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Back to the basics: Interpreting Vision Embeddings via Binary Sparse Autoencoders

Abstract

Sparse autoencoders (SAEs) have emerged as the primary framework for interpreting the internal representations of vision (and language) models, decomposing dense, entangled embeddings into sparse, more human-interpretable latent codes. Continuous activations trained under sparsity constraints have come to dominate this line of work, due to their manageable optimization dynamics. In contrast, latent codes remain scarce within the SAE setting, despite offering a natural and arguably unambiguous notion of concept presence. Binary SAEs trained with Gumbel relaxations or straight-through estimators are prone to training instability and typically underperform their continuous counterparts. In this work, we argue that binary SAEs are not intrinsically flawed: rather, it is they are trained that directly and disproportionately impacts the quality of their representations. To address this, we introduce (inary tom election by terative oordinate wapping), a binary SAE that draws inspiration from classical dictionary learning by casting binary code inference as a Gauss–Seidel local search over supports, in which every accepted coordinate swap strictly decreases the reconstruction objective. We compare BASICS-SAE against Gumbel-relaxed and Local Winner-Take-All binary SAEs, and against continuous TopK and BatchTopK SAEs, on CUB and ImageNet using CLIP and DINOv3 embeddings. Beyond reconstruction fidelity, we evaluate dictionary quality using downstream few-shot classification and formal mechanistic interpretability metrics, based on recently proposed concept alignment scores. BASICS-SAE is competitive against continuous baselines in reconstruction while substantially outperforming all binary and continuous models in downstream code quality and concept alignment in most settings. Our results establish binary SAEs, when paired with sequential coordinate selection, as a strong and promising foundation for vision interpretability.

Primary area:
interpretability and explainable AI
Keywords:
Sparse Autoencoders, Vision Interpretability, Dictionary Learning, Sparse Coding, Binary

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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_wQQkOpenReview ↗
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Paper summary

This paper revisits binary sparse representations for interpreting vision embeddings. Instead of learning a feedforward binary encoder through a continuous relaxation or a straight-through estimator, BASICS-SAE infers a fixed-cardinality binary code through iterative atom swaps. Each accepted swap reduces reconstruction error for the current dictionary. Dictionary learning uses ridge regression with exponentially decayed sufficient statistics. The experiments compare BASICS-SAE with continuous and binary SAE baselines on CLIP and DINOv3 embeddings, with additional DINOv2 and MP-SAE results in the appendix. The evaluation covers reconstruction, prototype-based few-shot classification, distribution shift, and concept alignment. The strongest results are the improvements over the relaxation-based binary baselines and the higher coalition-level TAPAScores.

Critical strengths

The method directly optimizes the binary reconstruction problem, and the local update is well motivated. Equations (7)–(9) correctly account for the interaction between the removed and inserted atoms. This gives a concrete guarantee for each accepted swap without relying on a surrogate gradient. The ablations also support the importance of refinement: on CUB, increasing the swap budget from 16 to 128 improves NMSE from 0.0777 to 0.0568 and 10-shot accuracy from 71.62% to 74.89%.

The evaluation goes beyond reconstruction and includes relevant checks in the appendix. BASICS improves substantially over the tested binary baselines, while remaining competitive with continuous models in several settings. For example, the DINOv3 Top-10 TAPAScore increases from 0.5278 for BatchTopK to 0.6822 for BASICS. The additional DINOv2 results, MP-SAE comparison, six-seed stability experiment, and inference-latency measurements make the empirical study more useful. I also appreciate that the paper reports cases where continuous models retain an advantage.

Critical weaknesses

The few-shot protocol needs clarification. The paper reports 50-shot CUB results, although the standard split has roughly 30 training images per class. An alternative split or sampling scheme could explain this, but it is not specified. The paper should also distinguish dictionary-training, prototype, and query images, clarify whether ImageNet-A/R prototypes use labeled target-domain data, and report the distance metric and feature normalization. These choices affect how the few-shot results should be interpreted.

The optimization guarantees go beyond what the algorithm establishes. Algorithm 2 only tries replacing the weakest active atom. If that replacement fails, it stops even when replacing another active atom could improve reconstruction, so it does not guarantee a one-swap local optimum. Similarly, combining historical codes, decayed statistics, and a separate moving-average bias update does not automatically guarantee consistent improvement of one fixed objective. The paper should distinguish the valid guarantee for individual swaps with a fixed dictionary from claims about the full online training procedure.

