correcting the closing propensity at every boundary removes 56–66% of the excess repetition and 84–92% of the excess context-limit endings on all 1,106 records, without loss of F1 (App. P.3). This also evaluates the intervention on complete generations, complementing the 8B short readouts (−17.77 / +15.43).

W2, W3 / Q2: mechanism, and organization of the argument

What we mean by mechanism. We use the term in the causal sense: a chain in which each link is supported by an intervention. We do not claim a circuit-level account.

  • Data → repetition: changing only target content (OBR; inputs, block counts, and termination targets fixed) increases repetition.
  • Data → decision: on identical prefixes, raw models close about 32 points less often, while EOS after a forced close stays above 0.99999. The failure lies in choosing to stop, not in executing it.
  • Decision → internal state: a direction estimated only from the cleaned − raw activation difference changes the decision in both directions, exceeds equal-norm random directions, and transfers to an independently trained OBR model. With weights and prefix fixed, this is an intervention, not an association.

How the closing decision connects to sustained repetition. This is what §3.3 and §4.4 establish. Every block boundary is a close-or-continue decision; each continuation is a chance to begin reuse, and once a three-copy pattern forms, recovery is rare. A small per-boundary drop in stopping therefore compounds: changing (g, h) from (0.5, 0.1) to (0.05, 0.08) raises capture probability from 9.09% to 60.32% despite a lower per-episode capture. Empirically, exchanging only the exposure components between raw and cleaned models accounts for +0.127 of the +0.269 capture increase at 4B, and fine-tuning raises Qwen3 repetition (1.29% → 5.52%) while local copy gain falls by 1.23 nats/token. The new experiments close the loop directly. A single-boundary shift changes repetition only through the continuations it stops there (App. P.2), whereas restoring the closing propensity at every boundary, with content generation untouched, removes most of the excess repetition (App. P.3). Changing the stop decision alone is thus sufficient to remove most of the sustained repetition.

Why violating targets weaken closing. In the raw data, violations concentrate at list ends (12.6% → 32.1%), so the model is trained to keep writing exactly where lists should close. Consistent with this, the input-support probe (App. K) shows that raw models still respond to how much support remains, but their overall closing preference is lower by more than 2 nats (−7.02 vs. −4.62). They do not misread what remains; they have learned to stop less.

Organization. The argument rests on three decisive comparisons; everything else supports them:

ClaimPrimary evidenceSupporting (appendix)
Violating content, not length, raises repetitionOBR (Table 1b)dose, label-noise, and input-edit controls
Repetition rises through less stopping and harder recoveryprocess decomposition (§4.4)motif gain
The failure lies in choosing to close, not executing EOSshared prefixes (§4.5)by role and source
An internal direction controls that decisionbidirectional pulse, random controls, OBR transfer (§4.6)layer sweep, SAE

Ancillary diagnostics (motif gain, SAE, input-support probe, full process tables) are already in the appendices, and the main text keeps these four comparisons in this order.

We hope these clarifications show that the paper addresses a recognized problem with consequences in practice, and we thank the reviewer again for the comments.

Dear Reviewer vSQr,

Thank you again for your time and effort in reviewing our paper. As the author-reviewer discussion period ends today, we would like to kindly ask whether our response has addressed your concerns. If there are any remaining questions, please do not hesitate to let us know, and we will do our best to clarify them.

We sincerely look forward to your feedback.

Best regards, The authors

Reviewer_vSQrOpenReview ↗

Response

The response clarifies three points. First, DocGNRE shows that out-of-candidate entities occur in an independent annotation workflow, so the defect is not merely a product of the paper's problem formulation. Second, the Gemma experiment shows that the effect is not confined to the Qwen3 family. Third, the per-boundary intervention shows that a weakened closing tendency contributes to sustained repetition.

