acceptodds
Under review as a conference paper at ICLR 2027

The Limits of Replacing Attention Heads: Capacity and Robustness in Static Retrieval

Abstract

Can query slots replace attention heads without sacrificing retrieval capacity or reliability? To the best of our knowledge, we establish the first joint sharp characterization of these two resources for static quadratic-coverage retrieval. For one tokenwise pooling round with heads, fixed query slots per head and reads, stable length-uniform approximation of coverage over prototypes is possible exactly when . The converse allows arbitrary finite value width, length-dependent scores and joint nonlinear Lipschitz decoding, without a data-dependent bypass. Reliability obeys a different law: against hidden whole-head corruptions, uniformly beating the constant baseline over unbounded count imbalance with bounded decoder–value sensitivity requires and , with matching constructions under sufficient contrast and noise margin. Exact finite-budget minimax frontiers quantify what read allocation, score contrast, value scale, noise and decoder sensitivity can and cannot compensate for. An exact decoder oracle isolates fixed-source representation limits, while a count-uniform certificate supplies trainable robust margins over an infinite known-prototype multiset class. All 20 construction-matched fits attain the predicted finite-budget frontiers, and 2,592 grouped-fault configurations match the exact formula. After a 100-step teacher prefix, direct-margin continuation recovers certified robustness in 15/15 fresh blocks at . Complementary frozen-Qwen3-4B stress tests probe bounded readout and native-head sensitivity, not transfer of the static theorem. The result separates interchangeable read channels from irreplaceable fault domains.

Primary area:
learning theory
Keywords:
attention heads, attention pooling, static retrieval, approximation theory, minimax bounds, robustness to head corruption

Reviews

Among:
Shape:
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_WwnQOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies when multiple query slots can substitute for multiple attention heads in static retrieval. Its central distinction is between read capacity and fault-domain diversity. For stable length-uniform coverage, the critical architectural resource is the total number of static reads, (K=hR), whereas robustness to grouped whole-head corruption additionally requires a sufficient number of independent fault domains. The paper derives sharp thresholds and exact finite-budget minimax frontiers that incorporate read allocation, score contrast, value scale, noise, and decoder sensitivity. It further evaluates these predictions through construction-matched experiments, certified margin-learning experiments, and complementary Qwen3-4B stress tests.

Critical strengths
  1. Sharp theoretical characterization within the stated model. The paper provides matching converses and constructions rather than only qualitative separations. In particular, it cleanly distinguishes interchangeable read capacity from non-interchangeable fault domains, while also quantifying the effects of finite contrast, value scale, noise, and decoder sensitivity.
  2. Broad lower bounds within the static-read model. The impossibility results allow arbitrary tokenwise score and value maps, arbitrary finite value dimensions, and joint nonlinear Lipschitz decoders. Thus, the main lower bounds are not artifacts of linear decoding, scalar-valued representations, or a particularly restrictive decoder class.
  3. Strong theory–experiment correspondence in the construction-matched setting. The equal-read comparison between (1\times24) and (3\times8), together with the separated-versus-concentrated replication control, cleanly isolates the effect of fault-domain allocation. The exhaustive grouped-fault evaluations also agree closely with the exact theoretical frontier, providing a strong internal validation of the analysis.
Critical weaknesses
  1. Restricted applicability beyond the static-read setting. The main theorems intentionally exclude contextualized token representations, positional pathways, query–query interaction, residual bypasses, and later access to token states. The paper is explicit about these boundaries, but they leave open how much of the proposed head–slot separation survives in standard contextual, multi-layer Transformers. The Qwen3-4B experiments provide useful diagnostics, but they do not validate the theoretical substitution frontier in such models.
  2. The robustness separation is conditional on a head-aligned correlated-fault model. The central reliability result assumes that all reads assigned to one head are corrupted jointly. This is mathematically clean and the paper appropriately presents it as a grouped-read abstraction rather than a hardware fault model. However, the empirical motivation for treating the head as the relevant correlated-failure domain remains limited. It is therefore unclear how directly the robustness separation should be interpreted when failures are partially correlated, overlap across heads, or are not aligned with the architectural head partition.
  3. The learning results rely on substantial structural supervision. Prototype identities, type-to-replica/head assignments, and the matched min-of-medians aggregation rule are supplied rather than discovered. The experiments therefore demonstrate that robust representations can be learned within a prescribed redundancy layout, but they do not establish that generic task training can discover the required cross-head redundancy structure or an appropriate robust readout automatically.
Questions for authors
  1. Scope of the static-read abstraction. Could the authors identify concrete, practically used attention modules that exactly satisfy the static-read assumptions, and separately discuss which conclusions they expect to remain informative for architectures that only approximately satisfy them? This would help clarify the practical scope of the theoretical results.
  2. Motivation for head-aligned fault domains. What empirical or systems evidence supports treating an attention head as the relevant correlated-failure domain? In particular, are realistic perturbations or failures expected to be substantially more correlated among reads within a head than across heads? More generally, how would the qualitative conclusions change under partially correlated or non-head-aligned fault structures?
  3. Dependence on the prescribed redundancy layout. How sensitive are the certified-learning results to the fixed replica-to-head assignment? A particularly informative ablation would make this assignment random, imperfect, or learnable and test whether margin-based training still develops cross-head redundancy. Such an experiment would help distinguish learning a robust representation from learning parameters within an already supplied error-correcting layout.
2 comments
AuthorsOpenReview ↗