Questions for authors
  1. How are the few-shot support and query sets constructed? Please explain the CUB 50-shot setting, including the number of distinct support images per class and any resampling. Please also specify the dictionary-training split, prototype metric, normalization, and whether ImageNet-A/R prototypes use source-domain or target-domain labels.
  2. Does the implementation stop after testing only the weakest active atom, as Algorithm 2 states? If so, how often do other improving single swaps remain at termination? A comparison with checking all active removal candidates, at least on a smaller subset, would help establish the cost–quality trade-off.
  3. What objective is guaranteed to decrease during dictionary and bias updates? Please clarify how historical statistics, changing codes, ridge regularization, and the bias EMA fit into the monotonicity argument. Appendix A.1 also lists a decoder learning rate of 0.01; how is this used alongside the closed-form dictionary update?
  4. What exact TAPAScore protocol is used? Please identify the perturbation dataset, the matching/evaluation split, and the treatment of continuous activations. Since inference starts from a random support, are random draws controlled across each original/perturbed image pair? The six-seed experiment addresses aggregate training stability, but does not directly establish the stability of an individual image’s code under repeated inference. This distinction matters for attributing latent changes to the image intervention. Additional Comments
3 comments

We thank the reviewer for the careful questions, which we answer point by point. New experiments are summarised in the comment to all reviewers; this response is split into two parts.

W1/Q1: Few-shot protocol. We will add the full protocol to the main text.

  • Support and query sets. Support images come from the labelled training split; for nn-shot we take the first nn images of each class in dataset order, so all methods share the same support set. Queries are the full held-out test split, disjoint from the support images.
  • CUB "50-shot". CUB has only 29–30 training images per class, so this setting uses all of them, each image once. We kept the name for consistency across datasets and will rename it "all-shot" for CUB.
  • Resampling. The paper uses the single default support set. We now also evaluate 5 random draws per setting (without replacement within each class, shared across methods, dictionary fixed); the ranking of methods is unchanged (Table F).
  • Dictionary-training split. The SAEs are trained without labels on the training split of each dataset (CUB, ImageNet-1k); few-shot support images may overlap with the training data, but their labels are never used in training.
  • Metric and normalisation. Prototypes are the mean support code per class; queries are assigned by the highest dot product. Continuous codes (TopK, BatchTopK, MP-SAE) are L2-normalised before averaging and scoring; binary codes (BASICS, Gumbel, LWTA) have a fixed number of active units and constant norm, so normalisation cannot change the prediction.
  • ImageNet-A/R. Only source-domain labels are used: prototypes are built from ImageNet-1k training images of the 200 shared classes, with the dictionary trained on ImageNet-1k; ImageNet-A/R images serve only as queries.

Table F. Few-shot accuracy with resampled support sets (CLIP ViT-L/14, CUB, training seed 42). Mean ± std over the default support set and 5 random draws, shared across methods. 50-shot uses all training images per class, so it varies only for BASICS-SAE, through its random inference initialisation.

Method1-shot10-shot50-shot
TopK46.83 ± 1.5068.40 ± 0.8673.01 ± 0.00
BatchTopK46.67 ± 1.5367.89 ± 0.6772.66 ± 0.00
Gumbel-sigmoid45.34 ± 1.0663.28 ± 0.5566.23 ± 0.00
LWTA43.65 ± 1.5064.67 ± 0.2767.79 ± 0.00
BASICS-SAE47.65 ± 1.0375.06 ± 0.3879.43 ± 0.29

W2/Q2: Behavior of Algorithm 2. Algorithm 2 is not clear enough, and we will rewrite it. The procedure applies a sequence of swaps: after each accepted swap the weakest active atom is recomputed, so many different atoms can be replaced during one encoding. At each step, however, only the weakest atom and its best replacement are tested, and the algorithm stops when this swap no longer lowers the loss or the budget is exhausted. Termination therefore does not certify a one-swap local optimum; what we guarantee, for a fixed dictionary, is that every accepted swap strictly decreases the loss.

