acceptodds
Under review as a conference paper at ICLR 2027

Learning to Select Source Domains: Proxy-Rewarded Policy Optimization for Molecular OOD Generalization

Abstract

Robust generalization under extreme out-of-distribution (OOD) shifts remains a fundamental challenge for molecular property prediction. Existing scaffold-based evaluation protocols often fail to eliminate subtle structural and semantic overlap between training and test molecules, leading to overly optimistic estimates of model extrapolation capability. Meanwhile, conventional domain adaptation approaches typically perform indiscriminate alignment across heterogeneous source domains, which may introduce irrelevant knowledge and cause negative transfer under severe distribution shifts. In this work, we investigate molecular OOD generalization from the perspective of adaptive source domain selection. We first introduce SCOPE-Bench, a challenging molecular OOD benchmark constructed through cluster-level partitioning in an explicit physicochemical descriptor space, enabling more rigorous evaluation of extrapolation ability beyond conventional scaffold splitting. Based on this benchmark, we propose Policy Optimization for Multi-source Adaptation (POMA), a framework that formulates knowledge transfer as a source selection problem. POMA learns a policy to identify transferable source subsets from a large candidate domain pool, followed by dual-scale adaptation that captures both global molecular topology and local pharmacophore patterns. Extensive experiments across diverse molecular prediction architectures demonstrate that current state-of-the-art models suffer substantial performance degradation under realistic OOD shifts, with prediction errors increasing by up to 8.0× and 5.9× on average compared with conventional evaluations. POMA consistently improves generalization performance across multiple backbone models, achieving up to 11.2% reduction in mean absolute error and an average relative improvement of 6.2%. These results reveal the importance of adaptive source utilization for reliable molecular learning and provide a general strategy for mitigating negative transfer under extreme distribution shifts.

Primary area:
applications to physical sciences (physics, chemistry, biology, etc.)
Keywords:
Out-of-Distribution Generalization, Molecular Property Prediction, Source Domain Selection, Domain Adaptation, Reinforcement Learning

Reviews

Among:
Shape:
1234this paper, Top 15%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
Reviewer_ruRsOpenReview ↗
Rating
3(+1)
Confidence
2(−1)
Informativeness
2
Presentation
2
Soundness
2(+1)
Read review
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
  1. 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.

  2. 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
  1. 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.

  2. 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.

  3. 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.

  4. 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.

  5. 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
  1. 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?

  2. 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?

  3. 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.

  4. 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.

  5. 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.

  6. 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.

  7. How is leakage or trivial self-transfer prevented when constructing each proxy-target environment? In particular, is the proxy-target scaffold s∗s* explicitly excluded from its own candidate source pool C(s∗)C(s*) 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 s∗s* can appear among its own candidate sources, the proxy task may become artificially easy.

13 comments
AuthorsOpenReview ↗

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:

Computational stageAverage GPU-hours per target
GRPO policy optimization1.54
Target-specific model adaptation1.98
Total3.52

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.

AuthorsOpenReview ↗

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 τ\tau, 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

s(x)=max⁡p∈PSim⁡Morgan(x,p),s(x)=\max_{p\in\mathcal P}\operatorname{Sim}_{\mathrm{Morgan}}(x,p),

where P\mathcal P denotes the proxy-scaffold set used during policy training. The threshold τ\tau 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.

AuthorsOpenReview ↗

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.
Reviewer_Q7GeOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper focuses on robust molecular property prediction under extreme out-of-distribution. To this end, the authors propose Policy Optimization for Multi-source Adaptation (POMA), a retrieve–compose–adapt framework for adaptive source domain selection when target property labels are unavailable. The results show the advantge of the proposed method.

Critical strengths
  1. The SCOPE-BENCH may inspire follow-up work.
  2. The overall idea of using unlabeled target structures to retrieve structurally similar labeled source scaffolds as a proxy target is reasonable.
Critical weaknesses
  1. Why choose covariance alignment between the source and target representations?
  2. The methodology contribution is somewhat incremental, as GRPO, DECOUPLing features can be founded at exisitng works.
  3. The comparison methods are limited. The advantage over existing works is not significant.
Questions for authors
  1. Why choose covariance alignment between the source and target representations?
  2. The methodology contribution is somewhat incremental, as GRPO, DECOUPLing features can be founded at exisitng works.
  3. The comparison methods are limited. The advantage over existing works is not significant.
3 comments
AuthorsOpenReview ↗

Author Response (1/3)

For w1 and q1:

We thank you for recognizing the improvements across multiple backbone–property combinations and for pointing out the need to clarify the respective roles of source selection and dual-scale adaptation.

