acceptodds
Under review as a conference paper at ICLR 2027

Strong Backbone, Simple Heads: The Case for Gradient-Free Class-Incremental Learning

Abstract

Recent class-incremental learning methods increasingly build on pre-trained vi- sion transformers, adapting only a small set of parameters such as lightweight adapters. However, these methods are typically developed and benchmarked on older foundation models. We ask how they transfer to modern backbones, and whether parameter adaptation is needed at all. Comparing adapter-based meth- ods with gradient-free, closed-form classifiers that keep only per-class statistics, under matched backbones, splits and seeds, we find that as backbones improve the gradient-free methods match or outperform gradient-based ones, even after extensive retuning of the latter. The gap is driven by forgetting rather than learning: the adapter method learns each task about as well as the closed-form heads, but forgets roughly three times as much, and its forgetting is higher on the stronger backbones while theirs falls. We also find that the composable, sufficient-statistic state of these heads enables two practical properties: federated merging across distributed instances and class-level machine unlearning. These results suggest that with strong foundation models, simple statistical decision rules can outperform increasingly elaborate adaptation mechanisms.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
Continual Learning, Computer Vision, Federated Learning, Foundation Models

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_q7TQOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This work studies exemplar-free class-incremental learning (CIL) methods with strong backbones (ViT-B, DINOv2 and v3) where the classifier is a closed-form solution (SimpleCIL, SLDA, S-QDA, FeCAM, RanPACK) or adjusted on frozen features during CIL (MiN, EASE). The authors evaluated methods on six commonly used dataset, and two with a bigger shift (OpenEarthSensing, MedMNIST). The main claim is that strong feature extractors, i.e., Dino-v3 allows state-of-the-art solution with simple closed-form classifiers, and that the performance gap comes from forgetting rather than learning. Moreover, such composable solutions give exact federated merging, class deletation and order-invariant solutions.

Critical strengths
  1. The authors tackle an important problem of transferring results from strong feature extractors, but older ones (e.g. ViT), to up-to-date backbones like Dino-v3, where simple methods yield good results and the main problem is not necessarily "catastrophic forgetting."
  2. The extensive evaluation results with many interesting results in the Appendix.
Critical weaknesses
  1. "On DINOv3 they outperform MiN on most benchmarks" -- but looking at the table A5, where all the results are reported, seems like a fixed version of MiN with per-cell hyper-pramaeters selection is still the best. Unfortunately, not all the experiments are presented with this version. This leaves the reader of this work in confusion. See also, for example, Table A9, which should support the claim "forgetting, not learning" is a problem. However, here still only a single result is with MiN repaired + hp per-cell selection, and it's the best with the biggest forgetting... . It would be nice to present the complete results and recheck all the claims, make it clear for the reader.
  2. In connection to the first point, looking at the results, the work would be stronger if it shows the results for few other adaptation methods, e.g. SLCA, MOS, E2-LoRA, etc.
  3. Federated learning setting is very limited; see works that introduce training-free methods like Fed3R, FedNCM to check the common setting for the evaluation.
  4. Presentation - there are too many MiN variants that the reader needs to follow, which one is used in what experiment? This could be simplified, and just use the best version everywhere to not cause confusion.
Questions for authors
  1. How do published RanPAC (with first-session adaptation) perform on DINOv3-B/L/H, including OES and MedMNIST?
  2. It's stated in the limitation that 3 out of 5 backbones are Dino-v3. Have you experimented with other non-DINO SOTA backbones?
1 comment
AuthorsOpenReview ↗

Reviewer q7TQ Rebuttal

We thank the reviewer for concrete, actionable requests. Changes are in purple in the revised PDF, which now reports full per-benchmark results for every method. Numbers below are eight-benchmark means.

Weaknesses

W1 and W4. MiN variants and claims. The "Repaired MiN" column was the per-cell best of six configurations chosen on the reported seeds, and MiN was scored by task rather than exact class. We now report one MiN everywhere: plain validation-tuned MiN, scored by exact class. It trails the best closed-form head by 0.8–1.1 pp on DINOv3-B/L, and collapses on some DINOv3-H seeds (65.8). The repaired MiN (L2-normalised features, γ = 1) appears only in the brittleness discussion (Table A13).