To measure how much this matters, we added an all-pairs variant that tests every (remove, add) pair at each step, and checked at termination whether any improving single swap remains (Table G). Improving swaps do remain after Algorithm 2 for most images, but the best remaining gain is about 0.02%0.02\% of the input energy. Removing them lowers NMSE by about 22% relative and leaves few-shot accuracy on par, at about 4×4\times the inference cost. We argue that the weakest-atom rule offers a favourable balance between cost and quality, and will report the all-pairs variant in the appendix.

Table G. Weakest-atom swaps vs. all-pairs search (CUB, CLIP ViT-L/14, mean of 6 training seeds). Swaps left: share of test images for which some single swap still lowers the loss at termination. Best gain: mean gain of the best remaining swap, relative to ∥xc∥2\|x_c\|^2. Cost: inference time per query batch relative to Alg. 2.

Code searchSwaps leftBest gainNMSE ↓1-shot10-shot50-shotCost
Weakest atom (Alg. 2)63.3%2.3⋅10−42.3\cdot10^{-4}0.056948.8375.0279.091×
All pairs0.4%2.1⋅10−9\mathbf{2.1\cdot10^{-9}}0.055848.1874.6778.893.8×

W2/Q3: Objective and decoder learning rate. No single objective decreases monotonically over the full online procedure, and we will remove that claim. For a fixed dictionary and bias, every accepted swap strictly lowers the exact reconstruction loss of the current batch. The dictionary update W=(A+λI)−1BW=(A+\lambda I)^{-1}B is the exact minimiser of a ridge-regularised loss over all past batches, exponentially down-weighted by γ\gamma (online dictionary learning with forgetting, Mairal et al., 2010). As stated in the paper, the bias is updated by an exponential moving average (rate η\eta) of the residual left after decoding; this is a stabilising heuristic, and we make no descent claim for it. These steps do not chain into one monotone objective: the statistics contain stale codes, each new batch reshapes the surrogate, the bias shifts the centring of later batches, and the ridge term appears only in the surrogate. The "decoder learning rate 0.01" in Appendix A.1 is mislabelled: it is the bias EMA rate η\eta. The dictionary has no learning rate, as it is set by the closed-form solve. We will correct the label.

Q4: TAPAScore protocol and inference randomness. We apply the protocol of Klotz et al. (2026) unchanged for all methods. Matching: latent–attribute matching is computed on the held-out CUB test split (5,790 images; the SAEs are trained on the training split without labels) against the CUB attribute annotations, using FBMP with F0.5F_{0.5} and coalition sizes {1,3,5,10}\{1,3,5,10\} (Top-1 to Top-10 in Table 3). Perturbation dataset: SynCUB (Klotz et al., 2026), 2,933 original/edited pairs in which exactly one attribute is replaced by another. Continuous activations: every unit with non-zero activation counts as active, and no threshold is tuned (see our response to Rev. GUFJ, Q2).

Inference randomness. The reviewer's distinction is correct: the six-seed experiment measures training stability, not the stability of an individual image's code. In the reported results, the two images of a pair were encoded with independent random initialisations. We now quantify this effect. For a single image, re-encoding with a different seed changes part of the code: the sets of active units of two encodings (K=3072,k=32K=3072, k=32) have a mean Jaccard index of 0.510.51, against 0.0050.005 for two random sets of kk units, while reconstruction error stays the same. Because TAPAScore compares the codes of an original/perturbed image pair, this variation from the initialisation adds noise to the measured latent change and can artificially degrade the scores. We therefore provide two ways to control the randomness for intervention-based metrics, both affecting only the inference stage: (i) shared random initialisation, where both images of a pair start from the same random initial set of active units, so the original stochastic inference is kept but the draw is paired; and (ii) deterministic initialisation with greedy BMP followed by the same swaps, which makes every code a fixed function of the image and matches random initialisation in quality on CUB (NMSE 0.0560.056 vs. 0.0570.057). Controlling the randomness only strengthens the TAPAScore results (Table H). We will add this analysis and both inference options to the paper.

Table H. TAPAScore of BASICS-SAE under different inference initialisations (CLIP ViT-L/14, CUB/SynCUB, FBMP F0.5F_{0.5} matching; same trained model).