Response to Reviewer WwnQ

Thank you for the careful assessment and for separating the static-read result from its possible architectural interpretations. We revised the paper to answer all three questions directly.

Q1. Scope of the static-read abstraction. Could the authors identify concrete, practically used attention modules that exactly satisfy the static-read assumptions, and separately discuss which conclusions they expect to remain informative for architectures that only approximately satisfy them? This would help clarify the practical scope of the theoretical results.

A1. One-pass HopfieldPooling and Set Transformer's PMA implement the analyzed interface when inputs are tokenwise, queries are input-independent, and all later computation accesses only pooled summaries. The joint decoder may include post-pooling interaction and an input-independent seed residual. Contextual token preprocessing, input-dependent query updates, token-dependent bypasses, and repeated token access require separate analysis. Appendix E.1 now states these exact interface conditions. Appendix E.2 gives a quantitative extension relative to a uniformly controlled static reference and bypass, but those premises have not been verified for full Qwen. Therefore, identifying an eligible pooling component does not imply that a complete Set Transformer, Perceiver, or language model satisfies the theorem.

Q2. Motivation for head-aligned fault domains. What empirical or systems evidence supports treating an attention head as the relevant correlated-failure domain? In particular, are realistic perturbations or failures expected to be substantially more correlated among reads within a head than across heads? More generally, how would the qualitative conclusions change under partially correlated or non-head-aligned fault structures?

A2. The theorem takes a declared support family as input rather than inferring natural fault groups. It permits partial or coordinated damage within at most ss declared groups without assuming independence. Overlapping or cross-group supports outside that family define a different adversary and do not automatically inherit the same ceiling formula.

Appendix F.8 adds a concrete correlated-error mechanism, not performance validation. In Qwen3-4B GQA, four query heads share each KV head. Across 32 fresh sources, the E1/4-bit normalized same-KV-group covariance increment is 0.787956[0.702901,0.874417]0.787956[0.702901,0.874417], close to the conditional analytic mean 0.7892380.789238. Shared and independent arms match single-head error distributions while changing their dependence, and sources are the replication units. The projected shared/independent variance ratio is 0.884624[0.868230,0.900896]0.884624[0.868230,0.900896], showing partial cancellation by output projection. All conditions retain 28/32 exact answers at E1 and 32/32 at E8, with no individual flips and margin intervals crossing zero.

This supports shared-KV/attention-overlap groups as one concrete correlated-error mechanism. It does not establish natural failure frequencies, arbitrary-replacement behavior, behavioral compensation, or the static threshold. Neither this result nor the donor patch is reported as an accuracy improvement.

