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Under review as a conference paper at ICLR 2027

ROUTING SHUFFLES DO NOT IDENTIFY ADAPTIVE BENEFIT: THEORY AND A CONTROLLED ACM-GCN AUDIT

Abstract

When a trained network loses accuracy after its routing gates are shuffled, it is natural to attribute the loss to the value of adaptive routing. We show why this inference requires care. Shuffling changes the assignment of gates while preserving their collection; replacing them by a constant changes both. For separable gate-to-output computation and additive node scores, the expected shuffled score equals an average of constant-gate scores. The shuffle drop therefore upper-bounds the frozen network’s advantage over the best constant gate. Once message passing couples the gates, either ordering is possible, as two explicit constructions show. We examine the distinction in ACM-GCN on five previously studied graphs, using 2,100 tuning fits and 750 final models. On Roman-empire, the joint shuffledrop is 11.59 accuracy points, the gap against a searched frozen constant is 4.27 points, and the advantage over a separately trained constant-routing model is 1.42 points. These comparisons concern different properties of the network. Our analysis explains when a shuffle test admits a bound and why a practical assessment of routing should also include searched constant gates and separately trained static controls.

Primary area:
learning theory
Keywords:
adaptive computation, routing, mixture-of-experts, graph neural networks, graph learning, conditional computation, theoretical analysis, model interventions, interpretability

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.33 over 3 reviews, above 2% of the others.
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Paper summary
  • This paper investigates whether the performance degradation caused by randomly shuffling learned routing gates is a reliable measure of the benefit of adaptive routing in neural networks, particularly graph neural networks (GNNs).
  • In mixture-of-experts (MoE) architectures, different nodes may receive different routing weights that determine how expert outputs are combined. A common experimental practice is to shuffle these routing weights across nodes and observe the resulting performance degradation.
  • The usual interpretation is that a large performance drop indicates that adaptive routing is important.
  • The paper challenges this interpretation, arguing that shuffling measures sensitivity to the particular assignment of gates, which is fundamentally different from measuring the actual benefit of adaptive routing.
  • The authors distinguish three comparisons: Shuffle sensitivity, Frozen constant gap, and Trained constant gap. The central argument is that these three quantities can differ substantially, so a shuffle-induced performance drop should not automatically be interpreted as evidence that adaptive routing improves predictive performance.
Critical strengths

The paper is overall easy to follow.

Critical weaknesses

W1. Limited novelty of the central observation.

The paper's central argument—that performance degradation under shuffled routing does not directly measure the benefit of adaptive routing—appears conceptually straightforward and closely related to established limitations of permutation-based interventions. Prior work has already emphasized that perturbation-based performance changes depend on the specific intervention and should not automatically be interpreted as evidence of a component's necessity or learning benefit (Jain & Wallace, 2019; Wiegreffe & Pinter, 2019; Hooker et al., 2021; Covert et al., 2021). More directly, Hassid et al. (2022) [not cited] investigated replacing input-dependent attention with constant attention, while Roller et al. (2021), Dikkala et al. (2023), and Fan et al. (2024) examined the benefits of learned versus non-learned routing.

  • 1. Jain, S., & Wallace, B. C. (2019). Attention is not Explanation. Proceedings of the 2019 Conference of the North American Chapter of the Association for Computational Linguistics: Human Language Technologies (NAACL-HLT), 3543–3556.
  • 2. Wiegreffe, S., & Pinter, Y. (2019). Attention is not not Explanation. Proceedings of the 2019 Conference on Empirical Methods in Natural Language Processing and the 9th International Joint Conference on Natural Language Processing (EMNLP-IJCNLP), 11–20.
  • 3. Hooker, G., Mentch, L., & Zhou, S. (2021). Unrestricted permutation forces extrapolation: Variable importance requires at least one more model, or there is no free variable importance. Statistics and Computing, 31, Article 82.
  • 4. Covert, I., Lundberg, S., & Lee, S.-I. (2021). Explaining by removing: A unified framework for model explanation. Journal of Machine Learning Research, 22(209), 1–90.
  • 5. Hassid, M., Peng, H., Rotem, D., Kasai, J., Montero, I., Smith, N. A., & Schwartz, R. (2022). How much does attention actually attend? Questioning the importance of attention in pretrained transformers. Findings of the Association for Computational Linguistics: EMNLP 2022, 1403–1416. [Not cited]
  • 6. Roller, S., Sukhbaatar, S., Szlam, A., & Weston, J. (2021). Hash layers for large sparse models. Advances in Neural Information Processing Systems (NeurIPS), 34, 17555–17566.
  • 7. Dikkala, N., Ghosh, N., Meka, R., Panigrahy, R., Vyas, N., & Wang, X. (2023). On the benefits of learning to route in mixture-of-experts models. Proceedings of the 2023 Conference on Empirical Methods in Natural Language Processing (EMNLP), 9376–9396.
  • 8. Fan, D., Messmer, B., & Jaggi, M. (2024). Towards an empirical understanding of MoE design choices. ICLR 2024 Workshop on Mathematical and Empirical Understanding of Foundation Models (ME-FoMo).