My central concern, however, remains unaddressed: whether this defect is prevalent in real model training beyond the authors' own data construction pipeline, and whether its impact is large enough to make it an important research problem. The external evidence comes from a 2023 study that used GPT-3.5 and GPT-4 as annotators and filtered the affected entries before training. This establishes that the defect has occurred. It does not establish that the defect persists with current flagship annotators once standard quality control is applied, or that it enters real training data and causes substantial harm. All evidence on the magnitude of the impact still comes from experiments on the authors' own annotations. The authors further argue that any task requiring long structured supervision over a closed set may face this problem. This argument states a possibility that cannot be tested and does not substitute for empirical evidence of prevalence.

The related work cited in the response shows that supervision content can affect model behavior beyond item-level correctness. That conclusion was established by prior work and is not a contribution of this paper. This paper verifies one specific instance of it in a single task, and its contribution is correspondingly limited in scope and depth. The mechanistic analysis localizes the effect to the list-closing decision, and the interventions support this localization. However, it stops short of a deeper explanation of why violating supervision weakens that decision. The authors' only account, that violations concentrate near the end of lists, is a correlational observation that has not been tested. Localizing the effect without explaining how it arises provides only limited mechanistic insight. On presentation, the response maps claims to evidence, but the revision has not been reorganized accordingly. The abstract still enumerates every analysis and still highlights a 10.94-point reduction in repetition from a single intervention. In the larger evaluation, that effect is −1.52 points, with a 95% confidence interval that includes zero.

In summary, the prevalence and importance of the problem remain unsupported, the contribution amounts to a specific verification of an established finding, and the mechanistic insight is limited. I maintain my rating of 1 (clear rejection).

Reviewer_qBAkOpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper studies how relation-extraction targets containing entities outside an explicit candidate list affect repetition and stopping. Experiments on Qwen3 models combine raw-versus-cleaned supervision with controlled block replacement that preserves inputs, block counts, and termination-target counts. Reuse analysis and shared-prefix tests link the resulting behavior to list-closing decisions. Activation interventions shift these decisions bidirectionally and transfer to a replacement-trained model, although their effects on complete continuations are less consistent.

Critical strengths
  1. The block-replacement experiment addresses an important confound in simple filtering comparisons. It holds inputs and block counts fixed and closely matches mean target length. At 15% replacement, repetition increases by 4.19 and 5.07 percentage points across two 4B training seeds (Table 1), while the generic label-noise control shows little change (Table 9). This provides credible evidence that the specific target defect affects generation beyond merely making training outputs longer.
  2. The shared-prefix design separates the closing decision from differences in generated histories. Raw models close about 32 points less often at natural-stop anchors, yet retain near-certain EOS execution after a forced close. Bidirectional activation effects, equal-norm random controls, and transfer to OBR add evidence that the supervision-related activation difference participates in local closing control (Sections 4.5–4.6).
Critical weaknesses
  1. The content-retention conclusion is stronger than the reported uncertainty supports. For raw restore, early-anchor remaining-pair recall changes by -0.43 points, with a 95% interval of [-3.77, 2.72] (Table 2). This fails the stated criterion requiring the lower bound to be at least -2 points (Appendix E). The significant repetition reduction is also confined to 16 natural-stop anchors; the overall interval includes zero, and OBR transfer does not establish a reduction. These results support local control, but leave reliable repetition reduction with preserved content unresolved.
  2. The close-bias comparison is uninformative in key conditions. Calibration uses almost exclusively early anchors, and selects zero bias for 4B raw restore and both 8B conditions (Appendix E; Table 15). Those controls leave logits unchanged, so they cannot test whether a simple, active increase in closing preference produces similar downstream effects. The random-direction results remain useful, but the comparison with direct closing bias needs better calibration.
Questions for authors
  1. Can you reconcile the content-retention statement in Section 4.6 with the criterion in Appendix E and the intervals in Table 2? Please distinguish outcomes supported by the current intervals from those that remain inconclusive.
  2. Would the intervention conclusions hold with close bias calibrated on a development set balanced across anchor roles, including natural stops, to match the direction’s closing effect? A comparison of repetition and remaining-pair recall under that control would clarify what the activation intervention adds.
3 comments

