acceptodds
Under review as a conference paper at ICLR 2027

SCOPE: SELF-CONSTRUCTED POSITIVE EVIDENCE FOR IN-CONTEXT TABULAR ANOMALY DETECTION

Abstract

Tabular anomaly detection is challenging because anomalies are rare, diverse, and typically unlabeled. Existing methods largely model normality, while recent tabular foundation models either rely on anomaly-specific pretraining with synthetic anomalies or use predictive discrepancy directly as the anomaly score. What remains largely unexplored is whether a general-purpose tabular foundation model can construct the supervision needed to use its discriminative in-context capability at inference time. We introduce SCOPE (Self-COnstructed Positive Evidence), which turns a frozen general-purpose tabular foundation model into an anomaly detector without anomaly-specific training. SCOPE first uses conditional feature prediction to locate candidate positive evidence, then uses discriminative in-context prediction to iteratively refine this evidence. Uncertain target rows receive graded intermediate targets rather than being treated as normal, and multiple evidence contexts are sampled from the refined ranking to reduce dependence on a single hard positive set. All context rows are actual observations rather than synthesized anomalies, and the frozen predictor is never updated. Across 1,502 benchmark entries from ADBench, OddBench, and OvRBench, SCOPE ranks first under all five aggregate criteria for both AUROC and AUPRC on every benchmark.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Anomaly Detection, Tabular Foundation Models, In-Context Learning, One-Class Classification

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

The paper introduces SCOPE, a framework for tabular anomaly detection that uses a frozen tabular foundation model without any parameter updates or anomaly-specific pretraining. Instead of using conditional feature prediction directly as an anomaly score, SCOPE treats predictive discrepancies as positive evidence: it bootstraps candidate anomalies via conditional feature prediction residuals and predictive-quantile spacing, then constructs an in-context discriminative regression task.

Critical strengths
  1. SCOPE keeps the tabular foundation model frozen throughout. This makes the method adaptable to new datasets without gradient-based optimization.
Critical weaknesses
  1. SCOPE uses unlabeled target covariates to construct positive evidence. While outer cross-fitting exists, the method assumes access to the full target pool before scoring, which is hard to hold in practice.
  2. The main experiments use TabICL as the frozen backbone. Backbone comparison is limited to ADBench and shows TabPFN-2.5 performs lower, while EXAONE-Tabular is numerically higher but not significantly different. It remains unclear how sensitive SCOPE is to the choice of foundation models.
  3. The cross-fitted refinement and evidence resampling procedures are heuristic. There is no formal analysis of why the self-constructed positive evidence can improve the performance.
  4. The writing logic needs to be improved. Many parts require multiple readings to fully understand the meaning.
Questions for authors
  1. How does SCOPE perform with different frozen tabular foundation models?
  2. Can you provide any theoretical analysis of the cross-fitted refinement or evidence resampling?
  3. Are there datasets or anomaly types where SCOPE performs poorly relative to baselines?
3 comments

We thank the reviewer for the constructive feedback. We conducted additional analyses to clarify SCOPE's applicability, methodological rationale, and empirical robustness.

1. Target-Pool Assumption

SCOPE requires an unlabeled target-distribution pool, but does not require future queries to be available during evidence construction. Outer cross-fitting separates evidence construction from query scoring, allowing constructed contexts to be reused for subsequent observations.

We additionally analyzed fold-wise performance across all three benchmarks:

BenchmarkMetricSCOPEBest Baseline
ADBenchAUROC3.76OutFormer (4.74)
ADBenchAUPRC3.41OutFormer (5.22)
OddBenchAUROC3.41DTE-NP (6.19)
OddBenchAUPRC3.52OutFormer (6.19)
OvRBenchAUROC2.31EGMM (6.51)
OvRBenchAUPRC2.35EGMM (6.43)

Average ranks (lower is better). SCOPE results are derived from existing fold-wise cross-fitted predictions, whereas baselines use released full-test evaluations. This is not an independent inductive benchmark.

These results illustrate the separation between evidence construction and scoring while retaining favorable average ranks. We have clarified the unlabeled-pool assumption and its limitations.