W2. The theoretical contributions appear relatively elementary.

Theorem 1 follows directly from separability, uniform permutation marginals, and the observation that a maximum is no smaller than an average. Theorem 2 establishes that either ordering is possible under coupled routing, but its counterexamples rely on highly constructed settings, including all-positive labels, complete graphs, and arbitrarily weak coupling. The remaining propositions largely apply standard algebraic, combinatorial, and concentration arguments.

W3. Insufficient evidence of the practical significance of the identified evaluation problem.

The practical significance of this issue is not sufficiently demonstrated. In particular, the authors do not identify representative studies in which shuffle-induced performance drops have actually been used to make unjustified claims about adaptive routing, nor do they demonstrate that applying their proposed evaluation controls would materially change conclusions from prior work. I encourage the authors to identify concrete examples of potentially misleading shuffle-based conclusions in existing GNN/MoE literature and demonstrate how the proposed controls would alter their interpretation.

W4. Limited empirical validation of the main theoretical findings.

Although the paper presents an extensive experimental study in terms of training runs, the empirical evidence supporting its central claims is relatively narrow. The substantial discrepancy between shuffle sensitivity and constant-routing performance is largely concentrated on Roman-empire, where the joint shuffle drop is 11.59 percentage points. In contrast, the other four datasets exhibit joint shuffle drops of only 0.06–0.12 points.

More importantly, Theorem 2 establishes that coupled routing can exhibit either ordering between shuffle sensitivity and the advantage over the best constant. However, the experiments only certify the direction in which shuffle sensitivity overstates the frozen advantage, and only on Roman-empire. This behavior is already possible under separable routing, as established by Theorem 1. The opposite phenomenon, in which shuffled heterogeneous routing outperforms every constant, is demonstrated only through synthetic constructions.

Furthermore, although Section 4 introduces coupling-specific diagnostics, including the decomposition into heterogeneous reassignment effects and constant-gate suboptimality, these quantities are not systematically investigated in the main experiments. I encourage the authors to provide direct measurements of coupling effects in trained networks and investigate whether the theoretically distinctive behavior of coupled routing arises in practice. Extending the analysis beyond ACM-GCN would also strengthen the empirical contribution.

Questions for authors

See weaknesses above.

2 comments

Thank you for separating the validity of the distinction from its significance. We agree that the paper must demonstrate a useful inference, beyond observing that interventions differ.

Prior work and theoretical scope (Appendix J). Intervention-dependent explanations, constant attention and fixed routing precede our work. Hassid et al. (2022) is a relevant omitted precedent; Roller et al. (2021) and Dikkala et al. (2023) also study alternatives to learned routing. Our narrower result concerns additive scores at a separable intervened interface: the expected shuffled score equals an average of broadcast-constant scores, so the shuffle drop upper-bounds the optimal frozen advantage. Coupling removes this guarantee. The proof is short; its value lies in the inference and applicability conditions. The constructions establish possibility, not prevalence. An extension characterizes the replacement laws preserving this guarantee for every bounded additive separable score on a finite gate bank: exactly those with common node-wise marginals. For scores in [0,1], the sharp allowance for unequal marginals is their minimum average total-variation distance from a common law.

