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Under review as a conference paper at ICLR 2027

AdaGeo: Adaptive Local Geometry Modeling for Long-Tail Out-of-Distribution Detection

Abstract

Long-tailed class imbalance presents a fundamental challenge for out-of-distribution (OOD) detection. Limited supervision yields sparse, unreliable representations for tail classes, and large intra-class variation prevents class-level representations from fully capturing the geometric structure of head classes. We observe that these head-class features often form multiple compact local structures rather than concentrating around a single global prototype. This motivates us to reconsider long-tailed OOD detection from the perspective of geometry modeling. Specifically, we propose AdaGeo, an adaptive local geometry framework that represents each class with multiple geometric components and jointly exploits their location, compactness, and empirical support. Based on this representation, we introduce a density-aware geometry learning objective that assigns stronger supervision to samples that deviate from their matched centers relative to the local geometric scale. Further, to keep this learned geometry aligned with the available evidence, we propose an adaptive mechanism that removes redundant local components according to their effective support and compactness. At the inference phase, we combine the global energy-based confidence with local geometric evidence, including intra-class cohesion and inter-class separation, to obtain a geometry-aware OOD score. Experiments on CIFAR-10-LT, CIFAR-100-LT, and ImageNet-LT demonstrate that AdaGeo improves in-distribution (ID) classification accuracy over the evaluated baselines and achieves competitive OOD detection performance, with the best average OOD results on CIFAR-100-LT and ImageNet-LT.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
OOD detection, long-tail recognition, adaptive local geometry, multi-center learning, density-aware reweighting, energy-based OOD scoring

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_gBu6OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
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Paper summary

This paper studies OOD detection under long-tailed distributions. The authors observe that ID class features often form multiple compact local structures beyond a single-center prototype, and propose AdaGeo: each class maintains an adaptively controlled geometric memory; geometric evidence is mixed into the classification logits with a weight during training; at inference, the energy score is fused with a geometric confidence that combines local cohesion and inter-class separation. The paper reports competitive results.

Critical strengths
  1. Clear motivation: the held-out multi-center distortion diagnosis directly supports the core observation that a single center is insufficient to characterize intra-class variation, and the conclusion holds consistently across the many/medium/few frequency groups.
  2. Training uses only ID data throughout (the auxiliary OOD set is used only for a one-time post-hoc calibration of α\alpha), and the method is 1.60–1.86× faster than PATT, which is practically appealing.
  3. ID classification accuracy is the best among all compared methods on all three benchmarks, with positive ACC gains over PATT.
Critical weaknesses
  1. The compared baselines are not comprehensive. PATT was published at AAAI 2025, and several related works have appeared over the past year, such as RSCL[1] (CVPR 2026, dynamic class-wise temperature + informative outlier mining), but none of them are compared.
  2. The post-hoc baselines are only MSP / Energy, etc.; the paper does not compare against recent strong post-hoc scoring baselines. The key question is: on the same geometry-trained encoder, directly applying post-hoc scoring methods — is it possible to achieve comparable or even better OOD performance without the geometric memory? In addition, BERL is cited but not included in the main comparison table.
  3. The paper does not run experiments on class-balanced ID data. Although this paper is mainly about LT data, I would like to see whether the geometric modeling is a general contribution. Under balanced data, the method should reduce to a "fixed multi-prototype + filtering by compactness/support" model, which can be directly compared with multi-prototype methods on standard OOD benchmarks. Moreover, under balanced data Logit Adjustment degenerates to plain CE and the "imbalance compensation" motivation of the density-aware re-weighting also disappears; only the remaining gains (if any) can then be attributed to the geometric modeling itself rather than to long-tail compensation.
  4. Too many hyperparameters and incomplete ablation. The paper newly introduces KK, kbasek_{\text{base}}, λBIC\lambda_{\text{BIC}}, EwarmE_{\text{warm}}, βm\beta_m, βr\beta_r, r0r_0, λgeo\lambda_{\text{geo}}, λLA\lambda_{\text{LA}}, τ\tau, μ\mu, etc. If I read the paper correctly, only KK, τ\tau, μ\mu, λBIC\lambda_{\text{BIC}} have sensitivity analyses, and only on the CIFAR-100-LT dataset. The overall construction is complex, but the experimental gains are limited (average AUROC on CIFAR-10-LT ties with PATT at 91.50 vs 91.50; CIFAR-100-LT +1.37; on SVHN the FPR95 of 9.84 vs PATT's 4.95 is clearly worse), which raises my concern that the gains may come from hyperparameter cherry-picking. In addition, τ\tau serves three purposes (shared across sample re-weighting, geometric logits, and inference-time cohesion), μ\mu enters both the training supervision and the OOD scoring through the combined logits, and the paper does not specify whether the energy score E(x)E(x) operates on the raw classification logits or the combined logits; such structural couplings cannot be attributed through one-at-a-time sweeps either.
  5. The OOD gains are unevenly distributed, in contrast to what the abstract suggests. Appendix B.2 shows that tail-class ACC improves (+6.04 / +8.96), yet tail-group OOD detection becomes slightly worse (AUROC −0.33/−0.12, FPR95 +1.96); the OOD gains concentrate in the well-supported many/medium groups. The paper itself admits that the tail-group OOD gap "is bounded by scarce supervision rather than by the learned geometry"; the geometric modeling therefore contributes little to the tail-group OOD scenario that needs help the most.

