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Under review as a conference paper at ICLR 2027

Retrieval Gains, Similarity Losses: Controllable Specialisation for Entity-Specific Few-Shot Adaptation

Abstract

Large pretrained image encoders capture general visual similarity well, but this can be too coarse when retrieval must identify an operationally defined entity such as a specific character, logo, or product variant. We study target-specific few-shot retrieval adaptation: independently learning a lightweight head for each target from ten target and ten non-target images while keeping the encoder frozen. The adaptation improves target retrieval, but systematically degrades similarity judgement on general image pairs that were not used for adaptation. Across CLIP ViT-L/14, DINOv3 ViT-B/16, and SigLIP base-patch16-224, with both a linear head and an MLP with one hidden layer, Recall improves and semantic AUROC declines in all six conditions; visual AUROC declines in five, with CLIP–MLP as the exception. On 100 entities, the linear head raises Recall@5 from 80.00% to 86.75% on CLIP, from 55.92% to 62.25% on DINOv3, and from 82.17% to 87.33% on SigLIP. The trade-off persists across head structures, while its magnitude varies: the MLP loses about twice as much semantic AUROC as the linear head on all three encoders, whereas retrieval ordering depends on the encoder and cutoff. Interpolating frozen and adapted scores with one per-target scalar lets a user select an operating point on this specialisation–generality frontier. It does not remove the trade-off: CLIP admits useful intermediate settings, whereas DINOv3 has no non-zero setting that preserves both AUROCs at their frozen levels. Thus, the central design question is not whether to adapt, but how much generality to exchange for target-specific retrieval.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
few-shot learning, image retrieval, representation learning, metric learning, adaptation, negative transfer, pretrained vision encoders

Reviews

Among:
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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_hi1rOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
Read review
Paper summary

The paper trains a small head for each entity on top of a frozen image encoder. Each entity uses 10 target images and 10 non-target images, with a two-group contrastive loss. The head is then used to rescore the gallery. The same heads are evaluated on two things. The first is retrieval (Recall@K over 100 entities). The second is 304 human-annotated image pairs (AUROC for semantic similarity and visual similarity). Across all six combinations of CLIP, DINOv3 and SigLIP with linear and MLP heads, Recall goes up and semantic AUROC goes down slightly. The paper proposes a per-entity scalar that mixes the frozen score and the adapted score, and uses it to choose an operating point. The authors say this works on CLIP and does not work on DINOv3.

Critical strengths
  1. Evaluating the same heads on two dimensions is a reasonable design, and the main numbers check out. Tables 1-4 match the results file shipped with the supplementary material. The manifests show no image overlap between the image-pair set and the retrieval images. The code does what Sec. 4 describes.
  2. The authors are fairly candid about the limitations. Only a single seed is used, Table 8 gives per-entity results, the margins are pre-registered, and the effect sizes are not overstated.
Critical weaknesses
  1. Writing and figures. The paper is hard to read. The setup, definitions and key concepts are scattered across different sections and appendices, and the logic does not flow. Some sentences look like internal notes that were not fully removed ("taken from the shipped checkpoints rather than from the design document", p12, and "accompany Appendix G and Appendix G", p17). PCSF is never spelled out, and the epsilon in Eq. 8 is never given. Figure 1 and Figure 2 are schematics built from icons. Neither of them clearly conveys the motivation or the method. The paper does not contain a single example of a real retrieval result. For a paper about operator-defined entities, this is strange. I had to read the code to understand what they actually did.

  2. Method. The way the method is built already determines that it will show the trade-off the paper reports, and the paper offers no way to deal with it. The two-group contrastive loss pulls ten unrelated non-target images into the same cluster. This is bound to distort the geometry of the similarity space. The authors say so themselves in Sec. 4.2, but they keep the loss anyway. The head projects 768 dimensions down to 128, so information is lost before training even starts. The only "control" mechanism is a per-entity linear interpolation between the frozen score and the adapted score. The authors acknowledge that this is structurally WiSE-FT (Sec. 2), and later say it is not their proposed method (Sec. 6.3, Sec. 8). So the paper designs a head that is bound to lose generality, measures that it loses generality, and in the end does not give the reader a method. The finding itself (specialising a representation costs generality) is already known from the feature-distortion literature that the paper cites.