W2. More adaptation baselines. We added MOS (AAAI 2025), run with the official code under our protocol on all 40 cells. It trails the best closed-form head by 1.1–1.9 pp on every backbone. Freezing its adapters costs 1.4–2.6 pp, most of it on OES, so most of its accuracy comes from its classifier. SLCA and E2-LoRA are listed as a limitation.

W3. Federated protocol. We now follow Fed3R and FedNCM: 100 clients, Dirichlet label skew with α ∈ {0, 0.01, 0.1, 0.5, 1000}, heads merged in one round. In float64 the merged SLDA and S-QDA heads equal the centrally trained heads at every skew level (at most 0.006 pp apart). On CIFAR-100 at α = 0 with ViT-B/16, S-QDA reaches 89.5%, level with Fed3R-RF (89.4%) and above Fed3R (84.5%) and FedNCM (77.4%). RanPAC's statistics also merge exactly, but its ridge penalty has to be set without data. With our data-free rule the merged head stays within 1.0 pp of central on CIFAR-100 and 0.6 pp on MedMNIST and loses up to 3.6 pp on ImageNet-R, but it falls to chance on CUB-200 for α ≤ 0.5; we state this as a limitation.

Questions

Q1. Published RanPAC with first-session adaptation. We ran it on all five backbones and eight benchmarks. It is the best method at every DINO backbone (84.9–89.9) and on OES and MedMNIST at every backbone, with its gains over frozen RanPAC concentrated on shifted domains. It adapts once and is a closed-form head from task 2 on, so we read this as support for our argument and treat our frozen RanPAC as its no-adaptation ablation.

Q2. Non-DINO backbones. We have not experimented with other backbone families. We chose these backbones because their architectures are very similar, which lets us show the effect of changing pretraining quality as well as parameter count.

Reviewer_62RnOpenReview ↗
Rating
1
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper asks whether continual adaptation is still needed for class-incremental learning when strong pretrained backbones are available. The authors compare frozen statistical classifiers, such as SLDA, S-QDA and RanPAC, with adaptation-based methods across several backbone generations. They find that simple classifiers become competitive as the backbone improves, and argue that avoiding changes to the representation reduces forgetting. They also discuss how the stored statistics allow federated merging and class-level unlearning.

Critical strengths
  1. The paper raises a useful practical question. If strong pretrained features are already available, it makes sense to check whether complicated adaptation methods actually improve over simple classifiers.

  2. The experiments cover several backbones and datasets. The authors also investigate why MiN becomes unstable instead of only reporting its poor results with the original settings.

  3. The ability to merge statistics across different instances is a useful property. Under a shared frozen backbone and fixed hyperparameters, this gives a simple way to reproduce a centralized classifier without sharing raw images.

Critical weaknesses
  1. My main concern is the scope of the conclusion. The difficulty of continual learning is largely about learning new representations without losing previous knowledge. Here, that difficulty is avoided by assuming that a strong pretrained backbone already provides useful features. What happens when we want to continually train the backbone itself on new data or domains? The proposed approach does not address this. I see its practical value, but the contribution is closer to maintaining a classifier on fixed features than solving continual representation learning. The MedMNIST results also show that a larger backbone does not automatically provide better features for every domain.

  2. Hyperparameters are selected using test-set performance, and some variants are also selected using the reported evaluation seeds. This is a serious problem, especially for a paper whose main contribution is an empirical comparison. Applying test-set tuning to several methods does not make the comparison fair, since the search budgets and sensitivity to tuning differ. A separate validation set should be used, followed by evaluation on an untouched test set.

  3. The MiN comparison does not use a consistent evaluation protocol. On the standard benchmarks, MiN is evaluated by whether its prediction belongs to the correct task, while the other methods must predict the exact class. This makes the learning and forgetting numbers directly incomparable. In particular, task-level accuracy can be 100% on the first task without correctly distinguishing its classes, which affects the claim that MiN forgets roughly three times as much. The ImageNet-R task splits also differ: MiN uses 20 tasks of 10 classes, while the other methods use 40 tasks of 5 classes. These settings should be matched before drawing conclusions about the methods.

  4. The unlearning claim needs a narrower description. Deleting class statistics can reproduce fitting the same head without that class, but it does not remove the class information or its pretraining influence from the backbone. This is a useful property of the classifier, but presenting it as a broader machine-unlearning advantage feels overstated. Also, whether exact deletion is possible depends on how independently the contributions are stored, not simply on whether the method uses gradients.