Q3. Dependence on the prescribed redundancy layout. How sensitive are the certified-learning results to the fixed replica-to-head assignment? A particularly informative ablation would make this assignment random, imperfect, or learnable and test whether margin-based training still develops cross-head redundancy. Such an experiment would help distinguish learning a robust representation from learning parameters within an already supplied error-correcting layout.

A3. Appendix F.3 adds a fifteen-fit assignment ablation while holding type semantics and the three-head fault model fixed. Five paired blocks compare dispersed, random-balanced, and learned placements. The learned arm starts from the same random assignment and uses training-only type-aware margin swaps, with its extra search compute disclosed. Type targets and min-of-medians aggregation remain supplied.

At count cap 8, random-fixed fault accuracy averages 15.78%, while learned placement reaches 100% fault accuracy and zero formula-evaluated uniform readout error in 5/5 blocks. Every arm has 100% clean accuracy. At caps 32/128, uniform error returns to 1, so placement cannot remove the score/count-budget limitation. These are errors of the supplied readout, not arbitrary-decoder lower bounds.

Thus the ablation answers the conditional placement question under a fixed threat, but it does not establish generic discovery of type semantics, redundancy, and aggregation. The separate task-only studies address that harder question without supplied type identities, replica assignments, or a fixed readout, and they retain the unresolved outcome rather than claiming success.

Thank you for the detailed response and the substantial revisions. I appreciate the authors’ efforts to address my three concerns.

The clarification of the static-read assumptions and their architectural scope largely addresses my first concern. The additional correlated-error analysis and replica-assignment ablation are also meaningful additions that help strengthen the paper.

However, I believe some limitations remain. The correlated-error analysis provides evidence of a plausible mechanism but does not fully establish the relevance of the assumed fault domains to realistic failure scenarios. Similarly, the assignment ablation demonstrates that robust placement can be learned under the provided type semantics and aggregation rules, but it does not establish that robust redundancy can emerge from task supervision alone.

I appreciate that the authors have acknowledged these limitations and narrowed their claims accordingly. Overall, the revisions have addressed several of my concerns, although the connection between the theoretical guarantees and practical robustness remains only partially established.

I will maintain my original rating. Thank you again for your careful response and your efforts to improve the paper.

Reviewer_nU3bOpenReview ↗
Rating
2
Confidence
2
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

The paper studies coverage retrieval over DD item types with a one-round static attention operator that has hh heads and RR fixed query slots per head. The main point is that total reads K=hRK=hR and independent fault domains (heads) play different roles. Stable length-uniform approximation of quadratic coverage is possible exactly when K≥DK\ge D (Theorem 3.1). Robustness to ss hidden whole-head corruptions needs h≥2s+1h\ge 2s+1 and hR≥(2s+1)DhR\ge(2s+1)D (Theorem 3.3). The paper also derives exact finite-budget minimax frontiers and a Lipschitz-decoder oracle. The experiments verify the theoretical constructions numerically, with some additional diagnostics on Qwen3-4B.

Critical strengths

The lower bound is strong. It allows any finite value width, length-dependent scores, and a nonlinear Lipschitz decoder, so the impossibility does not come from a linear readout or a fixed temperature. The matching construction and finite-budget frontier then characterize how the error depends on the available resources (Theorems 3.1–3.2). The robustness result is the part I found most useful. Under hidden corruptions, the frontier depends on whether h≥2s+1h\ge 2s+1 and on r=⌈(2s+1)D/(hR)⌉r=\lceil(2s+1)D/(hR)\rceil, so reads and heads are not interchangeable even at the same KK. The exhaustive check over 2,592 configurations and the matched h×Rh\times R controls agree with Equation (8), including the failure of concentrated replicas at K=24K=24 (Table 2; Appendix G).

Critical weaknesses

The headline suggests a general heads-versus-slots trade-off, which the results do not establish. The model has no contextual interaction, no positional information and no residual bypass, and there is no comparison at matched fixed width. The upper construction also needs a pooled width that grows with the number of types and the input dimension (D(d+1)D(d+1)), and a score contrast that grows with sequence length and with tighter tolerance. Appendix A says explicitly that the width is not held fixed when the head/slot configuration changes (p. 13). The intervention on native Qwen gives only small log-probability shifts, with no accuracy gain and no causal identification (Appendix P). So the connection to modern Transformers remains largely motivational.