We sincerely thank Reviewer qBAk for a careful and constructive review. We are grateful that the reviewer finds that the block-replacement experiment "addresses an important confound" and "provides credible evidence that the specific target defect affects generation beyond merely making training outputs longer", that the shared-prefix design "separates the closing decision from differences in generated histories", and that the bidirectional effects, random controls, and OBR transfer "add evidence that the supervision-related activation difference participates in local closing control". We also appreciate the rating of the presentation as clear and easy to follow. Both questions concern the intervention section. We answer them below; new results are in the new Appendix P, and all revisions are marked in blue.

Q1 / W1: content retention in §4.6 vs. Appendix E and Table 2

Thank you for catching this, and we apologize for the confusion. It comes from reporting errors on our side, now corrected in blue:

  1. Unit typo in Appendix E. The criterion was written as "at least −0.02" (a fraction), whereas §3.5 and Table 2 use percentage points. It now reads "at least −2 percentage points".
  2. Sign typos in §4.6. "15.50 [−19.19, −11.97]" now reads "15.50 [11.97, 19.19]", and "5.86 [−13.04, 0.83]" now reads "5.86 [−0.83, 13.04]".
  3. Over-strong summary. The last clause of §4.6 summarized content retention more strongly than our own intervals allow. In the original 64-anchor run, the criterion is met for cleaned reverse (+2.29 [−0.11, 4.59]) but not established for raw restore (−0.43 [−3.77, 2.72]) or OBR transfer (−1.87 [−4.22, 0.33]). The clause now states exactly this.

To separate supported from inconclusive outcomes with tighter intervals, we reran full continuations on all 99 test natural-stop and early anchors with eight draws per condition (3,168 continuations per model; App. P.2):

OutcomeResultStatus
Pulse shifts local closing in both directions4B: −15.50 / +11.17 / +14.67 pts (reverse / restore / transfer); 8B: −17.77 / +15.43; no random direction exceeds 4.49Supported
Content retention (early recall, lower bound ≥ −2)cleaned +0.79 [−0.97, 2.41]; OBR −0.33 [−1.79, 1.07]; raw −0.62 [−2.44, 1.28]Met for cleaned and OBR; raw within ±1 pt but lower bound 0.44 pts short, so inconclusive
No premature closing mid-listearly anchors: 0.0% closes for raw and cleaned under every conditionSupported
Single-pulse reduction of tail repetition at natural stops (raw)−1.52 [−4.92, 1.52] (66 anchors × 8 draws)Not established at this sample size

On the last row: the 16-anchor estimate came from a subset with above-average baseline repetition (21.1% vs. 14.8% over all 66 anchors) and four draws per cell, so it was optimistic. A decomposition explains the rerun effect. The pulse raises immediate closing at the anchor from 22.9% to 41.1%, but repetition among draws that continue is not reduced (19.2% → 22.5%), so a single-boundary pulse changes repetition only through the continuations it stops at that boundary. When the same closing shift is applied at every boundary during decoding (App. P.3), raw-model repetition over all 1,106 records falls from 33.63% to 17.99% (β = 1.5; −15.64 [−17.86, −13.43]) and 15.01% (β = 2; −18.63 [−20.71, −16.50]), context-limit endings fall from 22.51% to 4.70% and 3.16%, and pair F1 rises by 1.38 [0.71, 2.00] and 1.65 [1.03, 2.25] points.