[1] Feng, Shuai, et al. "Long-tailed out-of-distribution detection with refined separate class learning." Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2026.

Questions for authors

See Weaknesses.

5 comments
AuthorsOpenReview ↗

Thank the reviewer gBu6 very much for all comments.

Response to Reviewer gBu6

To W1: The main concern is whether the main tables are comprehensive. We address it below.

Our baselines are sufficiently comprehensive and reasonable. The main tables of Section 5.2 add RSCL (CVPR 2026) which we did not obtain through DBLP and Google Scholar previously. We thank the reviewer for recommending this new paper. The compared methods now cover the representative work of this line over the five years from 2022 to 2026. RSCL is evaluated on the same data split, the same six SC‑OOD test sets and the same metric implementation, so the protocol matches ours. Across the two benchmarks, AdaGeo has the best ACC and FPR95 of the three methods. On CIFAR‑100‑LT all five metrics lead: ACC is higher by a large margin of 7.88 points, and AUROC and FPR95 are better by 1.27 and 0.88 points. On CIFAR‑10‑LT ACC is higher by 8.39 points, AUROC ties with PATT at 91.50, and FPR95 is the lowest of the three. To summarize, our method is still competitive.

MethodCIFAR‑10‑LTCIFAR‑10‑LTCIFAR‑10‑LTCIFAR‑10‑LTCIFAR‑10‑LTCIFAR‑100‑LTCIFAR‑100‑LTCIFAR‑100‑LTCIFAR‑100‑LTCIFAR‑100‑LT
ACCAUROCAUPR‑InAUPR‑OutFPR95${{({{↓}})}}$ACCAUROCAUPR‑InAUPR‑OutFPR95${{({{↓}})}}$
PATT84.69±0.291.50±0.191.33±0.389.60±0.231.33±0.749.51±0.575.36±0.277.00±0.369.46±0.164.01±0.3
RSCL77.72±0.3492.78±0.1691.95±0.1792.60±0.2130.83±0.5244.17±0.2975.46±0.6777.00±0.8170.60±0.4464.35±1.14
AdaGeo86.11±0.391.50±0.191.55±0.189.63±0.130.55±0.152.05±0.276.73±0.177.66±0.171.32±0.363.47±0.4
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To W2: The main concern is twofold: (i) whether detection of comparable or better quality can be obtained on the same encoder without the geometric memory, and (ii) why BERL is not in the main table.

As for the first concern, the following two points address it:

  1. On the same encoder, geometric scoring is above every post‑hoc score. On CIFAR‑100‑LT we fix the trained encoder and replace only the inference score, comparing energy alone, ReAct + energy, global kNN and MSP; the kNN feature bank and the ReAct threshold are both estimated from ID training features.
Scoring methodAUROCAUPR‑InAUPR‑OutFPR95
MSP70.4772.1265.8571.73
Global kNN75.6676.2371.4865.61
ReAct + energy75.7276.6269.9264.60
Energy only76.1276.8470.9464.82
AdaGeo (energy + geometry)76.7377.6671.3263.47

We can see from the above table that, averaged over the six sets, AdaGeo is best on AUROC, AUPR‑In and FPR95. Fitting a post‑hoc score to this encoder does not improve detection, whereas the geometric term raises AUROC to 76.73 and lowers FPR95 by 1.35 points.