The learning experiments are also closely tied to the theoretical construction. Prototype identities, replica assignments, the aggregation rule and the imbalance budgets are all supplied (Appendices J–N; Table 9). The "fresh" inputs only change the multiplicities of known types, and the larger-imbalance tests manually increase the score budget. A useful comparison would be a task-only baseline trained on diverse count ratios. The related work should also discuss Adler (arXiv:2509.22840), Gated Slot Attention (NeurIPS 2024), Scalable-Softmax (arXiv:2501.19399), and ATTNChecker (arXiv:2410.11720).

Questions for authors
  1. If total width, parameter count and score scale are held fixed, does the choice of heads versus slots predict accuracy or robustness in a learned contextual Transformer?
  2. Can a task-only objective trained over diverse count ratios satisfy the direct certificate without supplied prototype identities, replica assignments or a fixed robust readout?
  3. How does your resource law differ from Adler's capacity result for a fixed key dimension and from Gated Slot Attention?
3 comments
AuthorsOpenReview ↗

Response to Reviewer nU3b

Thank you for the constructive questions. We revised the headline and scope. We do not claim task-only discovery of a certified robust code. The retained contribution is a sharp resource characterization for a static information interface with declared fault supports.

Q1. If total width, parameter count and score scale are held fixed, does the choice of heads versus slots predict accuracy or robustness in a learned contextual Transformer?

Our experiment does not establish a general head-count advantage. Appendix F.5 adds seven configurations over five paired training blocks (35 fits). Every model has width 64, 164,416 active parameters, and realized score range 8. The architecture includes two contextual Transformer blocks, positional information, residual connections, post-pooling query interaction, and a nonlinear decoder. The fixed-R=3R=3 panel additionally matches 192 pooled scalars and dense MACs, although read-dependent softmax work differs. The equal-hR=24hR=24 panel changes pooled state and query-interaction cost, so neither comparison matches every FLOP or latency term.

At fixed R=3R=3, the prespecified h=8h=8 minus h=1h=1 clean contrast is +2.40+2.40 points, with descriptive 95% interval [−0.16,+4.96][-0.16,+4.96] and sign-flip p=0.3125p=0.3125. The equal-read contrast is −1.13-1.13 points, with interval [−3.91,+1.64][-3.91,+1.64]. Secondary length, imbalance, and combined-shift contrasts are reported as descriptive, budget-dependent outcomes rather than confirmatory evidence. Robust-exact accuracy is 0% in every cell, and fixed-RR mask-averaged exact accuracy decreases from 12.51% to 5.56%. Training is clean-only, and mask alignment changes across configurations. Thus, the head/slot configuration affects some transfer outcomes in this architecture, but the experiment establishes neither a general head-count advantage nor robust substitution.

Q2. Can a task-only objective trained over diverse count ratios satisfy the direct certificate without supplied prototype identities, replica assignments or a fixed robust readout?

Our current experiments do not show that a task-only objective discovers the certificate. The supplied-layout BCE control reaches the analytic zero-error condition in 5/5 blocks, showing that margin loss is not necessary when type roles, replica assignments, and min-of-medians aggregation are provided. This control does not demonstrate discovery.

Appendix F.6 therefore adds two three-block paired studies with randomly initialized encoders and learned GroupSort decoders. Neither study supplies prototype-identity targets, replica assignments, a teacher, or a fixed robust readout. The first adds an all-pairs fault-aware hinge to task BCE/PGD. The second changes only mean aggregation to batch-max aggregation on fresh matched data.

The first modification raises clean accuracy from 78.91% to 97.92% but lowers worst-head PGD40 accuracy from 60.42% to 42.06%. The second raises clean accuracy from 77.21% to 97.40% but lowers fault accuracy from 49.48% to 16.80%. Full cross-head preference coverage improves from 0/3 to 1/3 blocks, yet every arm remains 0/3 on the actual-decoder uniform 1% target. The fully covered model still has 0% worst-head fault accuracy.