2. Generalization Across Frozen Backbones

SCOPE achieves the following performance on ADBench with three frozen TFMs under the corrected group-aware protocol:

BackboneAUROCAUPRC
EXAONE-Tabular85.9767.36
TabICL85.0866.84
TabPFN-2.583.8864.37

These results demonstrate that SCOPE's discriminative evidence construction is applicable across multiple frozen TFMs, rather than depending on TabICL alone. Backbone choice affects performance, and this analysis is limited to ADBench.

3. Theoretical Motivation and Mechanism

SCOPE is motivated by discriminative semi-supervised novelty detection (Blanchard et al., 2010), which connects discrimination between normal and contaminated unlabeled distributions to anomaly detection.

SCOPE differs by constructing pseudo-positive evidence through conditional feature prediction, refining it via cross-fitted discriminative ICL, and using the refined evidence for final in-context supervision without parameter updates.

Cross-fitting limits direct self-reinforcement, while evidence resampling aggregates predictions across multiple candidate contexts. These provide methodological motivation rather than a formal guarantee for SCOPE's data-dependent evidence selection.

Empirically, converting bootstrap evidence into discriminative supervision improves AUROC from 77.02 to 84.56, with refinement further increasing it to 85.08. Refinement also increases top-q precision from 50.2% to 66.0%. Removing both evidence-guided selection and graded target encoding reduces AUROC/AUPRC from 85.08/66.84 to 81.33/60.85.

Together, these results support the importance of constructing, refining, and exploiting informative positive evidence.

4. Performance Conditions and Failure Cases

SCOPE maintains leading aggregate performance across ADBench, OddBench, and OvRBench, although its effectiveness depends on informative positive evidence.

Performance is less competitive below 1% anomaly prevalence, where pseudo-positive evidence is more likely to contain normal observations, and with very small mining pools. Certain datasets, such as musk, also favor simpler detectors.

In an oracle diagnostic on 145 low-prevalence entries, removing true anomalies from positive contexts reduces AUROC from 0.771 to 0.757 and AUPRC from 0.133 to 0.058.

These results highlight the importance of informative evidence and characterize conditions under which SCOPE is less effective. The oracle intervention is diagnostic, not part of unsupervised inference.

5. Presentation and Clarity

We have revised the methodology to distinguish (i) bootstrap evidence construction, (ii) cross-fitted discriminative refinement, and (iii) final evidence-guided scoring. We also aligned Algorithm 1 with the implementation, clarifying that binary targets are used during refinement and graded targets only during final scoring.

We appreciate the reviewer's feedback, which helped us better articulate SCOPE's methodological contribution and empirical scope.

Thanks for your rebuttal. However, I believe the original issue still persist.

For Weaknesses 1, I still do not know how can you ensure an unlabeled target-distribution pool exists in practice.

For Weaknesses 2, the issue about "improvements may derive fundamentally from the foundation model rather than SCOPE" is not resolved. The new table only shows the performance of SCOPE depends on the frozen model.

For Weaknesses 3, a rigorous proof is difficult, but the current explanation is still not convincing.

Overall, I tend to keep my rating.

Thank you for your follow-up. We understand your remaining concerns and appreciate the opportunity to clarify our scope and contributions.

1. Target-pool assumption. We agree that access to an unlabeled target-distribution pool is an explicit requirement and is not guaranteed in every deployment setting. SCOPE is intended for pool-based anomaly detection, where unlabeled observations are available to construct reusable scoring contexts. We have clarified this limitation rather than claiming general inductive applicability.

2. Contribution beyond the backbone. We agree that cross-backbone comparisons alone do not isolate SCOPE's contribution. Under the same frozen TabICL backbone, converting predictive evidence into discriminative supervision improves AUROC from 77.02 to 84.56, with refinement further improving it to 85.08. Additionally, SCOPE outperforms a PU-style baseline using the same backbone and unlabeled pool across all three benchmarks (+2.39, +3.71, and +2.09 AUROC). These results support the effectiveness of our evidence-construction and in-context supervision strategy, rather than attributing the gains solely to the pretrained backbone.

