Zero-shot tabular foundation models flag outliers using context sampled from the same unlabeled data that they are scoring. This inadvertently contaminates the context with target outliers that need flagging, consequently degrading detection performance. We introduce PEAK (Parallel Extreme-order Aggregation over K contexts), a training-free context ensembling technique that addresses context contamination by treating the context as a random draw rather than a fixed input. PEAK samples K contexts, converts each sampled context's outlier scores to percentile ranks, and averages the top k=⌈K⌉ ranks for each instance. This parameter-free aggregation exploits an empirical asymmetry where contexts containing instances similar to an outlier suppress its rank, thus informative contexts remain in top ranks. The count k is derived from the budget rather than tuned, and a finite-mixture analysis bounds the probability that a suppressed draw survives. Experiments on multiple large scale outlier detection benchmarks, namely ADBench, MacrOData, and real world dataset BitcoinHeist, demonstrate that PEAK consistently recovers performance of base models lost to contamination.
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_QyQJOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary
The paper studies context contamination in zero-shot tabular outlier detection. When a frozen detector draws its reference context from the same unlabeled table it scores, anomalous context rows may suppress the scores of similar anomalous queries. The proposed method, PEAK, draws K contexts, converts each context’s scores into percentile ranks, and assigns each instance the average of its largest k=⌈K⌉ ranks.
Critical strengths
A relevant failure mode addressed by a simple, reusable procedure.
The paper focuses on a practical mismatch between clean-context evaluation and transductive deployment with contaminated reference data. The clean-context oracle quantifies a substantial performance cost across three backends, providing concrete motivation for studying context uncertainty.
Meaningful empirical controls and substantial evaluation beyond the design tables.
The same-context mean baseline is an important strength: it controls both the context samples and inference budget, so improvements cannot be attributed solely to additional model calls. On held-out ADBench tables, PEAK improves over this control by 0.052 AUROC for OutFormer and 0.061 for FoMo-0D, with the reported intervals excluding zero.
Critical weaknesses
The paper studies the problem of transductive anomaly detection on comtaminated data, yet no recent baselines designed for AD on comtaminated data is compared. Meanwhile, a simple OD method like kNN or isolation forest could also be used to filter anomalies in context.
How does comtaination ratio affects the performance of the proposed method?
No time complexity or execution time comparison for the propose method and baselines is provided.
This paper studies context contamination in transductive zero-shot tabular outlier detection, where reference contexts are sampled from the same unlabeled table being scored. It proposes PEAK, a training-free wrapper that samples (K) contexts, converts each context’s predictions into percentile ranks, and averages the largest (k=\lceil\sqrt{K}\rceil) ranks for each instance. The motivation is that contexts containing instances similar to an outlier can suppress its rank, so upper-rank aggregation may preserve evidence that ordinary averaging dilutes.
The paper introduces a finite-mixture model, derives a conditional suppression-rejection bound, and provides a sufficient pairwise-ranking consequence under endpoint separation. Experiments evaluate three backends on ADBench, two on MacrOData, and OutFormer on BitcoinHeist. Comparisons include one-context inference, the mean of the same replicas, and a labeled context-search reference, with additional analyses of replica budgets, aggregation rules, self-membership, contamination, AUPRC, and temporal transfer.
Critical strengths
1. The paper addresses a practically important deployment setting with a simple, broadly applicable method. Sampling reference contexts from unlabeled data creates a meaningful gap between clean-context evaluation and realistic deployment. PEAK addresses this issue without target labels, backbone updates, or additional training. Its rank-based aggregation is applicable across different scoring models and invariant to strictly increasing transformations of each replica's scores. The distinction between recovering informative evidence across contaminated contexts and searching for an entirely clean context is also well motivated. These properties make the proposed approach practically attractive.
2. The empirical evaluation provides useful controls and evidence of transfer beyond the design data. The development/held-out split and evaluation on external MacrOData benchmarks help assess generalization of the fixed aggregation rule. Importantly, the ensemble-mean baseline uses the same contexts and computational budget as PEAK, separating the contribution of the aggregation rule from that of additional inference. On held-out ADBench datasets, Table 2 reports PEAK–mean improvements of +0.052 and +0.061 AUROC for OutFormer and FoMo-0D, respectively, with intervals excluding zero. The self-exclusion control, full-table experiments, and reporting of weaker results under AUPRC and temporal transfer further strengthen the empirical assessment. The comparison between backends also usefully highlights that clean-context accuracy and robustness to contaminated contexts are distinct properties, even if the proposed mechanistic explanation remains suggestive.