  3. Experiments. The controls needed to attribute the effect to the adaptation are all missing. There is no untrained head, no random 768-to-128 projection, no label-shuffled head, and no prototype baseline on the same 10+10 images. The authors themselves say in Sec. 2 that a prototype is the most direct comparison. All heads start from the same seed, and the whole paper uses only one seed. The effect is also small. Semantic AUROC drops by 0.005 to 0.016, which falls within the authors' own pre-registered margin of 0.010 (Table 14). In addition, the results on "controllability" contradict each other. Fig. 3b shows R@5 of about 81.8 at alpha=1, while Table 1 reports 86.75. The alpha selected by outer-CV is 0.05, and the held-out gain is zero (Table 11).

Questions for authors
  1. Does the AUROC drop still hold up after a pair-level bootstrap or a DeLong test?
  2. Do the fused rows and the alpha=1 rows in Table 9 come from the same set of heads? Why does Fig. 3b give about 81.8 at alpha=1?
  3. How are the negatives chosen? What happens if the negative pool shares no identities with the gallery?
  4. Please show real retrieval results. Pick a few entities and show, side by side, the query, the top-k images returned by the frozen encoder, and the top-k images returned by the adapted head. Mark the non-target images that are easy to confuse. Right now there is no way to see what the head actually changes.
3 comments
AuthorsOpenReview ↗

Response to Reviewer hi1r

We thank the reviewer for the detailed critique. We agree that the original paper was hard to follow and lacked controls separating projection from training. We restructured the Introduction, protocol, results and limitations, clarified the role of PCSF, and removed internal-note text.

1. Presentation and retrieval examples. Figure 1 now shows top-5 rankings for three real queries as T/L/O/U-labelled outcome tiles (target/look-alike/other entity/unrelated), comparing frozen, MLP and logistic regression. Appendix I.1 (Table 22) describes each non-target item. We cannot redistribute the third-party images or entity names, so this is evidence from real rankings, but it does not fulfill the request for side-by-side image examples.

2. Same-support and untrained controls. We added positive prototype, positive-negative prototype, query expansion and logistic regression on frozen features using the same enrollment support set (Section 6.2, Table 1; Appendix I). Logistic regression exceeds the trained MLP in Recall@5 by +6.17 [95% CI +4.17,+8.33], +10.08 [+6.00,+14.17], and +3.92 [+2.00,+6.00] percentage points on CLIP, DINOv3 and SigLIP. This concerns registered-entity membership retrieval, not query-conditioned visual search.

Five-seed matched controls evaluate initial and trained heads, identity/random 768-D heads, random/transductive-SVD 128-D projections and 128-768-D widths (Section 6.4; Table 3; Appendices H/J). On CLIP, the trained identity-initialised 768-D head gains +6.70 Recall@5 points with a -0.04-point semantic-AUROC change; the random 128-D linear head already has a -0.74-point semantic-AUROC difference before training (95% CI [-1.66,+0.10]). Point estimates suggest much of the narrow-head gap precedes training, although most initial intervals include zero. The matched protocol uses cached features and 30 updates, unlike canonical training. SVD is transductive. We did not run a label-shuffled-head control.

3. Statistical uncertainty and loss. We excluded two support-content-overlap pairs, leaving 302 pairs and 187 image-connected components. Bootstrap intervals resample targets and pair components, and also training seeds for matched controls (Sections 5-6.4; Appendices G/H/J). Canonical heads remain single-seed. On CLIP, semantic-AUROC changes are -0.81 [95% CI -1.25,-0.42] for Linear and -1.44 [-3.26,+0.37] points for MLP. We do not report a DeLong test. The +/-1-point descriptive margin was set post hoc: inclusion within it does not establish zero effect. Some matched training-effect intervals exclude zero.

In loss ablations, SupCon-pos improves Recall@5 over SupCon in all nine tested encoder/head conditions; Pair-BCE is lower in seven (Appendix J, Table 23). SupCon-pos also removes negative-anchor terms, so it does not isolate negative-negative attraction as a single cause.

4. Interpolation and prior inconsistency. We now separate descriptive full-pair sweeps from image-component-disjoint CV and target-level outer CV (Appendix K). Revised Figure 4(b) uses canonical raw scores: at alpha=1, CLIP Recall@5 is 86.75% (Linear) and 87.33% (MLP), agreeing with the main tables. The source of the old Figure 3(b) ~81.8% endpoint remains unidentified. The deployed multi-feature system is a distinct pipeline, not evidence for the canonical comparison. Interpolation/PCSF is exploratory: outer CV chooses alpha=0 in 138/150 cells, with a +1.37-point gain for CLIP MLP but no established robust operating point.

