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Under review as a conference paper at ICLR 2027

Interpretable Differentially Private Continual Learning with Prototype-Based Classifiers

Abstract

Continual learning (CL) under differential privacy (DP) involves two competing objectives: a model must learn from new tasks while avoiding catastrophic forgetting, and the training pipeline must preserve privacy. Requiring the model’s decisions to be interpretable introduces an additional competing objective. These trade-offs become particularly pronounced when no sensitive state, such as memory buffers, can be retained across tasks. We introduce a DP prototype-based CL framework built on pretrained backbones, where each class is represented by a single DP prototype and predictions are made by nearest-prototype classification in a shared embedding space. This eliminates the need to store samples while making the decision rule inherently interpretable. We control the CL trade-offs through novel DP-friendly loss functions adapted from prior CL work. On the Split-CIFAR-100 and Split-ImageNet-R benchmarks, our method achieves similar or higher accuracy than a state-of-the-art interpretable DP CL baseline while remaining competitive with a stronger but non-interpretable DP CL baseline across challenging CL settings. Finally, we introduce two complementary methods for interpreting the learned DP prototypes: one based on publicly available pretraining data and another using synthetic samples generated by a generative model.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Differential Privacy, Continual Learning, Interpretability, Prototype-Based Learning

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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.
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Paper summary

This paper proposes an interpretable differentially private continual learning framework using DP prototypes and DP-friendly loss functions to mitigate catastrophic forgetting. Experiments on Split-CIFAR-100 and Split-ImageNet-R show competitive performance against existing baselines. The authors also introduce methods to visualize DP prototypes using public and generated images.

Critical strengths

The authors propose an interpretable DP prototype-based continual learning framework, supported by theoretical analysis and comprehensive experimental evaluations.

Critical weaknesses

The theoretical analysis in Section 4.4 only considers Gaussian perturbations of class prototypes under a fixed projection. It does not account for representation drift caused by updating the projection when learning new tasks, which is a central challenge in continual learning. Consequently, the theoretical results do not capture the continual learning dynamics or explain how the proposed method mitigates catastrophic forgetting.

Questions for authors

Could the authors provide a theoretical analysis of the impact of differential privacy in the continual learning setting? If a rigorous theoretical analysis is challenging, even some intuitive insights into how DP affects continual learning dynamics would be valuable.

2 comments

Thank you for your thoughtful and constructive feedback. Your comments helped us identify an important limitation of our original theoretical analysis. We have revised Section 4.4, now titled "Prototype stability and continual adaptation", and added Appendix C with four new theorems and proofs. All changes are highlighted in blue.

The theoretical analysis in Section 4.4 only considers Gaussian perturbations of class prototypes under a fixed projection. It does not account for representation drift caused by updating the projection when learning new tasks, which is a central challenge in continual learning. Consequently, the theoretical results do not capture the continual learning dynamics or explain how the proposed method mitigates catastrophic forgetting.

We agree that our original analysis did not account for representation drift across tasks. We now examine how old-class classification margins evolve from the initialization of the projection matrix through successive task updates.

The central idea is to study the classification margin: the difference between an input's similarity to its correct prototype and its most similar competing prototype. A positive margin means the correct prototype is preferred. Our analysis characterizes how this margin changes under local projection updates and how representation drift accumulates across tasks. If the initial margin is sufficiently large relative to these accumulated changes, the prediction remains correct among previously learned classes. This connects representation drift to the preservation of old-class predictions.

The revised Section 4.4 summarizes the following results, with proofs in Appendix C:

  1. Theorem 3 (Initialization): We show that a Gaussian random projection with sufficiently large output dimension approximately preserves the original classification margins.
  2. Theorem 4 (Representation drift): We provide a local, first-order analysis of how small projection updates affect old-class margins by changing both input embeddings and class prototypes, with a bounded higher-order error.
  3. Theorem 6 (Continual adaptation): We bound accumulated margin changes across tasks and provide sufficient conditions for preserving predictions among previously learned classes.

These results also help explain the roles of our losses. PCL and push-away encourage separation from competing prototypes, while preservation uses synthetic support points to limit changes to old-class representations.

Importantly, our analysis provides sufficient conditions for preserving old-class predictions, not an end-to-end guarantee against catastrophic forgetting. The representation drift analysis is local, and we do not establish that minimizing our objective necessarily satisfies these conditions or prevents interference from newly introduced classes.