  5. The methods and statistical properties themselves are mostly established, so the paper’s research value depends heavily on the quality of the comparison and analysis. Given the protocol issues above, I am not yet convinced by the broader claim that stronger backbones make continual adaptation unnecessary. The results seem to support a more limited conclusion: frozen statistical heads are important baselines for class-incremental learning with pretrained backbones.

Questions for authors

See weaknesses

1 comment
AuthorsOpenReview ↗

Reviewer 62Rn

We thank the reviewer. Changes made in response are in dark green in the revised PDF.

Weaknesses

W1. Scope: the paper avoids continual representation learning. We agree that we do not train the backbone continually, and the introduction now says so. We read our results as bearing on that question rather than sidestepping it. The parameter-adaptive methods we compare against (MiN, EASE, MOS) are the current approach to continual representation learning, yet their advantage shrinks or reverses as the backbone gets stronger. As backbone continue to improve the vast majority of tasks could be brought under a parameter free regime. Three results support this:

  • Adapting the backbone once, on the first task, then freezing it (RanPAC with first-session PETL) helps most under distribution shift: +1.2 to +7.5 pp over frozen RanPAC on ImageNet-A, OES and MedMNIST at the DINO backbones.
  • Switching continual adaptation off in MOS and EASE, keeping only their classifiers, costs little on strong backbones. On the eight-benchmark mean, EASE's adapters add 4.5 pp at ViT-B/16 and 0.4–1.0 pp on DINO. MOS's add 1.4–2.6 pp at every backbone, most of it on OES.
  • Continual adaptation in MiN adds instability: some DINOv3-H seeds collapse even after tuning.

W2. Hyperparameters were selected on the test set. We agree, and have fixed this for every method; see the general response. In short, the closed-form heads barely move, and we withdraw the claim that MiN forgets about 3× more.

W3. MiN is evaluated under a different protocol. We agree, and both settings are now matched for every method: MiN is scored by exact class, and ImageNet-R uses 40 tasks × 5 classes for all methods (see the general response). Under the matched protocol MiN's forgetting is level with the heads, which is why we withdraw the forgetting claim.

W4. Scope of the unlearning claim. We clarify it. The unlearning we claim is of data the continual learner was trained on, not of the pretraining corpus. Because the backbone is frozen, that data lives only in the head's per-class statistics: deleting them leaves no trace of it in the model and gives exactly the head fitted without it. We agree with the reviewer that exactness comes from storing each class's contribution independently, not from avoiding gradients: a method with fully independent per-class adapters could also delete exactly. None of the adaptation methods we test has them. EASE and MOS keep one adapter per task, but EASE estimates old-class prototypes in each new adapter's subspace from the new classes' prototypes, and MOS merges each new adapter with earlier ones. In these methods deletion is at best task-level and approximate. Influence from pretraining, such as a class that also appears in the pretraining corpus, is a separate question that we do not address. The revised section states this directly.

W5. Novelty. We agree the classifiers and their statistical properties are established. We see our contribution analysis of the interaction between these different techniques and new backbones, and our intuition on what makes methods robust to improvement in backbone.

Reviewer_X46BOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

This paper examines whether continual parameter adaptation remains necessary for class-incremental learning with strong pretrained backbones. It compares five closed-form classifiers with MiN and EASE across five backbones and eight benchmarks. The reported results show that closed-form heads become competitive on DINOv3, with the authors attributing much of the difference to reduced forgetting. The paper also formalizes composable classifier states and their implications for federated merging and class deletion.

Critical strengths
  1. The comparison across backbone generations addresses a relevant evaluation question. On the six standard benchmarks, RanPAC trails MiN on ViT-B/16-IN21k by 4.8 percentage points (78.70% vs. 83.50%), whereas it nearly matches repaired MiN on DINOv3-L/16 (89.79% vs. 90.13%). Subject to the evaluation concerns below, these results provide useful evidence that conclusions established on older backbones may not transfer to stronger representations. (Table A6)