FP64 diagnostics further indicate that local representation separation is insufficient for robust decoding: 226/256 sources satisfying the computed neighbor-gap check still fail saved attacks, while other pairs yield a numerical sigmoid-error lower bound of 0.074214. These diagnostics are not proofs. The revised test bucket was fixed before training or prediction, and all comparisons are paired within each study.

Therefore, Q2 remains unresolved. The controls identify a separation among type coverage, representation geometry, and robust decoding, but establish neither success nor impossibility of generic task-only discovery.

Q3. How does your resource law differ from Adler's capacity result for a fixed key dimension and from Gated Slot Attention?

Adler studies relational-recognition capacity while holding total key dimension fixed. Our law instead concerns the number of normalized static reads required for length-uniform prototype coverage and, separately, the number of declared fault domains required for robustness. The centered rank of a required score table connects these resources to key dimension, preventing the read-count result from being interpreted as a free fixed-width implementation.

Gated Slot Attention uses input-dependent, stateful slot updates over an iterative history, whereas our theorem concerns a single round of input-independent fixed queries followed only by pooled-state decoding. It therefore lies outside the exact static-read model rather than being dominated by our result. Section 6 similarly distinguishes Scalable-Softmax's length-dependent contrast mechanism and ATTNChecker's computation-fault model. These are differences in objects, resources, and guarantees, not dominance claims.

AuthorsOpenReview ↗

Follow-up regarding the revised overall rating

Dear Reviewer nU3b,

Thank you for your careful and constructive review. We noticed that the overall rating was revised from 3 to 2, while the Presentation, Informativeness, and Soundness assessments remain at 3. We fully understand that the overall recommendation is not an arithmetic function of these subratings, and we respect your independent judgment.

Could you kindly clarify which remaining concern was decisive for the revised overall recommendation? In particular, it would be very helpful to know whether the main issue is the architectural scope, task-only discovery of robust redundancy, the relationship to prior capacity results, or another aspect that our response has not adequately addressed.

We have revised the manuscript and responded directly to all three questions. Appendix F.5 adds a fixed-width, fixed-parameter, fixed-score-range contextual control. Appendix F.6 adds task-only learning controls without prototype-identity targets, replica assignments, a teacher, or a fixed robust readout, while honestly retaining their unresolved outcome. Section 6 now distinguishes our resource law from Adler's fixed-key-dimension result, Gated Slot Attention, Scalable-Softmax, and ATTNChecker. We have also narrowed the paper's claims so that the contextual experiments are not presented as establishing a general head-count advantage or robust substitution.

If you find that the revised manuscript and our response resolve the concern that motivated the change, we would be very grateful if you would consider revisiting the overall rating, including restoring the earlier recommendation if you believe that is warranted. If a decisive concern remains, even a brief indication would help us understand the limitation more precisely.

Thank you very much for your time and consideration.

Thank you for the new experiments. The revised scope is much clearer than before. The comparison to earlier work is also much clearer than before. I also appreciate the new controls. My main remaining concern is the importance of the contribution rather than its soundness. The primary matched-budget contextual comparisons remain inconclusive, and the task-only controls do not establish robust redundancy without the supplied structure. The above results do not disprove the static theory. They leave its broader design implications only partially supported. I see value in the theoretical characterization. I do not think its importance is enough for acceptance at ICLR. My score stays at 2.

Reviewer_3226OpenReview ↗
Rating
1(−1)
Confidence
4
Informativeness
1(−1)
Presentation
1(−1)
Soundness
2
Read review
Paper summary

The authors study coverage retrieval with fixed attention queries. They derive sharp read-count thresholds and exact error bounds under noise and whole-head faults. They also give a certificate for learned representations and test it in construction-guided experiments.