5. Negative identities and remaining limits. A retrospective filename-derived proxy audit finds proxy-identity overlap with the corresponding galleries in all 300 target-repeat units (3,000 negative-support uses, 300 unique image IDs, 100 proxy identities, and 12,000 different-image proxy matches), but no exact image-ID/hash overlap (Appendix J, Table 28). Proxies are not human-verified; no known disjoint replacement was available in the evaluated pool, and 1,500 gallery images lacked usable identity assignments. We therefore did not run identity-disjoint retraining. Generalization to unseen negative identities and catalog-scale effects remain untested.

The revised contribution is a diagnostic comparison under this protocol, not a new adaptation method or a universal trade-off claim.

I thank the authors for a detailed and honest response. The revision resolves two of my concerns. The paper is now readable, and most of the controls I asked for were run and reported as they came out: same-support baselines (Table 1), five-seed matched controls with untrained heads (Table 3), and intervals that account for pair dependence. Several concerns remain. The training hyperparameters of the canonical heads differ between the original paper and code (AdamW, learning rate 5e-5) and the revision (Adam, learning rate 1e-4), while the reported Recall values are unchanged. Negative supports share identities with gallery distractors in all 300 units, and no identity-disjoint control was run. The response says the source of the earlier ~81.8 endpoint is still unidentified. More importantly, the new controls did not confirm the original claim. They replaced it. A positive prototype and logistic regression on frozen features both beat the 128-D heads, and on point estimates most of the similarity change is already present in the untrained projection. The submission I reviewed claimed a controllable trade-off of a per-entity head, and the revision claims that standard frozen-feature baselines beat that head, with a new title and 35 pages in place of 20. I think this goes beyond what a revision in the discussion period should do, and the new paper would be better served by a fresh submission with a full review. I raise my rating from 1 to 2.

AuthorsOpenReview ↗

Response to Reviewer hi1r – Follow-up

Thank you for your thoughtful follow-up and for raising your rating. We appreciate your recognition of the improvements in readability and experimental controls. We also acknowledge that your remaining concerns are substantive.

1. Optimizer discrepancy and provenance

We investigated the discrepancy between the original submission, the distributed supplementary code, and the revised manuscript. The original submission and supplementary training recipe specified AdamW (learning rate 5×10−55\times10^{-5}, weight decay 10−410^{-4}, gradient clipping 0.85). However, archived trainer-initialization logs from June 2026 record Adam (learning rate 10−410^{-4}, weight decay 10−510^{-5}). The earlier trainer implementation and a September 2026 SigLIP experiment report also support Adam with these settings and gradient clipping at 1.0. Locally preserved manuscript source versions likewise specify Adam.

We acknowledge that the original submission and supplementary materials contained inconsistent training descriptions. We have corrected the supplementary training code, configurations, and documentation to reflect the settings supported by the execution records.

The reported canonical Recall values are unchanged because we did not retrain the canonical heads for this correction; we retained the previously reported results. Importantly, the available records do not link every individual checkpoint to its optimizer configuration. We therefore regard Adam as the best-supported configuration for the recorded training runs, but do not claim complete checkpoint-by-checkpoint provenance verification. We regret the original inconsistency.

2. Remaining experimental limitations

We agree that the identity-disjoint negative-support control remains missing. Our retrospective audit found filename-derived identity-proxy overlap with the corresponding galleries in all 300 target-repeat units, but these proxies were not independently verified as semantic identities. We found no exact support/gallery image-ID or hash matches and no known identity-disjoint replacement candidates in the evaluated pool. We do not claim generalization to unseen negative identities, and this limitation remains explicit in the revision.

The source of the earlier approximately 81.8% interpolation endpoint also remains unidentified. Revised Figure 4(b) was regenerated from the canonical raw-score series, and its CLIP linear endpoint at α=1\alpha=1 now agrees with the canonical Recall@5 of 86.75%. This corrects the current figure's consistency but does not explain the earlier discrepancy. We do not present its origin as resolved.

3. Interpretation of the revised contribution

We agree with your central observation: the additional controls did not confirm the original interpretation; they required us to change it.

The 128-D heads improve retrieval over frozen cosine ranking, but the new same-support comparisons show that logistic regression on frozen features outperforms the trained MLP on all three encoders. The matched controls further indicate, on point estimates, that much of the narrow-head semantic-AUROC gap is present before training.