A consequential example beyond Roman (Table 3; Appendix M). We completed 60 native Mowst*-GCN fits on Penn94 and ogbn-arxiv with the published 20,000-update joint budget and validation-selected checkpoints. On Penn94, adaptive accuracy is 82.25%. The shuffle drop is 0.01 points, while the learned-minus-frozen-constant gap is −1.08 [−1.70, −0.51] and the separately trained adaptive-minus-constant gap is +0.70 [0.14, 1.23]. Frozen replacement and training therefore give opposite rankings. Brackets are descriptive 95% split/seed bootstrap intervals, not population coverage. This evidence is separable and does not demonstrate the positive coupled extreme.

Direct measurement of coupling (Appendix I). On the original Roman checkpoints, paired validation interventions keep the evaluated node's gate fixed and change the surrounding field. Correctness gains and losses are 1.940 and 1.836 points, leaving a net 0.104 with conditional Monte Carlo SE 0.154. The average broadcast score falls 7.261 points below the best-found constant. Thus cross-node effects occur but largely cancel; the large measured discrepancy principally reflects poor average broadcast policies. This is a fitted-model explanation, not a universal graph-level cause.

A stronger static comparison (Appendix N; Tables 68-69). At a pretrained Switch Transformer's final decoder router, a certificate covers all declared soft positional gates repeated across documents without content access, with eight experts and capacity 64. On 512 calibration documents, learned accuracy is 68.878%, versus a certified positional optimum of 68.483%. This teacher-forced span-reconstruction certificate concerns real-arithmetic evaluation of stored binary32 states, not every native floating-point gate execution. The attaining policy passes native replay and uses the same 114 expert calls per document, without drops. On 512 fresh documents, the preselected policy scores 66.709% versus 68.108%; this does not certify the fresh class optimum.

We have not demonstrated an incorrect empirical conclusion in a prior paper or a competitive natural-task positive coupling gap. The Switch broadcast-comparator coupling gap remains negative. The stronger case is that these tests answer different practical questions, now illustrated beyond one graph and supported by a complete comparator-class analysis at one specified interface.

Thank you for the detailed rebuttal and revision. I have reviewed the newly added analyses in the revised PDF.

The additional experiments meaningfully strengthen the empirical contribution, particularly the Penn94 comparison, the direct coupling measurements, and the certified positional-routing analysis.

The expanded theoretical treatment in Appendix J also provides a useful clarification of the conditions under which the separable-routing bound applies.

My remaining reservation primarily concerns the novelty and broader practical significance of the contribution. The authors have not established that prior studies have actually drawn misleading conclusions from these comparisons.

Furthermore, the distinctive positive coupled composition gap remains supported only by synthetic constructions, while the new Mowst experiments primarily concern separable interfaces. The Penn94 result is interesting, but the nearly node-constant learned gates also suggest that its training-performance reversal should not be interpreted as direct evidence for the benefit of input-dependent adaptation.

Overall, I would like to keep my initial rating. I hope the authors can take more time to improve this work and submit it to a future venue.

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Paper summary

This paper studies whether performance degradation under routing-gate shuffling can be interpreted as evidence for the benefit of adaptive routing. The authors distinguish three quantities: shuffle sensitivity, the advantage of a trained model over its best constant-gate replacement, and the performance difference between separately trained adaptive and constant-routing models. They establish an upper-bound relationship between shuffle drop and frozen-model advantage under separable computation and additive scoring, and construct counterexamples showing that neither ordering holds in general for coupled computation. Experiments on ACM-GCN across five graph datasets illustrate that these quantities can differ substantially.

The paper addresses an important methodological issue in evaluating routing mechanisms. Its main strength is the explicit mathematical separation of comparisons that are often conflated in empirical analyses.

Critical strengths

A useful conceptual distinction.

The paper clearly explains why shuffling a learned collection of gates is not equivalent to replacing those gates with a constant policy. This distinction is particularly important when routing decisions affect subsequent message passing.

Precise theoretical characterization.

The separability result is clean and interpretable, while the coupled counterexamples establish that the proposed ordering cannot be extended to arbitrary routing computations. The authors also appropriately distinguish exact statements about permutation expectations from finite-sample estimates.

Multiple complementary evaluations.