  2. The analysis of MiN’s instability is informative and supported by targeted experiments. The authors investigate both feature-scale mismatch and the effect of continued adaptation. On MedMNIST with DINOv3-H/16, final first-task accuracy is 10.7% for standard MiN and 70.8% for fixed MiN, which uses a lower first-task learning rate and stops subsequent adaptation. The exact-class trajectories provide concrete support for the proposed forgetting mechanism, beyond simply reporting unsuccessful configurations. (Fig. 2, §5.2, Appendix E, Table A10)

Critical weaknesses
  1. Test-set model selection limits confidence in the reported comparisons. Hyperparameters are selected using final test accuracy at seed 1993, which is also included in the evaluation. FeCAM variants and some MiN repairs are selected directly on the reported seeds. RanPAC’s ridge selection is an exception, using held-out training data. Although these choices are disclosed, differing search budgets and selection procedures mean that the resulting optimism cannot be assumed to affect all methods equally. Averaging across seeds does not remove reuse of the test set for model selection. (§4.3, L205–210; Appendix C, L798–805; Table A6 caption)

  2. Differences in scoring and task partitioning complicate the forgetting comparison. MiN uses task-level accuracy on the six standard benchmarks, whereas the other methods use exact-class accuracy. The authors estimate that this increases MiN’s final accuracy by 1.0 percentage point on average and up to 3.7 points on ImageNet-A. However, a favorable bias in final accuracy does not establish a conservative comparison of forgetting, which depends on both earlier and final accuracies; MiN’s first-task accuracy is 100% by construction. ImageNet-R additionally uses 20 tasks for MiN and 40 for the heads, changing the task-level reference points. The claim of approximately threefold greater forgetting therefore requires evaluation under a common protocol. (§4.3; Appendix C, L780–784; Table A9; Fig. A2; Appendix E, L1376–1384)

  3. The scope of the conclusions exceeds the coverage of adaptation baselines. Only MiN and EASE are evaluated, and EASE retains its default hyperparameters. Moreover, repaired MiN achieves 90.13% and 90.97% on DINOv3-L/H, compared with RanPAC’s 89.79% and 90.75%, although MiN benefits from task-level scoring and selection on the reported seeds. These results establish the competitiveness of simple heads more directly than a general conclusion about adaptation methods. The limitations section acknowledges the restricted baseline coverage, but this qualification should also guide interpretation of the main claims. (§4.3, §6, Table A6)

  4. The empirical joint-versus-streaming results need reconciliation with the exact-equivalence claim. Appendix A.1 establishes equivalence under fixed features and hyperparameters. Nevertheless, Table A13 reports joint and streaming S-QDA accuracies of 64.575% and 63.721% on ImageNet-A with DINOv2-B/14, a difference of 0.854 percentage points. By comparison, Table A1 reports accuracy changes of at most 0.003 points in its separate composition experiment. The latter does not establish a universal numerical tolerance, but the larger discrepancy remains unexplained. This does not invalidate the algebraic result; it leaves uncertainty about whether the implementations and evaluation procedures realize the stated equivalence. (Appendices A.1 and A.3, Tables A1 and A13)

Questions for authors
  1. Could the authors repeat model selection using a separate validation set, including selection of FeCAM variants and MiN repairs, and report whether the rankings in Tables 2 and A6 remain unchanged on untouched test data? (§4.3, Appendix C)

  2. Could all methods be evaluated using exact-class accuracy and identical ImageNet-R task partitions, with learning accuracy, forgetting, and BWT recomputed accordingly? In particular, does the approximately threefold forgetting difference remain under this common protocol? (Table A9, Appendix C, Fig. A2)

  3. Could the authors tune EASE on a small set of representative backbone–dataset combinations? This would help determine whether its reported disadvantage reflects the adaptation method or the transfer of its default configuration. (Appendix C.3, Table A6)

  4. What explains the 0.854-point joint-versus-streaming discrepancy in Table A13? Were the features, hyperparameters, prediction rules, and accuracy aggregation identical? Reporting differences in the stored statistics and predictions would help distinguish numerical effects from implementation or evaluation differences. (Appendix A.1, Tables A1 and A13)

1 comment
AuthorsOpenReview ↗

Reviewer X46B Rebuttal

We thank the reviewer. Changes made in response are in blue in the revised PDF.

Weaknesses

W1. Test-set model selection. We agree this was a flaw and have fixed it for every method; the general response gives its effect on each method. The protocol, grids and per-cell winners are in §4 and Appendix "Hyperparameters".

