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- Informativeness
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Paper summary
This paper proposes regional mass auditing to identify under-represented regions in neural samplers and guide corrective sampling and model fine-tuning. By combining sample splitting with confidence bounds, the method estimates regional probability deficits and determines correction budgets that prevent over-filling. The authors further establish a KL divergence improvement guarantee under exact conditional target sampling. Experiments on synthetic distributions, particle systems, and proteins demonstrate improvements in regional probability estimates and several structural and free-energy metrics.
Critical strengths
The paper addresses the practically important problem of incorrect probability mass allocation in neural samplers, even when relevant modes are covered. Its experiments across diverse sampling models and molecular systems demonstrate that targeting under-represented regions can improve sampling accuracy compared with untargeted correction.
Critical weaknesses
The proposed framework primarily combines established techniques. While this integration is practically useful, its added value over simpler discrepancy-guided selection strategies remains insufficiently demonstrated. In the chignolin experiments (Table 3), deficit weighting reduces free-energy error only modestly compared with uniform-flagged allocation (1.351 to 1.297 kT). Given the additional costs of region discovery and statistical auditing, it remains unclear whether the full framework offers a sufficiently substantial methodological and computational advantage over simpler region-selection approaches.
Questions for authors
- Could the authors compare the proposed confidence-bound-based auditing procedure with a simpler baseline that directly selects under-represented regions using empirical probability differences, without sample splitting or confidence-bound estimation? This would clarify whether the statistical auditing mechanism itself improves correction performance beyond basic discrepancy-guided selection.
- In the DW4 experiments, basin discovery requires approximately 2.85 million force evaluations, substantially exceeding the cost of the additional simulations at the main budget. Although a compute-matched control is included, can the authors provide a more systematic end-to-end cost analysis, including region discovery and probability assessment, particularly for the protein experiments?
- In Tables 2 and 3, uniform-flagged allocation already provides most of the improvement on some important metrics, while deficit weighting offers relatively modest additional gains. Under what conditions does deficit weighting substantially outperform uniform allocation over flagged regions, and are these gains consistent across different partitions and sampling budgets?
- Proposition 1 assumes exact conditional target sampling from , whereas the DW4 and protein experiments use finite MALA or Brownian dynamics trajectories that may leave the selected region. Can the authors quantify the discrepancy between these practical corrective distributions and , and establish conditions under which the KL improvement guarantee remains valid?
5 comments
Part 2
Q3: Selection versus weighting.
Uniform-flagged and deficit-weighted allocation use the same audit-selected region; they differ only in how samples are allocated within it. As reported in Sections 5.2 and 6 of the original submission, region selection provides most of the gain in the main DW4 and chignolin comparisons. To test when weighting adds value, we varied how strongly 8 Gaussian components were downweighted while keeping their combined model probability fixed. Weighting by estimated deficits gives larger gains as these reductions become more unequal (revised Appendix D.1.3, Table S.2):
| Samples per split | Equal reductions () | Unequal reductions () |
|---|---|---|
| 1,500 | 0.0087 | 0.0236 |
| 6,000 | 0.0092 | 0.0283 |
Entries are mean reductions in TV error relative to uniform-flagged allocation. TV compares target and corrected cell probabilities, and we average over tested settings where the audit detects a deficit. Weighting by deficit lower bounds also reduces TV at , , : across 3 component arrangements, TV is 0.0617–0.0652, compared with 0.0744–0.0838 for uniform-flagged.
We also compared weighting with uniform-flagged allocation across chignolin partitions. The table gives paired differences in free-energy error (kT; revised Appendix E.3.2, Table S.9(a)):
| Weighted − uniform-flagged | |
|---|---|
| 4 | −0.019 |
| 8 | −0.099 |
| 16 | −0.120 |
| 32 | −0.111 |
Results are means over 5 seeds per , using 2,000-step simulations from model-generated structures. Weighting lowers mean free-energy error at each tested . In the supplementary-sampling experiments, it also lowers this error by 0.024–0.053 kT at (Appendix D.4 of the original submission).
Q4: Finite dynamics versus conditional sampling.
