I have many issues with this paper. Since only two are allowed at most, I am stating the two I believe are the most critical
Clarity: The AI usage paragraph states that AI assisted with polishing the writing of this paper in terms of flow and English
grammar. If so, that was done poorly, as some sentences of the work result very difficult to be interpreted, even after careful reading. Since I'm familiar with the topic, I believe this should not be the case. The method itself is not explained clearly. Perhaps the most important quantity for understanding the method, UN, is only defined informally and in natural language as "a simultaneous upper confidence envelope estimated from training data". I understand it as the simultaneous confidence bound satisfying P(maxRN<UN)>1−a. How to estimate the bound is not completely clear from the main text.
In the experimental section, most of the results are discussed briefly, and the discussion on the main text often refers to figures in the appendix; conversely, the only figure in the main text seems not to be discussed properly. As a result understanding the empirical benefit of the method is also not easy.
More references should be included in various points, as the current ones are not sufficient, when referring to previous methods, datasets. A broader related work discussion would help, especially on model selection for reservoir computing and related forecasting methods.
In general, I value clarity as the most important aspect when reading and evaluating a paper, therefore my assessment of the work is severely and negatively impacted.
The work needs to go through a substantial, hopefully humanly-assisted, rewrite.
Impact: It saddens me to say it as a practitioner of reservoir computing, however I think the work fundamentally lacks the impact to be published in a top-tier generalist deep learning venue. It tackles a very narrow problem on a very specific architecture (SCR) of reservoir computing.
I believe that a submission to a more neural nets or computational neuroscience-focused venue (after the aforementioned rewriting) would be better aimed.
Thank you for the concise review. We ran additional experiments addressing all three questions.
History length (L). The broad screen uses (L=48). We will move this value, together with the input dimension, gain, (W_{\rm in}) construction, preprocessing, and state-standardization details, into the main method description.
Role of the certificate once (N\ge L). For a scalar finite-history problem, we agree that if (N\ge L) and the finite map has full column rank, the ideal finite-history representation loss is zero. Our numerical audit revealed that the submitted Gram-pseudoinverse implementation could nevertheless drop geometrically attenuated directions, making some gate-2 failures numerically conservative. Stable SVD/QR projection confirms near-zero loss in these scalar full-span cases. We will explicitly state this boundary and distinguish it from the nontrivial compressed regime (N<dL). In new multivariate experiments with (dL) as large as 768 and (N\le128), 44/45 population-certified cases remain within 2% of unrestricted lag ridge, showing that the projection analysis is nontrivial when the cycle genuinely compresses the input history.
Tuned ESN and direct lag. With a stronger validation-tuned ESN that also varies spectral radius, input scale, and leak rate, 21/23 original frozen cycle recommendations remain within the 2% test-NRMSE margin; the mean online-multiplication reduction remains approximately 86.6%. Direct-lag ridge is essentially tied with the cycle in the original scalar certified regime (mean NRMSE approximately 0.29501 vs. 0.29512 for the cycle). We therefore revise the claim: the cycle should be viewed as a structured compressed history representation, not as universally superior to lag regression.
We will include these comparisons and the numerical-conditioning boundary in the revision. We hope these results address the baseline and certificate concerns and would appreciate reconsideration of the score.