acceptodds
Under review as a conference paper at ICLR 2027

Poisoning Leaves a Trace: Post-Hoc Auditing and Recovery for Text Summarization

Abstract

Training-time data poisoning can induce persistent changes in abstractive summarization on ordinary inputs while preserving fluent outputs and conventional quality metrics, making compromise difficult to detect in open-ended generation. We study whether such trigger-free poisoning leaves diagnostic traces that can be exploited after fine-tuning. We identify two complementary signatures under different defender-access settings. When the fine-tuning corpus is available, the influence structure exploited by influence-targeted poisoning remains partially observable after fine-tuning; we use this signal to localize suspicious samples, validate their behavioral inconsistency, and selectively unlearn their effect. When the target model's fine-tuning data are unavailable, poisoned summarizers exhibit amplified sensitivity to controlled input perturbations. We capture this behavior through Sensitivity to Adversarial Perturbations (SAP), which measures perturbation-induced source-content exclusion for model auditing. We evaluate sentiment, toxicity, factual-distortion, and representational-bias poisoning, together with mixed-influence and mixed-objective attacks and position-shifted probing that stress the assumptions of the proposed defenses. Across nine architectures and six benchmark datasets, we detect poisoning under both defender-access settings while preserving summarization utility, and targeted unlearning achieves 84.6% average behavioral recovery at 10% contamination across poisoning objectives. These results show that trigger-free poisoning leaves measurable traces in training influence and model behavior, enabling post-hoc auditing and, when fine-tuning data are available, targeted recovery without full retraining.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Data poisoning, abstractive summarization, machine unlearning, influence-based detection, model auditing, adversarial sensitivity, trigger-free poisoning

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

This paper discusses trigger-free data poisoning of abstractive summarization: an attacker rewrites the reference summaries of some fine-tuning examples so the model acquires a persistent behavior — inverted sentiment, injected toxicity, factual distortion, or demographic skew — that shows up on ordinary inputs with no inference-time trigger. Because the output space is open-ended and fluency and ROUGE survive, this is hard to spot.

The paper proposes two post-hoc defenses matched to two defender-access settings.

  • Defense-1 assumes the fine-tuning corpus is available: rank examples by DataInf influence, take the top K% as candidates, filter them with four behavioral checks (sentiment disagreement, toxicity, factual inconsistency, representational disparity) against clean-calibrated thresholds, then gradient-ascent unlearn what survives, stopping when clean utility degrades past a tolerance.
  • Defense-2 assumes only the checkpoint: probe it with character-, word-, sentence-, and document-level perturbations from prior summarization robustness work, measure how much more source content gets excluded from the summary under perturbation than without it, and call that Sensitivity to Adversarial Perturbations. A model is flagged when SAP exceeds a threshold calibrated from verified-clean reference checkpoints of the same architecture.

Evaluation spans 9 models (encoder-decoder and decoder-only), 6 summarization datasets, 4 poisoning objectives including 2 the paper introduces, and 7 contamination rates from 0.1% to 10%. There are also three defense-aware stress tests — mixed-influence poisoning, mixed-objective poisoning, and position-shifted probing — plus clean-model fragility controls. Headline numbers: 84.6% average behavioral recovery at 10% contamination against SISA's 76.1% and Antidote's 73.7%, and SAP at 0.93 AUROC against CLIBE's 0.84 and perplexity sensitivity's 0.71.

Critical strengths

The clean-model fragility controls are the right experiment and a lot of detection papers skip them. The obvious objection to "poisoned models are more perturbation-sensitive" is that any poorly-conditioned model is more perturbation-sensitive, so the signal might be detecting training pathology rather than poisoning. Section 6.2.3 and Figure 2 run undertrained, overfit, and reduced-data clean checkpoints through the same probes at the same architecture-specific thresholds and show the poisoned models separating from all three. That is what makes SAP a candidate poisoning signal rather than a fragility meter, and it is the reason I take the Defense-2 idea seriously even though I don't think the evaluation supports the numbers.