  1. Without the geometric memory the gap is larger. The first row of the ablation table (Section 5.2) is the configuration with no multi‑centre components, no density‑aware learning and no geometric score; AUROC on CIFAR‑100‑LT is 73.27, 3.46 points below the full configuration. Using geometry for training only and reverting to energy at inference gives 76.12, still 0.61 points lower. The geometric memory produces an increment at both ends: from 73.27 to 76.12 in training, 2.85 points, and from 76.12 to 76.73 in inference, 0.61 points. The former cannot be replaced by any post‑hoc score, and the latter is exactly the increment measured in the above table; the geometric memory is not an add‑on that post‑hoc scoring can stand in for.

As for the second concern, it can be addressed by the two points below.

‑ Different budget: BERL is initialized with long‑tailed self‑supervised pre‑trained weights and fine‑tuned for 20 epochs, while all methods in our main tables are trained from scratch. Directly grouping BERL alongside others within the same table would mainly reflect performance gaps stemming from backbone capacity and pre‑training corpora, rather than algorithmic improvements for long‑tailed OOD — which is the focus of our paper. Indeed, the CIFAR‑LT main tables of RSCL, PATT and EAT also exclude BERL under identical experimental conditions.

‑ Different role: Citation and a table entry serve different purposes. We cite BERL to highlight that our method is orthogonal to theirs, and thus numerical juxtaposition is unnecessary. By contrast, table entries demand results obtained under identical experimental protocols. In fact, BERL reports substantially lower in‑distribution (ID) accuracy compared with our approach and other baselines: 41.05 versus 52.05 on CIFAR‑100‑LT, an 11‑point gap. Its OOD detection metrics are produced by a model with much weaker closed‑set performance. Including BERL in the main table would mislead readers into treating it as an apples‑to‑apples baseline, despite the divergent starting conditions. For this reason, we discuss BERL via in‑text citation of its technical contribution rather than including it in the numerical table. This practice aligns with the main CIFAR‑LT tables of PATT and RSCL.

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To W3: The main concern is whether geometric modelling constitutes a general contribution, or merely a compensatory mechanism for longtailed imbalance. We address it below.

  1. One concept has to be separated first, because it decides how the experiment is read: the density used in density‑aware learning is the count of components within a class, not the class frequency. In Eq. (10), the log count of each component is shifted by the largest component of the same class:

bc,k=log max(nc,k,1)−maxk'∈Kc log max(nc,k',1),

where nc,k is the cumulative assignment count of component (c,k). Balanced data equalizes Nc across classes, but nc,k stays uneven within a class, so bc,k remains non‑zero under balanced data and does not disappear with the imbalance.

  1. The sample weight in Eq. (9) contains no frequency either. Its numerator and denominator are both the geometric unreliability 1−ρgeo, normalised within the batch:

w(f,y)=(1−ρgeo(f,y))/(1/B Σi[1−ρgeo(fi,yi)]).

It contains no class frequency, no prior, and no Nc: a head sample and a tail sample aligned equally well with their matched components receive the same weight. The only term that does become uniform under balanced data is the prior πy in LLA, which is exactly why the balanced experiment is a clean test of the remaining parts.

  1. We trained AdaGeo, PATT and RSCL on balanced CIFAR‑100 and evaluated them on the same six OOD test sets:
MethodACCAUROCAUPR‑InAUPR‑OutFPR95
PATT73.1480.6083.3373.8451.74
RSCL72.2884.4185.9878.9647.24
AdaGeo76.9285.2785.7480.5646.71

We can see from the table that on balanced datasets, AdaGeo achieves the best overall performance. It yields higher ACC and AUROC alongside lower FPR95. This further demonstrates that the ACC advantage cannot be attributed to longtailed compensation: under balanceddata settings, logit adjustment reduces to standard crossentropy and prior correction no longer takes effect. Consequently, the remaining performance gain must stem from geometric modelling itself. With these results, we believe the reviewer’s concern is largely addressed.