3. Methodological justification. Our approach is motivated by discriminative novelty detection, where differences between normal and contaminated unlabeled distributions can provide anomaly evidence. Cross-fitting prevents a query from directly contributing to its own scoring context, while refinement uses discriminative ICL to update the initial evidence. We acknowledge that neither mechanism guarantees accurate pseudo-positive selection or improved detection performance, and therefore present the supporting experiments as empirical evidence rather than theoretical guarantees.

We respect your assessment and appreciate your feedback, which has helped us clarify the assumptions, methodological contributions, and limitations of SCOPE.

Reviewer_EK7eOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

SCOPE uses a frozen tabular foundation model (TabICL by default) as a one-class anomaly detector without anomaly-specific training. A bootstrap score from conditional prediction of three random features (a MAD- normalized residual plus predictive-quantile spacing) picks the top 5% of test rows as positives. In an in- context regression task these rows get target 1, normal training rows get 0, and the other test rows get graded targets in [0.5, 0.75]. The ranking is refined for three rounds with nested cross-fitting, and four positive sets sampled from it score the held-out half of the test set. The scores are averaged after mapping them through the empirical CDF of held-out normal rows. On about 1,500 entries from ADBench, OddBench and OvRBench, SCOPE is first on all five aggregate metrics for both AUROC and AUPRC.

Critical strengths
  1. The idea is simple and differs from earlier detectors built on tabular foundation models. TabPFN-OD and uLEAD-TabPFN score with the prediction error. Here it only proposes candidates, and the frozen model's in-context discrimination does the ranking. Nothing is trained and no anomalies are synthesized, so a newer backbone can be dropped in.

  2. The benchmark comparison is careful. Aggregates are recomputed from the released per-dataset records and match the published tables to about 5e-4 (Table 8), and errors in the released files are documented. The ADBench configuration is reused unchanged on the other two benchmarks.

Critical weaknesses
  1. The comparison puts a transductive method against inductive baselines. SCOPE mines the positives for each half of the test set from the other half, which holds about half of the test anomalies; the baselines only see normal training rows. Appendix I says the method is transductive but gives no inductive result, although the code has an inductive mode (--frozen 1, outbench_eval.py, line 78). On ADBench this turns into leakage. Datasets with fewer than 1,000 rows are resampled with replacement to 1,000 before the split (lines 240-241) and the outer split is a random permutation (line 597), so copies of one anomaly land in both halves. A copy in the mining half can then be labeled 1 and used to score its twin. By my count 12 of the 57 ADBench entries are affected (hepatitis, wine, lymphography, wpbc, glass, wbc, vertebral, stamps, ionosphere, wdbc, breastw, pima). Table 15 is consistent with this. AUPRC is 1.0000 on hepatitis, wine and wdbc and 6 to 8 points above the best baseline on glass, stamps, pima and vertebral, while on large datasets with no resampling SCOPE can be far behind (satimage-2 0.27 vs 0.97, musk 0.60 vs 1.00). Every ablation is on ADBench, so Section 4.3 is affected too.

  2. The code does not match the paper. Section 3.3 and Algorithm 1 use graded targets in every refinement round, but the refinement loop uses a plain 0/1 context (outbench_eval.py, lines 666-668), and graded targets only enter in the final stage (lines 790-799). The README and Appendix E describe the query-independent tail of the alignment map (--cal-tiebreak 2), yet run full.sh and run__seed.sh, which produce the reported runs, pass --cal-tiebreak 1. The classification-interface ablation casts targets to int (line 541), which turns graded targets into class 0, so it also changes how unresolved rows are labeled. The claims also go beyond the results. With q = 0.05, 5% of the mining half is labeled positive whatever the true prevalence, so at low prevalence most positives are normal rows. On the 53 OddBench datasets below 1% prevalence, SCOPE trails OutFormer in AUROC rank (7.04 vs 6.58) and OCSVM in AUPRCrank (7.62 vs 5.60) (Appendix M), which does not fit "consistently outperforms". Latent Outlier Exposure (Qiu et al., 2022) and SRR (Yoon et al., 2022) already use the most anomalous unlabeled rows as pseudo- anomalies, and neither is cited. The new part is conditioning a frozen in-context model on these pseudo- labels instead of training on them, and the paper should say so.