The breadth and the willingness to attack the assumptions are good. 9 architectures across 2 families, 6 datasets, 7 contamination rates, 2 new poisoning objectives, and 3 stress tests explicitly designed to weaken the signals the defenses depend on. The position-shifted probing result — AUROC falling from 0.94 on Lead-3 to 0.92 on Middle-3 and 0.89 on Tail-3 while mean SAP stays elevated — is the kind of self-directed attack that builds confidence, and Section 6.1.3's influence-region ablation (85.52% recovery from unlearning a high-influence poisoned subset against 58.2% random and 37.1% low-influence, with exact retraining as the 100% oracle) is a real mechanism analysis rather than another table of scores.

Critical weaknesses

My main problem is that every statistical claim about Defense-2 is computed against six negative examples. Appendix 9.2 states that for each architecture the clean-reference distribution comes from six verified-clean checkpoints, one per dataset, and that the threshold is τ_m = Q_0.95 of that distribution with "a target false-positive rate of 5%." An empirical 95th percentile of 6 observations sits between the 5-th and 6-th order statistics — it is essentially the maximum of 6 numbers, and it carries no 5% guarantee in any non-parametric sense.

  • Everything downstream inherits this: the F1 and precision figures reported "at the architecture-specific clean-calibrated threshold," and the AUC, AUPR and TPR-at-5%-FPR numbers in Tables 3, 4 and 15, which Appendix 9.10.2 says are computed from clean and poisoned score distributions over the contamination sweep. With six negatives the standard error on an AUC is on the order of 0.1, which means Table 4's spread from 0.88 to 0.95 across nine models and six datasets is indistinguishable from noise, and TPR at 5% FPR is not estimable at all — 5% of six is 0.3, so the quantity reduces to "TPR at a threshold above the maximum clean score." No confidence intervals appear anywhere in the paper. The fix is cheap, since clean checkpoints are the easy thing to produce, but I don't see any of the Defense-2 operating-point numbers.
  • Compounding this, those six references are obtained by "fine-tuning the architecture on each of the six clean summarization datasets using the same training configuration as the corresponding poisoned models." That is a stronger assumption than the model-only threat model admits. Defense-2 exists because the defender has a suspicious checkpoint and no fine-tuning data, yet calibration requires clean fine-tuning data for the same task & architecture & training recipe — and a way to know those references are clean, which is the very property under audit. If a defender can produce a verified-clean fine-tuned model on the target task, the auditing problem is much less pressing than the paper's framing suggests.

My second concern is that Defense-1's localization signal is the attacker's own selection criterion, and the natural adaptive attack against it is never run. Section 5 says the paper follows influence-targeted poisoning in which examples are drawn from a high-influence region, and Defense-1 then ranks by influence and keeps the top K%. Even under that favorable match the candidate set captures only 76–84% of the poisoned examples at 10% contamination.

  • The mixed-influence stress test spreads the budget evenly across 1/3 of the influence ranking and recall falls to 73.8%, which is a useful check, but the obvious adaptive attack is to draw the poison entirely from the low-influence region, and that experiment is absent. Section 6.1.3 is what makes the omission conspicuous: unlearning a low-influence poisoned subset recovers only 37.1% of the behavior. If an attacker confines poisoning to low influence, the paper's own numbers suggest localization would find little and unlearning what it finds would undo little. The authors may argue "low-influence examples might be weak attack vehicles", but that is an empirical claim about attack success as a function of the influence percentile the poison is drawn from, and it is exactly the sweep the paper needs but lacks.
Questions for authors

Please recalibrate SAP with substantially more clean reference checkpoints — varying seed, data order, and hyper-parameters within each architecture-dataset cell, which is cheap — and report the measured false-positive rate on held-out clean models rather than a target. With a proper negative set, what happens to the AUC spread in Table 4 and to TPR at 5% FPR? Bootstrap intervals on those numbers would settle whether the cross-model and cross-dataset differences mean anything.

On Defense-1, could you run the attack with poison drawn from the low-influence region and report both attack success and defense recovery, alongside a sweep over the influence percentile the attacker samples from? That single figure would turn the mixed-influence stress test into a real adaptive-attack evaluation, and Section 6.1.3 suggests you have most of the machinery already.

Is the clean reference for a given target drawn from the same dataset as the target, or pooled across all six? SAP appears to vary by dataset, so pooling a single per-architecture threshold over six datasets inflates the reference spread in a way that should be characterized. And more fundamentally, how should a real defender obtain "verified-clean" references in the model-only setting? If the honest answer is that Defense-2 requires an organization that already trains its own clean models on the task, I'd rather see that stated plainly than left to the appendix.