  1. To further bring out the contribution of geometric modelling, we separate the training and inference contributions: we fix one checkpoint and switch only the geometric term in the score.
Scoring (same checkpoint)AUROCAUPR‑InAUPR‑OutFPR95
Energy only84.3185.3878.6548.25
With the geometric term85.2785.7480.5646.71
Δ+0.96+0.36+1.91−1.54

The results above show that the inferenceside performance increment does not shrink under balanceddata settings. AUROC improves and FPR95 degrades by magnitudes comparable to those observed in the longtailed setting, demonstrating that geometric scoring does not depend on prior correction. This ablation row further pinpoints the source of performance gains. With geometric scoring switched off, AUROC reaches 84.31 — nearly on par with RSCL’s 84.41 and 3.71 points above PATT’s 80.60. Therefore, the advantage over baselines under balanced data mainly stems from densityaware learning on the training side, while the inferenceside geometric term adds a further 0.96 points.

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

This paper proposes AdaGeo for long-tailed OOD detection, combining adaptive multi-center representations, local geometry-aware sample weighting, and geometry–energy score fusion. Experiments on CIFAR-10-LT, CIFAR-100-LT, and ImageNet-LT demonstrate improved ID classification and competitive OOD detection performance.

Critical strengths
  1. Controlling representational complexity according to training support and reusing local geometric statistics for both learning and detection are appropriate for long-tailed data. The method is well motivated and the evaluation is reasonably comprehensive.

  2. The experiments cover three major benchmarks and include per-dataset results, multiple runs, component ablations, and analyses across imbalance ratios.

  3. ID classification improves on all three benchmarks, with detection gains on several OOD datasets. Encoder training requires no auxiliary OOD images and takes less time than PATT.

Critical weaknesses
  1. Detection gains are uneven across OOD datasets. On ImageNet-LT, the average improvement is largely driven by DTD, while performance declines on SUN and Places365. The results support improved average performance, but provide limited evidence of consistent gains across different unknown distributions.

  2. The impact of auxiliary OOD calibration is insufficiently evaluated. Although the encoder is trained exclusively on ID images, the full pipeline uses auxiliary OOD data for feature calibration or fusion-weight selection. Results with alternative calibration sources or without auxiliary OOD calibration are missing, and the training-time comparison excludes calibration costs.

Questions for authors
  1. What explains the substantial improvement on DTD but degradation on SUN and Places365 under ImageNet-LT? Which distributional characteristics affect the effectiveness of geometric scoring?

  2. How sensitive is the final performance to the auxiliary OOD calibration source? Could the authors report results without auxiliary OOD calibration and the total cost including calibration?

1 comment
AuthorsOpenReview ↗

Thank the reviewer uzZS very much for all comments.

Response to Reviewer uzZS

To W1/Q1: The comments raise three concerns: (i) which distributional characteristics decide the effectiveness of geometric scoring, (ii) why DTD improves substantially on ImageNet‑LT while SUN and Places365 decline, and (iii) whether the gain is consistent across different unknown distributions. We address them in turn.

  1. Deciding the effectiveness of geometric scoring is how far an OOD image overlaps with the local structure of ID classes. The geometric term measures how well a sample matches the local component centers of each class: if an OOD image barely lands on the local structure of any ID class, “1−Q” supplies the separation that energy scoring lacks, where Q refers to the mean geometric confidence. To quantify this overlap, we ran an inference diagnostic with the trained encoder, counting for each image how many ID classes it matches at the local level, averaging those counts by dataset, and recording the mean geometric confidence Q. From this table, we can see that datasets with lower mean matched ID classes and smaller Q yield larger gains when incorporating geometric scoring; this geometric information helps separate ID classes from unknown distributions more effectively.
DatasetMean matched ID classesMean QΔAUROC with geometry
DTD1.910.167+9.3
iNaturalist2.220.210+3.4
SUN2.500.262−0.6
Places3652.710.277−0.2
ID validation (reference)2.720.341—
  1. As for the second concern (why DTD yields substantial improvements while SUN and Places365 do not), the underlying factor lies in whether the semantics of OOD images overlap with the local structure of ID classes, rather than our method inherently favoring certain distributions. DTD consists of texture images whose local structures barely overlap with any ID class. For such inputs, energy‑based scoring itself performs poorly for ranking, and DTD is the hardest subset among its four splits for every baseline. Our geometric term provides exactly the missing separation, lifting the AUROC from 83.61 to 92.88. In contrast, SUN and Places365 contain scene images. Their local structures heavily overlap with the local centers of multiple ID classes, at a level comparable to the ID validation set. Consequently, the geometric term carries little additional information, leading to negligible performance changes (−0.2 and −0.6 are negligible effects rather than degradations). The gain therefore emerges where existing methods struggle most: the geometric term compensates for the limitations of energy scoring when OOD semantics are far from ID, while leaving results unchanged when energy scoring already works adequately.