BASICS-SAE inferenceTop-1Top-3Top-5Top-10
Independent random init (paper)0.39490.61170.61590.6208
Shared random init per pair0.45240.67580.69230.7112
Deterministic (BMP) init0.42900.70330.71120.7301

Dear Rev. wQQk,

We would like to follow up on our response and the additional clarifications and experimental results provided. We welcome any further comments or remaining concerns that we might address prior to the close of the discussion phase. Thank you once again for your time and review.

Best regards, The Authors

Reviewer_N1ezOpenReview ↗
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Paper summary

This paper introduces BASICS-SAE, a binary sparse autoencoder for interpreting vision embeddings. It replaces gradient-based approximations to binary selection with iterative support swaps, alternating with closed-form dictionary updates. The method is evaluated on CLIP and DINOv3 embeddings, with additional DINOv2 results, using reconstruction, few-shot classification, distribution shift, and concept alignment metrics. The results suggest that better optimization can substantially improve binary SAEs, although the advantages are not uniform across settings.

Critical strengths
  • The paper revisits whether previous difficulties with binary SAEs reflect limitations of the representation or its optimization. The swap rule is straightforward and guarantees that each accepted swap reduces reconstruction loss for a fixed dictionary. This offers a well-motivated alternative without relying on approximate gradients through binary decisions.

  • The classification and interventional concept alignment results provide useful evidence about the learned representations. For example, on CLIP/CUB, BASICS improves 10-shot accuracy from 66.9% for the continuous baselines to 74.9%, alongside stronger interventional alignment (Tables 1 and 3). Experiments across backbones and the swap-budget ablation strengthen the empirical case.

Critical weaknesses
  • The sources of improvement are not fully separated. BASICS changes both code inference and dictionary learning, while also using more inference computation. The MP-SAE comparison in Appendix A.4 is helpful, but does not isolate the contributions of swap-based search and closed-form updates. The evidence therefore supports the overall method more clearly than it identifies which optimization choices explain the shortcomings of previous binary SAEs.

  • The optimization guarantees need a narrower statement. The decrease in loss from an accepted swap is clear for a fixed dictionary. However, it is less clear how decayed historical statistics, ridge regularization, and bias updates jointly decrease a single objective throughout training. Also, Algorithm 2 stops when the weakest active atom has no beneficial replacement, which does not rule out improvements from replacing another atom. These points do not invalidate the empirical results, but limit the interpretation of the convergence claims.

Questions for authors
  • Evidence request: Do you have a controlled comparison that separates swap-based inference from closed-form dictionary learning—for example, keeping the swap procedure fixed while changing the dictionary update? If not, please clarify which conclusions concern the complete method rather than an individual component.

  • Clarification: Does the monotonic optimization claim apply only to code inference with a fixed dictionary, or to the full online training procedure? If the latter, what shared objective is guaranteed to decrease? Please also clarify whether Algorithm 2 can terminate while beneficial swaps involving other active atoms remain.

3 comments

We thank the reviewer for the precise reading. Both points are addressed with new experiments and narrowed statements (shared comment (1) and (2)).

W1/Q1: Separating code inference from the dictionary update. Yes, we now have these controlled experiments (Table A in the shared comment). Keeping the swap search fixed and replacing the closed-form ridge update by gradient descent on the same objective lowers quality on both datasets (10-shot accuracy from 75.275.2 to 73.3%73.3\% on CUB and from 67.367.3 to 65.3%65.3\% on ImageNet-1k; ImageNet NMSE from 0.1000.100 to 0.1280.128), so the closed-form update accounts for a substantial part of the gain. Keeping the ridge update fixed and replacing the swaps by greedy BMP also lowers quality, by a small but consistent margin on CUB (6 seeds) and a larger one on ImageNet-1k. Additional inference compute alone does not explain the gain: exact OMPR search on a TopK dictionary improves reconstruction (NMSE 0.072→0.0510.072 \to 0.051) but not few-shot accuracy (67.967.9 vs. 67.7%67.7\% 10-shot, against 75.3%75.3\% for BASICS-SAE; Table B in our response to Rev. GUFJ). On our dictionary, a greedy start without swaps matches BASICS swap inference on CUB, while underperforming on ImageNet-1k (65.265.2 vs. 67.1%67.1\% 10-shot; Table C in our response to Rev. GUFJ). Hence both components contribute, with a dataset-dependent share for the swap search. We will state explicitly which conclusions concern the complete method and which concern individual components.

