- Rating
- 3(+1)
- Confidence
- 2(−1)
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2(+1)
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Paper summary
The paper introduces POMA, a proxy-rewarded source-selection framework for molecular OOD adaptation, together with SCOPE-Bench, a scaffold-cluster benchmark constructed from physicochemical descriptors. POMA uses unlabeled target structures to identify proxy targets, learns a source-subset selection policy through GRPO using post-adaptation MAE reduction as reward, and performs target adaptation with whole-molecule and BRICS-level covariance alignment.
Critical strengths
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The source-selection problem is practically meaningful. The paper explicitly considers negative transfer from heterogeneous source domains and learns source combinations using downstream adaptation performance rather than structural similarity alone.
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The proxy-reward formulation is interesting. Using structurally related labeled scaffolds as proxy targets provides a way to train a selection policy without accessing real-target property labels.
Critical weaknesses
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The computational cost is quite high for practical or large-scale deployment. POMA requires about 72 GPU-hours for offline GRPO optimization and, more importantly, approximately 4.5 GPU-hours of adaptation for every target scaffold on an RTX A6000. This per-target overhead makes deployment over hundreds or thousands of new targets difficult.
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It is unclear how reusable the offline policy training really is. Proxy targets are constructed using the unlabeled structures of the real target domain. Therefore, when the target domain changes substantially, it is unclear whether the 72-hour GRPO training can truly be reused or must be repeated.
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The empirical scope is limited. The evaluation is restricted to QM9, three closely related quantum properties (HOMO, LUMO, and Gap) and three backbones. This is insufficient to establish broad molecular OOD generalization, especially for more realistic drug-discovery tasks.
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The validation of SCOPE-Bench is not fully convincing. The authors explicitly state that the cache-to-split mapping and molecule-level identity provenance are not established, and therefore the feature-space diagnostics are only descriptive rather than a formal validation of the benchmark split.
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The presentation of Figure 2 is poor. The text, equations, and annotations are too small to read comfortably. A substantial redesign is needed to improve readability.
Questions for authors
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How is POMA expected to scale to a large number of target scaffolds? With approximately 4.5 GPU-hours of adaptation per target, evaluating 1,000 new targets would require roughly 4,500 GPU-hours. Can the target adaptation be amortized or avoided?
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Is the reported 72 GPU-hour GRPO optimization truly a one-time cost? Since the proxy targets are constructed from the current real target structures, would a substantially different future target domain require rebuilding the proxy set and retraining the policy?
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How well does proxy-task reward reflect the actual utility of a source subset on the real target? The central assumption appears to be that source combinations producing larger post-adaptation gains on structurally retrieved proxy targets will also be more useful for the real unlabeled target. Could the authors directly quantify this relationship, for example by measuring the correlation between proxy rewards and true held-out target utilities in the evaluation setting? The manuscript itself describes the proxy rewards as surrogate feedback rather than guarantees of optimal real-target selection.
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Could the authors report results over multiple random seeds? Given the stochastic GRPO training and subset sampling, mean and standard deviation across independent policy-training runs seem necessary.
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Can the authors evaluate POMA on additional molecular datasets and tasks beyond QM9? In particular, experiments on realistic drug-like datasets would help establish whether the conclusions transfer beyond quantum-property prediction.
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Could the authors more clearly isolate the contribution of GRPO-based source selection from that of dual-scale CORAL adaptation? Detailed source-selection comparisons are mainly presented for ViSNet–HOMO, where the gain over the strongest heuristic is relatively modest, while removing either CORAL component causes a larger degradation. Extending the source-selection baselines to all backbone–property combinations would clarify whether the learned policy consistently contributes beyond the adaptation module.
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How is leakage or trivial self-transfer prevented when constructing each proxy-target environment? In particular, is the proxy-target scaffold explicitly excluded from its own candidate source pool during reward computation? The manuscript defines both the proxy targets and candidate sources from the labeled source pool but does not clearly state this exclusion. If can appear among its own candidate sources, the proxy task may become artificially easy.
13 comments
Author Response (2/9)
For w2 and q2:
The analysis for Question 3 provides evidence for policy reuse. For a new unlabeled target scaffold, we first calculate its maximum Morgan similarity to the proxy-scaffold set used by the existing policy. If this similarity reaches a predefined threshold , the existing GRPO policy can be reused preferentially. If it falls below the threshold, the new target may lie in a region insufficiently covered by the existing proxy set; in this case, the proxy set should be reconstructed and the policy re-optimized.
Specifically, we define
where denotes the proxy-scaffold set used during policy training. The threshold can be calibrated in advance by running the complete POMA pipeline on a labeled dataset from the relevant domain, and then used to assess new targets.