We chose CORAL because it aligns the second-order statistics of source- and target-domain features without requiring target-property labels or instance-level source–target correspondences, making it suitable for our unsupervised domain-adaptation setting. CORAL was not our initial choice: we also experimented with MMD and DANN, but both were more prone to negative transfer in our multi-source, structurally heterogeneous molecular OOD setting. We attribute this behavior to the relationship between molecular structural differences and property prediction. DANN uses adversarial training to suppress domain-discriminative information; when domain differences include structural information relevant to molecular properties, enforcing domain invariance too strongly may impair property prediction. MMD can measure nonlinear distribution differences through kernel functions, but matching the overall distributions does not guarantee correspondences between different scaffolds and local chemical structures that are beneficial for property prediction. By comparison, CORAL directly constrains feature covariances and can be jointly optimized with source-domain supervised regression through a relatively simple statistical alignment objective. In our experiments, it exhibited greater stability.

Our early experiments also showed, however, that applying CORAL only to whole-molecule representations was insufficient to address local structural differences in molecular OOD generalization. Similar covariance statistics of whole-molecule representations do not imply similar distributions of functional groups and local chemical fragments across domains. We therefore further tested alignment using only BRICS substructure representations. However, local fragments considered independently of their parent molecules' global topology and chemical context cannot fully preserve the structural relationships among fragments or their joint effects on molecular properties.

Based on these observations, we designed dual-scale CORAL over whole molecules and BRICS substructures. The whole-molecule pathway aligns global structural representations, while the substructure pathway aligns local chemical-fragment representations. The two pathways have independent weights and are jointly optimized with source-domain property supervision. This design accounts for global structural shifts in the target domain while retaining an adaptation constraint at the local-fragment level.

The ablation study in Table 2 of the main paper supports this design. With the POMA source-selection strategy fixed, the complete dual-scale configuration achieves an MAE of 0.1540 eV. Removing molecular-level CORAL or substructure-level CORAL increases the MAE to 0.1689 and 0.1672 eV, respectively; both are higher than the supervised baseline of 0.1621 eV. These results show that both whole-molecule and local-substructure alignment contribute to adaptation in the molecular OOD setting considered here, and neither single-scale configuration matches the complete dual-scale configuration.

Thus, our contribution is not a new CORAL operator. Rather, we design two independently weighted adaptation pathways at the whole-molecule and BRICS-substructure levels to address distribution shifts in both global molecular structures and local chemical fragments, and integrate them with source-domain supervision and learned source selection.

AuthorsOpenReview ↗

Author Response (2/3)

For w2 and q2:

We agree that GRPO, CORAL, and BRICS each have established foundations in prior work; we do not claim these underlying tools themselves as our original contributions. POMA addresses two related challenges in multi-source molecular OOD adaptation: determining which combinations of source scaffolds are genuinely beneficial after adaptation, and handling shifts in both global molecular structures and local chemical fragments in the target domain.

For source selection, our preliminary exploration used Mixed, a heuristic we designed by combining WL graph-structural similarity with physicochemical information for static source selection. Structural similarity alone, however, cannot indicate whether a source domain will actually improve property prediction after target adaptation. Moreover, the gains from this heuristic were not stable, with negative gains on multiple target domains. We therefore developed proxy tasks: we retrieve proxy scaffolds using the unlabeled structures of real targets, evaluate candidate source combinations by the change in prediction error after adaptation on the proxy targets, and use this feedback to optimize the GRPO policy. This enables the model to learn scaffold-level source combinations conditioned on different targets, rather than relying on a fixed similarity ranking.

For target-domain adaptation, we use dual-scale CORAL over whole molecules and BRICS substructures, based on the different structural information represented at the global-topology and local-fragment levels. The former constrains whole-molecule representations, while the latter adds distribution alignment at the local-fragment level, avoiding adaptation based on only one scale.

Accordingly, POMA's contribution is not to propose GRPO or CORAL anew, but to combine proxy-domain-adaptation-feedback-driven scaffold-level source-combination selection with whole-molecule/local-substructure dual-scale adaptation in a Retrieve–Compose–Adapt framework. The former addresses source selection, while the latter addresses target-specific adaptation after source selection. Together, they support molecular OOD generalization when target-property labels are unavailable.

This design also provides a structural basis for policy reuse. For a new unlabeled target scaffold xx, we calculate its maximum Morgan similarity to the 20 proxy scaffolds used for policy training, denoted by P\mathcal P:

s(x)=max⁡p∈PSim⁡Morgan(x,p).s(x)=\max_{p\in\mathcal P}\operatorname{Sim}_{\mathrm{Morgan}}(x,p).