W2/Q2: Scope of the guarantees.

  • Fixed dictionary only. The monotonicity claim applies only to code inference with a fixed dictionary: each accepted swap strictly decreases the exact reconstruction error (Eq. (7)–(9)).
  • Online training. The dictionary step exactly minimises the decayed, ridge-regularised surrogate built from past batches, as in online dictionary learning (Mairal et al., 2010). Because codes change between batches, the statistics are decayed, and the bias follows an EMA, we do not claim that a single objective decreases during training, and we will remove any wording that suggests it.
  • Termination of Algorithm 2. Yes, Algorithm 2 can stop while improving swaps involving other active atoms remain, since it only tests the weakest active atom. An all-pairs variant that certifies a one-swap local optimum lowers NMSE slightly (0.05580.0558 vs. 0.05690.0569), leaves few-shot accuracy on par (74.774.7 vs. 75.0%75.0\% 10-shot, 6 seeds) and is about 4×4\times slower at inference (Table G in our response to Rev. wQQk). We therefore argue that the weakest-atom rule offers a favourable balance between cost and quality, and will describe it accurately.

Dear Rev. N1ez,

We would like to follow up on our response and the additional clarifications and experimental results provided. We welcome any further comments or remaining concerns that we might address prior to the close of the discussion phase. Thank you once again for your time and review.

Best regards, The Authors

Reviewer_N1ezOpenReview ↗

following comment from reviewer N1ez

The authors have conducted corresponding experiments and included the concise explanation about optimization scope. My concerns are mostly addressed. However, I still think a score of 3 is suitable for this paper, so my positive attitude remain.

Reviewer_GUFJOpenReview ↗
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Paper summary

In this paper, the authors make the key observation that binary sparse autoencoders (SAEs) are not intrinsically inferior to continuous SAEs. Their performance has been limited by poorly trained Gumbel relaxations or straight-through estimators. To address this issue, the authors propose BASICS-SAE (Binary Atom Selection by Iterative Coordinate Swapping), a binary SAE that formulates binary code inference as a Gauss–Seidel local search over supports. The proposed method is evaluated using CLIP and DINOv3 embeddings on the CUB and ImageNet datasets and compared against various baselines. The experimental results demonstrate that the proposed method achieves competitive performance compared with the evaluated baselines.

Critical strengths
  1. In general, the paper is well written and easy to follow, and the proposed method is well motivated. Extracting support-swap inference with a closed-form dictionary step is simple and effective. It addresses the failure modes of previous binary SAEs and achieves better performance in both NMSE and few-shot learning accuracy. These results support the important claim that the failures of previous binary SAEs were due to their optimisers rather than binarity itself.

  2. Across two or three backbones and two datasets, BASICS achieves competitive NMSE and the best few-shot accuracy and TAPAScore in most configurations. Its results are stable across random seeds (standard deviation ≤ 0.45%), and the code is provided.

Critical weaknesses
  1. Some key controls are missing from the evaluation or require further investigation: (i) continuous kk-sparse codes inferred using the same swap/OMPR solver on a learned dictionary; (ii) a TopK-SAE dictionary with BASICS-style iterative inference; (iii) a BASICS dictionary with one-shot TopK-of-hh inference; and (iv) binary matching pursuit (BMP) as a training-time solver. In addition, the scope of the proposed method appears somewhat limited, as it is evaluated only with pooled embeddings.

  2. Several aspects require further clarification or additional evidence: (i) Few-shot prototype accuracy measures discriminability rather than interpretability. Why is this considered sufficient evidence for demonstrating the effectiveness of the proposed method? (ii) The interpretability evaluation relies on a single family of recent metrics and is conducted on only one dataset (CUB). (iii) It would be beneficial to include qualitative results. (iv) The baselines are reported based on a single run, and several performance margins are smaller than one percentage point.

Questions for authors

Please address the previous comments and provide a point-by-point response. In addition, please address the following questions:

What specific few-shot classification method is used (including the distance metric, normalization, and prototype averaging) for binary versus continuous codes? Why do sparse codes outperform raw features?