  2. The gain is consistent across distributions. The changes across the four sets, ranging from +9.3 to −0.2, follow a single monotonic trend with no counterexamples in the opposite direction: the lower the overlap, the larger the gain, and the gain approaches zero as the overlap approaches that of the ID validation set. In other words, the gain does not fluctuate arbitrarily across datasets; it varies monotonically with this measurable structural overlap quantity. Thus, knowing the overlap between an OOD set and local ID structures is sufficient to predict the improvement brought by the geometric term.



To W2/Q2: The main concerns are (i) how strongly calibration depends on auxiliary data, and (ii) the total cost once calibration is included. We address them in turn.

  1. Final performance is robust to the source of auxiliary OOD calibration. The result without any auxiliary OOD calibration is already in the ablation table (Section 5.3). Calibration selects only the fusion weight α, and the candidate set for α contains 0; with no auxiliary data, calibration stops at α=0; the geometric term is multiplied by zero, and the score falls back to energy alone. To further confirm that the auxiliary set is not hand‑picked, we reduce its size by halving the TinyImages images used for calibration on CIFAR‑100‑LT at random, and recalibration still selects the same result as before. (Actually, our responses to R1‑W3 also validate that performance is insensitive to the choice, quality or diversity of the auxiliary data.)

  2. We have re‑measured the total cost including calibration. On ImageNetLT, the forward pass over the ID partition of the calibration set takes 1,303 seconds, accounting for 1.8% of total training time. When this overhead is included, the combined cost of training plus calibration forward passes totals approximately 20 hours and 55 minutes. Note that PATT’s reported 37 hours and 37 minutes in Table 4 of their paper excludes its own posthoc calibration.

Reviewer_CqqnOpenReview ↗
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2
Confidence
4
Informativeness
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Soundness
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Paper summary

This paper proposes representing in-distribution classes with multiple local centers to improve OOD detection. The number of centers is adapted to each class’s frequency.

Critical strengths
  1. The paper is clearly written and easy to follow.

  2. The method achieves consistent improvements over the evaluated baselines on several benchmarks.

Critical weaknesses
  1. The novelty is limited. The method appears to be an incremental combination of existing ideas, without a substantial new technical insight. Representing classes with multiple centers is a well-established direction. The main contribution is to apply this idea to long-tailed OOD detection and the PATT framework. I am not convinced that this level of contribution is sufficient for a top-tier conference.

  2. The compared baseline methods are insufficient. The evaluation focuses on a limited set of methods, with PATT serving as the primary point of comparison. OOD detection has a long history and includes a broad range of approaches, but the paper does not cover several relevant categories, such as representation-learning-based or synthetic-data-based methods. In particular, recent vision-language models (VLMs) offer strong visual representations that can support OOD detection through embedding-based scores or few-shot prompting. The absence of VLM-based comparisons makes it difficult to assess AdaGeo’s progress relative to current alternatives.

  3. The method requires auxiliary OOD data for calibration before evaluation, which limits its practicality. Moreover, the auxiliary OOD datasets used in the experiments are diverse and of high quality. So it is unclear whether the method would perform as well with less diverse or lower-quality auxiliary data. How sensitive is performance to the choice and diversity of the auxiliary data? For example, would it change if calibration used images from only a few TinyImages categories? The paper also does not clearly explain how each baseline uses auxiliary OOD data. Some baselines may not require such data, which could make the comparisons unfair.

  4. The group-wise results suggest that the OOD detection gains come primarily from head and medium-frequency classes, while performance on tail classes does not improve. This raises a concern about the paper’s motivation. If the gains are concentrated in head classes, what does AdaGeo contribute specifically to long-tailed OOD detection? The authors should clarify why this setting is appropriate and demonstrate that the method addresses the tail-class detection challenge, rather than primarily improving OOD detection for well-represented classes.

Questions for authors

See my comments in weaknesses.

12 comments
AuthorsOpenReview ↗

Thank the reviewer Cqqn very much for all comments.

Response to Reviewer Cqqn

To W1: The main concern is about novelty and contribution. We next address them one by one.