We have also revised Section 6 (Conclusion and Discussion) to acknowledge these limitations and identify stronger, end-to-end guarantees against catastrophic forgetting as an open research question.

Could the authors provide a theoretical analysis of the impact of differential privacy in the continual learning setting? If a rigorous theoretical analysis is challenging, even some intuitive insights into how DP affects continual learning dynamics would be valuable.

Thank you for this suggestion. We have also added Theorem 5 (Appendix C.2), which extends our local representation drift analysis to DP-SGD. For sufficiently small updates, it separates the first-order effects of clipped learning gradients and privacy noise on old-class margins, with a bounded higher-order error. We also derive a high-probability bound on the first-order noise contribution.

This provides two insights:

  1. Privacy noise can increase or decrease old-class margins, potentially changing previous predictions.
  2. Privacy noise can perturb old-class representations even when learning gradients would otherwise leave them unchanged. For example, when an old backbone feature is orthogonal to new-task features, PCL and push-away gradients do not change its representation under a standard gradient update, whereas privacy noise can still affect it.

Theorem 5 is a local analysis of DP-SGD, not a global convergence or forgetting guarantee. Although our experiments use DP-Adam, Theorem 4 also applies to sufficiently small DP-Adam updates, while the Gaussian noise bound in Theorem 5 is specific to DP-SGD.

Together, these results provide further insight into how continual adaptation and privacy noise affect previously learned classes and identify conditions for preserving their predictions. We hope these additions address the reviewer's concerns and strengthen our theoretical contribution.

Thank you for the clarification. I will maintain my positive score.

Reviewer_pjU7OpenReview ↗
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Paper summary

This paper proposes an interpretable differentially private continual learning framework based on class prototypes. The method freezes a pretrained backbone and trains a linear projection using three objectives: prototype contrastive learning, push-away loss, and MMD-based representation preservation. To mitigate catastrophic forgetting without retaining private training samples, it constructs synthetic support points from DP prototypes. Experiments on Split-CIFAR-100 and Split-ImageNet-R demonstrate competitive performance under disjoint and blurry class-incremental settings. The paper also introduces public-image retrieval and diffusion-based generation to visualize learned prototypes.

Critical strengths
  • The proposed framework combines DP prototypes with a representation preservation mechanism that does not require retaining previous training examples. Its synthetic support construction provides a practical way to mitigate catastrophic forgetting while respecting privacy-related storage constraints.

  • The method achieves meaningful improvements over the DP cosine classifier on CIFAR-100, with accuracy gains of 4.26 and 2.86 percentage points at ϵ=8\epsilon=8 and ϵ=1\epsilon=1, respectively.

Critical weaknesses
  • The proposed method adapts only a linear projection while keeping the pretrained backbone frozen, which substantially restricts its ability to learn new representations beyond those already encoded in the pretrained feature space. Although this design is computationally efficient and privacy-friendly, the paper does not sufficiently investigate the resulting stability–plasticity trade-off. In particular, the limited improvement over the cosine classifier on ImageNet-R raises concerns about whether the learned projection provides sufficient adaptation capacity for challenging continual learning scenarios. Comparisons with established rehearsal-free methods, such as CODA-Prompt and InfLoRA, as nonprivate references, together with stronger privacy-matched PEFT baselines, would help characterize this limitation.

  • The experimental evaluation is limited to ten sequential tasks, leaving the long-term stability and adaptability of the proposed method insufficiently explored. Since the same linear projection is continually updated while preserving previously learned prototype representations, the accumulation of preservation constraints may restrict the model's ability to accommodate additional classes. Evaluations with longer task sequences, such as 20 or 50 tasks, would help establish whether the method maintains a favorable stability–plasticity trade-off over extended continual learning.

  • The experimental evaluation primarily focuses on class-incremental learning, including blurry settings where task boundaries and class distributions vary. However, these experiments do not adequately assess the method's adaptability under domain shifts, where the visual characteristics of previously learned classes may change substantially. This limitation is particularly relevant because the proposed method freezes the pretrained backbone and updates only a linear projection. Evaluating domain-incremental benchmarks such as DomainNet would provide valuable evidence regarding the method's robustness to distribution shifts and its applicability beyond class-incremental scenarios.

  • Although the proposed framework avoids storing private training samples, the paper does not provide a quantitative analysis of its memory and computational overhead. In particular, the preservation mechanism constructs multiple synthetic support points for every previously learned class, potentially increasing training cost as the number of classes grows. Reporting peak training memory, persistent storage, and per-task training time would help substantiate the efficiency and scalability of the proposed approach.