If s(x)s(x) reaches a threshold τ\tau, calibrated in advance on independent development/validation targets, the existing GRPO policy can be reused. If it falls below the threshold, the proxy set is updated and the policy is re-optimized.

This criterion is supported by a subsequent paired quantitative analysis on 15 real targets. Following the Hub Selection procedure in our GRPO code, we constructed 20 proxy scaffolds, calculated the maximum Morgan similarity of each real target to the proxy set, and paired it with the Seed-42 ViSNet–HOMO MAE improvement on that target. The Spearman rank correlation was ρ=0.6638\rho=0.6638, with a two-sided p=0.00696p=0.00696 and a bootstrap 95% percentile confidence interval of [0.2395,0.8514][0.2395,0.8514]. The complete results are shown below.

ScaffoldTarget fileMaximum Morgan similaritySeed-42 ViSNet–HOMO MAE improvement
1a0130.7606+11.37%
2a0010.4899+18.06%
3a0220.4622+0.00%
4a0090.5715+22.44%
5a0310.5103+0.00%
6a0160.7606+17.40%
7a0290.5893+4.19%
8a0150.7606+1.44%
9a0370.4615+0.00%
10a0300.4622+0.00%
11a0330.5000+2.91%
12a0340.3846+0.00%
13a0360.3846+0.00%
14a0110.4419−30.84%
15a0230.4725+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; without this reversion, they would theoretically also have incurred negative gains. By comparison, targets with higher similarity generally show more positive gains. This result also provides supporting evidence for reusing the learned policy.

AuthorsOpenReview ↗

Author Response (3/3)

For w3 and q3:

We conducted two controlled groups of experiments to examine the respective contributions of source selection and dual-scale adaptation. The results are reported in Table 2 (Section 4.4) of the main paper.

In the first group, we fixed dual-scale CORAL and changed only the source-selection strategy. The comparisons include Random, Shallow, Deep, Physical, WL, and Mixed, which we designed in our earlier source-selection exploration. Four fixed rules resulted in negative transfer, while WL and Mixed reduced MAE by 0.3% and 2.8%, respectively. POMA reduced MAE to 0.1540 eV, a 5.0% reduction relative to the supervised baseline, and further reduced MAE by 0.0036 eV compared with Mixed. This shows that, with the adaptation module held constant, learning source combinations from proxy adaptation feedback achieves a better overall result than fixed heuristic source-selection rules.

In the second group, we fixed the GRPO source-selection strategy and separately removed molecular-level and BRICS-substructure-level CORAL. Removing Mol-CORAL increases MAE to 0.1689 eV, while removing Sub-CORAL increases it to 0.1672 eV. Both are clearly higher than the 0.1540 eV achieved by the complete dual-scale configuration and also higher than the supervised baseline of 0.1621 eV. These results further show that both whole-molecule and local-substructure scales contribute importantly to adaptation, and that the complete dual-scale design outperforms either single-scale configuration.

In addition, Table 1 of the main paper reports the complete POMA results across three backbones—ViSNet, ETNN, and GotenNet—and three properties—HOMO, LUMO, and Gap. POMA outperforms the corresponding supervised baseline in all nine backbone–property combinations, showing that its improvements are not limited to one model architecture or one property task. Together with the two ablation groups in Table 2, these results verify the effectiveness of learned source selection and dual-scale adaptation, and show that their combination is an important factor in the performance gains of the complete POMA framework.

Beyond QM9, to evaluate POMA on a drug-like molecular dataset closer to real drug-discovery settings, we further applied the complete POMA pipeline to eight target scaffolds in QMugs. QMugs is derived from bioactive molecules in ChEMBL. Its dataset description reports 665,911 drug-like molecules and approximately 1.99 million conformers, with an average of 30.6 heavy atoms and a maximum of 100. In comparison, QM9 has an average of approximately 8.8 heavy atoms and a maximum of 9. QMugs therefore extends the evaluation to larger molecular structures with greater relevance to drug discovery. POMA achieves a lower MAE on seven of the eight targets, as shown below.

Target scaffoldSupervised ViSNet MAE (eV)POMA MAE (eV)MAE reduction
10.11380.1097+3.6%
20.12210.1188+2.7%
30.11780.1070+9.1%
40.13570.1365−0.6%
50.13470.1295+3.9%
60.09300.0852+8.3%
70.15490.1492+3.7%
80.08210.0761+7.3%

For HOMO prediction on the eight real target domains in QMugs, POMA improves performance on seven targets, with only a small negative gain on target scaffold 4. This further shows that POMA is effective not only on QM9 quantum-property prediction tasks but also on a larger drug-like molecular dataset.