When the chemical space of a future target domain changes, whether the proxy set and policy need to be updated can first be assessed using this structural-coverage check. If the chemical space has changed substantially and the maximum similarity is very low, the proxy set should be reconstructed and the existing policy re-optimized.
Author Response (3/9)
For q3:
Thank you for this insightful question. It prompted us to further examine whether proxy targets retrieved from real-target structures provide a training environment relevant to the real targets, and whether this structural relationship can be observed in the gains on real targets. This analysis not only examines the relationship between proxy-target representativeness and real-target gains, but also provides quantitative support for the policy-reuse question in Question 2: the structural similarity between a new target and the existing proxy set can serve as a computable indicator of whether the target lies within the coverage of the current policy.
We followed the Hub Selection procedure implemented in GRPO to score all scaffolds in the source-domain pool and selected 20 unique proxy scaffolds according to their HubScores. For each real target scaffold, we then calculated its maximum Morgan cosine similarity to these 20 proxy scaffolds. The real-target gains were measured using the Seed-42 ViSNet–HOMO results, consistent with the task used for policy training, and calculated as
{MAE_i^{\mathrm{supervised}}}\times100\%.$$ Across the 15 real targets, the maximum similarity to the proxy scaffolds showed a significant positive rank correlation with the real-target MAE improvement. The Spearman correlation was $\rho=0.6638$, with a two-sided $p=0.00696$ and a bootstrap 95% percentile confidence interval of $[0.2395,0.8514]$. The Pearson correlation was $r=0.4042$, with $p=0.1351$. This indicates that, overall, real targets structurally closer to the selected proxy set tend to obtain greater gains from the source-selection policy trained using domain-adaptation feedback on proxy targets. We use Spearman correlation as the primary statistic because our interest is in whether the ranking of target gains changes with structural proximity to the proxy set. The results for all 15 targets are shown below: | Scaffold | Maximum Morgan similarity to the selected proxy scaffolds | Seed-42 ViSNet–HOMO MAE improvement | |---:|---:|---:| | 1 | 0.7606 | +11.37% | | 2 | 0.4899 | +18.06% | | 3 | 0.4622 | +0.00% | | 4 | 0.5715 | +22.44% | | 5 | 0.5103 | +0.00% | | 6 | 0.7606 | +17.40% | | 7 | 0.5893 | +4.19% | | 8 | 0.7606 | +1.44% | | 9 | 0.4615 | +0.00% | | 10 | 0.4622 | +0.00% | | 11 | 0.5000 | +2.91% | | 12 | 0.3846 | +0.00% | | 13 | 0.3846 | +0.00% | | 14 | 0.4419 | -30.84% | | 15 | 0.4725 | +12.32% | As shown in the table, negative or zero gains occur toward the lower-similarity end. The six real targets with zero gain were reverted to the supervised model by our gating mechanism; that is, without this reversion, they would theoretically also have incurred negative gains. In contrast, targets with higher similarity generally show more positive gains. These results connect proxy-target construction with performance on real target domains: structural retrieval provides a target-relevant proxy environment, and domain-adaptation gains on proxy tasks provide feedback for training the source-selection policy. On real targets, the structural proximity to the proxy set is significantly positively associated with POMA's actual improvement ranking. Thus, the proxy set is used not only to construct the policy-training environment, but also as a reference for assessing whether a new target lies within the structural coverage of the existing policy at deployment. This quantitative result therefore also provides an actionable basis for policy reuse in Question 2.
Author Response (1/9)
We thank you for carefully reviewing our paper and for raising specific questions about computational cost, policy reuse, and proxy tasks.
For w1 and q1:
The 72 GPU-hours mentioned in your comment were measured in a shared GPU environment, where other tasks were running on the same device and slowed down our GRPO policy optimization. When conducting the supplementary experiments on QMugs, we remeasured the computational cost in an isolated NVIDIA H200 environment. Averaged over the eight QMugs targets, the cost per target is as follows:
Here, 1.54 GPU-hours is the average GRPO policy-optimization cost per target, while 1.98 GPU-hours is the average cost of domain adaptation for each target.
Regarding scalability to a large number of target scaffolds, structurally similar targets can first be organized into scaffold families or groups of related structural regions. Fine-grained domain adaptation can then be performed only for sub-scaffolds where necessary. This avoids dividing all targets into the finest-grained units from the outset and repeating the complete procedure for every closely related target.
Therefore, for the 1,000 new targets mentioned in your question, the policy-optimization cost should not be counted repeatedly for every target. If these targets fall within the coverage of the same proxy set, the policy-optimization cost only needs to be incurred once. For domain adaptation, targets with highly similar structures can be handled at a coarser granularity, since a scaffold does not necessarily have to be defined at the finest Bemis–Murcko level.