  • The paper claims formal differential privacy guarantees but explicitly excludes the privacy cost of hyperparameter optimization. Since model selection is performed using validation accuracy over multiple configurations, the reported privacy budget does not necessarily characterize the complete training procedure. Furthermore, the privacy allocation procedure relies on class-count information whose privacy status is unclear. The authors should clarify the scope of their guarantee and provide appropriate accounting or justify that these operations use exclusively public information.

Questions for authors
  • Were hyperparameter tuning and class-count-dependent privacy allocation performed using public or private data? If private, how are these operations accounted for in the reported DP guarantees?

  • Given the limited improvements over the cosine classifier on ImageNet-R, could the authors clarify whether the frozen backbone and linear projection restrict the model's ability to learn new representations?

  • How does the method compare with established rehearsal-free CL approaches, such as CODA-Prompt and InfLoRA, as nonprivate references, or stronger privacy-matched PEFT baselines?

  • Does the method maintain accuracy and low forgetting over longer task sequences (e.g., 20–50 tasks), where accumulated preservation constraints may limit adaptation?

  • Evaluation on domain-incremental benchmarks such as DomainNet would help assess robustness under distribution shifts.

  • Reporting memory consumption and per-task training time would help establish scalability as the number of learned classes increases.

5 comments

We thank the reviewer for their careful evaluation of our work and constructive feedback.

The proposed method adapts only a linear projection while keeping the pretrained backbone frozen, which substantially restricts its ability to learn new representations beyond those already encoded in the pretrained feature space.

Given the limited improvements over the cosine classifier on ImageNet-R, could the authors clarify whether the frozen backbone and linear projection restrict the model's ability to learn new representations?

This is a deliberate design choice, inspired by the interpretable prototype-based CL framework of Aghasanli et al. (2025), which we adapt to the DP setting. Our method addresses three competing objectives: differential privacy, continual learning, and interpretability.

Our method aims to balance these objectives by retaining the rich representations of a pretrained backbone while learning a shared projection that adapts the geometry of the prototype space. Our improvements over the cosine classifier on Split-CIFAR-100 demonstrate that this adaptation can be very beneficial. The smaller improvements on Split-ImageNet-R suggest that more flexible representations may be advantageous in challenging settings.

Extending adaptation to the pretrained backbone, for example through parameter-efficient adapters, is a promising direction for future work. However, incorporating such mechanisms into an interpretable DP CL framework would require carefully balancing the additional adaptation capacity against representation stability and interpretability. Our objective is not to maximize adaptation capacity alone, but to achieve a favorable balance between privacy, continual learning, and interpretability.

We have revised Sections 4.1 and 6 to clarify this design choice, its limitations, and potential directions for future work.

Although this design is computationally efficient and privacy-friendly, the paper does not sufficiently investigate the resulting stability–plasticity trade-off. In particular, the limited improvement over the cosine classifier on ImageNet-R raises concerns about whether the learned projection provides sufficient adaptation capacity for challenging continual learning scenarios.

To better investigate the stability-plasticity trade-off, we additionally evaluate accuracy on newly introduced classes (plasticity) and previously learned classes (stability) using our existing experimental runs on Split-CIFAR-100 and Split-ImageNet-R at ϵ∈{1,8}\epsilon \in \{1,8\}.

On Split-CIFAR-100, our method generally achieves higher plasticity and stability than the cosine classifier and also outperforms the PEFT ensemble at ϵ=1\epsilon=1. On Split-ImageNet-R, our method shows modest improvements over the cosine classifier, while the PEFT ensemble generally performs best. These results suggest that the learned projection provides additional adaptation capability, although its benefits are more limited on ImageNet-R.

We have revised the Section 5.2 (Disjoint Class-Incremental Setting Results) to summarize these findings and added a detailed stability-plasticity analysis, including metric definitions and figures, to Appendix H.

Comparisons with established rehearsal-free methods, such as CODA-Prompt and InfLoRA, ...

How does the method compare with established rehearsal-free CL approaches, such as CODA-Prompt and InfLoRA, as nonprivate references, or stronger privacy-matched PEFT baselines?