Q2 / W2: close bias calibrated on a role-balanced development set

We agree that the earlier calibration was uninformative: its first 32 development anchors were almost all early anchors, where no bias produces a close, so ties defaulted to β = 0. We recalibrated on all development anchors (4B: 62 natural stop, 31 early, 36 before first reuse; 8B: 58 / 37 / 32), weighting the three roles equally, on β ∈ {0, 0.25, …, 4}. Re-running the baseline with the original seeds reproduces the published readouts anchor by anchor (127/127 at 4B, 128/128 at 8B), so the new bias pairs directly with the existing results (App. P.2, Table 35). Changes in next-event close frequency on held-out test anchors (pp):

ModelNew βDirectionCalibrated biasDirection − bias
4B cleaned reverse−1.25−15.50−15.70+0.20 [−1.62, 2.18]
4B raw restore+1.5+11.17+11.12+0.05 [−1.97, 2.08]
4B OBR transfer+1+14.67+12.25+2.41 [0.40, 4.68]
8B cleaned reverse−1.25−17.77−17.72−0.05 [−2.07, 1.92]
8B raw restore+1.5+15.43+16.85−1.42 [−3.28, 0.35]

All five models now receive an active, frequency-matched bias. Downstream, direction and bias do not differ significantly (raw natural-stop tail repetition: direction − bias = +2.27 [−1.14, 6.44]; early recall: −0.49 [−1.75, 0.73]). Measured at natural stops, the direction moves the stop margin by +1.52 nats (raw), −1.46 (cleaned), and +0.99 (OBR) at 4B, and by +1.54 / −1.43 at 8B, essentially the independently calibrated biases.

The conclusions about local closing control therefore hold under the calibrated control, and the comparison clarifies what the activation intervention adds: not a larger downstream effect, but an identification. A direction estimated only from the cleaned − raw activation difference acts at the decision point as a closing-propensity shift of about 1.5 nats, in both directions, at both scales, and transfers to the independently trained OBR model, while equal-norm random directions produce nothing comparable. The supervision difference is thus written into the model as a shift of the close-or-continue decision, and its logit form is the deployable version evaluated on all 1,106 records in App. P.3.

We sincerely thank the reviewer again for this expert and detailed feedback. Both questions went to the core of how the intervention evidence should be read, and they have clearly improved the paper. In response, we corrected the reporting errors in §4.6 and Appendix E. We now separate outcomes our intervals support from those that remain inconclusive, using a larger rerun of the full continuations. We also recalibrated the close bias on a role-balanced development set, so that it is now an active, frequency-matched control at both scales. Finally, we added an every-boundary experiment showing the downstream effect of the closing shift on all 1,106 records. We hope these revisions address the reviewer’s concerns, and we would welcome any further questions or suggestions during the discussion period. If the reviewer finds the revisions satisfactory, we would be grateful if this could be reflected in the final assessment. Thank you again for your time and constructive engagement with our work.

Dear Reviewer qBAk,

Thank you again for your valuable comments on our paper. As the author-reviewer discussion period ends today, we would like to kindly check whether our response has addressed your concerns. Thanks again for your time and help in improving the quality of this paper.

Best regards, The authors

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

The paper studies how relation-extraction targets containing entities outside an explicit candidate list affect repetition and stopping. Experiments on Qwen3 models combine raw-versus-cleaned supervision with controlled block replacement that preserves inputs, block counts, and termination-target counts. Reuse analysis and shared-prefix tests link the resulting behavior to list-closing decisions. Activation interventions shift these decisions bidirectionally and transfer to a replacement-trained model, although their effects on complete continuations are less consistent.