The experiments compare shuffled routing, searched frozen constants, and separately trained static alternatives. On Roman-empire, the reported joint shuffle drop is 11.59 percentage points, compared with a 4.27-point gap against the selected frozen constant and a 1.42-point difference between separately trained models. These results illustrate why the comparisons should not be interpreted interchangeably.

Reasonable acknowledgment of limitations.

The paper recognizes that its experiments cover a single routing architecture, that independently tuned models can differ in parameter count, and that finite-budget constant-gate searches do not establish global optimality.

Critical weaknesses
  1. The empirical contribution does not yet establish how broadly the proposed distinction changes conclusions in routing research.

The theoretical distinction is convincing, but the empirical investigation is restricted to two-layer ACM-GCN on five graph datasets. The paper would be stronger if it demonstrated how its evaluation framework changes conclusions drawn from existing learned-versus-random routing experiments.

For example, prior work on the benefits of learning to route in MoE models (Dikkala et al., EMNLP 2023) investigates the value of trainable routing, while subsequent work has also compared learned and randomized routing in trained MoE systems. These studies address related questions, although their intervention protocols are not necessarily equivalent to the gate permutations considered here.

A more systematic comparison of these protocols would help clarify whether the paper contributes a broadly applicable evaluation methodology or primarily formalizes a distinction within a particular family of interventions.

  1. The experiments do not fully separate the value of gate heterogeneity from the value of learning the assignment.

The paper correctly observes that heterogeneous messages may be useful even when their assignment is arbitrary. However, this insight is primarily established through theoretical constructions rather than a systematic empirical decomposition of these effects in trained networks.

I would encourage the authors to compare adaptive routing against both constant routing and fixed heterogeneous routing under carefully controlled training and evaluation conditions. The fixed heterogeneous control should preserve expert diversity without using a learned, input-conditioned assignment. Additional analyses of expert specialization, gate entropy, and expert utilization could further clarify whether observed gains arise from heterogeneous expert outputs or from the learned assignment itself.

Such experiments would make the distinction between heterogeneity, assignment sensitivity, and adaptive benefit more concrete.

  1. The strength of the frozen constant baseline remains uncertain for non-separable interventions.

The authors search a large collection of candidate constant gates and correctly acknowledge that a found constant only provides an upper bound on the advantage over the optimal constant. This caveat is important because an incomplete search can make adaptive routing appear more beneficial than it actually is.

However, the first-layer and joint interventions do not receive a general optimality certificate. Consequently, some empirical comparisons remain inconclusive about the advantage over the best possible constant gate.

The paper would benefit from stronger search-convergence diagnostics, sensitivity analyses with increasing search budgets, and a clearer separation between results that establish a positive advantage and those that merely fail to find a sufficiently strong constant alternative.

  1. The comparison between separately trained models does not isolate the routing mechanism as cleanly as the frozen-model analysis.

The separately trained adaptive and constant-routing models are tuned independently, and the selected configurations can differ in width, parameter count, and actual computation. Although this is a reasonable practical comparison, the resulting performance difference reflects the entire training procedure rather than the isolated effect of adaptive routing.

A more tightly controlled comparison, with matched active parameter counts, optimization budgets, and checkpoint-selection procedures, would strengthen the interpretation. Multiple seeds and additional graph architectures would also help establish whether the small reported differences are robust beyond the particular experimental setup.

  1. The related-work discussion could better connect the proposed framework to subsequent routing analyses.

The paper relates its contribution to attention interpretability, permutation-based explanations, and learned-versus-fixed routing. However, the discussion could more explicitly distinguish its contribution from empirical studies that compare learned routing with randomized alternatives, as well as work investigating expert homogenization and routing collapse in graph MoE models.

This would help position the paper's contribution more precisely: its main novelty is not simply that randomization can hurt performance, but that the interpretation of such degradation depends on the intervention, the computational coupling, and the target estimand.

Questions for authors

The reviewer wrote all the questions in the weakness part.

1 comment

We address the five concerns separately, with references to the accompanying revision.

W1 — Protocol scope (Appendix J). The separable result requires an additive score and the same marginal replacement-gate distribution at every evaluated node; replacements need not be independent. For finite gate banks, this condition is also necessary for the ordering to hold for every bounded additive separable score. Node-conditioned randomization can violate this condition, and downstream message passing or attention can violate separability. Training with nonlearned routing, as in Dikkala et al. (2023), asks a different question from permuting a trained gate field. We do not treat these protocols as interchangeable or claim their conclusions are refuted.