Reviewer_vgcbOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies molecular property prediction under scaffold distribution shift. It introduces SCOPE-BENCH, a QM9 benchmark that represents the 1,247 Bemis-Murcko scaffolds by a four-dimensional physicochemical descriptor, groups them into five levels by ring count and maximum ring size, clusters within each level into 12 scaffold clusters, and partitions these into six source, one validation, and five target clusters, giving 15 target-scaffold tasks. The paper reports a mean MAE degradation of 5.9x relative to conventional scaffold splitting. It then proposes POMA for the case of unlabeled targets: structurally similar source scaffolds are retrieved as proxy targets, a GRPO-trained policy selects at most five source scaffolds from a 50-candidate pool, and the reward is the proxy-task MAE reduction obtained under a dual-scale CORAL adaptation at the whole-molecule and BRICS-substructure levels. Across HOMO, LUMO, and gap prediction on three 3D backbones with a single seed, the paper reports a mean relative MAE reduction of 6.2%.

Critical strengths
  1. The reported improvements are consistent in sign across the whole evaluation grid. Against a supervised model trained on all available source data without adaptation, POMA attains lower reported MAE on all nine backbone-property combinations, with an average relative reduction of 6.2% and a maximum of 11.2%. The same procedure is applied to three structurally different 3D backbones and to three properties, and the per-scaffold results behind each main-table entry are given in the appendix, so the aggregate numbers can be inspected rather than only taken on trust.
  2. Negative transfer is real and measurable in this setting, and the selection step turns it around. In the ViSNet-HOMO ablation the adaptation module is held fixed across all selection rules, so the spread across rules is attributable to which source domains are selected rather than to how alignment is performed. Four of the six non-RL heuristics end up worse than performing no adaptation at all, by the reported margins of 5.3% for random selection, 2.5% for shallow-feature similarity, 2.9% for deep-feature similarity and 1.2% for the physical heuristic. The learned policy improves on the no-adaptation baseline by 5.0%, a spread of more than ten percentage points under an identical alignment procedure. I find this the most informative result in the paper, and it is useful well beyond the particular method: it shows that source composition is not a second-order implementation detail, and that a badly chosen source set actively damages a model that would have been better left alone.
Critical weaknesses
  1. The benchmark excludes the regime in which scaffold-level OOD generalization matters most. The 1,247 scaffolds retained in Section 3.2 are those with at least ten molecules each, and the 15 target-scaffold evaluation tasks in Section 4.2 are further restricted to scaffolds with N >= 200. Real scaffold distributions are heavy-tailed, and a large share of scaffolds occur once or a handful of times. Those are exactly the cases in which a predictor has no local support and in which source selection would matter most. The method also depends on sample counts structurally, through the ln(1 + |D_cj|) weighting in Equation (4) and through supervised regression on each selected source scaffold, so its behaviour on scaffolds holding one or two molecules is not merely untested but unclear. Relatedly, all experiments use QM9 and three closely related electronic properties. Whether the selection signal transfers to properties with a different structure-property relationship, for example docking scores or other pose-dependent quantities, is not examined.
  2. The construction of the benchmark does not deliver its stated motivation. Section 3.1 motivates the split by observing that scaffold disjointness alone does not ensure separation of local structural patterns. The construction that follows clusters a four-dimensional physicochemical descriptor with k-means++, which constrains neither substructure overlap nor local structural patterns directly. The paper acknowledges this twice, in Section 4.2 and again in the appendix, stating that the splits do not establish complete chemical or substructure isolation. The distance between the motivation and the construction is therefore not a matter of interpretation. A split that constrains substructure overlap directly would close it: holding out BRICS fragments or functional groups, or imposing a hard cap on the maximum Tanimoto similarity or the maximum common fragment between the training and the evaluation sets. Such a comparison would also separate how much of the reported 5.9x degradation comes from scaffold disjointness and how much from the descriptor-space separation.
  3. Reduced to its essentials, the method trains a general model on all source data and then adapts it on a selected small subset. Two cheaper alternatives are not considered, and either would clarify where the gain comes from. (a) Cluster the source scaffolds and adapt using only the source cluster nearest to the target, with no learned selection. Since the target domain carries no property labels by construction, the comparison has to use the nearest source cluster rather than the target cluster itself, but it remains a trivially cheap baseline and it tests selection granularity directly: scaffold-level learned selection against cluster-level assignment. The same baseline would also test whether the first stage is necessary. Section 4.1 trains the supervised stage on the full source domain of 94,562 molecules for 200 epochs; if adapting within the relevant cluster alone performs comparably, then most of that pretraining is unnecessary and the contribution of the global stage should be reported separately from the contribution of selection. (b) Train one small expert per source cluster and combine them with a mixture-of-experts gate over the scaffold descriptors. With six source clusters this is inexpensive, and it avoids the subset-selection problem altogether by learning a weighting instead of a discrete subset. If a gated mixture matched POMA, the case for reinforcement learning over subsets would need to be made on grounds other than accuracy.
