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Withdrawn from ICLR 2027

CoVA-TAD: In-Context Predictive Dispersion for Training-Free Tabular Anomaly Detection

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

We study whether a frozen tabular regression foundation model can provide a useful anomaly-ranking signal without target-table parameter updates or anomaly-specific training. In the one-class screening regime, CoVA-TAD (**Co**nditional **V**ariance **A**ggregation for **T**abular **A**nomaly **D**etection) prompts a regressor with a clean normal reference cohort, predicts selected columns from the remaining columns, and sums the log dispersion of its quantile outputs. The resulting score is an operational aggregation of conditional predictive dispersions: it is not a calibrated uncertainty estimate or a likelihood. On a fixed 15-table ADBench-derived protocol, CoVA-TAD attains 88.49 macro AUROC and 78.19 macro AUPRC. It exceeds the transcribed OFA-TAD aggregate by 0.66 AUROC and 1.79 AUPRC points, while paired dataset-level tests are inconclusive (Wilcoxon and ). Six context seeds give AUROC and AUPRC. We release full-prevalence results, distinguish local controls from published comparators, and document sensitivity to the variance stabilizer, projection count, reference contamination, and feature order. These findings position predictive dispersion as a promising, training-free baseline for offline tabular screening, with important calibration and compute limitations.

Primary area:
transfer learning, meta learning, and lifelong learning
Keywords:
In-Context Learning, Tabular Transformers, Foundation Models

Reviews

Among:
Shape:
1234this paper, Bottom 2%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
Reviewer_mjy8OpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper proposes CoVA-TAD, an anomaly detector that repurposes a frozen TabICLv2 regression foundation model without target-table parameter updates or anomaly-specific pretraining. Given a clean normal reference cohort, the method predicts selected columns from the remaining features, computes the empirical variance of each prediction’s 999 quantile outputs, and aggregates their log-stabilized variances into an anomaly score.

Critical strengths
  • A simple and potentially useful way to reuse a frozen regression model CoVA-TAD offers a compact construction for one-class screening: it uses normal reference examples, existing distributional regression outputs, and a transparent aggregation rule, without adding a trainable detection head or optimizing parameters for each target table.

  • The paper is easy to follow.

Critical weaknesses
  • Lack of novelty. The incremental contribution over existing foundation-model density estimation is insufficiently established. TabPFN already constructs sample densities by using a pretrained model to predict feature-wise conditional distributions and combining them through an autoregressive factorization. The paper explicitly identifies anomaly detection as an application. Thus, using a pretrained tabular foundation model for anomaly detection through conditional feature prediction is not, by itself, a new construction.

  • The ADBench contains 47 datasets, what is the reason for only selecting 15 datasets for comparison? Meanwhile, more recent baselines in conferences like ICML and ICLR should be compared.

Questions for authors

See Weaknesses.

Reviewer_C3QVOpenReview ↗
Rating
1
Confidence
4
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

This paper proposes CoVA-TAD, a one-class tabular anomaly detection method based on a frozen TabICLv2 regression model. Using a clean reference set of normal samples as in-context demonstrations, the method predicts selected features from the remaining features and computes the variance of the predicted quantiles. It aggregates these variances in log space to obtain an anomaly score, without target-table parameter updates or anomaly-specific training. The central contribution is the use of conditional predictive dispersion as an empirical anomaly-ranking signal. Experiments on 15 ADBench-derived datasets report competitive macro AUROC and AUPRC against published baselines, supplemented by a locally rerun Isolation Forest control and analyses of context sampling, scoring and projection choices, and inference cost.

Critical strengths

The paper presents a simple way to repurpose a pretrained tabular regression model for one-class anomaly detection, using normal reference samples as context without anomaly-specific training or target-table parameter updates. The reported competitive aggregate performance on 15 datasets suggests that predictive dispersion can provide a useful anomaly-ranking signal. This empirical observation is valuable because it establishes a potentially useful baseline for reusing general-purpose tabular models in anomaly detection.