Critical strengths
  1. The block-replacement experiment addresses an important confound in simple filtering comparisons. It holds inputs and block counts fixed and closely matches mean target length. At 15% replacement, repetition increases by 4.19 and 5.07 percentage points across two 4B training seeds (Table 1), while the generic label-noise control shows little change (Table 9). This provides credible evidence that the specific target defect affects generation beyond merely making training outputs longer.
  2. The shared-prefix design separates the closing decision from differences in generated histories. Raw models close about 32 points less often at natural-stop anchors, yet retain near-certain EOS execution after a forced close. Bidirectional activation effects, equal-norm random controls, and transfer to OBR add evidence that the supervision-related activation difference participates in local closing control (Sections 4.5–4.6).
Critical weaknesses
  1. The content-retention conclusion is stronger than the reported uncertainty supports. For raw restore, early-anchor remaining-pair recall changes by -0.43 points, with a 95% interval of [-3.77, 2.72] (Table 2). This fails the stated criterion requiring the lower bound to be at least -2 points (Appendix E). The significant repetition reduction is also confined to 16 natural-stop anchors; the overall interval includes zero, and OBR transfer does not establish a reduction. These results support local control, but leave reliable repetition reduction with preserved content unresolved.
  2. The close-bias comparison is uninformative in key conditions. Calibration uses almost exclusively early anchors, and selects zero bias for 4B raw restore and both 8B conditions (Appendix E; Table 15). Those controls leave logits unchanged, so they cannot test whether a simple, active increase in closing preference produces similar downstream effects. The random-direction results remain useful, but the comparison with direct closing bias needs better calibration.
Questions for authors
  1. Can you reconcile the content-retention statement in Section 4.6 with the criterion in Appendix E and the intervals in Table 2? Please distinguish outcomes supported by the current intervals from those that remain inconclusive.
  2. Would the intervention conclusions hold with close bias calibrated on a development set balanced across anchor roles, including natural stops, to match the direction’s closing effect? A comparison of repetition and remaining-pair recall under that control would clarify what the activation intervention adds.
3 comments

We sincerely thank Reviewer qBAk for a careful and constructive review. We are grateful that the reviewer finds that the block-replacement experiment "addresses an important confound" and "provides credible evidence that the specific target defect affects generation beyond merely making training outputs longer", that the shared-prefix design "separates the closing decision from differences in generated histories", and that the bidirectional effects, random controls, and OBR transfer "add evidence that the supervision-related activation difference participates in local closing control". We also appreciate the rating of the presentation as clear and easy to follow. Both questions concern the intervention section. We answer them below; new results are in the new Appendix P, and all revisions are marked in blue.

Q1 / W1: content retention in §4.6 vs. Appendix E and Table 2

Thank you for catching this, and we apologize for the confusion. It comes from reporting errors on our side, now corrected in blue:

  1. Unit typo in Appendix E. The criterion was written as "at least −0.02" (a fraction), whereas §3.5 and Table 2 use percentage points. It now reads "at least −2 percentage points".
  2. Sign typos in §4.6. "15.50 [−19.19, −11.97]" now reads "15.50 [11.97, 19.19]", and "5.86 [−13.04, 0.83]" now reads "5.86 [−0.83, 13.04]".
  3. Over-strong summary. The last clause of §4.6 summarized content retention more strongly than our own intervals allow. In the original 64-anchor run, the criterion is met for cleaned reverse (+2.29 [−0.11, 4.59]) but not established for raw restore (−0.43 [−3.77, 2.72]) or OBR transfer (−1.87 [−4.22, 0.33]). The clause now states exactly this.

To separate supported from inconclusive outcomes with tighter intervals, we reran full continuations on all 99 test natural-stop and early anchors with eight draws per condition (3,168 continuations per model; App. P.2):

OutcomeResultStatus
Pulse shifts local closing in both directions4B: −15.50 / +11.17 / +14.67 pts (reverse / restore / transfer); 8B: −17.77 / +15.43; no random direction exceeds 4.49Supported
Content retention (early recall, lower bound ≥ −2)cleaned +0.79 [−0.97, 2.41]; OBR −0.33 [−1.79, 1.07]; raw −0.62 [−2.44, 1.28]Met for cleaned and OBR; raw within ±1 pt but lower bound 0.44 pts short, so inconclusive
No premature closing mid-listearly anchors: 0.0% closes for raw and cleaned under every conditionSupported
Single-pulse reduction of tail repetition at natural stops (raw)−1.52 [−4.92, 1.52] (66 anchors × 8 draws)Not established at this sample size

