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REVIEW 4 major objections 6 minor 2 cited by

Out-of-Distribution Detection Methods Answer the Wrong Questions

T0 review · 4 major / 6 minor · reviewed 2026-08-06 · deepseek-v4-flash

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Pith's one-line read Out-of-distribution detection methods built on supervised classifiers are fundamentally misspecified: a model trained only on in-distribution classes cannot be expected to identify out-of-distribution points.

desk verdict A genuinely useful reframing of supervised OOD detection, but the 'irreducible error' headline is quantitatively unsupported because the Oracle is a linear classifier, not a ceiling. read the letter →

arxiv 2507.01831 v1 pith:GNM5N2LA submitted 2025-07-02 cs.LG stat.ML

Yucen Lily Li , Daohan Lu , Polina Kirichenko , Shikai Qiu , Tim G. J. Rudner , C. Bayan Bruss , Andrew Gordon Wilson This is my paper
classification cs.LGstat.ML
keywords out-of-distributiondetectionmodelmisspecificationfeature-basedlogit-basedlabeluncertaintyepistemicgenerativelikelihoodsemanticshift
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

This paper argues that the dominant family of out-of-distribution (OOD) detection methods—scoring test inputs by the features, logits, or uncertainty of a supervised classifier trained only on in-distribution data—is fundamentally misspecified. A model trained to separate cats from dogs has no reason to learn what an airplane looks like, so its confidence and feature distances cannot be trusted to say whether an input comes from a different distribution. The authors show the two main families fail in opposite ways: feature-based methods cannot distinguish OOD inputs whose learned features overlap with in-distribution features, and logit-based methods cannot separate label uncertainty from distributional uncertainty. They quantify these failures as irreducible errors using an oracle classifier, and argue that hybrid methods, outlier exposure, Bayesian uncertainty, extra classes, scaling, and generative likelihoods all fail to fix the misalignment. If correct, the conclusion is that current OOD benchmarks reward the wrong objective and that detection should be treated as a task distinct from classification.

What carries the argument

The load-bearing objects are the two scoring families and the oracle used to bound them. Feature-based detectors answer 'does this input land far from training features?'; the paper defines the Oracle—a binary linear classifier trained on the true penultimate-layer features of in-distribution and OOD examples—as the ceiling for any such detector, so (1 − Oracle AUROC) quantifies irreducible error from indistinguishable features, and the gap between a practical method and its oracle-PCA variant quantifies the cost of irrelevant features. Logit-based detectors answer 'is the model unsure which in-distribution label to assign?', and the paper's key distinction is between label uncertainty and OOD uncertainty, demonstrated through multi-label ImageNet images and confidently classified textures. For generative models, the central identity is the Bayes-rule ratio p(OOD|x) ∝ p(x|OOD)/p(x), against which p(x) alone carries no information.

What would settle it

Train a classifier on a fixed in-distribution set, freeze its penultimate features, and compare every feature-based OOD score against the paper's linear oracle trained on true in-distribution and OOD features from a held-out split; any score that beats the oracle's AUROC on the same test set would falsify the claimed floor. A complementary check: find an OOD class (for example, dogs for a cars-versus-trucks classifier) whose features fall inside the in-distribution feature cloud and whose softmax confidence is high, and show a detector separates that pair with near-perfect AUROC—the paper predicts this cannot happen.

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Extended reading notes

Core claim

The paper's central claim is that a classifier trained only on in-distribution classes cannot be expected to identify OOD points. Feature-based detectors answer 'does this input produce atypical features?', but supervised training only shapes features to separate in-distribution classes, so OOD inputs can map onto in-distribution regions or far regions for reasons unrelated to distribution shift; the paper measures the floor this creates by training an oracle binary linear classifier on true in-distribution and OOD features and calling (1 − oracle AUROC) irreducible error. Logit-based detectors answer 'is the model unsure which in-distribution label to assign?', which conflates label uncertainty with OOD uncertainty: multi-label in-distribution images look OOD, while OOD classes such as striped textures look confidently in-distribution. Because the objective is misspecified rather than merely noisy, the paper argues that hybrid feature-logit scores, outlier exposure, epistemic-uncertainty models, explicit OOD classes, and scale all leave the same pathologies, and that unsupervised density estimation fails for the related reason that knowing p(x) does not determine p(OOD|x).

Load-bearing premise

The paper's strongest quantitative claim assumes that a linear classifier trained on the true in-distribution and out-of-distribution features is the best any feature-based detector could ever do; if a nonlinear score on those same features separated the two better, the 'irreducible' errors would be smaller than claimed.