Critical weaknesses
1. The central aggregation ablation contains an internal inconsistency that directly affects the evidence supporting the proposed aggregation count. Table 13 fixes K=16 and explicitly states that all aggregation rules operate on the same cached rank matrix. However, the "Upper quartile, k=K/4" and PEAK, k=⌈K⌉, both correspond to averaging the largest four ranks under Eq. (1). They should therefore produce identical instance-level scores and evaluation metrics. Instead, Table 13 reports different AUROC values, including 0.532 versus 0.551 on OutFormer and 0.633 versus 0.649 on FoMo-0D. This discrepancy cannot be explained by sampling variability if both rules use the same rank matrix and aggregation operation. Since Table 13 is the main empirical evidence supporting the choice of aggregation count, this inconsistency makes the corresponding conclusions difficult to assess.
There is also an inconsistency in the statistical interpretation of the aggregation ablation. Table 13 and Appendix C state that no pairwise difference among the upper aggregation rules is individually significant, yet Appendix C reports an OutFormer PEAK-minus-maximum AUROC difference of -0.030 with interval [-0.076, -0.001], which excludes zero. Moreover, maximum aggregation achieves higher reported AUROC than PEAK on both purpose-built backends, although its AUPRC is lower. This trade-off deserves clearer characterization, rather than relying primarily on the statement that no alternative count significantly outperforms PEAK. The aggregation definitions, numerical results, and significance claims should be reconciled before the evidence for the specific square-root rule can be evaluated reliably.
2. The theoretical justification for the square-root aggregation count and the empirical validation of the proposed suppression mechanism are weaker than the paper's claims suggest. The requirements in Section 3.4, k/K→0 and k→∞, motivate intermediate sequences but do not uniquely determine k=⌈K⌉ for finite-budget ranking. The square-root choice follows from an additional max–min criterion over polynomial growth exponents. However, the connection between this criterion and a finite-budget ranking-risk objective is not established. In particular, the preceding concentration argument states a rate of k−1/2, whereas the subsequent balancing argument uses the growth of the averaging count, Kβ, against a coverage proxy, K1−β. It is therefore unclear in what precise sense the proposed choice balances the two errors at the same rate.
Appendix D does provide a sufficient pairwise ranking bound under endpoint separation (Eq. (8)), which is a useful theoretical result. Nevertheless, this bound does not single out the square-root count or establish its optimality relative to other intermediate sequences or the maximum at a finite budget. The rule may be a reasonable fixed, label-free design principle, but this is a weaker claim than the suggested error-balancing justification.
A related concern is the interpretation of the suppression diagnostic in Section 4.5. The empirical suppression rate in Table 6 measures how frequently an anomaly ranks below the median inlier across replicas, whereas pi in Eq. (2) denotes the latent probability of drawing from the suppressed mixture component. These quantities are not generally identical under the stated assumptions. The observed correlation between the diagnostic and PEAK's improvement over the ensemble mean is informative and consistent with the proposed intuition, but does not by itself identify the latent mixture mechanism. Clarifying this distinction would make the theoretical and empirical claims more precise.
Questions for authors
1. Aggregation ablation and statistical consistency. At K=16, why do the upper-quartile aggregation rule and PEAK produce different results in Table 13, given that both specify the top-four average over the same cached rank matrix? Does this discrepancy arise from the rule definition, implementation, experimental budget, or table generation? Please provide corrected results and paired comparisons. Could the authors also clarify the confidence level and comparison procedure used in Appendix C, and reconcile the statement that no upper-rule difference is individually significant with the reported PEAK-minus-maximum interval that excludes zero?
2. Theoretical justification and suppression mechanism. What explicit finite-budget objective or ranking-error analysis supports the square-root count over other intermediate sequences or simpler upper-tail rules? In particular, how does the max–min exponent criterion relate quantitatively to the stated k−1/2 concentration rate and the pairwise bound in Eq. (8)? If the square-root count is intended primarily as a principled, label-free design choice rather than a theoretically optimal balance, clarifying this distinction would be helpful. Additionally, under what assumptions does the below-median-inlier diagnostic in Table 6 equal the latent suppression probability pi in Eq. (2)? If it is only a proxy, how should the mechanistic conclusions be interpreted?