Critical strengths
  • Thm 3.1 allows arbitrary finite value width and nonlinear Lipschitz decoding. The lower bound uses one input pair that defeats every read.
  • Thm 3.2-3.3 give matching bounds and constructions. The fault analysis covers an infinite multiset class.
  • The authors clearly state the limits of their learning and Qwen experiments.
Critical weaknesses
  1. My main concern is the missing comparison with modern Hopfield networks. Ramsauer et al. [1] analyze one-step retrieval and introduce HopfieldPooling with learned static queries. Wu et al. [2] and Hu et al. [3] further study separation and memory capacity. These works are directly relevant to Sec 3 and 6. In particular, the singleton formula g(1) follows from the same softmax separation-versus-interference calculation. The coverage and grouped-fault results may still be new, but the authors need to explain what they add. Without this comparison, I do not find the novelty sufficiently established for acceptance.

  2. The architectural conclusion is limited. The authors count static reads without matching parameters, compute, or state width. The exact fault law also assumes equidistant prototypes. I see value in this characterization, but its broader significance remains unclear.

  3. The experiments provide limited additional support. Most retain the prescribed types, replicas, and readout. The direct-margin and task-loss arms also differ in count coverage. The Qwen studies neither test the predicted threshold nor improve exact-set accuracy. The authors acknowledge these limits, but the experiments do not resolve the significance concern.

[1] Ramsauer et al. Hopfield Networks Is All You Need. ICLR 2021.

[2] Wu et al. Uniform Memory Retrieval with Larger Capacity for Modern Hopfield Models. ICML 2024.

[3] Hu et al. Provably Optimal Memory Capacity for Modern Hopfield Models. NeurIPS 2024.


after rebuttal note: the latest revision somehow managed to validate above weaknesses. thus, i decided to lower my score.

Questions for authors
  • Which parts of Thm 3.1-3.3 go beyond existing Hopfield retrieval bounds? Please compare the assumptions and guarantees explicitly.
  • What does the joint characterization teach us about fixed-query pooling beyond softmax concentration and standard replication?
3 comments
AuthorsOpenReview ↗

Response to Reviewer 3226

Thank you for identifying the missing comparison with modern Hopfield retrieval. We revised the Introduction and Section 6, and Tables 1 and 7 now compare the assumptions and guarantees explicitly.

1. What is inherited and what is new. We now state that the singleton mass formula g(1)g(1) specializes Ramsauer et al., Lemma A4, Eq. (135), and that learned static queries, one-step retrieval, feature separation, and classical replication are inherited foundations. Our additional results concern simultaneous coverage by an entire fixed-read bank:

  • Theorem 3.1 uses one common input pair to constrain all K<DK<D reads jointly, even with arbitrary finite value widths, length-dependent scores, and nonlinear Lipschitz decoding. Together with the construction, this gives the length-uniform threshold K≥DK\ge D under bounded decoder-value sensitivity.
  • Theorem 3.2 gives the exact finite-budget minimax allocation under heterogeneous logit-range, value, noise, and decoder budgets, including several types sharing one softmax normalization.
  • Theorem 3.3 combines this allocation with declared group faults on the infinite equidistant-prototype multiset class. Thus the head requirement comes from independent declared fault domains, whereas K=hRK=hR controls read coverage.

The common-input converses establish necessity across the stated class, rather than only sufficiency of a particular Hopfield retrieval or replication construction.

2. What the joint characterization teaches. Equation (8) is a resource-feasibility test for one-pass fixed-query pooling. In Table 3, with D=n=8D=n=8 and one hidden group replacement, (1,24)(1,24) has normalized minimax error 1/21/2 regardless of contrast. Three groups satisfy the classical replication count, but (3,4)(3,4) still has limiting error 29/9029/90. Increasing to (3,8)(3,8) permits zero error at B=log⁡16B=\log 16. Therefore, more groups, more reads, and greater contrast repair different bottlenecks. Extra slots cannot compensate for too few fault domains, and extra heads do not compensate for insufficient read allocation or score margin. The converse also rules out alternative stable encodings at an infeasible budget within the same model class.