  4. The per-scaffold results in the appendix do not support the aggregate improvement. I recomputed all 150 cells of Table 5; the ten column means reproduce the values printed in Table 2, with random selection differing by 0.0001. On that reading the fifteen ViSNet-HOMO targets divide as follows. POMA is the unique best method on four of them. On three more it ties for best, in every case with the unadapted baseline. On the remaining eight another column is better: a non-learned heuristic on six of those, and the unadapted baseline itself on scaffold 14, where POMA is worse by 0.0177. Separately, on six targets the Baseline, w/o Mol, w/o Sub and POMA columns are identical to four decimal places, so adaptation changed nothing there; three of those six fall among the ties and three among the eight. The gain is concentrated to a matching degree: the per-target reductions sum to 0.1228, of which scaffold 4 alone supplies 37% and the four largest 86%. Two further details bear on the ablation's conclusion. Scaffold 4, the target supplying 37% of the gain, is also where removing the substructure alignment beats the full method, 0.1473 against 0.1576. And those same six targets take an identical value across all five configurations of Table 6; since K = 1 forces one source domain to be selected, an empty selection cannot explain them. Table 5 does show that a well-chosen source set helps and a badly chosen one hurts. It does not show that the learned policy is the right instrument for choosing: a non-learned rule from the same table does better on six of the fifteen targets, and the unadapted baseline matches or beats POMA on seven. Please discuss the per-target distribution alongside the mean, and explain the identical rows.
  5. Parts of the method cannot be reproduced, and no result carries a variance estimate. All experiments use a single seed (42), while two of the nine main-table reductions are 1.4% and 1.8% and POMA's margin over the strongest non-learned rule is 0.0036. The loss weighting is not specified: Section 3.3.2 states that the controller rules and any applicable clipping bounds "are backbone-specific and are therefore not represented by a single shared formula", yet these weights balance the regression term against both alignment terms and are updated once per epoch. This also sits awkwardly beside Section 4.3, which reports results obtained "without backbone-specific tuning". Four details of the GRPO procedure depart from the standard formulation without comment. Proposals exceeding Kmax = 5 are truncated to the entries with the largest logits, but Equation (8) still scores the executed subset with the factorized Bernoulli expression, which is not the probability of the action actually taken, so the gradient is biased. The ratio in Equation (11) is taken against the reference policy rather than the behaviour policy that drew the samples, while the same reference policy supplies the KL penalty, so clipping does not bound the step relative to the sampling distribution. Whether the designated empty control slot enters the group statistics used for advantage normalisation is not stated. And a slot counts as valid "only if its evaluator successfully returns a metric", with no failure condition, rate, or treatment of invalid slots given, which leaves the effective group size unknown.
Questions for authors
  1. What labelling situation does the SCOPE-BENCH label pattern correspond to? The split leaves five of the twelve descriptor clusters with no labelled molecules. Those twelve cells partition the whole scaffold space, so a broad labelling effort would be expected to touch every cell, and standard practice in experimental design and active learning is to sample across a space rather than to leave regions of it empty. QM9 sharpens the point: it is an exhaustive enumeration of a bounded region of GDB-17, so the five empty clusters are produced by the split rather than observed in the data. What acquisition process would produce this pattern?
  2. Is SCOPE-BENCH intended as a stress test, or as an estimate of the degradation to expect in practice? If it is a stress test, then 5.9x is a stress-test figure. Figure 1 is labelled "Overestimated Generalization", which is a claim about how the community currently assesses generalization, and a claim of that kind needs a realistic setting behind it. I would ask for the abstract and Figure 1 to be calibrated to whichever reading the authors intend.
  3. If the split is instead meant to model real acquisition bias, where regions such as macrocycles and rare heterocycles are under-represented because of medicinal-chemistry practice and patent avoidance, why is k-means++ over four descriptors of an exhaustive enumeration the right model of that bias, rather than a split built from an actually biased source, for instance scaffold frequencies in ChEMBL? Answering these requires no new experiments, and a clear answer to any of them would raise my assessment of the benchmark contribution.
  4. What is included in 4.5 Hours per target? Does deployment re-run GRPO, and how many adaptation epochs does the target receive? Is it possible to reuse some model or skip some steps if the targets are very similar?
  5. On scaffold 14 of Table 3 (ViSNet, HOMO), POMA raises the error from 0.0574 to 0.0751. Since the target has no property labels, is any observation available that would predict this and fall back to the unadapted model?
7 comments
AuthorsOpenReview ↗