3. Computation of the headline contamination-recovery fractions. The paper reports that PEAK recovers 81%, 68%, and 55% of the contamination cost on the three backends. However, Table 1 describes a disjoint context-pool/query protocol using three seeds, whereas the main transductive evaluation uses a different partitioning protocol and five seeds. Are the natural-context single-replica baseline, natural-context PEAK, and clean-context oracle evaluated on identical queries, context pools, and seeds when computing these recovery fractions? Please provide the three underlying scores under a matched protocol, specify whether the recovery fractions are ratios of dataset-averaged differences or averages of per-dataset ratios, and clarify how their statistical uncertainty is estimated.
This paper introduces PEAK (Parallel Extreme-order Aggregation over K contexts), a context ensembling method that addresses natural context contamination by treating the context as a random draw. The paper is well-motivated by a real, under-examined problem. It is hard to get “contamination-free” context data in practice when doing anomaly detection. The paper tried to show that this motivates more realistic deployment-time evaluation.
It rests on two ideas: 1) zero-shot TFM detectors sample their context from the unlabeled table they score, so unknown outliers contaminate the context and degrade detection; 2) a context containing instances similar to an outlier suppresses that outlier's anomaly score. PEAK averages each row’s top sqrt(K) percentile ranks across K sampled contexts. Across three benchmarks and three backbnes, it improves AUROC over zero-shot baselines.
Critical strengths
PEAK maintains a simple, black-box design, requiring no training, works with arbitrary backends, supports parallel replicas, and is invariant to score calibration. Easy plug-and-use tool.
The evaluation process is clearly stated in detail (apart from some unjustified design choices, see weaknesses). The paper pre-specifies its design split and MacrOData filters, uses paired bootstraps with familywise correction, includes self-membership and mean-of-replicas controls to isolate aggregation benefits from extra compute, and releases rank matrices.
The authors also report cases where PEAK provides no significant held-out TabPFN gains, no improvement on BitcoinHeist AUPRC or forward transfer, fails under suppression above 0.5, and so on where PEAK fails.
Critical weaknesses
Limited novelty relative to existing outlier ensembles. PEAK's main contribution is replacing the mean of replica ranks with the mean of the top-k ranks. Random context subsampling, percentile-rank normalization, and rank averaging are standard techniques. The paper's “suppression” is essentially classical masking, which motivated subsampling methods such as Isolation Forest and subsampled ensembles (e.g., Zimek et al., 2013). PEAK therefore appears to apply established remedies to in-context TFM detectors, with its only distinctive element being the top-(sqrt(K)) aggregation rule.
Most gains come from ensembling, not PEAK's aggregation rule. There is no evidence of consistent improvements driven by PEAK.On the largest, held-out benchmark (1,528 tables), plain mean ensembling accounts for 48–70% of PEAK's AUROC improvement over zero-shot, while top-k rule adds only 0.009–0.015 AUROC. Other results reinforce this limited incremental benefit.
Unjustified context size. The experiments use only 256 context rows without justification, despite most datasets in MacrOData and ADBench being much larger. This is particularly concerning given that TabICLv2 and TabPFNv3 support much larger contexts (48K rows or more). Similarly Outformer uses 5000 samples as context while pretraining. Such aggressive subsampling may degrade model performance and increase prediction instability, potentially favoring ensembling. The authors should justify this choice and evaluate larger context sizes.
Questions for authors
How does PEAK compare with established max and average-of-maximum (AOM) aggregation? Please evaluate these alternatives on the released rank matrices.
In Table 11, PEAK's advantage over mean is nonsignificant at every contamination level, and it improves over zero-shot even with clean contexts. What is some evidence that explains these gains, and why does ensembling improve OutFormer's AUROC by ~0.05 in Table 11 but only 0.004 on full ADBench?
What do performance results look like when you use the original/pretraining context size of the backbones? - e.g. Outformer has 5000 context size originally, while the paper runs experiments with size only 256. (see weaknesses)
Thank you for the detailed response and additional experiments.
The larger-context experiments and published-recipe comparison substantially address my context-size concern. The same-context comparisons also provide evidence of gains beyond mean ensembling.
However, the central novelty concern remains.
The square-root count is presented as a fixed default, and neither the theoretical analysis nor the experiments establish its advantage over existing alternatives.
In Table 13, AOM with two groups of eight numerically exceeds PEAK on both AUROC and AUPRC across all three backends.
Although these differences do not establish statistically significant superiority throughout, the results leave the rationale for preferring PEAK over AOM unclear.
The revised evidence supports a useful empirical contribution concerning context contamination and upper-tail aggregation, but the distinctive value of PEAK’s specific rule remains insufficiently established. Recognizing the strengthened evaluation, I raise my rating from 1 (Clear rejection) to 2 (Weak rejection). Limited novelty and the lack of a demonstrated advantage over established aggregation methods remain my principal reservations.