In TAPAScore and the matching procedure, how are continuous activations thresholded to determine whether a unit is “firing” or “not firing”? Could a continuous SAE with an optimized per-unit threshold close the performance gap?

5 comments

We thank the reviewer for the detailed review. New experiments are summarised in the comment to all reviewers; this response is split into two parts.

W1: Missing controls. We ran all four (shared comment (1)): (i) continuous kk-sparse codes from exact OMPR search on a learned TopK dictionary improve reconstruction (NMSE 0.072→0.0510.072 \to 0.051) but not few-shot accuracy (67.967.9 vs. 67.7%67.7\% 10-shot, against 75.3%75.3\% for BASICS-SAE; Table B); (ii) BASICS-style binary inference on a TopK dictionary fails (10-shot 28.0%28.0\% at best), since that dictionary was learned for continuous coefficients; (iii) the BASICS dictionary with one-shot top-kk-of-hh inference degrades sharply (NMSE 0.1840.184 vs. 0.0570.057, 10-shot 66.066.0 vs. 75.3%75.3\%; Table C); (iv) BMP as training-time solver is slightly but consistently worse on CUB over 6 seeds and clearly worse on ImageNet-1k (Table A in the shared comment).

Table B. OMPR on a learned TopK dictionary (CLIP ViT-L/14, CUB, single runs, default support set; continuous coefficients with least-squares refit, up to 128 iterations).

DictionaryEncodingNMSE ↓1-shot10-shot50-shot
TopK-SAETopK encoder0.071846.0867.7373.01
TopK-SAEOMPR, top-kk of hh init0.051245.0767.2972.80
TopK-SAEOMPR, random init0.051246.1167.9072.57
TopK-SAEBinary Swap search (random init)12.600.430.390.60
TopK-SAEBinary Swap search (top-kk of hh init)12.208.3028.036.40
BASICS-SAEBinary swap search0.056946.9875.3279.40

Table C. Inference initialisation on a trained BASICS dictionary (CLIP ViT-L/14, one training seed, default support set; swap budget in brackets). BMP: greedy binary matching pursuit (deterministic).

DataInference initNMSE ↓1-shot10-shot50-shot
CUBTop-kk of hh (0)0.183845.3965.9870.76
Top-kk of hh (128)0.060244.7372.6377.98
Random (128)0.056946.9875.3279.40
BMP (0)0.056648.2075.1879.70
BMP (128)0.056147.9175.0979.69
ImageNetRandom (128)0.100941.5367.1370.81
BMP (0)0.109138.6065.2069.63
BMP (128)0.103039.6266.2970.20

W1: Pooled embeddings. All experiments use pooled image embeddings, which we now state explicitly. This is the representation used by retrieval, zero-shot and concept-bottleneck pipelines, and the level at which TAPAScore's interventions are defined. Extending BASICS to per-token activations is an important next step that we leave to future work and will discuss in the limitations.

W2-i: Few-shot vs. interpretability. We agree that few-shot accuracy measures discriminability, not interpretability. We use it to check that binary codes retain semantic information; interpretability claims rest on concept alignment (FBMP matching, TAPAScore) and activation prevalence. We will reword the abstract and Sec. 4 accordingly.

W2-ii: Single metric family, single dataset. CUB is the only dataset we use with attribute annotations suitable for concept matching, and SynCUB provides the matching interventions, which is why concept metrics are reported there. We will state this as a limitation.

W2-iii: Qualitative results. We will add a figure of randomly drawn (uncurated) units, showing for each unit the images most and least aligned with its atom. We will label it as illustrative, not as evidence of monosemanticity.

W2-iv: Statistical significance. All baselines now have 6 training seeds (Table D), and few-shot results are repeated over resampled support sets (Table F in our response to Rev. wQQk). BASICS-SAE's gains in NMSE and 10-/50-shot accuracy lie far outside the seed spread; at 1-shot the differences are about the size of the spread, and we now describe them as "on par".

Table D. Training-seed variability (CLIP ViT-L/14, CUB, K=3072K=3072, k=32k=32). Mean ± std over 6 training seeds; default support set.