3 comments
AuthorsOpenReview ↗

Response to Reviewer fFqx

We thank the reviewer for the careful assessment and constructive suggestions. We appreciate the recognition of our clean-model fragility controls, broad experimental evaluation, and defense-aware stress tests. We address the concerns about statistical reliability, clean-reference calibration, and adaptive low-influence poisoning below.

Statistical Reliability and Clean-Reference Calibration:

  1. Clean references: For each architecture-dataset pair, we trained clean checkpoints using 18 hyperparameter configurations, varying the learning rate (1e-5, 2e-5, 5e-5), batch size (8, 16), and number of training epochs (2, 3, 5), yielding 108 clean checkpoints per architecture (972 total), with matching poisoned checkpoints. SAP was computed individually for every checkpoint, the six values reported per architecture are dataset-level averages. For calibration, we use 54 clean checkpoints per architecture to estimate the empirical 95th-percentile threshold τₘ, reserving the remaining 54 for held-out evaluation. Across 486 held-out clean checkpoints, the observed FPR is 4.73% (23/486), compared with the nominal 5% target.

  2. SAP calibration: Thresholds are set per architecture, not per dataset. Clean-reference SAP scores from all six datasets are pooled into a single distribution, and its 95th percentile defines τₘ, which is applied to targets from every dataset. Clean SAP varies only modestly across datasets. For Qwen, it ranges from 3.5 to 3.8, below the calibrated threshold τ_Qwen = 4.45 (Section-6.2.1), so pooling does not place any dataset’s clean models near the threshold. We will report per-dataset clean SAP distributions and false-positive rates for all architectures in the final version.

  3. Statistical reliability: On Qwen-MultiNews (Table-3), SAP achieves AUROC 0.93 (95% CI: 0.80 - 0.98), AUPRC 0.91, F1 0.86, and TPR@5% FPR 0.81 (0.75 - 0.86). Across all nine architectures and six datasets, contamination-stratified AUROCs are 0.82 (0.68 - 0.91) at 0.1-0.25%, 0.94 (0.82 - 0.98) at 0.5 - 1%, and 0.99 (0.93 - 1.00) at 2.5 - 10%, confirming reduced separability at very low contamination. Most differences between architectures and datasets in Table-4 fall within overlapping confidence intervals. We will include checkpoint-level intervals and the held-out calibration protocol in the final version.

  4. Obtaining verified-clean references: Defense-2 assumes the defender can fine-tune the same public base architecture on trusted public task data. Such references are clean by construction, and they do not require the suspicious model’s training data, recipe, or poisoning objective. They cannot reveal whether a third-party checkpoint is poisoned, which is the setting Defense-2 addresses. This fits organizations that deploy or audit third-party fine-tuned models but cannot inspect how those models were trained. We will state this assumption explicitly in Section-3.

Adaptive low-influence poisoning and influence sweep:

Defense-1 deliberately uses the same signal as the attack. Influence-based poisoning works because high-influence samples drive model behavior, so evading localization forces the attacker to give up that leverage.

Beyond the influence-region analysis in Section-6.1.3, we evaluated the adaptive attack in which all poisoned samples are drawn from the middle and low-influence region. At 10% contamination, this attack success falls from 81.2-90% under standard high-influence poisoning to 44-57% for middle-influence and only 17-19.3% for low-influence. Confining poison to low-influence samples therefore weakens the attack itself, so evading influence-based localization comes at the cost of attack effectiveness.

As Defense-1 measures influence on the poisoned model, poisoned samples tend to rise in the ranking. The Top-20% set captures 49% of middle-influence and 28% of low-influence poison. Defense-1 recovers 80.2% of the behavior under middle-influence poisoning, close to the standard setting (84.6%), and 52% under low-influence poisoning, where the attack induces only a small shift to begin with. Defense-1 therefore remains effective where the adaptive attack remains effective. The 37.1% in Section-6.1.3 is consistent with this result. It comes from unlearning a low-influence subset within the poisoned model, whose samples contribute little to the learned behavior. We will add these results to Section-6.1.3.

Reviewer_fFqxOpenReview ↗

Response to rebuttal

Thanks for your new results and clarification. I decide to maintain my score.