Editorial extensions

If this is right

  • Standard OOD benchmarks mainly reward the wrong objective: improving AUROC on a fixed ID/OOD split does not mean the model has learned to detect inputs from a different distribution.
  • Interventions that currently boost OOD scores—outlier exposure, ensembles, hybrid feature-logit scores, extra classes, and scale—leave the same pathologies, so their gains on benchmarks should be interpreted as limited to those benchmarks.
  • Logit-based detectors will misclassify OOD inputs whenever the OOD class is confidently mapped to an in-distribution label, and will misclassify genuinely in-distribution inputs that are inherently ambiguous, so deployed detectors need to account for both failure modes.
  • Epistemic uncertainty approaches become less discriminative as in-distribution data grows, meaning Bayesian methods should not be assumed to give OOD detection that improves with more data.
  • Generative-model quality and OOD detection performance can move in opposite directions, so likelihood-based detection needs to be replaced by explicit estimates of the likelihood ratio p(x|OOD)/p(x) rather than p(x).

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

  • A testable extension: a detector that estimates p(OOD|x) directly—for example by training an 'anything else' class on a broad, structured set of negatives—should beat every feature and logit score on semantic shift benchmarks; the paper's argument predicts it will do so only when the training negatives are representative of test OOD classes.
  • The Oracle error decomposition suggests a new reporting standard: every OOD method could be evaluated against a linear oracle trained on the same ID/OOD feature split, so benchmark progress is measured as the fraction of a known floor rather than raw AUROC.
  • Extending the generative-model result to practice: likelihood-ratio or typicality-based detectors need a user-chosen coarse-grained representation, and the paper's critique implies that discovering that representation from unlabeled in-distribution data alone is an open problem, since the relevant features are OOD-dependent.
  • The posterior-collapse result implies that Bayesian OOD benchmarks should separate covariate from semantic shift, since epistemic uncertainty may grow on covariate-shifted inputs while shrinking on semantic novelties as in-distribution data increases.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Referee Report

4 major / 6 minor

Summary. The paper argues that the popular family of OOD detection methods built on supervised classifiers trained only on in-distribution classes is fundamentally misspecified. Feature-based methods answer 'are the features far from training features?', logit-based methods answer 'is the model uncertain about the ID label?', and neither question is 'does this input come from a different distribution?'. The authors demonstrate concrete failure modes on ImageNet, CIFAR, and language benchmarks, and argue that common interventions—hybrid feature/logit methods, outlier exposure, Bayesian and ensemble uncertainty, adding an unseen class, scaling model and data size, and generative models—do not resolve the misalignment. They conclude that principled OOD detection requires methods that directly estimate the probability that an input comes from a different distribution.

Significance. If the conceptual argument holds, the paper is an important field-level corrective: it names a systematic objective mismatch, supports it with evidence across dozens of models and several domains, and provides code for reproduction. Several empirical demonstrations are compelling and falsifiable, especially the multi-label ImageNet failure, the 'Striped' class overconfidence, and the Multi-NLI/BART language results. The paper also gives credit where due to prior critiques and distinguishes its claim from incremental benchmark fixes. However, the strongest quantitative claim—that feature-based methods have 'irreducible errors'—is not established by the current oracle construction, because a linear classifier on frozen features is not an upper bound on achievable AUROC. The qualitative misalignment argument is likely to survive, but the 'no easy fix' conclusion is quantitatively overstated in its present form.