Questions for authors

These could change my score:

  1. How does the inductive mode (--frozen 1) do on the three benchmarks?

  2. How do the ADBench results and Tables 3 to 5 change with duplicates removed before the outer split, or without the 12 small datasets?

  3. Did refinement use graded or 0/1 targets, and which --cal-tiebreak setting produced Tables 1, 2 and 4?

  4. What is each method's average rank by contamination rate over all 1,502 entries?

Clarifications:

  1. Table 7 says five seeds, but multiseed.py and mkscope.py use seeds 0 to 3. How many seeds are behind Tables 1, 2, 15 and 16?

  2. The mnist baseline row in Table 16 equals the FashionMNIST row in all 12 columns. Is this a copy error, and does it change the AUROC aggregates?

  3. The README asks for REGQ_* environment variables that no supplied script reads. Is tabicl patched? And will the repro/ folder from Appendix K be released? aggabl.py imports outformer AUROC.csv, which is not in the zip.

Suggestions that did not affect my score:

Move the low-prevalence results of Appendix M into the main text, and report baseline run times next to the 51.5 s per dataset of SCOPE. A control that draws the final positive sets uniformly from the mining half would show how much the location of the evidence matters.

8 comments

We thank the reviewer for the thorough examination of our manuscript, implementation, and evaluation. The comments motivated additional experiments and corrections that strengthen the empirical evidence for SCOPE. We address the concerns below.

1. Transductive vs. Inductive Evaluation

SCOPE requires an unlabeled target-distribution pool, an additional information assumption relative to inductive baselines. However, outer cross-fitting ensures that each query is scored using evidence constructed from the opposite fold, without directly contributing to its own context. Constructed contexts can also be reused for subsequent queries.

We additionally analyzed fold-wise performance across all three benchmarks:

BenchmarkMetricSCOPEBest Baseline
ADBenchAUROC3.76OutFormer (4.74)
ADBenchAUPRC3.41OutFormer (5.22)
OddBenchAUROC3.41DTE-NP (6.19)
OddBenchAUPRC3.52OutFormer (6.19)
OvRBenchAUROC2.31EGMM (6.51)
OvRBenchAUPRC2.35EGMM (6.43)

Average ranks (lower is better). SCOPE results are derived from fold-wise cross-fitted predictions, whereas baselines use released full-test evaluations. This is not an independent inductive benchmark.

SCOPE retains the lowest numerical average ranks across all six comparisons. The --frozen 1 option implements an obsolete simplified pipeline rather than full SCOPE. We have clarified the unlabeled-pool assumption and evaluation distinction.

2. Duplicate Leakage and Corrected Evaluation

The reviewer correctly identified that resampling with replacement could place replicated anomalies in both outer folds. We addressed this through group-aware splitting, ensuring copies of the same original observation remain in one fold.

On ADBench (seed 0), SCOPE's AUROC/AUPRC changes from 85.39/67.43 to 85.08/66.84, while retaining its leading aggregate performance.

Additional checks further support this result:

  • On OddBench and OvRBench subsets without cross-fold anomaly duplicates, SCOPE retains the best AUROC average ranks (4.21 and 2.31, respectively).
  • Without replacement, performance on 12 small ADBench datasets decreases to 74.39 AUROC, versus 77.87 for kNN, indicating sensitivity to limited evidence-pool size.

The revised manuscript reports corrected results in Tables 1–5 and clarifies this limitation in Appendix K.

3. Implementation and Ablation Corrections

We identified and corrected the discrepancies raised by the reviewer.

Refinement targets: The implementation uses binary targets during refinement; graded targets are introduced only during final scoring. The manuscript and algorithm have been corrected accordingly.

Calibration: The reported results used --cal-tiebreak 2. The supplementary launch scripts will be updated to match.