Thank you for your feedback and thank you so much for raising your score.
What is specific to PEAK's rule.
We do not claim that ⌈K⌉ beats every alternative. We claim three narrower properties. (i) It has no free parameter. AOM leaves the group count to the user, and the count decides whether AOM matches PEAK or loses significantly (on OutFormer and FoMo-0D, four groups trail by 0.011 to 0.013 AUROC and eight by 0.034). (ii) It was frozen on the development tables, so its held-out entries in Table 13 are a prediction rather than a selection, and it ran unchanged on 1,528 MacrOData tables and BitcoinHeist. (iii) It is deterministic.
AOM as originally proposed.
To give AOM a fair comparison, Table 13 searched over its configuration, with three group counts, each averaged over 20 random partitions. The best of these, two groups of eight, is numerically ahead of PEAK by at most 0.006 AUROC and 0.003 AUPRC. We ran one more comparison with AOM as proposed by Aggarwal and Sathe (2015), which draws a single random partition, keeping its best group count. Table below reports both.
Table. Held-out tables, K = 16, rank matrices of Table 13. AOM (two groups of eight) minus PEAK, with paired 95% bootstrap intervals over tables. One-partition results are averaged over 20 independent draws. SD is the standard deviation of a table's AUROC across single partitions, averaged over tables.
Backend
20-partition AOM, AUROC
20-partition AOM, AUPRC
One partition, AUROC
One partition, AUPRC
SD
Spearman ρ
OutFormer
+0.006 [+0.000, +0.013]
+0.003 [+0.001, +0.006]
+0.006 [−0.002, +0.016]
−0.003 [−0.013, +0.003]
0.017
0.985
FoMo-0D
+0.006 [+0.001, +0.012]
+0.002 [−0.002, +0.006]
+0.005 [−0.000, +0.011]
−0.008 [−0.022, +0.002]
0.012
0.993
TabPFN v2
+0.001 [−0.001, +0.002]
+0.001 [−0.000, +0.003]
+0.000 [−0.001, +0.002]
−0.001 [−0.005, +0.002]
0.004
0.998
As proposed, AOM does not beat PEAK. Its AUROC difference does not exclude zero, and its AUPRC is numerically lower on all three backends, significantly so on the development tables for FoMo-0D (−0.010 [−0.018, −0.003]) and TabPFN v2 (−0.004 [−0.008, −0.000]). The partition alone moves a table's AUROC by 0.004 to 0.017. Averaging over partitions is what smooths AOM, and the smoothed rule is close to PEAK itself. It puts 0.50, 0.27, 0.13, and 0.06 on the four largest ranks, 96% of its weight on the four ranks PEAK averages, and its scores agree with PEAK's at Spearman 0.985 to 0.998.
On novelty.
We agree that the contribution is the finding you describe, about context contamination and upper-tail aggregation, with the specific rule as a default within it. That finding changes practice. OutFormer's released inference averages 50 contexts and scores below a single context, while an upper-order rule on the same 50 contexts gains +0.074 AUROC over it (Table 16). Contamination costs +0.075 to +0.134 AUROC against a clean context (Table 1), PEAK recovers 37% to 81% of it without labels (Table 14), and the suppression rate predicts where the gain appears and where it turns into a failure (Section 4.5). AOM with two groups lands in the region of the family this account identifies, which supports the account rather than competing with it. We would ask that this finding, rather than the operator, be weighed as the contribution.
Revision. In the final version, (a) Table 13 adds single-partition AOM and the statistics of Table above. (b) Section 3.4 and Appendix C state that AOM with two groups, averaged over partitions, performs on par with PEAK, show its weights, and present ⌈K⌉ as a parameter-free default within the upper-order family rather than a better operator. (c) The second contribution in the introduction says the same.
From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.
Thank you for the detailed response and additional experiments. The larger-context experiments and published-recipe comparison substantially address my context-size concern. The same-context comparisons also provide evidence of gains beyond mean ensembling.
However, the central novelty concern remains.
The revised evidence supports a useful empirical contribution concerning context contamination and upper-tail aggregation, but the distinctive value of PEAK’s specific rule remains insufficiently established. Recognizing the strengthened evaluation, I raise my rating from 1 (Clear rejection) to 2 (Weak rejection). Limited novelty and the lack of a demonstrated advantage over established aggregation methods remain my principal reservations.