1. The theoretical synthesis makes sense, but it is an incremental contribution and the demonstrated consequences are limited.
A synthesis can make an important contribution by resolving a consequential ambiguity, deriving a broadly useful characterization, or explaining an observed phenomenon. This paper provides some such value, especially through Theorem 1, but I do not find that value sufficiently substantial beyond the specific separation it establishes.
There are close antecedents to the underlying formulation. Gao et al., Rate Distortion For Model Compression: From Theory To Practice (ICML 2019, Section 3), already define compression distortion through differences in model predictions rather than parameter reconstruction. Hafez-Kolahi et al., Rate-Distortion Analysis of Minimum Excess Risk in Bayesian Learning (ICML 2021, Equation 12 and Section 6), constrain information retained from training in a learned predictor and express squared prediction distortion in an L2 function space. Both are cited in the manuscript, but the relationship needs to be explained at the level of the mathematical formulations, not only their general subject matter.
Within this setting, Lemma 2 applies the established conditional-mean estimation-and-quantization structure to functions of peer responses; a closely related finite-quantizer decomposition is stated in Proposition 1 of On Noisy Source Vector Quantization via a Subspace Constrained Mean Shift Algorithm. Once Gaussian predictable behavior is expanded in orthonormal coordinates, Theorem 3 is Gaussian vector rate-distortion. Theorem 4 then derives the explicit all-budget comparison through concave duality. The latter is not empty: it supplies a necessary-and-sufficient criterion within the Gaussian model and covers cases beyond coordinatewise eigenvalue dominance. Nevertheless, I view it as a semi-interesting direct corollary of the known error curve, rather than a separate foundational advance. I am not asserting that the exact finite-state reversal or this particular spectral transform has already been published.
The clearest additional inference is therefore that unrestricted accuracy cannot serve as a budget-independent ordering, even after eliminating training uncertainty and restrictions on predictor expressiveness. This strengthens the rationale for budget-matched evaluation. However, the broader characterization remains specific to a Gaussian mutual-information model. It does not supply the corresponding general comparison for literal finite-state storage; the paper correctly states that ordering the relaxed risks does not order the fixed-state risks. Proposition 5 provides a more general finite-state lower bound, but not an all-budget ordering criterion for that problem.
Nor do the experiments establish an additional explanatory consequence of the spectral analysis. They neither estimate the covariance of predictable behavior across targets and training observations nor test a quantitative prediction derived from it. The empirical KRR eigenbasis comes from the peer kernel matrix, not that behavioral covariance, and the comparisons use TV rather than squared prediction loss. These distinctions are acknowledged and do not invalidate the theory. They do mean that the empirical crossovers cannot currently be credited as evidence that the spectral characterization explains the observed model preferences.
I therefore regard the work as a sound conceptual separation accompanied by useful specializations of established compression theory, but a very incremental theoretical advance. There needs to be some further inference from the synthesis, or strong independent empirical evidence that its selection perspective matters in the proposed replacement setting.
2. The experimental protocol has a significant sampling defect, and the comparisons do not establish the additional peer-selection benefit needed to strengthen the contribution.
The most serious empirical issue is the distribution used for fitting, selection, and evaluation. In kernel_isqed/data.py:417–423, clusters are sorted by domain|gold, with a hash only as a secondary key. After minimum coverage is allocated, lines 481–497 fill residual capacity from the same sorted records. Thus, alphabetically early domains consume the residual sample budget. In the released MMLU-Pro test set, 996 of 1,024 items come from six included domains, while each of the remaining seven contributes exactly four. The manuscript does not specify a target query distribution that justifies this allocation.
The HellaSwag records establish a validation/test weighting discrepancy directly. Sixty-six domains have exactly four test examples each, accounting for 264/1,024 = 25.8% of test. Because the allocator requires at least four examples from every included domain in each partition, those same domains occupy at least 264/512 = 51.6% of validation. Validation therefore evaluates substantially different domain weights from the nominally IID test, by construction.
This matters specifically to the paper's selection claims: validation jointly selects peers, regularization, rank, precision, and encoding, so the selected systems can be optimized for a different mixture from the one on which their performance is reported. The published Qwen/MMLU-Pro crossover reproduces from the released losses, and the defect does not prove that it would disappear under corrected sampling. It does, however, prevent the current protocol from establishing reliable same-distribution selection. Bootstrapping fixed test predictions cannot repair a mismatched selection distribution; fitting and selection need to be repeated under a consistently specified distribution.
There is also a problem in the direct evidence for peer selection. The prominent convex-versus-KRR crossover compares adapter families using the same peers. Table 2 is closer to the theoretical interface comparison, and the released records support its literal claim that the validation-selected pair changes with budget. However, both competing pairs' held-out errors are not reported at both budgets. Consequently, the study does not quantify whether changing peers improves held-out performance over retaining a fixed pair and changing only the adapter. This missing comparison is consequential because choosing the peer interface, rather than merely choosing a regressor, motivates the paper.
The inexpensive calibration comparator is likewise important. Appendix C.6 reports mean TV 0.2892 from three nonnegative coefficients, compared with 0.3028 for convex mixing and 0.2784 for full-precision KRR, recovering approximately 55.6% of that improvement. Yet it is absent from the matched-budget comparison. Three FP64 coefficients plus the stated 176-bit header would require 368 bits, assuming a public decoder for this family. It fits below 1,024 bits without low-bit quantization. A per-cell, budget-matched evaluation is therefore needed to distinguish the additional benefit of richer adaptation from inexpensive logit rescaling. The aggregate result does not establish that calibration eliminates the reported crossover, but it leaves the practical comparison incomplete.
The 848-bit result remains useful evidence that a fitted replacement can be compressed with little change in its measured fidelity. Its reference, however, is full-precision KRR—not an established irreducible error floor or an application-defined replacement requirement. Together with the adapter-family crossover, it supports compressibility and budget sensitivity of particular fitted methods, but does not independently establish a reliable benefit from budget-dependent peer choice.
Overall, I recommend Reject. I find the incremental theoretical contribution modest, and the empirical study does not yet supply the reliable selection insight that would make the combined contribution compelling. Correcting the split protocol is necessary; merely reproducing the convex-versus-KRR crossover and fixing the split protocol would not fully resolve the contribution concern. A stable held-out benefit from budget-aware peer selection beyond inexpensive alternatives (note that I will be rigorous in analyzing your reply), or a clearer substantial consequence of the theoretical synthesis, would materially change my assessment.
I aim to reply every 24-48 hours during review period. Please submit a https://anonymous.4open.science for all claims made in rebuttal to me.
I do not agree with this review or that the "presentation is poor and very difficult to follow," it seems that this reviewer did not have the expertise to actually evaluate this paper (stated in confidence score). In my opinion this is a decently written paper (even if my review argues it is too incremental in current form).