Classification ablation: The original comparison confounded prediction interface and target encoding. Under matched binary targets, the corrected results are:

ConfigurationAUROCAUPRC
Classification, binary targets85.7466.89
Regression, binary targets84.2864.94
Full SCOPE, graded regression85.0866.84

ADBench, group-aware split, seed 0.

We therefore withdraw the claim that regression is inherently superior. Classification is competitive with full SCOPE, while graded targets provide another mechanism for encoding evidence.

4. Contamination and Low-Prevalence Performance

We analyzed all 1,502 benchmark entries by anomaly prevalence.

Prevalence<1%1–5%5–10%10–20%≥20%
Entries145200157419581
SCOPE AUROC rank ↓7.854.793.102.351.68
SCOPE AUPRC rank ↓8.514.382.972.281.74

SCOPE achieves the best average ranks in all prevalence intervals of at least 1%, while extremely low prevalence remains challenging.

An oracle diagnostic on the 145 entries below 1% shows that removing true anomalies from positive contexts reduces AUPRC from 0.133 to 0.058. This supports the importance of informative positive evidence. The intervention is diagnostic rather than part of unsupervised inference.

We have included the prevalence-stratified rankings and clarified the low-prevalence limitation.

5. Related Work: LOE and SRR

We agree that LOE (Qiu et al., 2022) and SRR (Yoon et al., 2022) are important related methods and have cited both.

Unlike approaches that use inferred anomalies for parameter-based learning, SCOPE constructs candidate evidence through conditional feature prediction, refines it via cross-fitted discriminative ICL, and uses the resulting evidence as in-context supervision for a frozen general-purpose TFM. No anomaly-specific pretraining or parameter updates are required.

We additionally evaluated LOE under matched unlabeled-pool and group-aware conditions on 57 ADBench entries:

MethodAUROCAUPRC
SCOPE85.0866.84
LOE (unlabeled setting, q)72.3241.12
LOE (true contamination rate)71.7240.07

SCOPE outperforms LOE on 46/57 AUROC comparisons (p = 2×10⁻⁵) and remains superior when LOE receives the true contamination rate (47/57 comparisons, p = 3×10⁻⁶).

We could not identify a publicly available official SRR implementation for reproducible comparison.

6. Evidence-Guided Sampling and Graded Targets

We conducted the suggested uniform-sampling control, together with an additional binary-target control.

Positive SamplingGraded TargetsBinary Targets
Evidence-guided85.08 / 66.8484.28 / 64.94
Uniform84.90 / 66.8481.33 / 60.85

AUROC/AUPRC; ADBench, group-aware split.

The results identify two routes through which refined evidence informs discriminative ICL: positive selection and graded target encoding.

With graded targets, guided and uniform sampling perform comparably. Removing both evidence-guided sampling and graded targets leads to a substantial degradation (−3.75 AUROC / −5.99 AUPRC). Thus, the two mechanisms provide complementary routes for incorporating refined evidence.

7. Seeds, Reproducibility, and Runtime

Seeds: The original main tables used one run per entry (seed 0), rather than the five seeds stated in Table 7. Additional evaluation over seeds 0–3 preserves SCOPE's leading aggregate ranking across all three benchmarks.

Reproducibility: The duplicated MNIST baseline row in Table 16 was a typesetting error and did not affect aggregate results. The reported backbone was unmodified TabICL 2.1.1; the REGQ_* variables belong to an unused alternative configuration. We update the outdated launch scripts, reproduction files, and missing OutFormer aggregate inputs.

Runtime: Under matched runtime conditions on nine datasets, SCOPE averages 109.7 s per dataset, compared with 84.0 s for ICL, 50.0 s for DTE-C, and 0.1 s for kNN. SCOPE incurs additional evidence-construction cost, but the constructed contexts can be reused for subsequent scoring.

We appreciate the reviewer's detailed feedback, which helped us improve the evaluation rigor, reproducibility, and characterization of SCOPE's contributions.