major comments (4)
  1. [Section 4.1, Eq. (1) and Figure 2] The linear Oracle is not an upper bound on feature-based OOD detection, so defining (1 − Oracle AUROC) as 'irreducible error' overstates the claim. A binary linear classifier trained on true ID and OOD penultimate-layer features is one element of the set of all score functions on those features; any nonlinear score—a kernel SVM, a nearest-neighbor rule, or a small MLP on the same features—could in principle achieve higher AUROC. Mahalanobis distance is itself quadratic in the features, so the linear Oracle is not even an upper bound on the method family the paper analyzes. The paper calls the Oracle a 'proxy' in one sentence and then treats it as a ceiling in the next; these are incompatible unless the proxy is validated as an upper bound. I recommend either training a nonlinear oracle (e.g., kernel SVM or kNN on frozen features) and reporting its AUROC, or reformulating all 'irreducible error' statements as 'error under linear scoring rules'.
  2. [Section 4.1, Figure 2] The 'irrelevant features' component of the error decomposition is computed with an 'Oracle PCA' whose component count is selected from {32, 64, 128, 256} by maximizing Mahalanobis AUROC on OOD test data. This is acknowledged as an oracle, but it means the reported 'irreducible' part is obtained after removing an optimistically selected subspace, and the decomposition conflates two distinct privileges: access to OOD labels for the linear classifier and access to OOD labels for feature selection. The qualitative conclusion that feature selection is hard without OOD data is well supported, but the specific numbers in Figure 2 (left) should be reported with standard errors over seeds and with a clear statement that both oracle components use OOD labels.
  3. [Section 5.3, Figure 6] The claim that epistemic uncertainty becomes less useful for OOD detection as more ID data is observed rests on a single last-layer Laplace approximation experiment on three CIFAR-10 classes, with AUROC values 0.769, 0.764, 0.741, and no error bars or multiple seeds. The differences are small relative to plausible stochasticity, yet Section 6 generalizes this to 'Bayesian methods and ensembles ... become worse at distinguishing between in-distribution and OOD points as we acquire more in-distribution data.' This load-bearing conclusion needs additional replicates, a second setting, and ideally a quantitative measure of posterior contraction before it can support the paper's strong wording.
  4. [Section 5.5, Figure 8] The scaling analysis states that even ViT-G/14 DINOv2 has 'over 5% irreducible error due to indistinguishable features.' This inherits the linear-Oracle problem from Section 4.1, and the gap between the best method and the Oracle is described as if it were a clean decomposition into 'indistinguishable' and 'irrelevant' features. Since the Oracle is trained with OOD labels, the gap is an upper bound on what could in principle be gained from better methods plus oracle feature selection; it is not a lower bound on unavoidable error. Please rephrase the scaling conclusions to avoid claiming quantitative irreducibility, or provide a non-oracle lower bound.
minor comments (6)
  1. [Section 5.6] The sentence 'We demonstrate the OOD detection performance of diffusion' is incomplete and is immediately followed by 'In Appendix A.6, we discuss additional pathologies'; please complete or delete this sentence.
  2. [Table A.1] The table and caption use 'FPR@95' to mean the fraction of OOD examples classified as ID at a threshold where 95% of ID examples are correctly classified; this is a false-negative rate for the OOD class, not the standard FPR@95 used in the OOD literature, and should be renamed (e.g., FNR@95) or defined unambiguously to avoid confusion.
  3. [Figure 4] The y-axis label 'IN-ODD AUROC' is a typo and should read 'IN-OOD AUROC'.
  4. [Appendix A.2] The text contains the typo 'the OOD class of od dogs' in the LeNet-5 demonstration; it should read 'the OOD class of dogs'.
  5. [References] The reference list contains duplicate Nalisnick et al. entries: the 2019 and 2020 entries have the same title 'Detecting out-of-distribution inputs to deep generative models using typicality'; please consolidate or disambiguate them.
  6. [Section 5.2, Figure 5] The outlier-exposure generalization results are averaged over three seeds, but Figure 5 shows no error bars; given that the claim of a >10% accuracy drop is central to the critique of outlier exposure, please add error bars or confidence intervals.

Circularity Check

0 steps flagged · score 0.0 of 10

No circularity: the central 'wrong questions' argument is supported by external benchmarks, pretrained checkpoints, and explicitly labeled oracle analyses, not by fitting inputs and reporting them as predictions.

full rationale

The paper's load-bearing claims—that supervised classifiers trained only on in-distribution classes are misspecified for OOD detection, that logit-based methods conflate label uncertainty with OOD uncertainty, and that feature-based methods suffer from indistinguishable and irrelevant features—are argued conceptually and tested against external benchmarks and pretrained models. The Oracle binary classifier in Section 4.1 is trained on true ID and OOD features and is explicitly called a 'proxy for the best possible performance'; defining (1 − Oracle AUROC) as 'irreducible error' is an optimistic upper-bound assumption, not a circular reduction, because the Oracle is not fitted to the methods being critiqued and its output is not fed back as a fitted prediction. Similarly, the 'Maha with Oracle Features' / 'Oracle PCA' procedure in Appendix A.1 selects PCA components using OOD test data and is explicitly described as using 'the true ID and OOD features, which is not possible in realistic settings'; this inflates an upper bound but is not presented as a held-out prediction. The paper's self-citations (e.g., Kirichenko et al. 2020 on normalizing flows, Wilson and Izmailov 2020 on ensembles, Rudner et al. 2022 on Bayesian methods) are background context and are not load-bearing for the central misspecification argument. No equation is defined in terms of the conclusion it is supposed to establish, and no fitted parameter is renamed as a prediction. The derivations and demonstrations are therefore self-contained with respect to the paper's own claims, and any weakness in the Oracle-as-ceiling assumption is a correctness concern rather than circularity.