Accordingly, we no longer claim that the per-entity head is superior to standard same-support baselines or that interpolation establishes a controllable trade-off. We have reframed the contribution as a diagnostic comparison, with narrower conclusions and explicit limitations.

We acknowledge that this is a substantial change in the paper's interpretation and scope. We understand your concern that such a revision may warrant a fresh submission and full review. We respect the Area Chair's judgment regarding how the revision should be treated within the current review process. We do not ask that the new controls be regarded as confirmation of the original claim.

Thank you again for your constructive criticism and for acknowledging the improvements.

Reviewer_m3i4OpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper studies per-entity few-shot retrieval adaptation. For each entity, a small head is trained on a frozen encoder (CLIP, DINOv3, SigLIP) using 10 positive and 10 negative images and a two-group supervised contrastive loss. Retrieval improves; for example, Recall@5 on CLIP goes from 80.00 to 86.75. The same heads give slightly lower AUROC on 304 human-labeled image pairs, which the authors describe as a specialization/generality trade-off. They also propose interpolating between frozen and adapted scores using a per-entity αc\alpha_c approach to select an operating point.

Critical strengths
  • The question is sensible. It is worth asking whether a head trained only to separate one entity keeps the similarity structure it never sees during training.

  • The experimental protocol is consistent across three encoders and two head types, and the paired bootstrap over targets is a reasonable choice.

  • The authors are open about the limits of their work, including the small effect size, the near-chance visual AUROC on CLIP, and the lack of reproducibility in some analyses.

Critical weaknesses
  • The practical relevance of the measured cost is unclear. Each head scores queries only for its own entity, and the frozen encoder remains available for general similarity judgments. It is unclear when the adapted score would ever be used for unrelated pairs, and the catalog-scale argument has not been tested.

  • The effect is very small (semantic AUROC drops by 0.008 on CLIP), and its uncertainty is likely underestimated. The bootstrap resamples targets, but all heads are scored on the same 304 pairs, and only one seed is used. Also, with about 30 training steps 5*10^-5, the head may stay close to its random initialization. A random-head or PCA-128 control is needed to show that the drop is due to adaptation rather than to the projection.

  • The frozen baseline does not use the 20 support images, while the adapted method does. Training-free baselines, such as prototype scoring or query expansion with the positives, could use the same information without changing the frozen geometry. It is also unclear where the negatives NcN_c come from, and whether they overlap with the hard negatives in the gallery.

  • The interpolation knob is claimed as a contribution but does not hold up. PCSF calibrates αc\alpha_c on the same pairs used for evaluation. Under target-level outer CV the selected α\alpha is around 0.04 with almost no gain, DINOv3 selects α\alpha=0, and the code is not released.

  • Some results need explanation. The unadapted numbers for the "multi-feature fused" deployed system (Tables 5 and 6) are identical to those of the single-encoder baselines: the shape-oriented row matches DINOv3, and the balanced row matches SigLIP. Figure 3(b) also does not seem to match Table 9 at α\alpha=0.75 and α\alpha=1

Questions for authors
  • How large is the AUROC drop for a random untrained head or a PCA-128 projection?

  • Where are the negatives NcN_c sampled from, and do any of them appear in the retrieval gallery?

  • How do training-free baselines that use the same support set compare on both Recall and AUROC?

  • How were the deployed-system baselines in Tables 5 and 6 computed?

2 comments
AuthorsOpenReview ↗

Response to Reviewer m3i4 (Part 1/2)

Thank you for your detailed critique. We agree that our original frozen-only comparison did not provide a fair same-support baseline and that pair dependence, seed variability, and projection effects required stronger controls. We have revised the experiments, clarified their limitations, and narrowed the paper's conclusions accordingly.

1. Practical relevance of task-external similarity

Our setting is membership retrieval for a known, registered entity, not general query-conditioned visual search. The frozen encoder remains available for general-similarity queries. Task-external AUROC measures what changes if an adapted representation is used beyond its registered task; it does not establish catalog-scale harm.

We additionally report descriptive other-entity-query results. On CLIP, the 128-D MLP reduces Off R@5 by 14.79 percentage points relative to frozen features, compared with 0.92 points for the trained 768-D linear head (Appendix J, Table 26). These findings characterize the evaluated heads but do not establish catalog-scale costs or effects.