We appreciate the suggestion. However, our work specifically addresses interpretable DP CL. Although CODA-Prompt and InfLoRA are rehearsal-free, they do not provide formal DP guarantees or intrinsic prototype-based interpretability. Adapting these methods to DP would require additional mechanisms and privacy accounting, which is beyond the scope of this work. While they could serve as useful nonprivate references for continual learning methods such as Aghasanli et al. (2025), their results are not directly comparable under the same privacy constraints.

For this reason, we compared with the models in Tobaben et al. (2026), which establish strong DP continual learning baselines under the same privacy setting. Importantly, our experimental evaluation in Section 5 already includes their PEFT ensemble, which uses DP-SGD to train FiLM adapters and classification heads, providing substantially greater adaptation capacity than our linear projection. We also evaluate their DP cosine classifier, which is inherently interpretable through its nearest-prototype decision rule, although interpretability was not explicitly investigated in Tobaben et al. (2026).

These baselines allow us to evaluate our central contribution: whether continual adaptation can improve an interpretable prototype-based classifier under DP constraints. Our experiments demonstrate improvements over the cosine classifier in several settings, while highlighting the trade-off between adaptation capacity and interpretability.

AuthorsOpenReview ↗

Response (continued)

The experimental evaluation is limited to ten sequential tasks, leaving the long-term stability and adaptability of the proposed method insufficiently explored.

Does the method maintain accuracy and low forgetting over longer task sequences (e.g., 20–50 tasks), where accumulated preservation constraints may limit adaptation?

To evaluate the performance of our method over longer task sequences, we conducted additional experiments on Split-CIFAR-100 with 20 sequential tasks (5 classes per task). We compared our method against the cosine classifier and PEFT ensemble at ϵ=8\epsilon=8, using five random seeds. We performed HPO for 50 iterations following our original HPO protocol.

The results show that our method maintains higher accuracy and lower forgetting than both baselines throughout the 20-task sequence. Specifically, after the final task, our method achieves approximately 83% accuracy and exhibits the lowest forgetting among the compared methods. These results show that our approach remains effective over longer task sequences.

We have revised Section 5.2 (Disjoint Class-Incremental Setting Results) to summarize these findings and added the detailed experimental results and discussion to Appendix I.

The experimental evaluation primarily focuses on class-incremental learning, including blurry settings where task boundaries and class distributions vary. However, these experiments do not adequately assess the method's adaptability under domain shifts…

Evaluation on domain-incremental benchmarks such as DomainNet would help assess robustness under distribution shifts.

To evaluate our method under distribution shifts, we extended our experiments to the domain-incremental learning setting using CORe50, following the 11-task configuration of Aghasanli et al. (2025), where each task corresponds to a different session (s1–s11) with varying object conditions. We compare our method against the PEFT ensemble and cosine classifier baselines under ϵ=8\epsilon=8, using seed=0. We followed the same HPO protocol as in our main experiments.

The results show that our method generally outperforms the cosine classifier in earlier tasks and achieves comparable accuracy in later tasks, while the PEFT ensemble consistently achieves the highest accuracy. Overall, our method achieves competitive accuracy with moderate forgetting, demonstrating its applicability to domain-incremental learning under distribution shifts.

We have added Section 5.4 (Domain-Incremental Setting Results) to summarize these findings, with the detailed experimental setup and results provided in Appendix J.

Although the proposed framework avoids storing private training samples, the paper does not provide a quantitative analysis of its memory and computational overhead…

Reporting memory consumption and per-task training time would help establish scalability as the number of learned classes increases.

We have added an asymptotic complexity analysis (Big-O notation) and empirical measurements of memory and computational overhead for the longer task sequence experiments in Appendix I, including comparisons with the baselines. The results show that our method’s per-task training time increases with the number of learned classes, while peak GPU and CPU memory remain relatively stable and retained inference memory is lower than that of the PEFT ensemble.

AuthorsOpenReview ↗

Response (continued)

The paper claims formal differential privacy guarantees but explicitly excludes the privacy cost of hyperparameter optimization. Since model selection is performed using validation accuracy over multiple configurations, the reported privacy budget does not necessarily characterize the complete training procedure. Furthermore, the privacy allocation procedure relies on class-count information whose privacy status is unclear. The authors should clarify the scope of their guarantee and provide appropriate accounting or justify that these operations use exclusively public information.

Were hyperparameter tuning and class-count-dependent privacy allocation performed using public or private data? If private, how are these operations accounted for in the reported DP guarantees?