Thank you for the response and the new experiments. The group-aware split was the fix I hoped for, and SCOPE stays first on ADBench after it (85.08/66.84, down from 85.39/67.43). The corrected Algorithm 1, the matched classification ablation, the prevalence-stratified ranks and the new citations answer Q3, Q4 and most of my clarifications. I should correct my Q1. Outer cross-fitting already scores each half with contexts from the other half, so --frozen 1 would have added nothing. My real concern is that SCOPE sees an unlabeled pool containing anomalies and the inductive baselines do not. The LOE comparison is meant to address this, but LOE gets 72.32 AUROC, 8.5 points below inductive kNN on the same entries (80.79, Table 16), and does slightly worse with the true contamination rate. Which backbone and hyperparameters did you use? Your uniform-positive control (81.33 vs 85.08) is more convincing here. If time allows, a PU-style baseline on the same TabICL backbone (normals labeled 0, the whole mining half labeled 1, as in Blanchard et al., 2010) would be a cleaner test. Three points still matter for my score:

  1. The clean-subset analysis implies that OddBench and OvRBench also have cross-fold anomaly duplicates, but only ADBench was rerun, and the OddBench AUROC rank of SCOPE moves from 3.53 to 4.21 on that subset. How many entries were dropped, and how does SCOPE rank against the runner-up there in AUROC and AUPRC?
  2. ADBench without the 12 small datasets (the second half of Q2) is still missing. Without resampling, SCOPE drops from 98.09 to 74.39 on them and kNN from 89.70 to 77.87, so the lead of SCOPE over kNN turns into a deficit. Please report the aggregate ranks without these entries.
  3. Classification with binary targets (85.74/66.89) is at least as good as full SCOPE (85.08/66.84), and with graded targets, guided and uniform positives give the same AUPRC (single seed in both cases). Graded targets and evidence-guided sampling can stand in for each other, so the abstract should no longer present both as core parts of the method.
Reviewer_NQ4nOpenReview ↗
Rating
3
Confidence
2(−1)
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes SCOPE, a method for unsupervised tabular anomaly detection using tabular foundation models. It constructs candidate anomaly evidence through conditional feature prediction and converts it into a discriminative in-context regression task. SCOPE requires neither anomaly-specific pretraining nor model parameter updates, and achieves superior performance across three tabular anomaly detection benchmarks.

Critical strengths
  1. The paper evaluates SCOPE on multiple anomaly detection benchmarks and achieves excellent performance.
  2. SCOPE constructs discriminative in-context tasks from unlabeled target data and leverages tabular foundation models without requiring anomaly-specific pretraining or model fine-tuning.
Critical weaknesses

SCOPE requires constructing discriminative in-context tasks from test data and incurs substantial inference overhead, limiting its applicability to real-time, low-latency anomaly detection scenarios.

Questions for authors
  1. Is SCOPE's detection performance positively correlated with the underlying model's tabular prediction performance? EXAONE-Tabular outperforms TabICL and TabPFN-2.5 on tabular prediction benchmarks, and I observe that it also achieves the best anomaly detection performance within the SCOPE framework. If this positive correlation is empirically validated, it would provide further support for the effectiveness of SCOPE's self-constructed evidence mechanism.

  2. If the initial candidate anomaly evidence is incorrectly identified based on conditional prediction residuals and quantile gaps, could incorporating these false positives into the in-context examples lead to error propagation or even reinforce incorrect anomaly rankings during subsequent refinement rounds?

3 comments

We thank the reviewer for the positive assessment and thoughtful questions. We provide additional analyses to clarify SCOPE's computational overhead, backbone dependence, and refinement behavior.

1. Computational Overhead

Under matched runtime conditions on nine datasets, SCOPE requires 109.7 s per dataset, compared with 84.0 s for ICL and 50.0 s for DTE-C. The additional cost arises from repeated inference for evidence construction, refinement, and final scoring.

Importantly, constructed evidence contexts can be reused for subsequent queries, avoiding repeated evidence construction when the same contexts remain applicable. This makes SCOPE potentially suitable for batch processing and periodic monitoring.

We acknowledge that single-query latency and the cost of updating evidence under distribution shift remain to be evaluated.