We respectfully disagree that the novelty is limited. Specifically, the novelty of our work is at least fourfold:

  1. To the best of our knowledge, AdaGeo is the first work to represent classes with multiple centers for long‑tailed OOD detection. Note that, although other works such as P‑ODN (Shu et al., 2020) and MGPL (Liu et al., 2023) use multiple centers in multi‑prototype learning, they focus on other problems instead of long‑tailed OOD detection. In addition, we must emphasize that although representing classes with multiple centers is a well‑established direction, our method is significantly different from existing multi‑centers methods, such as how the number of centers is determined and how multi‑centers geometry is used; this will be clarified in the next paragraphs.

  2. Our method adaptively estimates how many centers each class can reliably support from training evidence. Note that, existing multi‑prototype learning methods such as Sub‑center ArcFace (Deng et al., 2020) and MPCL (Jia et al., 2025) fix the number of centers in advance.

  3. Our method uses the estimation to drive both training supervision and inference‑time scoring. In contrast, the prototypes in existing learning methods either serve for classification during training or scoring at inference, not both.

  4. Last but not least, none of the existing longtailed OOD detection papers defines componentlevel reliability based on each prototype's radius. This idea is also thoroughly new in OOD detection community. Through reliability, our method builds a closed loop where the same geometric reliability governs both training supervision and inference‑time OOD scoring. This is a real new technical insight.

On the other hand, the main contributions of our work are threefold at least:

  1. We introduce Adaptive Multi‑Center Geometry Modeling, which couples online estimation of local component statistics with class‑dependent complexity control to accommodate imbalanced training support. Note that, our method is not an incremental combination of existing ideas, since basic ideas of our method are obviously different from the so‑called existing ideas. For example, recall the clarifications in the previous paragraphs, we can easily understand that our multicenter geometry modeling method is significantly different from existing multiprototype learning methods: our method adaptively estimates the number of centers while the latter use a fixed number; our method defines componentlevel reliability while the latter do not, to mention just a few.

  2. We couple Density‑Aware Geometry Learning with Geometry‑Aware OOD Scoring, leveraging a shared local representation to guide training supervision and augment energy‑based detection with cohesion and separation evidence. This is the real new technical contribution. None of existing works developed such a technique/strategy.

  3. Besides the framework and technical‑level contributions above, important experimental results are also our contributions, since they provide interesting and insightful findings for the readership in relevant research fields. Specifically, we conduct extensive experiments on standard long‑tailed benchmarks. The results demonstrate improved ID classification and competitive OOD detection. Moreover, AdaGeo requires less training time than PATT, as it does not leverage outlier evidence during training.

We emphasize that "using multi‑centers to address the limitation of PATT method" is just an initial idea, or a highly simplified one‑sentence description of our method, and it is obviously not equivalent to our main contributions. Note that, treating such a highly simplified description as a paper’s main contribution while ignoring technical details easily introduces bias.

With the above clarifications, we sincerely hope and believe the reviewer's concern about novelty and contribution has been basically alleviated.

AuthorsOpenReview ↗

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To W2: one main concern is why the compared methods do not include representation‑learning‑based, synthetic‑data‑based or VLM‑based approaches. We address each point below.

  1. Representation‑learning‑based methods are already inside the main tables. The methods we compare, PASCL (ICML 2022, asymmetric contrastive learning), MGPL (2023, multiple Gaussian prototypes), EAT (AAAI 2024, tail‑class augmentation with abstention classes) and PATT (AAAI 2025, implicit semantic augmentation), all belong to this category.

  2. Synthetic‑data‑based methods differ substantially from our experimental condition. They synthesise pseudo‑outliers from a generator or from class‑conditional distributions in feature space, and use them as a training or calibration signal; our training uses ID images only, so the training signal itself differs. More importantly, how far a pseudo‑outlier sits from ID is decided directly by the sampling radius, the generator's capacity and the sampling strategy. It is an adjustable quantity, not the real distribution shift under test. Measured against such a reference, what is reported is how far the synthesiser pushes samples away from ID, not how well a method tells apart real unknown distributions. In short, comparing with synthetic‑data‑based methods is not meaningful under our experimental setting.