AuthorsOpenReview ↗

Response to Reviewer fFqx

Thank you for reviewing our response and for your constructive feedback throughout. We have uploaded a revised manuscript that incorporates the changes discussed. Section 5 describes the SAP calibration with 108 verified-clean checkpoints per architecture and the measured held-out false-positive rate (4.73%). SAP detection is now reported separately at each contamination rate in Table 10 (Appendix 9.10.2). The clean-reference assumption is stated explicitly in Sections 3 and 4.2, and the low- and middle-influence poisoning results, including attack success and recovery, are reported in Section 6.1.5. We hope these revisions address your concerns.

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

The paper studies post-hoc defenses against trigger-free, training-time data poisoning in abstractive summarization, under two different threat models.

  1. Dataset-access setting. Defender ranks training samples by its influence and screens the top 20% with four behavior-specific validators. Flagged samples are then removed from the trained model by gradient-ascent unlearning.

  2. Model-only setting. Defender introduces SAP, which measures how much controlled input perturbation increase the exclusion of targeted source content. A model is flagged when its SAP exceeds a threshold calibrated on clean reference models of the same architecture.

The experiment cover nine models, six datasets and four poisoning objectives.

Critical strengths
  1. The problem and setting are interesting and practically relevant. The division of threat model by defender access (dataset vs model only) is a sensible framing.

  2. The paper is well written and easy to follow. The threat model and both defenses are clearly described.

  3. The empirical evaluation is broad: nine models, six datasets, and four poisoning objectives.

Critical weaknesses
  1. Both the defenses are built around a single attack. Defense-1's localization assumes poison sits in high-influence samples, which is exactly how Thota & Nilzadeh (2024) select their poison, and Defense-2's probe come from the same work. The defenses are therefore evaluated on the attack they were designed around. The mixed-influence stress test helps only partly, since a third of the poison still sits in the highest-influence region. The authors should evaluate other poisoning strategies, such as randomly selected poison, content injection and over-refusal [1], low-rate misinformation poisoning [2], and summarization-specific model spinning [3], to show the defenses generalize beyond this one attack.

[1] Shu, Manli, et al. "On the exploitability of instruction tuning." Advances in Neural Information Processing Systems 36 (2023),

[2] Alber, Daniel Alexander, et al. "Medical large language models are vulnerable to data-poisoning attacks." Nature Medicine 31.2 (2025),

[3] Bagdasaryan, Eugene, and Vitaly Shmatikov. "Spinning language models: Risks of propaganda-as-a-service and countermeasures." 2022 IEEE Symposium on Security and Privacy (SP).

 

  1. The paper does not explain why higher perturbation sensitivity indicates poisoning. Section 4.2 states this as a hypothesis, and the support for it is purely empirical. The clean-model fragility controls in Section 6.2.3 help rule out some alternative explanations. However, there is no mechanism or analysis of why poisoning sentiment, toxicity, facts or bias should increase source-content exclusion under unrelated perturbations.

 

  1. Defense-1 requires the attack objective to be in a predefined set. A sample is flagged only if one of four objective-specific validators fires. The defender does not need to know which of the four the attacker used, but any objective outside the set (e.g., product promotion or political slant) would pass validation undetected. This effectively turns the open-ended generation problem back into detection with fixed classifiers, which is the setting the paper motivates itself as being different from.

 

  1. The scope is limited to summarization. Both the attack and the quantity SAP measures are specific to summarization. The paper does not discuss whether the influence trace or the sensitivity trace would carry over to other open-ended generation tasks.

 

  1. There is no evaluation against truly adaptive attackers. The stress tests in Section 4.3 change the attack configuration, but they are not adaptive in the sense of an attacker who knows the defense and optimizes to evade it. The authors defer stronger adaptive attacks to future work. I believe evaluating at least some of these is necessary to validate the hypotheses behind both defenses.
Questions for authors

Please refer to weaknesses.

2 comments
AuthorsOpenReview ↗

Response to reviewer Zrjt

We thank the reviewer for recognizing the practical relevance of the problem, and the breadth of our evaluation. We address each concern below.

Generalization beyond influence-targeted poisoning:

Beyond standard attack, we evaluate poison selected from the middle- and low-influence regions (attack success rates: 44- 57% for middle-influence and 17-19.3% for low-influence poisoning). Defense-1 recovers 80.2%, 52%, and 89.2% in these settings, with the lowest value where the attack itself is weak. SAP’s probes are inference-time perturbations of benign documents and do not depend on how poison is selected.