Author Response (1/7)

We thank you for carefully reviewing our paper and raising specific questions. We have added results on computational cost, structural diagnostics, the nearest complete source-cluster comparison, and cross-dataset experiments.

For q4:

The approximately 4.5 GPU-hours per target mentioned in your comment were measured in a shared GPU environment, where other tasks were running concurrently and slowed down our GRPO policy optimization. To re-evaluate the computational cost, we measured it in an isolated NVIDIA H200 environment. The average cost per target is as follows:

Computational stageAverage GPU-hours per target
GRPO policy optimization1.54
Target-specific model adaptation1.98
Total3.52

Here, 1.54 GPU-hours is the average GRPO policy-optimization cost per real target, and 1.98 GPU-hours is the average domain-adaptation cost per target.

For a new real target with a similar structure, the structural similarity to the existing proxy-scaffold set can be used to assess whether the previously optimized source-selection policy can be reused. Specifically, for a new unlabeled target scaffold xx, we calculate its maximum Morgan similarity to the 20 proxy scaffolds used for policy training, denoted by P\mathcal P:

s(x)=max⁡p∈PSim⁡Morgan(x,p).s(x)=\max_{p\in\mathcal P}\operatorname{Sim}_{\mathrm{Morgan}}(x,p).

If s(x)s(x) reaches a threshold τ\tau, calibrated in advance on independent development/validation targets, the existing GRPO policy can be reused preferentially. If it falls below the threshold, the proxy set is reconstructed and the policy is re-optimized.

We obtained quantitative evidence for this criterion from real targets in a supplementary experiment. We followed the proxy-scaffold selection procedure used in GRPO, calculated the maximum Morgan similarity of 15 real targets to the existing proxy set, and paired these values with the Seed-42 ViSNet–HOMO MAE improvements. The Spearman rank correlation was ρ=0.6638\rho=0.6638, with a two-sided p=0.00696p=0.00696 and a bootstrap 95% percentile confidence interval of [0.2395,0.8514][0.2395,0.8514]. The target-level results are as follows:

ScaffoldTarget fileMaximum Morgan similaritySeed-42 ViSNet–HOMO MAE improvement
1a0130.7606+11.37%
2a0010.4899+18.06%
3a0220.4622+0.00%
4a0090.5715+22.44%
5a0310.5103+0.00%
6a0160.7606+17.40%
7a0290.5893+4.19%
8a0150.7606+1.44%
9a0370.4615+0.00%
10a0300.4622+0.00%
11a0330.5000+2.91%
12a0340.3846+0.00%
13a0360.3846+0.00%
14a0110.4419−30.84%
15a0230.4725+12.32%

As shown in the table, targets with lower similarity include negative- or zero-gain cases. The six real targets with zero gain were reverted to the supervised model by our gating mechanism; 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 serves 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 provides an actionable basis for policy reuse.

AuthorsOpenReview ↗

Author Response (2/7)

For w1:

You point out that the current benchmark excludes many long-tailed scaffolds containing only one or two molecules, and that POMA's performance in extremely low-resource settings therefore remains unclear. Here, it is important to distinguish source-domain sample size from target-domain sample size. POMA does not use target-domain property labels, but it still requires a sufficient number of target molecular structures to construct proxy tasks and perform unlabeled adaptation. For source domains, sample size affects the reliability of supervised regression and contributes to source-domain weighting through log⁡(1+∣Dcj∣)\log(1+|D_{c_j}|) in Eq. (4).

The minimum sample-size requirement for target scaffolds in this work is intended primarily to ensure that each scaffold-level test MAE is evaluated with sufficient test samples; it does not require property labels from the target domain. For a source scaffold containing only one or two molecules, treating it as an independent adaptation unit indeed makes it difficult to obtain stable covariance estimates and supervised signals. In practical applications, such rare scaffolds can be assigned to higher-level scaffold families according to their chemical structural relationships before source-domain organization and selection, avoiding independent adaptation based on extremely few samples.