2. Fair comparisons using the same support information

We added four baselines using the same available enrolment support set: positive prototype, positive-negative prototype, query expansion, and logistic regression (Section 4.2; Section 6.2, Table 1; Appendix I). Each uses the support information appropriate to its scoring rule.

Logistic regression on frozen features outperforms the trained MLP head on all three encoders. Recall@5 improves from 87.33% to 93.50% on CLIP, 63.33% to 73.42% on DINOv3, and 89.25% to 93.17% on SigLIP. The paired gains are +6.17 [95% CI: +4.17, +8.33], +10.08 [+6.00, +14.17], and +3.92 [+2.00, +6.00] percentage points, respectively.

These baselines leave the embedding unchanged, so pairwise AUROC remains that of the frozen encoder. We do not interpret classifier membership scores as pairwise similarity. The conclusion is limited to the evaluated registered-entity membership task.

3. AUROC uncertainty, initialisation, and training effects

We excluded two pairs with support-content overlap, leaving 302 human-labelled pairs and 187 image-connected components. Canonical confidence intervals now resample targets and pair components; five-seed matched-control intervals additionally resample training seeds (Sections 5-6.4; Appendices G/H/J).

The matched controls compare heads before and after training, including random and identity-initialised projections, transductive SVD projections, and output widths from 128 to 768 dimensions.

On CLIP, untrained random and SVD-initialised 128-D linear projections change semantic AUROC by -0.74 [-1.66, +0.10] and -1.50 [-3.06, -0.02] percentage points, respectively (95% CIs; Appendix H). The SVD basis is fitted to uncentred, normalised retrieval features and is transductive; we do not present it as an independent, gallery-disjoint PCA control.

The matched controls use cached features and 30 Adam updates, unlike canonical training, which remains single-seed. Point estimates indicate that much of the 128-D semantic-AUROC gap predates training, although most individual initial intervals include zero. The ±1-point practical margin was set post hoc and does not establish zero change.

AuthorsOpenReview ↗

Response to Reviewer m3i4 (Part 2/2)

4. Negative-support selection and identity overlap

Negative supports are out-of-entity images selected to include visually confusable examples.

A retrospective filename-derived identity-proxy audit found that all 3,000 negative-support uses across 300 target-repeat units were associated with other enrolled entities represented in the corresponding galleries. These uses comprise 300 unique image IDs and 100 proxy identities. We found 12,000 different-image support/gallery pairs sharing a proxy identity, but no exact image-ID or hash matches (Section 5; Appendix J, Table 28).

No known identity-disjoint replacement was available in the evaluated candidate pool, and 1,500 gallery images had no usable filename-derived identity. The proxies were not independently adjudicated. We therefore did not perform identity-disjoint retraining and cannot establish generalisation to unseen negative identities or infer that gallery identity labels were used to select negatives.

5. Interpolation and held-out calibration

We now treat interpolation as exploratory rather than a proposed solution to the trade-off. Appendix K distinguishes the descriptive full-pair sweep, image-component-disjoint pair-fold selection, and target-level outer cross-validation.

In the latter, α=0 is selected in 138 of 150 cells. CLIP MLP obtains a +1.37-point Recall@5 gain, but we do not claim a robust operating point. Fusion and calibration scripts are supplied; the original data and model assets required for full reproduction are not.

6. Figure endpoint and deployed-system results

We regenerated the revised Figure 4(b) from the canonical raw-score results. At α=1, the CLIP Recall@5 endpoints now agree with the canonical results: 86.75% for the linear head and 87.33% for the MLP. The origin of the old Figure 3(b)'s approximately 81.8% endpoint could not be established from the retained analysis records.

We also separate the deployed multi-feature system (Appendix A), which combines normalised module scores using a weighted sum, from the canonical single-encoder experiments. The reason some deployed baseline values coincide with single-encoder values at displayed precision remains unresolved. We do not interpret these coincidences as evidence that the systems or heads are identical, and the deployed results are not used to support the canonical comparisons.

The supplementary package supports regeneration of selected aggregate analyses, but not a complete clean-room rerun from the original images and model assets.

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

This paper studies entity-specific few-shot retrieval adaptation with frozen image encoders. An independent projection head is trained for each entity using ten positive and ten negative images. The authors evaluate both target retrieval and general similarity discrimination on human-labelled image pairs. Across three encoders and two head architectures, adaptation improves retrieval while reducing semantic AUROC. The paper also explores interpolation between frozen and adapted scores to control this trade-off.