  1. Over-refusal poisoning: Following Shu et al., we evaluated over-refusal poisoning, replacing reference summaries with refusal-style responses, at 0.5-10% contamination rates across different architectures. Using GPT-5-Mini as a refusal validator, Defense-1 recovers 80.4-87.1% of the induced behavior, indicating that the pipeline extends beyond the four objectives.
  2. Relation to other cited attacks: Toxicity injection and factual distortion insert unsupported content, related to but distinct from the brand-name injection of Shu et al. Factual distortion is evaluated down to 0.1% contamination through fine-tuning instead of pretraining, as in Alber et al. Model spinning (Bagdasaryan et al.) is trigger-activated backdoor and falls outside our trigger-free threat model. Sentiment inversion and representational bias are its closest trigger-free counterparts. We will add the over-refusal results and discuss the remaining attack families in the final version.

Mechanism behind SAP:

Our reasoning builds on Fares et al. (https://ieeexplore.ieee.org/stamp/stamp.jsp?tp=&arnumber=10657217), who showed that poisoned classifiers are more sensitive to adversarial perturbations than clean ones, even when those perturbations are generated independently of the poisoning.

In summarization, source-content exclusion is an established adversarial attack (https://aclanthology.org/2024.findings-emnlp.804/), so SAP tests poisoned summarizers are likewise more vulnerable than clean ones. Since Fares et al.’s explanation relies on trigger-induced backdoors, absent in our setting, we propose a different mechanism: all four objectives train on summaries containing content unsupported by the source, which we hypothesize weakens the model’s reliance on the source and manifests as increased source-content exclusion under perturbation.

Consistent with this, SAP increases with contamination for all four objectives (Figure-4), while undertrained, overfit, and reduced-data clean models show no comparable increase (Section-6.2.3). We will add this reasoning to Section 4.2.

Dependence on predefined validators:

We agree that Defense-1 can only validate objectives covered by its criteria. This dependence is limited to the validation stage, localization and unlearning are objective-agnostic. The validators do not classify text for fixed attributes, each compares a reference summary with its own source, measuring source-relative deviations (Appendix-9.1). New criteria can be added without changing other stages, as the over-refusal validator above shows. Defense-2 requires no knowledge of the objective. We will state explicitly in Section-7.

Scope Beyond Abstractive Summarization:

Our study intentionally focuses on summarization, but we expect both traces to carry over in part. Influence trace: Influence estimation and unlearning are task-agnostic (DataInf was developed for LoRA-tuned LLMs and diffusion models), and only the validators are summarization-specific. Sensitivity trace: SAP measures whether a model drops source content under perturbation, so it applies to source-grounded tasks such as retrieval-augmented QA, document-grounded dialogue, and translation. Tasks without a source would need a different measure. We will explain them clearly in Section-7.

Adaptive attacks against both defenses:

We agree that our original stress tests are defense-aware rather than adaptive. We therefore evaluated an attacker who avoids high-influence samples, drawing all poison from the middle- or low-influence regions, and measured both defenses on the resulting models.

At 10% contamination, attack success falls from 81.2-90% (high-influence) to 44-57% (middle) and 17-19.3% (low). Defense-1 still recovers 80.2% under middle-influence, close to the standard (84.6%), and 52% under low-influence poisoning, where the attack induces a minor shift. We also measured SAP on these models. Under middle-influence poisoning with Qwen, SAP ranges from 3.4-5.7 (τ_Qwen = 4.45), partly exceeding the threshold, and from 1.8 to 4.5 under low-influence poisoning, largely below it.

Overall, avoiding high-influence samples weakens the attack, while Defense-1 still recovers and SAP detects the stronger poisoning more reliably. We will add these results to Section 6.1.3 and discuss adaptive attacks.

AuthorsOpenReview ↗

Response to reviewer Zrjt

Thank you again for your detailed review and constructive feedback. We have uploaded a revised manuscript incorporating the changes discussed in our response. Section 6.1.6 now evaluates over-refusal poisoning, and Section 6.1.5 reports middle- and low-influence poisoning with attack success, Defense-1 recovery, and SAP behavior. Section 4.2 describes the proposed mechanism behind SAP. Section 4.1 and the Limitations clarify that only the behavioral-validation stage is objective-specific. We also describe our stress tests as defense-aware, and defer attacks that directly optimize against both defenses to future work. We hope these revisions address your concerns.