MethodNMSE ↓1-shot10-shot50-shot
TopK0.0724 ± 0.000646.56 ± 0.9267.11 ± 1.0972.27 ± 0.86
BatchTopK0.0686 ± 0.000446.01 ± 0.4967.16 ± 0.6772.51 ± 0.74
Gumbel-sigmoid0.1978 ± 0.001245.81 ± 0.5963.75 ± 0.4866.42 ± 0.52
LWTA0.1330 ± 0.000344.82 ± 0.3664.75 ± 0.2368.07 ± 0.36
BASICS-SAE0.0569 ± 0.000247.85 ± 0.4575.17 ± 0.2878.94 ± 0.32

Q1: Few-shot protocol. Each class prototype is the mean of the codes of its support images (first nn per class, or 5 random draws in the new experiments), and each query is assigned to the prototype with the highest dot product, for all methods. Continuous codes are L2-normalised before averaging and scoring; binary codes have a fixed number of active units and thus constant norm, so normalisation cannot change the prediction.

Why do sparse codes outperform raw features? We hypothesise that part of the gain over raw features comes from training the SAEs, without labels, on the target dataset: their dictionaries capture the concepts that vary within that domain, such as the fine-grained parts and colour patterns that distinguish bird species on CUB, so a sparse code describes each image by the few such concepts it contains. Raw CLIP embeddings, in contrast, are general-purpose and mix these cues with many factors irrelevant to the task, so comparing images by their active concepts emphasises the class-relevant information that prototype-based classification relies on. We offer this as an intuition rather than a verified explanation.

Q2: Thresholding of continuous activations. We use the matching and TAPAScore protocol of Klotz et al. (2026) unchanged for all methods. No threshold is tuned: a unit is "firing" when its activation is non-zero (>0>0), i.e. when it belongs to the set of active units chosen by the SAE's own sparsifier, e.g., top-kk for TopK, so every method is evaluated on the same set of units it uses for reconstruction. To test whether per-unit thresholds close the gap, we applied post-hoc thresholds to TopK codes at per-unit activation percentiles p∈{25,50,75}p \in \{25, 50, 75\} (Table E). The best setting (p=25p=25) improves TopK but remains below BASICS-SAE at every coalition size. Tuning thresholds against the attribute labels themselves would use the evaluation annotations, so we do not consider it a fair comparison.

Table E. TAPAScore of TopK with post-hoc per-unit thresholds (CLIP ViT-L/14, CUB, FBMP F0.5F_{0.5}). τj\tau_j is the pp-th percentile of unit jj's positive activations; a unit fires iff zj≥τjz_j \ge \tau_j; p=0p=0 is the standard non-zero rule. Active: mean number of firing units per image.

MethodActiveTop-1Top-3Top-5Top-10
TopK, p=0p=0 (paper)320.35320.51280.52400.5319
TopK, p=25p=2524.00.38900.57790.59600.6140
TopK, p=50p=5016.10.35050.48180.50940.5486
TopK, p=75p=758.10.22470.41600.43470.4811
BASICS-SAE (paper)320.39490.61170.61590.6208

Dear Rev. GUFJ,

We would like to follow up on our response and the additional experimental results provided. We welcome any further comments or remaining concerns that we might address prior to the close of the discussion phase. Thank you once again for your time and review.

Best regards, The Authors

Comments on the paper

1 comment

We thank the reviewers for careful and constructive reviews. Three concerns recur: where the improvement comes from, the scope of the guarantees, and statistical reliability. We address them here with new experiments; Table A is below, and the remaining tables (B–H) are in the individual responses, as indicated.

(1) Where the improvement comes from (Rev. GUFJ W1, Rev. N1ez W1/Q1). We added controls that change one component at a time.