Assumptions & free parameters 1 free parameters · 4 assumptions · 0 invented entities

The paper adds no physical or algorithmic entities. Its argument relies on standard probability and information theory, plus the Oracle proxy assumption, which is the main ad hoc modeling choice. All empirical quantities are measured on existing datasets and models.

free parameters (1)
  • Oracle PCA component count = selected from {32, 64, 128, 256} to maximize AUROC on OOD test set
    In Section 4.1 and Appendix A.1, the 'Maha with Oracle Features' upper bound is computed by choosing the number of principal components that gives the highest Mahalanobis AUROC on the target OOD data. This is a parameter fitted to test data, so the resulting 'irrelevant features' error is an oracle quantity, not an achievable method.
assumptions (4)
  • ad hoc to paper A binary linear classifier trained on true ID and OOD penultimate-layer features is an upper bound on the AUROC achievable by any feature-based OOD detection method.
    Introduced in Section 4.1 to define the Oracle and quantify 'irreducible error'. Not derived; if a nonlinear feature-space method can separate better than the linear Oracle, the irreducible-error estimate is too high.
  • standard math The predictive entropy decomposition H(pred) = aleatoric + epistemic implies that in the infinite-data limit epistemic uncertainty vanishes, so epistemic uncertainty cannot by itself indicate OOD.
    Section 5.3 uses this standard identity and the posterior collapse phenomenon to argue Bayesian and ensemble methods are misaligned with OOD detection.
  • domain assumption OOD detection is defined as determining whether an input comes from a different distribution, with a meaningful distinction between semantic and covariate shift.
    Section 2 and Section 6 define the task this way; the entire misspecification argument depends on this definition of the goal.
  • standard math For generative models, the quantity of interest for OOD detection is p(OOD|x), which by Bayes' rule is proportional to p(x|OOD)/p(x), and knowing p(x) alone is insufficient.
    Section 5.6 and Appendix A.6 use this decomposition to argue density estimation is not aligned with OOD detection.

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Cite this review

Pith. "Pith review of Out-of-Distribution Detection Methods Answer the Wrong Questions." pith.science (2026). https://pith.science/paper/GNM5N2LA

@misc{pith2026250701831,
  author       = {Pith},
  title        = {Pith review of: Out-of-Distribution Detection Methods Answer the Wrong Questions},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/GNM5N2LA}},
  note         = {Machine review of arXiv:2507.01831}
}
read the original abstract

To detect distribution shifts and improve model safety, many out-of-distribution (OOD) detection methods rely on the predictive uncertainty or features of supervised models trained on in-distribution data. In this paper, we critically re-examine this popular family of OOD detection procedures, and we argue that these methods are fundamentally answering the wrong questions for OOD detection. There is no simple fix to this misalignment, since a classifier trained only on in-distribution classes cannot be expected to identify OOD points; for instance, a cat-dog classifier may confidently misclassify an airplane if it contains features that distinguish cats from dogs, despite generally appearing nothing alike. We find that uncertainty-based methods incorrectly conflate high uncertainty with being OOD, while feature-based methods incorrectly conflate far feature-space distance with being OOD. We show how these pathologies manifest as irreducible errors in OOD detection and identify common settings where these methods are ineffective. Additionally, interventions to improve OOD detection such as feature-logit hybrid methods, scaling of model and data size, epistemic uncertainty representation, and outlier exposure also fail to address this fundamental misalignment in objectives. We additionally consider unsupervised density estimation and generative models for OOD detection, which we show have their own fundamental limitations.

Figures

Figures reproduced from arXiv: 2507.01831 by the authors.