W2. Scoring and task partitioning. Exact-class scoring and a single ImageNet-R partition (40 tasks × 5 classes) now apply to every method; see the general response. As a result, we remove the claim that MiN forgets about 3× more; the general response gives the BWT numbers and the cause.

W3. The conclusions go beyond the adaptation baselines. We agree, and have changed both the evidence and the claims.

  • More baselines. We added MOS (AAAI 2025) and published RanPAC with first-session adaptation on all 40 cells, ran MOS and EASE with continual adaptation switched off, and tuned EASE on every cell. Results are in the general response.
  • The repaired-MiN comparison. As the reviewer notes, the 90.13 / 90.97 on DINOv3-L/H came from task-level scoring and selection on the reported seeds. With exact-class scoring and validation selection, MiN reaches 89.85 at L/16, against 90.24 for RanPAC and 90.12 for MOS, and collapses on some H/16 seeds. We now report one MiN recipe throughout (see our response to q7TQ).
  • Claims. We adopt the reviewer's reading: the results show that simple closed-form heads are competitive on strong frozen features, not a general conclusion about adaptation methods. The abstract and §4.3 now say this and match Tables 2 and A6. The limits on baseline coverage and backbone family, and that continual representation learning is out of scope, now sit beside the main claims rather than only in §6.

W4. The 0.854 pp joint-versus-streaming S-QDA gap. This comes from two protocol differences, not from the method:

  • 0.326 pp: our harness replayed each task's data (5 epochs, 10 on the first task) instead of making a single pass. This changed 32 of 1,578 predictions.
  • 0.528 pp: streaming's task-averaged A_B was compared with joint training's pooled accuracy.

With a single pass and matched scoring, the gap closes. With statistics accumulated in float64, streaming S-QDA and SLDA make exactly the same predictions as joint training in every cell. The small residuals we saw in float32 (at most 0.27 pp in 10 of 24 cells) are accumulation error. Table A15 is rebuilt from this matched run.

Questions

Q1. Selection on a separate validation set. Done for every method, including FeCAM and MiN (see W1). The rankings change in part: MiN leads the six-benchmark mean at ViT-B/16, DINOv2-B and DINOv3-B, the closed-form heads are level with the adaptation methods at DINOv3-L, and they lead MiN and MOS at DINOv3-H. The table is in the general response.

Q2. Exact-class accuracy and identical ImageNet-R partitions. Done for every method (see W2). The threefold forgetting difference does not remain: MiN's BWT is −3.5 to −4.4, against about −5 for the heads.

Q3. Tuning EASE. We tuned EASE on every cell rather than a representative few. Tuning adds 0.8 to 2.4 pp on the six-benchmark mean. Tuned EASE still trails the best closed-form head by 2.7–5.3 pp on the DINO backbones, so its disadvantage is not only a matter of its default configuration.

Q4. The 0.854-point discrepancy. See W4. The features, hyperparameters and prediction rules were identical; the gap came from the replayed passes and from the accuracy aggregation.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Comment

We thank the reviewers for careful and constructive reviews. The main shared concern (R1, 62Rn) was that hyperparameters were selected on test data. We re-ran the full study with selection on a held-out validation split for every method, and added the baselines and protocols requested. Changes in the revised PDF are colour-coded by reviewer.

What changed, for every method

  1. Validation selection. All tuning uses a stratified 10%-per-class validation split of the training data. Test data is used only for the final runs at five seeds. Selection barely moves the closed-form heads (S-QDA's mean changes by at most 0.1 pp on each DINOv3 backbone; Table A5), so they were not inflated by test selection; MiN gains 0.6 pp at DINOv3-B/16 and 2.5 pp at L/16.
  2. Exact-class scoring for all methods, including MiN: we changed its scoring to match the other methods. This alone lowers MiN by about 1 pp on average (up to 3.7 pp on ImageNet-A).
  3. One MiN. Repaired MiN is taken out of the results tables to avoid confusion. Every table reports plain validation-tuned MiN; the fixed repair appears only in the MiN brittleness analysis.
  4. One protocol. EASE's B0-IncN splits for every method; ImageNet-R is 40 tasks × 5 classes for everyone.
  5. MedMNIST split. Slices from one CT volume had landed on both sides of our validation split. We now use the official patient-disjoint split and re-select every method on it; the closed-form heads move by at most 0.3 pp in most cells.
  6. New baselines and protocols. MOS (Sun et al., AAAI 2025) and RanPAC with its first-session adaptation, on all 5 backbones × 8 benchmarks; MOS and EASE with continual adaptation switched off; the Fed3R/FedNCM federated protocol.