Critical strengths
  1. The evaluation beyond target retrieval. Measuring semantic and visual similarity on separate human-labelled pairs reveals changes that retrieval metrics alone would miss.

  2. The experiments cover three pretrained encoders and two head architectures under a largely matched protocol. The authors also acknowledge the small absolute effect sizes and the limitations of score interpolation.

Critical weaknesses
  1. The main comparison confounds training with the projection, frozen 768-dimensional features are compared with learned 128-dimensional representations. Without evaluating the same heads before training and including dimension-matched controls, it is unclear how much of the similarity loss is caused by adaptation.

  2. The training objective explicitly pulls all non-target examples together despite their potentially unrelated semantics. This could explain the observed degradation, but no alternative objective is tested. Changing the encoder or head architecture does not resolve this shared confound.

  3. The methodological novelty is limited, and the controllable-adaptation results remain exploratory. Held-out-entity calibration yields almost no retrieval gain, while the fusion and calibration code is excluded from the supplementary package.

  4. The practical significance of preserving general similarity within an entity-specific head is not sufficiently established. Since the backbone remains frozen, general similarity queries can still use the original representation. A clearer explanation of when the measured degradation becomes an operational limitation.

Questions for authors

same as the weakness

1 comment
AuthorsOpenReview ↗

Response to Reviewer hkWZ

We thank the reviewer for identifying a central confound in our original comparison. Comparing frozen 768-D features with trained 128-D heads could not separate the effects of projection and optimisation. We have added matched controls and revised our interpretation: retrieval gains do not, by themselves, establish an unavoidable loss of general similarity.

1. Projection versus optimisation (Section 6.4; Table 3; Appendices H/J).

We evaluated initial and trained heads across three encoders and five seeds, including identity- and random-initialised 768-D linear heads, random- and SVD-initialised 128-D heads, and a 128-768-D width sweep.

On CLIP, a trained identity-initialised 768-D head improves Recall@5 by 6.70 percentage points while changing semantic AUROC by -0.04 points. Before training, a random 128-D linear projection changes semantic AUROC by -0.74 points (95% CI [-1.66, +0.10]).

Point estimates indicate that much of the narrow-head gap predates training, but most individual initial intervals include zero. Some training-effect intervals exclude zero; notably, the CLIP linear result is bootstrap-sensitive, while the MLP result provides more stable evidence of a small additional decline.

All matched training-effect intervals fall within a post-hoc ±1-point descriptive margin, which was not pre-registered and does not imply zero effect. These controls use cached features and 30 Adam updates, unlike canonical single-seed training. SVD is transductive (using retrieval images), so we do not claim a general causal effect of dimensionality.

2. Loss function (Section 4.3; Appendix J, Table 23).

We added SupCon-pos and Pair-BCE. SupCon-pos improves Recall@5 over SupCon in all nine evaluated encoder/head conditions; Pair-BCE performs worse than SupCon in seven of nine.

For the 128-D MLP, semantic-AUROC point estimates remain below frozen under both alternative losses, although some confidence intervals cross zero. SupCon-pos also removes negative examples as anchors, so this ablation does not isolate negative-negative attraction alone. We restrict our conclusion to the tested loss changes.

3. Novelty and practical meaning (Sections 6-8).

We no longer present interpolation as a new adaptation method or a solution to the trade-off. The contribution is diagnostic: separating projection from optimisation and testing whether embedding adaptation is needed for registered-entity retrieval.

In a new same-support comparison (Section 6.2, Table 1), logistic regression on frozen features outperforms the trained MLP on all three encoders (Recall@5: 93.50% vs 87.33% on CLIP; 73.42% vs 63.33% on DINOv3; 93.17% vs 89.25% on SigLIP).

The frozen encoder can still serve general-similarity search; task-external AUROC matters when adapted representations are reused outside their registered-entity task. We have not measured catalogue-scale costs or impact.

4. Interpolation and reproducibility (Appendix K; Supplementary README).

Interpolation/PCSF is now explicitly exploratory, with full-pair sweeps and held-out selection reported separately. Target-level outer CV selects α=0\alpha=0 in 138/150 cells; CLIP MLP gains 1.37 Recall@5 points, which does not support a robust operating point.

We supply fusion/calibration scripts and aggregate outputs, but not the original inputs needed for a complete clean-room rerun. Our revised claims concern the evaluated diagnostic evidence, not a new, broadly validated deployment mechanism.

Comments on the paper

1 comment
Area_Chair_SRvJOpenReview ↗

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