As discussed in Section 4.3, we use hyperparameter optimization (HPO) to ensure a fair comparison between methods and isolate the effect of hyperparameter choices. This is important in a benchmark setting, where a potentially stronger method could appear worse simply because its hyperparameters are suboptimal. We applied HPO consistently across methods, while explicitly acknowledging that its additional privacy cost is not included in our accounting. This is a standard practice in DP research (see e.g. Tramer & Boneh 2021: DP Learning Needs Better Features (or Much More Data) for some comments on this).

Prior empirical work cited in Section 4.3 (Pradhan et al., 2025) also suggests that HPO introduces limited additional vulnerability to membership inference attacks. However, this empirical observation does not establish a formal DP guarantee, and we do not claim that our reported privacy budget accounts for HPO.

Regarding class-count-dependent privacy allocation, the minimum class count used to determine the upper bound on the label-release budget fraction is publicly available benchmark information, not a statistic computed from private training data. This step therefore incurs no additional privacy loss. The actual private class counts are used only within the DP label-release mechanism, whose privacy cost is included in our PLD accounting. The remaining privacy allocation and DP-SGD noise calibration do not depend on private class counts.

We have revised Section 4.3 to further clarify the scope of our privacy guarantees.

Reviewer_rP2JOpenReview ↗
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Paper summary

The paper investigates the three-way trade-off among privacy, continual learning, and interpretability under the constraint that no sensitive state can be retained across tasks. Its framework freezes an ImageNet-21K-pretrained ViT-B/16 backbone and trains only a linear projection using DP-Adam, representing each class with a single differentially private (DP) prototype. Predictions are made based on nearest-prototype cosine similarity (Eq. 3). Privacy is guaranteed on a per-task basis through three mechanisms, with privacy costs composed via PLD and further combined across tasks using parallel composition, under the assumption that each individual participates in at most one task. As a second contribution, the paper provides visual interpretations of DP prototypes through public nearest-neighbor retrieval and SDXL+IP-Adapter-based generative proxies, which are evaluated using a self-referential fidelity metric.

Critical strengths

S1. Requiring no sample buffer, no retention of sensitive statistics across tasks, and explicit DP release of the label space addresses a side channel ignored by most DP continual-learning work. Using sums rather than means, and restricting prototype visualization to public data plus released parameters show good privacy awareness.

S2. Select appropriate baseline. Choosing Tobaben et al. (2026) as the primary baseline. They are the prior work with comparable, side-channel-aware DP continual-learning accounting.

Critical weaknesses

W1. The central ablation may be confounded by missing re-tuning. Table 5 attributes the method's gains largely to L_preserve, showing accuracy collapses from 83.28% to 40.43% (ϵ=8) when it is removed. But accuracy collapses from 81.39% to 58.82% (ϵ=1) which is better. These ablations reused the original hyperparameters without re-tuning, so the collapse maybe conflates the loss's actual contribution with hyperparameter mis-specification.

W2. The public proxy retrieves the nearest ImageNet-1K image, yet the backbone is pretrained on ImageNet-21K (which includes ImageNet-1K), so retrieval may reflect pretraining memory rather than the semantics of the private prototype. Fidelity (Eq.43) then checks whether the classifier assigns the proxy to its own prototype in the same latent space used for selection. I tend to self-consistency rather than human interpretability.

Questions for authors

Explain why the no-preservation variant scores higher at ϵ=1 (58.82%) than at ϵ=8 (40.43%). Justify the fixed preservation geometry (L=5 directions, r=0.1, σ_MMD=1, λ=(1,10,10)) relative to the scale of frozen ViT features. For retrieved ImageNet-1K images, would it be better to report agreement between the DP prediction and the public ground-truth label?

4 comments

We thank the reviewer for their careful evaluation of our work, constructive feedback, and recognition of the privacy-aware design and choice of baselines.

The central ablation may be confounded by missing re-tuning. Table 5 attributes the method's gains largely to L_preserve, showing accuracy collapses from 83.28% to 40.43% (ε=8\varepsilon=8) when it is removed. But accuracy collapses from 81.39% to 58.82% (ε=1\varepsilon=1) which is better. These ablations reused the original hyperparameters without re-tuning, so the collapse maybe conflates the loss's actual contribution with hyperparameter mis-specification.

Explain why the no-preservation variant scores higher at ε=1\varepsilon=1 (58.82%) than at ε=8\varepsilon=8 (40.43%).