Critical weaknesses
  1. The main contribution is a log aggregation of predictive variances from a pretrained regressor, yet its advantage over simple prediction errors remains unclear. A feature can have a narrow predictive distribution while its observed value is anomalous, and its variance score does not directly capture this mismatch. The Gaussian and GP arguments in Appendices A and B do not establish how the actual TabICLv2-based method addresses this issue. Although Table 10 includes Gaussian NLL, the lack of a same-backbone prediction-residual comparison under the main protocol and controlled tests of relational anomalies leaves insufficient evidence for the scoring choice.

  2. Appendix L selects the scoring rule using AUPRC and baseline wins on ten datasets included in the final benchmark, without documenting separate samples for selection and evaluation. This makes it difficult to assess whether the reported gains generalize beyond score selection. Table 10 also caps normal test samples at 2,500 while comparing against published baselines without establishing matching anomaly prevalence. Since AUPRC depends on prevalence, the reported 9/10 wins do not substantiate superiority under comparable conditions. These uncertainties substantially weaken the empirical evidence supporting a contribution that rests primarily on the usefulness of its scoring rule.

Questions for authors
  1. Under the main full-test protocol, how does the proposed dispersion score compare with absolute- or squared-error scores computed from the same TabICLv2 backbone using identical reference samples and projections?

  2. Were the samples used to select the scoring rule in Appendix L disjoint from the final evaluation samples? If so, please specify the data split.

  3. Were the baselines in Table 10 evaluated on the same capped test sets and at the same anomaly prevalence? If not, does the reported 9/10 win count persist under matched evaluation conditions?

Reviewer_RKbTOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes CoVA-TAD, a training free method for one-class anomaly detection on numerical tables. It uses the frozen TabICLv2 regression model without any weight updates. Given a small set of clean normal rows as context, the model is asked to predict each of up to eight columns from the remaining ones, and the spread of its predicted quantiles is used as a measure of uncertainty. The anomaly score is the sum of the log of these spreads over the columns, so rows where the model is more uncertain are ranked as more anomalous. The authors motivate this with a Gaussian argument and a Gaussian process argument in the appendix, but they state that the score is a ranking heuristic and not a calibrated likelihood.

The method is evaluated on 15 ADBench datasets under the OFA-TAD one-class split, where it gets a slightly higher macro AUROC and AUPRC than OFA-TAD (although the difference is not statistically significant).

Critical strengths
  1. The main strength is that the idea is simple and works reasonably well. A frozen general purpose regressor with no anomaly specific pretraining and no per table fitting ends up roughly on par with a dedicated anomaly detection foundation model, and on fraud dataset it reaches AUPRC 0.537 vs 0.387 for OFA-TAD. This matter because if it held up under controlled comparisons it would be a cheap baseline that needs no synthetic anomalies. But as I explain below, the paper does not show that the foundation model is what makes it work.

  2. A smaller strength is that the main evaluation is set up sensibly: natural prevalence test sets, a local Isolation Forest control, dropping an earlier fraud result that was inflated by subsampling, and honest reporting that the Wilcoxon tests are not significant. Unfortunately the same care is not applied to the ablations or to the conclusion.

Critical weaknesses
  1. The score does not measure what the paper claims.

The paper says CoVA-TAD finds rows that break the normal relations between features. To score a row, it hides one column at a time, asks TabICLv2 to predict it from the other columns, and uses how spread out that prediction is as the uncertainty. The problem is that the actual value of the hidden column is never compared to the prediction; it isn't used at all for that column's term. So if a row looks normal everywhere except one column that clearly does not fit the others, the prediction for that column stays confident, and that column adds little to the score. What the score really measures is how unfamiliar the rest of the row looks compared to the 200 normal context rows. That is much closer to a distance from the reference data than to a check of the relations between features.

The theory in the appendix does not fix this. The Gaussian process argument in Appendix B shows that predictive variance grows when a query is far from the context points, but this variance does not depend on the target values at all, so it also describes a distance and not a broken relation. The Gaussian argument in Appendix A has a bigger problem: for Gaussian data the variance of a column given the others is the same for every row, so it can not explain why anomalies would get higher scores. In a Gaussian model it is the prediction error that separates anomalies, which is exactly the part CoVA-TAD leaves out. The authors' own comparison of scoring formulas (Appendix L) includes a version that also uses the prediction error, and it performs worst, which is hard to square with their explanation.