On the last row: the 16-anchor estimate came from a subset with above-average baseline repetition (21.1% vs. 14.8% over all 66 anchors) and four draws per cell, so it was optimistic. A decomposition explains the rerun effect. The pulse raises immediate closing at the anchor from 22.9% to 41.1%, but repetition among draws that continue is not reduced (19.2% → 22.5%), so a single-boundary pulse changes repetition only through the continuations it stops at that boundary. When the same closing shift is applied at every boundary during decoding (App. P.3), raw-model repetition over all 1,106 records falls from 33.63% to 17.99% (β = 1.5; −15.64 [−17.86, −13.43]) and 15.01% (β = 2; −18.63 [−20.71, −16.50]), context-limit endings fall from 22.51% to 4.70% and 3.16%, and pair F1 rises by 1.38 [0.71, 2.00] and 1.65 [1.03, 2.25] points.

Q2 / W2: close bias calibrated on a role-balanced development set

We agree that the earlier calibration was uninformative: its first 32 development anchors were almost all early anchors, where no bias produces a close, so ties defaulted to β = 0. We recalibrated on all development anchors (4B: 62 natural stop, 31 early, 36 before first reuse; 8B: 58 / 37 / 32), weighting the three roles equally, on β ∈ {0, 0.25, …, 4}. Re-running the baseline with the original seeds reproduces the published readouts anchor by anchor (127/127 at 4B, 128/128 at 8B), so the new bias pairs directly with the existing results (App. P.2, Table 35). Changes in next-event close frequency on held-out test anchors (pp):

ModelNew βDirectionCalibrated biasDirection − bias
4B cleaned reverse−1.25−15.50−15.70+0.20 [−1.62, 2.18]
4B raw restore+1.5+11.17+11.12+0.05 [−1.97, 2.08]
4B OBR transfer+1+14.67+12.25+2.41 [0.40, 4.68]
8B cleaned reverse−1.25−17.77−17.72−0.05 [−2.07, 1.92]
8B raw restore+1.5+15.43+16.85−1.42 [−3.28, 0.35]

All five models now receive an active, frequency-matched bias. Downstream, direction and bias do not differ significantly (raw natural-stop tail repetition: direction − bias = +2.27 [−1.14, 6.44]; early recall: −0.49 [−1.75, 0.73]). Measured at natural stops, the direction moves the stop margin by +1.52 nats (raw), −1.46 (cleaned), and +0.99 (OBR) at 4B, and by +1.54 / −1.43 at 8B, essentially the independently calibrated biases.

The conclusions about local closing control therefore hold under the calibrated control, and the comparison clarifies what the activation intervention adds: not a larger downstream effect, but an identification. A direction estimated only from the cleaned − raw activation difference acts at the decision point as a closing-propensity shift of about 1.5 nats, in both directions, at both scales, and transfers to the independently trained OBR model, while equal-norm random directions produce nothing comparable. The supervision difference is thus written into the model as a shift of the close-or-continue decision, and its logit form is the deployable version evaluated on all 1,106 records in App. P.3.

We sincerely thank the reviewer again for this expert and detailed feedback. Both questions went to the core of how the intervention evidence should be read, and they have clearly improved the paper. In response, we corrected the reporting errors in §4.6 and Appendix E. We now separate outcomes our intervals support from those that remain inconclusive, using a larger rerun of the full continuations. We also recalibrated the close bias on a role-balanced development set, so that it is now an active, frequency-matched control at both scales. Finally, we added an every-boundary experiment showing the downstream effect of the closing shift on all 1,106 records. We hope these revisions address the reviewer’s concerns, and we would welcome any further questions or suggestions during the discussion period. If the reviewer finds the revisions satisfactory, we would be grateful if this could be reflected in the final assessment. Thank you again for your time and constructive engagement with our work.

Dear Reviewer qBAk,

Thank you again for your valuable comments on our paper. As the author-reviewer discussion period ends today, we would like to kindly check whether our response has addressed your concerns. Thanks again for your time and help in improving the quality of this paper.

Best regards, The authors

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

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