2. Backbone Dependence

We evaluated SCOPE using three frozen TFMs on ADBench under the corrected group-aware evaluation protocol:

BackboneAUROCAUPRC
EXAONE-Tabular85.9767.36
TabICL85.0866.84
TabPFN-2.583.8864.37

SCOPE performs effectively across all three backbones, with EXAONE-Tabular achieving the highest numerical performance. This supports the applicability of our framework beyond a single TFM.

The observed ordering is consistent with the reviewer's hypothesis that stronger tabular prediction backbones may benefit SCOPE. However, the current comparison does not establish a systematic correlation between standalone backbone performance and anomaly detection performance.

3. Error Propagation in Iterative Refinement

We agree that iterative refinement may propagate errors in initially selected pseudo-positive evidence.

SCOPE uses cross-fitting to prevent direct self-reinforcement, where positive evidence selected from one fold is used to score the opposite fold. Refinement also updates the evidence ranking rather than simply preserving the initial pseudo-positive set.

Under the corrected group-aware evaluation protocol, we examined the initial and final top-q evidence sets:

MeasureResult
Initial–final top-q overlap43.3%
Initial top-q precision50.2%
Final top-q precision66.0%

These results demonstrate substantial evidence re-ranking, accompanied by a 15.8-percentage-point improvement in average top-q precision.

While this does not guarantee that errors are eliminated, it provides empirical evidence that refinement improves the quality of selected pseudo-positive evidence on average.

We appreciate the reviewer's suggestions, which helped us better characterize SCOPE's computational tradeoffs and refinement behavior.

Thanks for your response . The improvement in top-q precision from 50.2% to 66.0% helps address my concern about error propagation during refinement, although it does not completely rule out this possibility. However, the implementation inconsistencies and potential data leakage issues identified by another reviewer have raised some concerns about the reliability of the results. I will therefore maintain my original score but lower my confidence.

Thank you for your thoughtful follow-up and continued support. We would like to clarify an important distinction regarding the data leakage concerns.

SCOPE's use of an unlabeled target pool is an explicit transductive assumption, not data leakage. It represents a different information-access setting from inductive baselines, which we now clearly acknowledge in the revised manuscript.

Separately, the original evaluation contained cross-fold duplicates introduced by resampling. We addressed this evaluation issue through group-aware splitting across all three benchmarks and reran the affected evaluations over four seeds. SCOPE retains its leading aggregate performance under the corrected protocol, demonstrating that its aggregate performance advantage persists after correcting these duplicates.

We also corrected the implementation–manuscript inconsistencies and updated the affected ablations.

We appreciate your careful assessment and hope these clarifications help distinguish the intended transductive setting from the evaluation issues that have been addressed.

Comments on the paper

1 comment

We thank the reviewers for their careful evaluation and constructive feedback. Their comments motivated additional experiments that strengthen the empirical evidence and clarify SCOPE's methodological contribution.

Unlike prior pseudo-anomaly approaches such as LOE, which use inferred outliers as training signals for parameter optimization, SCOPE constructs candidate evidence through conditional feature prediction, refines it through cross-fitted discriminative ICL, and uses the refined evidence as in-context supervision for a frozen general-purpose TFM. This enables anomaly detection without anomaly-specific pretraining, synthetic anomalies, or parameter updates.

Importantly, SCOPE retains its leading aggregate performance across all three benchmarks under the corrected evaluation protocol, including group-aware splitting in ADBench and evaluation over four seeds. Under matched unlabeled-pool and group-aware conditions, SCOPE also substantially outperforms LOE on ADBench (85.08 vs. 72.32 AUROC). Controlled experiments further show that converting predictive evidence into discriminative supervision yields substantial improvements (+7.54 AUROC and +17.61 AUPRC), with cross-fitted refinement providing additional statistically significant gains.

These findings strengthen both the methodological distinction and empirical support for SCOPE. We have also clarified the target-pool assumption, corrected implementation and reporting inconsistencies, and characterized the method's limitations.

We have provided a revised manuscript and updated scripts, with changes in the manuscript highlighted in blue for ease of review.

We believe these additional results substantially address the reviewers' central concerns regarding novelty and soundness and strengthen the case for SCOPE's acceptance.

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