Thank you for raising this important point. Our initial submission used imprecise language by saying we perform HPO on representative data, while we perform HPO on the first task following Tobaben et al. (2026), i.e. for each method and each seed, hyperparameters are optimized on the first task from the corresponding benchmark. HPO is performed independently each time, using a 70/30 training-validation split, and the selected hyperparameters are kept fixed throughout the continual learning sequence. Importantly, the preservation loss is zero on the first task because no previous classes have been learned. Thus, the HPO procedure does not directly optimize the preservation loss weight.

This protocol reflects a practical challenge in CL: future tasks are unavailable during initial hyperparameter selection. We therefore retain the hyperparameters selected on the first task and vary only the loss components in the ablations. This allows us to assess their contributions under a common training configuration.

Regarding the higher accuracy of the no-preservation variant at ε=1\varepsilon=1 (58.82%) compared to ε=8\varepsilon=8 (40.43%), one possible explanation is the implicit regularization induced by stronger privacy. Without the preservation loss, the projection is not explicitly constrained to preserve previously learned representations. Stronger privacy may reduce harmful adaptation to new tasks, whereas weaker privacy may allow greater representation drift. Additionally, we examined the learning rates selected by HPO across the five seeds. At ε=1\varepsilon=1, the selected learning rate is smaller in four out of five seeds, with a median of 0.00154 compared to 0.00269 at ε=8\varepsilon=8. These smaller learning rates may also limit representation drift and contribute to the observed difference: in these cases, smaller learning rate consistently leads to better accuracy.

We emphasize that these are plausible explanations. Nevertheless, the full method substantially outperforms the no-preservation variant at both privacy levels, supporting the importance of the preservation loss under our evaluation protocol.

We have revised Section 5 (Implementation Details) and Appendix F (Experimental Details) to clarify the HPO protocol. We have also added per-task accuracy and forgetting plots in Appendix G to illustrate the learning trajectories of different loss configurations and further demonstrate the role of the preservation loss in mitigating forgetting.

Justify the fixed preservation geometry (L=5 directions, r=0.1, σ_MMD=1, λ=(1,10,10)) relative to the scale of frozen ViT features.

Our choice of preservation geometry is motivated by Aghasanli et al. (2025), from which we adopt the number of directions (L=5L=5) and the MMD kernel bandwidth (σMMD=1\sigma_{\mathrm{MMD}}=1).

The radius r=0.1r=0.1 was selected based on preliminary experiments and the distances between released prototypes in the frozen backbone feature space. We experimented with several radius values and observed relatively little sensitivity to this parameter, so we fixed it across all experiments.

Finally, the loss weights λ=(1,10,10)\lambda=(1,10,10) were selected through preliminary experiments to balance the contributions of the three loss components. We kept them fixed across datasets and privacy budgets because they cannot be tuned in a realistic setting. As discussed regarding the previous comment, HPO in continual learning is particularly challenging because future tasks are unavailable during initial tuning. This is especially relevant to the preservation loss, which is inactive on the first task.

We have revised Appendix F (Experimental Details) to clarify the motivation for our preservation geometry and the selection of the radius. The justification for the loss weights was already provided in Appendix F.

AuthorsOpenReview ↗

Response (continued)

The public proxy retrieves the nearest ImageNet-1K image, yet the backbone is pretrained on ImageNet-21K (which includes ImageNet-1K), so retrieval may reflect pretraining memory rather than the semantics of the private prototype.

We used the ViT-B/16 architecture of [2] with the checkpoint of [1] whose training set explicitly excludes the ImageNet-1k validation set which we used for our public pool. (See [1], Section 3.1, following the procedure of [2], Section 4.1).

  1. Steiner, A., Kolesnikov, A., Zhai, X., Wightman, R., Uszkoreit, J., & Beyer, L. (2021). How to train your vit? data, augmentation, and regularization in vision transformers. arXiv preprint arXiv:2106.10270.
  2. Dosovitskiy, A. (2020). An image is worth 16x16 words: Transformers for image recognition at scale. arXiv preprint arXiv:2010.11929.

Fidelity (Eq.43) then checks whether the classifier assigns the proxy to its own prototype in the same latent space used for selection. I tend to self-consistency rather than human interpretability.

For retrieved ImageNet-1K images, would it be better to report agreement between the DP prediction and the public ground-truth label?