Because of this, it is unclear whether the foundation model adds anything over a simple distance based detector. I would like to see (i) a kNN detector run on the same 200 context rows, (ii) a score based on the prediction error from the same model, (iii) the same pipeline with a simpler regressor in place of TabICLv2, and (iv) results on ADBench's synthetic dependency anomalies [3]. These are rows whose values are each normal on their own but whose combination is not, which is exactly the case the paper claims to handle. The idea of predicting each feature from the others to find anomalies is also not new: FRaC [1] and ALSO [2] do this, scoring the prediction error, and neither is discussed.

  1. The evidence is weak and some numbers can not be reproduced from the code.

The gain over the strongest baseline, OFA-TAD, is small (+0.66 AUROC, +1.79 AUPRC), and the authors' own tests show it is not significant. It also comes mostly from two datasets: if Hepatitis and fraud are removed, CoVA-TAD is slightly behind OFA-TAD on both metrics. The benchmark uses only 15 of the 47 standard ADBench datasets, all with at most 62 features, and every baseline except Isolation Forest is copied from the OFA-TAD paper rather than rerun.

Code repo: I found two results in Table 4 that do not come from the main experiment. (a) The table suggests that raising the small constant ϵ\epsilon in the score from 10−410^{-4} to 10−310^{-3} improves AUPRC from 78.19 to 81.28. But only the 78.19 row is from the main experiment. The rows for larger ϵ\epsilon come from a separate script with a different setup: it does not shuffle the context rows, and it keeps only 2,500 normal test rows for fraud, campaign and shuttle. Removing normal rows makes anomalies more common in the test set, which raises AUPRC by itself, as the paper acknowledges in Appendix G. In that script's own run, ϵ=10−4\epsilon=10^{-4} gives 81.32, the best value of all. So the improvement comes from comparing two different setups, and within one setup ϵ\epsilon makes no real difference. (b) The pima results for context size and number of columns are typed in by hand in generate_visualizations_and_ablations.py (lines 163 to 169), and no script in the repo computes them. They also disagree with the repo's own output: the default setting is reported as 75.20 AUROC / 75.60 AUPRC, but full_test_results.csv gives 74.07 / 74.71 for the same setting.

There are other inconsistencies as well. The seed study is described as measuring the effect of sampling different context rows, but lympho has only 71 reference rows, so all of them are used for every seed, and yet its AUPRC still changes by 12.53 points across seeds. Also, the fraud result, one of the two datasets driving the gain, comes from an earlier run that the authors could not repeat.

  1. Clarity.

The steps of the algorithm are clear enough to reimplement. However, the paper never says that the observed value of a column is not used in that column's uncertainty term, and the introduction and discussion describe the method as if it compares observed values to predictions, so readers will get the wrong idea of what the score does. Some details also contradict each other. Eq. (9) is called "evenly spaced", but for wide tables it never selects the last columns (for campaign, with 62 columns, it only goes up to column 49). Appendix M says breastw and glass have at most 8 features, while Table 5 says 9. Several cross references point to the wrong algorithm, table or appendix. The conclusion claims the method "surpasses all 10 published baselines" and gives "interpretable attributions", which the paper's own results and caveats do not support. Finally, the text in Figures 1, 3 and 4 is too small to read.

[1] Keith Noto et al. FRaC: A Feature-Modeling Approach for Semi-Supervised and Unsupervised Anomaly Detection. Data Mining and Knowledge Discovery, 2012.

[2] Heiko Paulheim et al. A Decomposition of the Outlier Detection Problem into a Set of Supervised Learning Problems. Machine Learning, 2015.

[3] Songqiao Han et al. ADBench: Anomaly Detection Benchmark. NeurIPS, 2022.

Questions for authors

To change my assessment, I would need the controlled comparisons in point 1, a larger benchmark with baselines rerun in the same pipeline, all ablations rerun under the main protocol with the scripts in the repo, and explanations for the inconsistencies above.

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

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