W2 — Heterogeneity versus adaptation (Appendices K-L and N). The ACM follow-up includes trained constants, hard hashes and two fixed soft-hash arms under shared expert widths and training budgets. Hard hashes alone are weak controls. A new Switch audit optimizes the entire declared content-independent positional class at one final-decoder interface, including overflow, with eight experts and capacity 64. Calibration accuracy is 68.878% for learned routing and 68.483% for the positional optimum. An attaining policy and the original each execute 114 expert calls per document with no drops. This isolates more than a broadcast comparison, but upstream routing remains adaptive and total FLOPs are not exactly matched. On fresh documents the preselected policy trails by 1.398 points; we do not infer a fresh full-class optimum.

W3 — Search versus certification (Appendices I, M.1 and N). The original nonlinear ACM search remains best-found: learned minus found-constant score upper-bounds optimal frozen advantage. Larger recorded searches change Roman validation cross-entropy by less than 2 × 10⁻⁹, which demonstrates search stability, not global optimality. For native Mowst* terminal probability mixtures, all 20 scalar convex validation-NLL optimality intervals have width below 10⁻¹⁰; these do not certify held-out accuracy. The Switch certificate separately bounds the full specified positional class for real-arithmetic evaluation of stored binary32 states. Native replay verifies the attaining policy, not all possible native floating-point executions.

W4 — Training fairness (Table 3; Appendix M). All 60 native Mowst*-GCN fits on Penn94 and ogbn-arxiv execute the published 20,000-update joint budget with paired expert initialization and validation selection. On Penn94, adaptive exceeds the trained constant by 0.70 [0.14, 1.23] accuracy points and fixed-soft routing by 0.61 [0.17, 1.02]. These are descriptive 95% bootstrap intervals over overlapping splits and seeds. Arxiv's accuracy comparison is inconclusive. The shared adaptive recipe is not independent per-arm tuning or exact capacity matching: adaptive versus constant parameter counts are 617,221 versus 616,837 on Penn94 and 320,849 versus 220,241 on arxiv. We retain these limitations.

W5 — Interpretation and related work (Section 6; Appendices I-J). The diagnostics measure gate variation, concentration and expert-output distances; nearly constant gates do not establish identical experts. We distinguish nonlearned router parameters, content-independent heterogeneous fields and shared constants. Constant-attention work, including Hassid et al. (2022), is an important precedent. These distinctions make the evaluation procedure applicable without turning evidence about one intervention into a claim about another.

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Paper summary

The authors argue that the accuracy drop from permuting a trained network’s routing gates across nodes does not measure the benefit of adaptive routing. They prove that the shuffle drop bounds the advantage over a constant gate when each node’s output depends only on its own gate, but with message passing either can be larger. Experiments on ACM-GCN across five graphs show these comparisons disagree, most notably on Roman-Empire.

Critical strengths

S1 Clear conceptual distinction: shuffling preserves the collection of gates, while constant routing removes it, and the decomposition in Eq. (3) makes explicit what the shuffle drop leaves out. The separability condition is something practitioners can check, letting them know when a shuffle result bounds anything.

S2 The experiments are well documented, and I have no concerns about the reported results. The supplementary material also supports reproduction, from rebuilding the tables to replaying checkpoints and repeating training.

Critical weaknesses

W1 My concerns are mostly limited to the significance of the paper. The theoretical results are underwhelming. In particular, Theorem 1 is a short averaging argument, and the authors themselves describe their tools as “elementary facts” (Section 6). The novelty is therefore mainly in the framing, which feels below the standard of ICLR.

W2 While the experiments are well documented, they feel limited. Roman-Empire has consdierably different performance compared to the other four datasets, investigating additional datasets would help establish if the shuffle/constant discrepancy is general or specific to Roman-Empire. Same goes for including other architectures like Node-MoE or FilterMoE, currently the main result is dependent one dataset on one architecture.

Questions for authors

Q1 Can the authors expand their empirical results to one other routing architecture, or to more datasets where routing helps meaningfully?

Q2 (Clarification) What explains the stark difference in Roman-Empire vs the other four datasets?