Reviewer_aGQrOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
3(+1)
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Paper summary

This paper studies post-hoc auditing and recovery for trigger-free data poisoning in abstractive summarization. It proposes two defenses under different access assumptions. With access to the fine-tuning corpus, Defense-1 uses DataInf-based influence ranking, behavioral validation, and gradient-ascent unlearning to identify suspicious examples and mitigate their effects. Without access to that corpus, Defense-2 measures perturbation-induced source-content exclusion through a summarization-specific SAP score, calibrated against clean reference checkpoints. The paper evaluates four poisoning objectives across nine models and six datasets. It reports improved behavioral recovery and poisoned-model detection, together with limited summarization-utility degradation. Additional experiments examine mixed-influence and mixed-objective poisoning, position-shifted probes, and clean models with different forms of training-related fragility.

Critical strengths

1.Trigger-free behavioral poisoning in summarization is a meaningful problem because fluent outputs and conventional quality metrics may conceal behavioral changes. Separating dataset-access recovery from model-only auditing makes the proposed framework practically relevant. The mixed-influence, position-shifted, and clean-fragility controls are useful attempts to test explanations beyond the standard attack configuration. 2.At 10% contamination, Table 1 reports average behavioral recovery of 84.6%, compared with 76.1% for SISA, the strongest listed recovery baseline. Table 3 reports AUROC of 0.93 and TPR@5% FPR of 0.81 for SAP, compared with 0.84 and 0.68 for CLIBE. Table 9 additionally reports small ROUGE-Avg changes relative to the clean reference in the Qwen–MultiNews setting. These results motivate further investigation of the proposed signals.

Critical weaknesses

1.Table 1 reports 84.6% average recovery at 10% contamination, whereas Table 2 reports 90.5% for the standard setting, also described as averaged across models and datasets. The relationship between these settings is not explained. In addition, the default candidate set is Top-20%, for which Table 11 reports 78.4% average poisoned-sample coverage, while Table 2 reports 90.4% standard-setting recall. If these results use matching configurations and aggregation weights, final recall cannot exceed candidate coverage; otherwise, the differing configurations should be explicitly identified. Methodologically, influence estimation, gradient-based unlearning, and sensitivity-based poisoned-model detection build on established ideas [1–3]. The paper acknowledges these connections, and the summarization-specific adaptation is potentially useful. However, the candidate-size ablation reports coverage without establishing the recovery–cost trade-off against behavioral validation over the full corpus followed by identical unlearning. Reporting this control, together with absolute clean, poisoned, and recovered behavioral severities, would clarify both the contribution of influence ranking and the practical meaning of normalized recovery.

Questions for authors
  1. What happens when the same behavioral validators are applied to the full corpus, followed by the same unlearning procedure? 2.Can the authors provide detection results separately for each contamination rate? This would clarify the pooled results in Table 10 given the below-threshold mean SAP values at low contamination in Figure 4.
3 comments
AuthorsOpenReview ↗

Response to reviewer aGQr

We thank the reviewer for constructive feedback, and recognizing the practical relevance of separating dataset-access recovery from model-only auditing, as well as our fragility and stress-test controls. We address each concern below.

Recovery and Recall Inconsistencies:

We thank the reviewer for identifying this. The Standard row of Table-2 included results from contamination rates up to 20%, instead of 10% as in Table-1. Correcting this gives 84.6% recovery, consistent with Table-1. We also clarify that recall is measured over all ground-truth poisoned samples and therefore cannot exceed candidate coverage. The corrected results at 10% contamination, averaged across nine models and six datasets, are:

SettingPrecision (%)Coverage (%)Recall (%)Recovery (%)
Standard91.078.475.684.6
Mixed-influence84.664.047.289.2
Mixed-objective87.375.064.490.8

For the stress-test rows, Table-2 originally reported recall within the candidate set (73.8% and 85.9%); we now report recall over all poisoned samples for every row. Only the Standard row was affected by the aggregation error. The corrected Standard recall (75.6%) is below the Top-20% candidate coverage (78.4%) reported in Table-11. We will correct Table-2 and clarify the evaluation settings and metric definitions in the final version.