  • Code search, same dictionary update (Table A). Replacing the swaps by greedy binary matching pursuit (BMP) during training lowers quality: slightly but consistently on CUB over 6 seeds (NMSE 0.05830.0583 vs. 0.05690.0569; 10-shot 74.274.2 vs. 75.2%75.2\%; 1- and 50-shot on par), more on ImageNet-1k (NMSE 0.1390.139 vs. 0.1000.100; 10-shot 63.663.6 vs. 67.3%67.3\%).
  • Dictionary update, same code search (Table A). Gradient descent on the same objective instead of the closed-form ridge solve lowers quality (10-shot 75.2→73.3%75.2 \to 73.3\% on CUB, 67.3→65.3%67.3 \to 65.3\% on ImageNet-1k).
  • Swap-based inference on a continuous dictionary (Table B, response to Rev. GUFJ). Exact OMPR search with least-squares refit on a frozen TopK-SAE dictionary lowers its NMSE from 0.0720.072 to 0.0510.051 (below BASICS-SAE) but does not alter few-shot accuracy (67.967.9 vs. 67.7%67.7\% 10-shot; BASICS-SAE 75.3%75.3\%).
  • Binary inference on a continuous dictionary. Our binary swap search on the same TopK dictionary fails (10-shot 28.0%28.0\% from a top-kk-of-hh start, chance level from a random start) suggesting that binary inference requires a dictionary trained jointly with binary codes.
  • One-shot inference on our dictionary (Table C, response to Rev. GUFJ). Encoding the BASICS dictionary with one-shot top-kk-of-hh inference degrades it sharply (CUB NMSE 0.1840.184 vs. 0.0570.057; 10-shot 66.066.0 vs. 75.3%75.3\%), whereas a greedy BMP start without swaps is on par with swap-based inference on CUB but not on ImageNet-1k (10-shot 65.265.2 vs. 67.1%67.1\%).

Both the code search and the dictionary update contribute, and better code search alone does not explain the results: exact search on a dictionary learned for continuous codes improves reconstruction but not discriminability. We will add these controls and state which conclusions concern the full method and which single components.

Table A. Separating code search from the dictionary update (CLIP).

DataCode searchDictionary updateNMSE ↓1-shot10-shot50-shot
CUBGreedy (BMP)Closed-form0.058347.1574.2378.71
Swaps (BASICS)Gradient descent0.059046.3773.3377.04
Swaps (BASICS)Closed-form0.056947.8575.1778.94
ImageNetGreedy (BMP)Closed-form0.138941.0863.6167.63
Swaps (BASICS)Gradient descent0.128041.5365.3269.13
Swaps (BASICS)Closed-form0.10041.867.371.0

(2) Scope of the optimisation guarantees (Rev. N1ez W2/Q2, Rev. wQQk W2/Q2/Q3). We agree that our wording overstated them, and we will narrow it.

  • For a fixed dictionary, each accepted swap strictly decreases the exact reconstruction error (Eq. (7)–(9)).
  • The dictionary step exactly minimises a ridge-regularised loss over past batches, exponentially down-weighted, with their codes frozen (Mairal et al., 2010). We do not claim that any specific objective decreases over the full online procedure.
  • Algorithm 2 tests only the weakest active atom at each step, so termination does not certify a one-swap local optimum. An all-pairs variant that does ensure it (Table G, response to Rev. wQQk) lowers NMSE by about 22% relative, leaves few-shot accuracy on par, and costs about 4×4\times more at inference, so the weakest-atom rule offers a favourable balance between cost and quality.

(3) Statistical reliability (Rev. GUFJ W2-iv, Rev. wQQk). All baselines now have 6 training seeds on CUB (Table D, response to Rev. GUFJ). BASICS-SAE has the best NMSE and the best 10- and 50-shot accuracy (75.2±0.375.2 \pm 0.3 and 78.9±0.378.9 \pm 0.3%, against at most 67.267.2 and 72.572.5% for the continuous and relaxed binary baselines), far outside the seed spread; at 1-shot the differences are about the size of the spread, and we now describe them as "on par". The ranking is unchanged under 5 random support draws (Table F, response to Rev. wQQk). Inference randomness of individual codes, and two ways of controlling it that improve TAPAScore, are discussed in our response to Rev. wQQk (Q4, Table H).

Smaller revisions. We will (a) fully specify the few-shot and TAPAScore protocols in the main text (details in the individual responses); (b) present few-shot accuracy as a measure of discriminability, not interpretability; (c) relabel the "decoder learning rate" (A.1) as the bias EMA rate; (d) rewrite Alg. 2 to show the swap loop and stopping rule explicitly; (e) add uncurated qualitative examples of randomly drawn units.

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

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