1 comment

Thank you for recognizing the distinction and the reproducibility of the experiments. We address your two questions with additional benchmark evidence and a direct diagnostic of Roman-Empire.

Q1 — Another architecture and meaningful routing benefit (Table 3; Appendix M). We completed native Mowst*-GCN on Penn94 and ogbn-arxiv: 45 and 15 final fits, respectively, across adaptive, trained-constant and fixed-soft arms. Each fit executed the published 20,000-update joint budget, with validation-selected checkpoints. Adaptive accuracy is 82.25% on Penn94 and 71.79% on arxiv. These runs use the released probability-mixture inference rule; the earlier post-review logit-mixture implementation is now explicitly distinguished as Mowst-L. This correction does not affect the submitted ACM-GCN results.

On Penn94, shuffling loses only 0.01 [−0.01, 0.03] accuracy points. A validation-selected frozen constant improves accuracy by 1.08 [0.51, 1.70] points, yet separately trained adaptive routing beats the trained constant by 0.70 [0.14, 1.23] and the fixed-soft arm by 0.61 [0.17, 1.02]. Thus the frozen and trained comparisons give opposite rankings on a second architecture and a different graph. On arxiv, the trained accuracy difference is 0.14 [−0.14, 0.43], so we retain the inconclusive result. These descriptive 95% split/seed bootstrap intervals are not population guarantees. Training budgets and expert initialization are paired; active parameter counts and per-arm tuning are not fully matched.

Q2 — Why is Roman different (Appendix I)? In the original ACM checkpoints, mean squared gate distances from the layer mean are 0.05096 and 0.04691 on Roman, versus maxima of 0.00118 and 0.00042 on the other graphs. More importantly, paired validation interventions keep the evaluated node's gate fixed while changing the surrounding field. They yield correctness gains of 1.940 points and losses of 1.836, leaving a small net effect of 0.104 points with conditional Monte Carlo SE 0.154. The average broadcast policy scores 7.261 points below the best-found constant. The measured discrepancy therefore mainly reflects broadcast-policy suboptimality, alongside substantial individual effects that cancel. This explains the decomposition in these fitted models, without identifying a universal graph property or attributing the result to heterophily alone.

Significance and limits. The practical procedure is to specify the intervention, check additivity and separability, compare credible frozen alternatives, and retrain static controls when the claim concerns learning. Penn94 shows why the final step changes the conclusion. The proof remains elementary, and the new Mowst* interface is separable. We do not claim that the positive coupled extreme has been established on a competitive natural task; its role remains an existence result.

Comments on the paper

2 comments
AuthorsOpenReview ↗

Additional evidence and scope of the claims

We thank the reviewers for identifying the need for broader evidence, stronger static controls and a clearer account of significance. We have completed additional evaluations addressing these concerns; the individual replies give the results and their limitations. The accompanying revised paper contains the benchmark comparison in Table 3 and Appendix M, Roman diagnostics in Appendix I, the replacement-law extension in Appendix J, and the Switch certificate and fresh evaluation in Appendix N (Tables 68-69).

The clearest new example is native Mowst*-GCN on Penn94. Shuffling barely changes accuracy, a validation-selected frozen constant improves it, yet separately trained adaptive routing outperforms the trained constant. Thus frozen replacement and training comparisons can give opposite rankings on a standard benchmark. We also evaluated ogbn-arxiv and directly measured the cross-node effects behind the original Roman-Empire discrepancy.

A separate audit of a pretrained Switch Transformer compares its final decoder router with a full class of content-independent positional policies. On 512 calibration documents, the shuffle drop, advantage over the best broadcast constant and advantage over the best positional policy are 1.661, 1.566 and 0.396 accuracy points. The positional optimum is certified for a specified reference computation. On 512 fresh documents, the preselected positional policy falls behind by 1.398 points; this is a policy comparison, not a fresh full-class certificate.

These additions support a practical distinction between routing sensitivity, frozen replacement and training benefit. They do not establish a competitive natural-task positive coupling gap or overturn a published paper's empirical conclusion. The individual replies distinguish what is proved, what is measured and what remains unresolved.

Dear authors, I do think it is truly disrespectful to upload such an AI-generated rebuttal after already submitting such an AI-generated submission.

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

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