3. Scope, costs, and experimental evidence. We now expose the construction costs: Theorem 3.1 uses D(d+1)D(d+1) useful pooled coordinates, contrast grows with length and tighter tolerance, and Table 2/Appendix E.3 report state and projection costs. Appendix B.2.1 gives the retained non-equidistant geometry bounds. Appendix F.5 matches width, parameter count, and score range in a contextual control; its primary clean contrast is inconclusive and its robust-exact endpoint does not improve. Appendix F.2 shows that BCE and sample-margin training both reach the supplied-layout zero-error condition in 5/5 blocks, so we no longer imply margin-specific superiority in that control. Structural supervision remains, and the Qwen study is explicitly presented as a mechanism diagnostic with no exact-answer gain or validation of the static threshold.

Accordingly, the revised paper limits its architectural conclusion to conditional budget screening for the eligible static pooling interface in Appendix E.1, rather than claiming a general Transformer head-versus-slot law.

thanks for the revision and clarifications. I've read it and am not satisfied.

  1. the inclusion of the pointed-out literature does not feel well thought out. for example, when comparing against a "prior ingredient" in table 1, shouldn't the authors cite the intended reference for that comparison?

  2. the authors should think carefully about clarity. the newly added discussion in the intro and related work feels abrupt and not well thought out. this makes the already hard-to-read narrative even more difficult to follow. the paper's narrative is now far from smooth, coherent, or convincing. For example, after the comparison with the modern hopfield literature, the main contributions feel incremental, or at least it is hard for me to tell their significance. why are these contributions important and worth pursuing? the current narrative fails to convey the basic motivation for the research.

  3. overall, the quality feels even worse after the revision, and the paper remains far from the bar for acceptance.

I really hope the authors take my comments into consideration. please spend time understanding the surrounding literature. then revise the draft in a professional fashion. ai can help, but it does not replace a careful reading and understanding of the relevant work.

AuthorsOpenReview ↗

Response to reviewer 3226

Dear Reviewer 3226,

Thank you for reading the revision. We agree that Table 1 should have cited its sources directly and that the introduction left the motivation for our results too implicit.

1. Which ingredients come from prior work?
The first row of Table 1 should credit Lee et al. for the learned seed queries in PMA and Ramsauer et al. for HopfieldPooling. The second should cite Ramsauer et al., Lemma A4, Eq. (135). When the competing types each occur nn times as often as the favored type and all score gaps equal BB, their softmax calculation gives our singleton mass g(1)=1/[1+n(D−1)e−B]g(1)=1/[1+n(D-1)e^{-B}]. The third row should cite Chen et al., Theorem 3.2, for the 2s+12s+1 repetition construction against ss corruptions.

2. What question remains after the modern Hopfield results?
Wu et al. study how a learned feature map separates stored patterns, and Hu et al. relate memory capacity to the geometry of those patterns. Consider what happens after a set has been compressed into a few pooled summaries. Suppose all eight required types appear, but one appears only once. Giving each type its own query is a natural way to retain evidence of its presence. Could four wider reads encode that evidence just as reliably for a decoder that sees all four jointly?

The difficulty is that a type overlooked by one query may still be detected by another. Theorem 3.1 constructs one pair of inputs that challenges the entire query bank simultaneously. Replacing the rare token changes the coverage target by at least γ\gamma, the minimum normalized squared prototype separation. As the background types are repeated, the decoder outputs can be made arbitrarily close. Thus, under the stated stability bound, even arbitrary finite value width and joint nonlinear decoding cannot give four reads a fixed error guarantee below γ/2\gamma/2 across all input lengths.

3. Why does the distinction matter for design?
Table 3 gives a concrete choice. Both designs have three distinct fault groups and must tolerate one hidden corruption. With four reads per head, the optimal error approaches 29Δ/9029\Delta/90 even as score contrast grows without bound. With eight reads per head, finite contrast suffices for zero error under the same value, noise, and decoder budgets. A designer who already has three fault groups can therefore determine whether increasing score contrast will reach the target or whether more reads are needed. This is the consequence we should have made clear when first introducing the coverage problem.

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

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