Figure 1
Figure 1. There are irreducible errors when using supervised models for OOD detection because the problem is inherently misspecified. Supervised models can only determine if an input leads to atypical representations or uncertain predictions, which is fundamentally different than determining if the input belongs to the training distribution. When training on ID data (left), the model accurately clusters the features by class … view at source ↗
Figure 2
Figure 2. Feature-based methods have two key failure modes: indistinguishable features and irrelevant features. (Left): The error decomposition of Mahalanobis distance into irrelevant features, indistinguishable features and other components. (Right): The most relevant features for OOD detection are specific to each OOD dataset. For ViT-S/16 features, selecting the features that are the most discriminative for one OOD dataset… view at source ↗
Figure 3
Figure 3. Logit-based methods incorrectly conflate label uncertainty with OOD uncertainty. (Left): The circles show OOD detection on standard ImageNet vs ImageNet-OOD, while the triangles show degraded performance when comparing a subset of ImageNet samples (“Multi-label”) against ImageNet-OOD. The histogram shows that the multi-label subset has significantly higher label uncertainty compared to other ID inputs. (Right): All … view at source ↗
Figures from the paper (5 more)
Figure 4
Figure 4. Figure 4: Hybrid OOD methods (ViM, Hybrid-Add) do not consis￾tently outperform stand-alone feature-based methods (Maha) and logit-based methods (MSP) and suffer from the same pathologies. Hybrid approaches that combine model features and logits have been proposed for OOD detecti…
Figure 5
Figure 5. Figure 5: Training a ResNet-18 with outlier exposure hurts OOD generalization for covariate shifts compared to standard training. Another popular approach to improve OOD detection is outlier exposure, which incorporates OOD examples when training the model (Hendrycks et al., 201…
Figure 7
Figure 7. Figure 7: Adding an OOD class is only effective if the train OOD examples are similar to test OOD examples. lasidasan et al., 2020). During training, we can then expose models to OOD examples, and use this additional class for OOD detection on test samples. However, we find this…
Figure 8
Figure 8. Figure 8: Even scaling to ViT-G/14 DINOv2 pre-trained on internet scale data (right-most), the best method still contains significant error from indistinguishable features and irrelevant features. Increasing model size and pre-training on large datasets have been shown to reliab…
Figure 9
Figure 9. Figure 9: Better generative models of ID data can lead to worse OOD detection. (Left): We create GMMs for ResNet-50 ImageNet features with various covariance matrices ranging from the empirical covariance estimations to identity matrix. The models which better fit the ID data ha…

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Forward citations

Cited by 2 Pith papers

Reviewed papers in the Pith corpus that reference this work. Sorted by Pith novelty score.

  1. Decodable but Not Detectable: A Leakage Fingerprint for Near-OOD Benchmarks

    cs.LG 2026-07 conditional novelty 7.0 of 10

    A trained class left in the detector's fit set and reused as 'OOD' flips AUROC from 0.326 to 0.911 when removed, and a supervised-decodability plus unsupervised-collapse fingerprint detects such leaks (sensitivity 18/...

  2. Beyond Binary Out-of-Distribution Detection: Characterizing Distributional Shifts with Multi-Statistic Diffusion Trajectories

    cs.LG 2025-10 unverdicted novelty 7.0 of 10

    DISC extracts multi-statistic trajectories from diffusion denoising to both detect and classify types of distributional shifts in OOD data.

Reference graph

Works this paper leans on

13 extracted references · 12 canonical work pages · cited by 2 Pith papers

  1. [1]

    ResNet-18 trained on ImageNet-1k

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  2. [2]

    ResNet-34 trained on ImageNet-1k

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  3. [3]

    ResNet-50 trained on ImageNet-1k

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    ViT-S/16 trained on ImageNet-1k

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    ViT-B/16 trained on ImageNet-1k

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    ViT-S/16 trained on ImageNet-1k with DINO

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    ViT-B/16 trained on ImageNet-1k with DINO

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    ViT-B/16 trained with CLIP

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Show all 13 references
  1. [9]

    ViT-L/14 trained with CLIP

  2. [10]

    ViT-B/16 pretrained on CLIP, finetuned on ImageNet-1k

  3. [11]

    ViT-B/14 trained on 142M images with DINOv2

  4. [12]

    ViT-G/14 trained on 142M images with DINOv2 26

  5. [2021]

    Oracle PCA

    URL https://proceedings.mlr.press/ v130/morningstar21a.html. Eric Nalisnick, Akihiro Matsukawa, Yee Whye Teh, Dilan Gorur, and Balaji Lakshminarayanan. Do deep generative models know what they don’t know? arXiv preprint arXiv:1810.09136, 2018. Eric Nalisnick, Akihiro Matsukawa...

    2021 arXiv

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Reviewed August 6, 2026 · model on record in the stance chip above.