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Paper summary
The paper argues that GNN failure on molecular activity cliffs stems not from oversquashing or oversmoothing during propagation, but from dilution at readout: localized substituent edits carry energy at nonzero graph frequencies, while mean pooling retains only the zero-frequency (constant) component, so a signal concentrated on a few atoms contributes weakly to the pooled graph vector. The proposed model, SpecLiff, keeps GraphCliff as a low-pass scaffold branch predicting μ, and adds a high-pass branch: Chebyshev-approximated spectral graph wavelets at two scales, bridge-decomposition features, and ℓ2-magnitude summation yielding z_high, from which an effect head predicts a correction τ, with ŷ = μ + τ. A matched-pair consistency loss supervises τ via τᵢ − τⱼ ≈ yᵢ − yⱼ on training cliff pairs. On all 30 MoleculeACE tasks, SpecLiff reports the best average RMSE (0.654 vs. 0.665 for GraphCliff) and the most dataset-level wins.
Critical strengths
The problem framing is the paper’s main contribution, and it is a good one. Relocating the failure from propagation to pooling is a clean and useful reframing. The empirical audit in Appendix A supports it constructively: attachment edges are shown not to be topological bottlenecks (lower betweenness, higher Ollivier-Ricci curvature than scaffold-internal edges, p = 1.0 in both one-sided tests), which argues directly against curvature-guided rewiring as the right remedy for this benchmark. The dilution account is intuitive, formalized at an appropriate level, and the paper is careful to state where each proposition does and does not apply.
Critical weaknesses
W1. The central mechanistic claim is asserted rather than demonstrated. The paper’s causal story has three links: (i) local structural differences between cliff pairs manifest as high-frequency graph signals; (ii) the chosen wavelet scales g_s(λ) = 1 − e^(−sλ) actually isolate that frequency band; (iii) what the high-pass branch isolates corresponds to the structural edit. None is directly verified.
Section 5.3 is the closest attempt, but it measures a different quantity: the spatial concentration of single-molecule representation energy on branch-labeled atoms, not the spectral content of the pairwise difference signal that Proposition 1 is about.
W2. RMSE_cliff is missing, and this is not optional for this benchmark. MoleculeACE was introduced specifically to argue for “activity-cliff-centered” metrics. A paper whose entire motivation is cliff performance, evaluated only on aggregate RMSE over all test molecules, leaves open whether the gain comes from cliff compounds at all or from the non-cliff majority. Given cliff ratios of 8.8–54%, an overall improvement of 0.011 could be produced either way.
Questions for authors
Q1 (W1). Can the authors provide direct evidence for the spectral premise? Concretely: (a) for aligned cliff pairs, compute the graph Fourier transform of the difference signal h(G) − h(G′) and report the energy distribution over λ, compared against non-cliff pairs of similar size; (b) report the selected s₁, s₂ per dataset together with the resulting filter gain curves, to show which band is actually passed; (c) quantify the correspondence between high-pass energy and the MCS-derived edit atoms (not the authors’ bridge labels), e.g. as an attribution AUC. Without (a) the motivating theory is untested on real data; without (c) Figure 5 remains anecdotal.
Q2 (W2). Please report RMSE_cliff for SpecLiff and all baselines, per dataset and averaged, using the official code.
Q3 . Please provide the full search space: ranges and priors for every tuned hyperparameter, the number of Optuna trials, and the selected values per dataset, in particular s₁, s₂, K, and β. Is any ordering (s₁ < s₂) or minimum separation enforced, and how often do the two selected scales end up close enough that the branch is effectively single-scale?
Q4. SpecLiff is GraphCliff plus an additional branch, yet reports lower training time per epoch (0.61 vs 0.94 s) and lower inference latency (11.03 vs 11.72 ms). Could the authors clarify: are the two models compared under matched batch size, hidden dimension, and number of message-passing layers?
Q5. Two ablations would disentangle architecture from supervision: (a) Low-pass + pair loss, i.e. no high-pass branch but with pairwise supervision applied to μ (μᵢ − μⱼ ≈ yᵢ − yⱼ). If this recovers much of the gain, the contribution is the supervision, not the spectral branch. (b) High-pass branch with β = 0 but retuned, rather than inheriting full-model hyperparameters. Given w/o pair loss (0.698) and w/o high-pass (0.702) differ by only 0.004, does the gain in fact require both components jointly? If so, the paper’s narrative, in which the high-pass branch is the primary contribution and the pair loss a training detail, may need rebalancing.
Q6. How many qualifying cliff pairs exist per dataset in train split? Given single-seed results and a 0.011 margin, can the authors report mean ± std over at least 3–5 seeds for the full model and the ablations? Specifically, is the pair-loss ablation gap statistically distinguishable from seed noise?
Q7. Why is the kernel fixed rather than learned? Appendix C calls the branch “a fixed-kernel Chebyshev approximation rather than a freely learned ChebNet filter”, but it is the same object as ChebNet, at the same O(K|E|d) cost, with coefficients frozen. ChebNet, GPR-GNN, BernNet and ChebNetII learn these end-to-end; none is cited or compared. Two controls would settle the branch’s contribution: (a) the same branch with learned coefficients, and (b) the same branch with a low-pass kernel. If (b) also beats the no-high-pass variant, the gain is added capacity, not high-pass filtering. Corollary 1 only requires |h(λ)| ≥ η above the cutoff — a constraint on the response, not a reason to freeze it.