Thank you for noting that our current experiments focus on QM9 and three electronic properties: HOMO, LUMO, and Gap. Although HOMO, LUMO, and the HOMO–LUMO gap all describe frontier molecular orbitals, they are distinct prediction targets: HOMO is the energy of the highest occupied molecular orbital, LUMO is the energy of the lowest unoccupied molecular orbital, and Gap is the difference between the two. A statistical summary of the full QM9 dataset reports means and standard deviations of −6.5300 and 0.6022 eV for HOMO, 0.3027 and 1.2772 eV for LUMO, and 6.8328 and 1.2931 eV for Gap. Their central values and dispersions therefore differ. Our results across the nine backbone–property combinations also show different improvement ranges: 2.8%–8.6% for HOMO, 8.5%–11.2% for LUMO, and 1.4%–7.3% for Gap. These results show that POMA improves performance across the three frontier-orbital targets, although the gains vary with the property and backbone.

To demonstrate that our method is not limited to QM9, we selected a drug-like molecular dataset closer to real drug-discovery settings for supplementary experiments. We further ran the complete POMA pipeline on eight target scaffolds in QMugs. QMugs is derived from bioactive molecules in ChEMBL. Its dataset description reports 665,911 drug-like molecules and approximately 1.99 million conformers, with an average of 30.6 heavy atoms and a maximum of 100. In comparison, QM9 has an average of approximately 8.8 heavy atoms and a maximum of 9. QMugs therefore extends the evaluation to larger molecular structures with greater relevance to drug discovery. POMA achieves a lower MAE on seven of the eight targets, as shown below.

Target scaffoldSupervised ViSNet MAE (eV)POMA MAE (eV)MAE reduction
10.11380.1097+3.6%
20.12210.1188+2.7%
30.11780.1070+9.1%
40.13570.1365−0.6%
50.13470.1295+3.9%
60.09300.0852+8.3%
70.15490.1492+3.7%
80.08210.0761+7.3%

For HOMO prediction on the eight real target domains in QMugs, POMA improves performance on seven targets, with only a small negative gain on scaffold 4. This result indicates that our method is effective not only on QM9 but also on a drug-like molecular dataset.

AuthorsOpenReview ↗

Author Response (3/7)

For w2 and q1-3:

First, SCOPE-Bench is designed as a controlled cluster-level OOD stress test, rather than a probabilistic model of the real-world molecular annotation process. The five target clusters without training labels in QM9 result from the experimental protocol's deliberate holdout. Clustering is used to construct reproducible structural-region holdout conditions and to evaluate prediction and unlabeled adaptation when property labels are unavailable in the target regions.

Accordingly, the 5.9× value represents the average error ratio relative to a conventional scaffold split under the current controlled partition. It measures the challenge that this stress test poses to model extrapolation; it does not represent a performance-degradation factor that generally occurs in real-world drug discovery. We will make the positioning consistent across the abstract, introduction, and Figure 1 in the revision.

The ChEMBL scaffold frequencies you suggest are suitable for studying data-collection bias in real drug discovery. In contrast, the k-means++ procedure in this work is used to organize reproducible structural regions within a fixed molecular pool. These approaches address different questions. Regarding your concern about local structural overlap and whether SCOPE-Bench sufficiently realizes its stated motivation, we added a comparison with conventional Bemis–Murcko splitting. The results are shown below.

MetricRandom molecular splitConventional Bemis–Murcko scaffold splitSCOPE-Bench cluster-level split
Mean nearest-training-molecule Tanimoto similarity0.61180.52980.4991
Median nearest-training-molecule Tanimoto similarity0.61540.50000.4828
95th percentile of nearest-training-molecule Tanimoto similarity0.76190.75000.6923
Fraction of test molecules with nearest-neighbor similarity ≥ 0.80.03640.03330.0113
Fraction of test molecules with nearest-neighbor similarity ≥ 0.90.00920.01050.0018
BRICS fragment-type coverage0.21570.03950.0134

Morgan fingerprints encode local atomic environments, and the Tanimoto coefficient measures the similarity between two fingerprints. For each test molecule, we calculate its maximum similarity to the training molecules and then report the mean, quantiles, and fractions of test molecules with highly similar nearest neighbors. BRICS fragments molecules according to chemical-bond rules. Fragment-type coverage is the number of distinct fragment types in the test set that also appear in the training set, divided by the total number of distinct fragment types in the test set.