  3. VLM‑based OOD methods often build upon a pre‑trained multimodal backbone, where CLIP, for instance, operates zero‑ or few‑shot detection via prompts or embedding similarity without learning an extra classifier on the ID set. In contrast, the encoder of AdaGeo is trained from scratch on long‑tailed ID sets ranging from 11k images (CIFAR‑100‑LT) to 116k images (ImageNet‑LT). The two families therefore differ drastically in pre‑training scale, roughly by three to four orders of magnitude. We emphasize two separate points. First, while VLM‑driven OOD detection exists, these approaches rely on large pre‑trained multimodal backbones and are typically validated on class‑balanced in‑distribution data. Second, within the specific line of long‑tailed OOD detection, existing published methods including PASCL, EAT, PATT and RSCL all adopt encoders trained from scratch, and none of them report comparisons against VLM‑based baselines. As a result, there is no budget‑matched counterpart on this track. Directly grouping them in the same table would primarily reflect the gap in backbone capacity and pre‑training corpora rather than algorithmic advances for long‑tailed OOD, which is not the focus of our paper.

Another main concern is that AdaGeo's progress over current approaches is hard to assess. This concern is understandable, and it can be addressed as follows:

‑ First, PASCL, EAT, PATT and RSCL, a group of papers recently published at top venues (ICML 2022, AAAI 2025, CVPR 2026), likewise do not bring in VLM‑based methods, and their progress over existing work is still assessable.

‑ Second, our work is assessable in the same way, because long‑tailed OOD detection is evaluated along two dimensions at once: recognizing ID classes under scarce support, and rejecting unknown inputs. On the recognition side, ID accuracy is the highest among the compared methods on all three benchmarks. On the rejection side, it is the best of the three methods on CIFAR‑100‑LT, including against the most recent RSCL (CVPR 2026), and it obtains the best result on the most imbalanced benchmark.

With the above clarifications, we sincerely hope and believe the reviewer's concern about the scope of baselines and the assessment of progress has been basically alleviated.

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To W3: This comment raises three concerns: (i) whether the need for auxiliary OOD data limits practicality, (ii) whether performance is sensitive to the choice, quality and diversity of the auxiliary set, and (iii) whether the comparison across baselines is fair. We address each in turn.

  1. We use auxiliary OOD data before evaluation, but this does not limit the practicality of the method. The following explains the reasons. Auxiliary data determines only a single scalar, and that scalar is not sensitive. Calibration happens after training, once the model is frozen; it does not enter the optimization loop, and training itself uses no auxiliary images. What calibration selects is the fusion weight α, a single scalar; fixing its value anywhere between 9 and 13 changes the mean AUROC on CIFAR‑100‑LT by no more than 0.12 percentage points. Even if no auxiliary data were available at deployment, fixing α to a constant would not affect the conclusion claimed in our paper, since auxiliary data here carries a one‑off scalar choice: it changes neither the training pipeline nor the deployment requirement.

  2. Performance is not sensitive to the choice, quality or diversity of the auxiliary data. We should first note that the auxiliary set we use is not a hand‑picked, diverse and high‑quality one. On CIFAR‑LT we use the public TinyImages pool that PASCL, PATT and the other baselines also adopt, a random subset of 300,000 web images with no category annotation and no original‑sample index, containing many non‑object images, with no semantic alignment to the ID classes and no quality filtering. As for using only a few of its categories, the released files only contain pixel data; splitting by semantic category would require additional annotations and is therefore not feasible on this public dataset. To test the sensitivity of the auxiliary data instead, we randomly halve the images used for calibration, and recalibration still selects α=10. Together with the sweep just described, this indicates that the choice of α does not depend on the composition of one particular auxiliary set, and is insensitive to both the size and the source of the auxiliary data.

  3. The comparison is fair. The methods we compare fall into three groups by how they use auxiliary data: PATT uses it both during training and before evaluation; OE, EnergyOE, PASCL, EAT and RSCL use it during training; MGPL and MSP use it in neither. Six of the eight methods therefore use auxiliary OOD data during training, whereas we use auxiliary images only once, after the model is frozen. Furthermore, we also conduct a more direct control experiment, that is, to remove auxiliary data from our pipeline altogether. We achieve that mean AUROC on CIFAR‑100‑LT is 76.12, still above PATT's 75.36, and within 0.61 points of the 76.73 obtained with geometric scoring and calibration. Auxiliary data therefore changes neither our conclusion nor the fairness of the comparison: the baselines use it during training to shape the optimization, whereas we use it once after freezing to pick a scalar, and removing that step leaves our conclusion intact.

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

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