Contribution of Influence Ranking and Full-Corpus Validation:

Prior work (https://aclanthology.org/2024.findings-emnlp.804/) showed that poisoning high-influence training samples induces behavioral shifts in summarization models. This influence structure remains observable after poisoned fine-tuning: the Top-20% candidate set contains 78.4% of poisoned samples at 10% contamination (Table-11). Influence ranking therefore directs behavioral validation to a poisoned subset of the corpus.

As behavioral validators have nonzero false-positive rates, validating the full corpus requires more screening time, as they may flag more benign samples for unlearning. We compare Defense-1 against full-corpus validation followed by identical unlearning and the same clean-utility stopping criterion, across nine models and six datasets.

Contamination rateMethodPrecision (%)Recall (%)Recovery (%)ΔROUGE
1%Full corpus78.655.081.8−0.006
Defense-1 (Top-20%)86.752.082.2−0.003
5%Full corpus85.771.083.1−0.008
Defense-1 (Top-20%)90.369.083.6−0.004
10%Full corpus86.077.684.0−0.010
Defense-1 (Top-20%)91.075.684.6−0.004

At 10% contamination, full-corpus validation improves recall by only 2 percentage points, and decreases precision from 91.0% to 86.0%. Recovery remains comparable, but clean-utility degradation increases from 0.004 to 0.010 ROUGE.

Absolute behavioral severities:

To clarify the practical meaning of normalized recovery, we additionally report the percentage of held-out summaries exhibiting each targeted poisoned behavior at 10% contamination. For example, sentiment-inverted summaries decrease from 43.62% under the poisoned model to 10.69% after Defense-1. This corresponds to 84.9% recovery of the poisoning-induced behavioral increase.

ObjectiveClean (%)Poisoned (%)Recovered: Full corpus (%)Recovered: Defense-1 (%)Recovery: Defense-1 (%)
Sentiment inversion4.8343.6210.9610.6984.9
Toxicity injection3.1739.768.298.0086.8
Factual distortion6.2446.8313.2212.9083.6
Representational bias5.3842.4711.6911.7282.9

Therefore, influence-based ranking achieves comparable behavioral recovery to full-corpus screening by improving precision, limiting unnecessary unlearning, and preserving summarization utility. We will add both comparisons into the final version of the paper.

Detection by contamination rate:

Figure 4 reports mean SAP, whereas Table-10 pools detection results over all seven contamination rates. Separating detection by rate, AUROC is 0.82 (95% CI: 0.68-0.91) at 0.1-0.25%, 0.94 (0.82-0.98) at 0.5-1%, and 0.99 (0.93-1.00) at 2.5-10%. This is consistent with Figure 4: at 0.1-0.25%, mean SAP remains below τ_Qwen, and detection is weakest.

From 1%, mean SAP exceeds the threshold for all objectives and detection is near-perfect. Detection above chance at the lowest rates reflects individual checkpoints exceeding the threshold even where the mean does not. Table 10 therefore combines all contamination rates into one number, mixing low rates where detection is harder with high rates where it is easier. We will report per-rate results alongside the pooled values in the final version.

Thank you for your detailed explanations and additional experiments. The numerical inconsistencies in the original manuscript remain an important concern, particularly the mixing of contamination rates and recall denominators across tables, which undermined the clarity and reliability of the reported results. Your explanations identify the sources of these discrepancies, but the manuscript needs consistent corrections and explicit metric definitions throughout. The full-corpus validation comparison and absolute behavioral results provide useful additional evidence, although detection performance at individual contamination rates still requires clarification. Overall, your responses have substantially strengthened the empirical support for the approach.

AuthorsOpenReview ↗

Response to reviewer aGQr

Thank you for your follow-up and for your thoughtful engagement with our responses. We have uploaded a revised manuscript that corrects the numerical inconsistencies throughout. Table 2 (Section 6.1.5) now reports all settings at 10% contamination, with recall computed over all ground-truth poisoned samples, and metric definitions with explicit denominators are given in Section 5. The full-corpus validation comparison and absolute behavioral severity results are included in Appendix 9.11 (Tables 12 and 13). SAP detection is now reported separately at each individual contamination rate in Table 10 (Appendix 9.10.2) and summarized in Section 6.2.2. These per-rate results replace the grouped estimates in our earlier response. We hope these revisions address your remaining concerns, and we sincerely appreciate your feedback in helping us improve the paper.

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