Compared with the conventional Bemis–Murcko split, SCOPE-Bench reduces the mean nearest-neighbor similarity from 0.5298 to 0.4991, the fraction of test molecules with nearest-neighbor similarity of at least 0.8 from 0.0333 to 0.0113, and BRICS fragment-type coverage from 0.0395 to 0.0134.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Manuscript revisions following the discussion

Dear Reviewers and Area Chairs,

Thank you for your careful reading and suggestions. The revised manuscript now includes the additional experiments and clarifications discussed in our rebuttal. To make these changes easier to find, we have marked the revisions and additions in blue.

  • The choice of CORAL and the need for dual-scale alignment require an explicit rationale. Section 3.3.2 on p. 5, lines 243–250, now explains this design through our preliminary observations with MMD and DANN and the complementary roles of whole-molecule and BRICS-substructure alignment.

  • The use of backbone-specific controllers raised questions about target-specific tuning. We clarified on p. 9, lines 473–475, that each backbone's controller settings remain fixed across targets rather than being tuned separately for each target.

  • The GRPO description lacked sufficient detail about action scoring, reward processing, and policy updates. The revised description covers action scoring after truncation, the empty control, reward processing, valid evaluations, the reference penalty, entropy regularization, and frozen old-policy scores on p. 6, lines 282–323, and p. 7, lines 352–354. Appendix A, Algorithm 1, on p. 13, lines 653–687, specifies the corresponding sequence, proxy self-exclusion, duplicate filtering, reference synchronization, and supervised fallback. The positive-reward multiplier α+=20\alpha_{+}=20 is listed in Appendix F, Table 12, p. 19, line 1014.

  • The relevance of proxy coverage to real-target gains and the conditions for policy reuse needed further examination. The added coverage–gain analysis appears on p. 9, lines 484–485, with Pearson and Spearman statistics in Table 4 on p. 10, lines 486–493. Section 3.3.3 on p. 7, lines 362–369, describes a reuse criterion with a threshold to be calibrated on independent development or validation targets. Lines 359–361 explain the compatibility gate and supervised fallback.

  • Concurrent GPU workloads can affect the reliability of runtime measurements. Measurements were repeated on an isolated NVIDIA H200 GPU without competing workloads. Section 3.4 on p. 8, lines 390–392, reports 1.54 GPU-hours per target on average for GRPO policy optimization and 1.98 GPU-hours for target-specific adaptation.

  • Scaffold disjointness alone does not establish reduced local structural overlap. To examine this directly, we added Morgan nearest-training-molecule similarity and BRICS fragment-type coverage comparisons across random, Bemis–Murcko, and SCOPE-Bench splits. Table 2 on p. 8, lines 378–386, gives the results, and lines 424–431 define the measures and discuss the comparison.

  • The contributions of source selection and dual-scale adaptation needed to be distinguished. Section 4.4 on p. 10, lines 509–524, now explains the controls in the two existing ablation groups: fixed dual-scale CORAL when comparing selectors and a fixed GRPO policy when removing one alignment scale. Table 3 on p. 9, lines 432–448, reports the results.

  • The need for scaffold-level selection required comparison with the simpler nearest-cluster alternative. We added this comparison on p. 9, lines 476–480. Appendix D.1 defines the baseline on p. 17, lines 913–917, and Table 10 on p. 18, lines 918–941, provides the full 15-target comparison and its aggregate results.

  • Only one random seed does not show how much performance varies across runs. An independent seed-21 ViSNet–HOMO run was added on the same 15 targets. The setup is on p. 8, lines 402–404, and the summary on p. 9, lines 480–483. Appendix B.1 explains the mean and sample SD on p. 14, lines 734–738. Table 6 on p. 15, lines 756–773, gives the target-level statistics for seeds 21 and 42.

  • Evaluating the generalization ability of our method should not be limited to QM9. To assess performance beyond this dataset, the complete POMA pipeline was evaluated for HOMO prediction on eight QMugs target scaffolds. The motivation appears on p. 9, lines 484–485, followed by the dataset comparison and results on p. 10, lines 494–499. Appendix B.2 and Table 7 on p. 15, lines 775–790, give the individual results. This extension is also summarized in the abstract on p. 1, lines 29–31, and conclusion on p. 10, lines 535–536.

  • Figure 2 was difficult to read, while Figure 4 occupied more space than necessary. We redesigned and enlarged Figure 2 on p. 3, lines 108–134, removing dense formulas, replacing “Meta Features” with “Similarity and Sample Size,” and describing the weight controller in words. Figure 4 now uses a more compact layout on p. 9, lines 449–461. Related Work was streamlined on p. 2, lines 106–107, and p. 3, lines 136–146. The conclusion is now one paragraph on p. 10, lines 528–539.

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

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