Eight-benchmark mean A_B (CIFAR-100, ImageNet-R, ImageNet-A, CUB-200, OmniBench, VTAB, OES, MedMNIST; five seeds):

BackboneMiNMOSRanPACS-QDAEASERanPAC + first-session PETL
ViT-B/16 IN21k81.8378.4878.8379.9370.7281.40
DINOv2-B/1484.4180.8482.6982.2173.2184.88
DINOv3-B/1683.8982.9984.3884.6776.8085.59
DINOv3-L/1686.4886.4887.5687.3680.5288.89
DINOv3-H/1665.7786.5187.8187.7478.9089.85

What we now claim

  • On strong frozen backbones, closed-form heads match or beat continual adaptation. On the eight-benchmark mean they lead both MOS and MiN on every DINOv3 backbone, by at least 0.8, 1.1 and 1.3 pp at B/16, L/16 and H/16. MiN leads only at ViT-B/16 and DINOv2-B (by 1.9 and 1.7 pp).
  • Adapting once on the first task and then using a closed-form head (published RanPAC) is the strongest method: it has the highest mean at every DINO backbone and is best on OES and MedMNIST at every backbone.
  • Continual adaptation adds little on strong backbones. MiN improved when its adaptation was removed, EASE performed similarly with its adapters removed on the DINO backbones, and MOS loses 1.4–2.6 pp without its adapters.

Adapter ablation. Our MiN analysis already showed continual adaptation to be unstable on strong backbones (some DINOv3-H seeds collapse even after validation tuning). In addition, we ran MOS and EASE with continual adaptation switched off, keeping only each method's classifier on frozen features (for EASE this is SimpleCIL). On the eight-benchmark mean, the adapters add 4.5 pp to EASE at ViT-B/16 and 0.4–1.0 pp on the four DINO backbones. They add 1.4–2.6 pp to MOS at every backbone, most of it on OES. On strong backbones, nearly all of these methods' accuracy comes from their classifiers rather than from adapting the backbone.

Forgetting claim. We withdraw the claim that MiN forgets about 3× more: validation-tuned, exact-class MiN has BWT of −5.2 (DINOv2-B), −5.7 (DINOv3-B) and −4.8 (DINOv3-L), within 0.6 pp of S-QDA's (−5.8, −5.2 and −4.5). The main driver is the smaller learning rate chosen on validation (min_lr ≤ 1e-5 in 29 of 40 cells).

Per-benchmark results behind the numbers in our responses; the eight-benchmark means are in the general response. All values are A_B in %, selected on validation, mean of five test seeds, with matched preprocessing on the DINO backbones.

Distribution-shift benchmarks (S-QDA is the best closed-form head in every cell here except ViT-B/16 MedMNIST, where RanPAC is 80.27)

BackboneOES: S-QDA / MOS / RanPAC + first-session PETL / MiNMedMNIST: S-QDA / MOS / RanPAC + first-session PETL / MiN
ViT-B/16 IN21k80.35 / 67.69 / 82.90 / 82.2980.09 / 81.28 / 82.14 / 76.19
DINOv2-B/1477.68 / 65.56 / 82.51 / 81.4575.44 / 75.81 / 81.30 / 74.27
DINOv3-B/1681.28 / 72.03 / 84.51 / 78.1879.33 / 77.08 / 83.01 / 72.74
DINOv3-L/1682.86 / 75.16 / 85.85 / 79.9277.12 / 75.91 / 82.56 / 72.80
DINOv3-H/1682.96 / 76.81 / 87.25 / 26.6975.93 / 71.51 / 82.54 / 53.11

Adaptation switched off (eight-benchmark mean; gain = full method − classifier alone)

BackboneMOS gainEASE gain (vs SimpleCIL)
ViT-B/16 IN21k+2.07+4.50
DINOv2-B/14+1.37+0.73
DINOv3-B/16+1.90+0.39
DINOv3-L/16+2.08+0.95
DINOv3-H/16+2.58+0.71

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.