The result in Section 4.2 of the original submission prevents over-filling for any corrective distribution on , including samples that leave , when the audit bounds hold and the budget rule is followed. The KL guarantee additionally requires samples from the target conditioned on . For DW4, we examined deficit-weighted correction with 1,172 chains of 200 MALA steps: 91.8% fall in , compared with 33.4% of original-model samples. The table compares samples within against held-out references (revised Appendix D.3, Table S.4):
| Samples within | Pair-distance | Energy | TV across basins |
|---|---|---|---|
| Additional samples | 0.0111 | 0.090 | 0.036 |
| Original model samples | 0.0147 | 0.109 | 0.020 |
| Independent reference samples | 0.0068 | 0.059 | 0.011 |
We match sample counts and report means over 10 seeds; the last row compares 2 finite reference sets. Additional samples are allocated according to the original model's deficits to correct the combined set. We therefore also compare the combined set with model samples, again matching counts within . This gives basin TV of 0.016 versus 0.019 for model samples, and pair-distance of 0.0103 versus 0.0145.
Appendix A.4 of the original submission analyzes approximate conditional sampling. In the revision, we give an explicit sufficient condition for KL divergence to decrease. Assume and finite , and let bound . When the audit bounds hold and the correction weight satisfies the limit in Section 4.2, overall KL decreases if
\qquad \beta = \frac{\lambda}{m_\lambda(A)}.$$ Here $\Delta_{\mathrm{audit}}$ is Proposition 1's lower bound on KL reduction, and $\beta$ is the fraction of the mixture within $A$ contributed by corrective samples. The inequality requires conditional sampling error to be small enough to preserve the KL reduction. The molecular results measure structural and energy errors; applying this KL result also requires a bound on conditional KL error.Dear Reviewer,
We are looking forward to your feedback and would greatly appreciate any further questions or concerns you may have.
If there are additional issues that require clarification or further experiments, an earlier response would help us better address them within the remaining rebuttal period.
Thank you again for your time and consideration.
Part 1
We thank the reviewer for recognizing the importance of regional probability errors and the benefits of targeting under-represented regions.
Q1: Added value over empirical selection.
Sections 4.1–4.2 of the original submission distinguish choosing where to correct from deciding whether and how much to correct. To test the added value of the audit, we compared it with an empirical baseline on a 20-component GMM, using 135 settings and 200 repetitions each (revised Appendix B.1). We hold the total data budget and the Bend formula fixed, and vary whether selection and assessment share data and whether the budget uses empirical probabilities or confidence bounds. The over-filling rates below are averaged over the 27 settings where p=q (revised Table S.1):
Both independent assessment and confidence bounds help avoid unnecessary correction. Across all 135 settings, the maximum observed over-filling rate is 2.5% for either audit budget at the nominal 10% level, assessed using independent Monte Carlo probability estimates. The audit thus checks whether the data support a deficit and limits the correction amount to control over-filling risk. Empirical correction can give lower error when deficits are large, but does not provide this risk guarantee.
Q2: Discovery and assessment costs.
The DW4 control in Appendix D.3 of the original submission matches the total force-evaluation budget, including search and dynamics. We additionally reduced the search force evaluations by 98.2% and obtained similar correction accuracy over 10 simulation seeds (revised Appendix D.3, Table S.3):
The selected regions have a Jaccard overlap of 0.985. We recompute the correction budget for each search; the control spends the corresponding total force-evaluation budget on simulations from model-generated structures. For proteins, we measured audit times including loading, basin search, cell assignment, and computation of the probability bounds. Training times are averaged across methods in the recorded runs (revised Appendix E.3.1, Table S.6):
The CPU timings come from a separate test with 22,500 frames and 8 centers used in place of discovered minima. They exclude search, clustering, and loading. Protein basin search uses 115,200 force evaluations, compared with 2,048,000 for fine-tuning dynamics and 2,000,000 for adding B=4000 samples. Search therefore uses 5.6% and 5.8% as many force evaluations, respectively. Fine-tuning also uses 204,800 parameter-gradient evaluations. For each potential and initialization, evaluating 1,200 chains for 2,000 steps requires 2,400,000 force evaluations. Search uses the protein-specific potential for chignolin and the general potential for villin and protein G; reference-generation costs are excluded, as specified in Section 5 of the original submission.