This would be very useful, but difficult because the label spaces do not align. A number of CIFAR-100 classes have no ImageNet-1K counterpart, and a direct label mapping holds only loosely for several others. Moreover, ImageNet-1K frequently contains more than one object, so single labels describe the frame only in part. An image labelled “baby”, for instance, will almost always show a diaper as well, and both are plainly visible.

To efficiently label the images, we used Claude to identify all visible CIFAR-100 classes in each public image. We conducted five independent runs and retained labels reported at least three times. We then evaluated the fidelity of the public proxies by measuring the fraction of classes whose retrieved images were annotated as containing the corresponding CIFAR-100 class. This metric, which we call fidelity (LLM judge), achieves 78/96 (81.25%) on Split-CIFAR-100 at ε=8\varepsilon=8. The annotation protocol, prompt, and five runs are provided in Appendix F.1, while the fidelity results are reported in Section 5.5 (Table 2).

We also renamed our original classifier-based fidelity metric (Eq. 43) to self-consistency, distinguishing agreement with the classifier's own predictions from the new LLM-based evaluation of whether the proxies visually represent their intended classes.

The corresponding revisions and additions are detailed in Sections 5.1 and 5.5 and Appendices F.1 and K.4.

We appreciate the authors' efforts to address my concerns. However, after considering Reviewer pjU7's comments, I agree that comparisons with established non-DP continual learning methods are necessary to better assess the proposed approach. This is particularly important given that the authors' method is largely inspired by [1], which is itself a non-DP continual learning method. In light of this concern, I have decided to lower my score to 2 (Weak Reject). [1] Agil Aghasanli, Yi Li, and Plamen Angelov. Prototype-based continual learning with label-free replay buffer and cluster preservation loss. In Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition Workshops, pp. 6545–6554, 2025.

Thank you for the clarification. We have added a comparison with two established non-private continual learning methods, CODA-Prompt (CODA-P) and InfLoRA, on Split-CIFAR-100 and Split-ImageNet-R, using the same task configurations. The results for both baselines are taken from Liang & Li (2024) and do not provide differential privacy guarantees nor interpretability.

On Split-CIFAR-100, our method achieves 83.15% final accuracy at =8, compared with 86.62% for CODA-P and 86.51% for InfLoRA. The performance gap is larger on Split-ImageNet-R.

We have added a summary in the main text and included the full comparison, along with evaluation metric definitions, in Appendix I.

On the performance, we emphasize that our method establishes a new SOTA for the problem. We demonstrate that our approach works clearly better than the previous SOTA (Cosine classifier) on Split CIFAR-100, and also show the limitations for future work (marginal improvement on Cosine classifier on Split-ImageNet-R).

Comments on the paper

1 comment
AuthorsOpenReview ↗

Global Comment

We thank all reviewers for their constructive feedback and suggestions, which have helped us substantially strengthen the manuscript. We have addressed the concerns raised and revised the paper accordingly. All changes are highlighted in blue.

The main revisions and additions are summarized below:

  1. Method and privacy guarantees (Sections 4.1 and 4.3) in response to reviewer pjU7: We clarified the motivation for freezing the pretrained backbone and adapting only a linear projection, as well as the scope of our privacy guarantees.

  2. Theoretical analysis (Section 4.4 and Appendix C) in response to reviewer HQLC: We substantially extended our theoretical analysis with four new theorems and proofs, examining Gaussian projection initialization, representation drift, the effects of DP-SGD noise, and accumulated margin changes across tasks.

  3. Experimental methodology (Section 5.1 and Appendix F) in response to reviewers rP2J and pjU7: We clarified the hyperparameter optimization protocol, the selection of preservation-loss parameters, and the experimental setup.

  4. Additional experimental evaluations (Sections 5.2 and 5.4; Appendices G-J) in response to reviewers rP2J and pjU7: We extended our evaluation to 20 sequential tasks on Split-CIFAR-100 and introduced domain-incremental experiments on CORe50. We also added stability-plasticity analyses, per-task accuracy and forgetting results, and computational and memory overhead analyses.

  5. Interpretability (Section 5.5 and Appendices F.1 and K.4) in response to reviewer rP2J: We strengthened the evaluation of prototype visualizations by distinguishing classifier self-consistency from semantic fidelity assessed using independent LLM annotations of public images.

  6. Limitations and discussion (Section 6) in response to reviewers pjU7 and HQLC: We expanded the discussion of the stability-plasticity trade-off, the limitations of adapting only a linear projection, and the scope of our theoretical and empirical findings.

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