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Under review as a conference paper at ICLR 2027

Regional Mass Audits for Correcting Neural Samplers

Abstract

Neural samplers can generate samples from every mode of a target distribution while producing them in the wrong proportions. We propose regional mass auditing to guide correction using target probabilities or reference data. The audit selects an under-represented region and estimates its probability deficit on data held out from selection. This deficit guides where to obtain additional samples and which examples to use for fine-tuning. Valid probability bounds determine how many samples can be added without over-filling the region at a specified confidence level. When the additional samples follow the target distribution conditioned on the region, the same bounds give a computable lower bound on the reduction in Kullback-Leibler divergence. We compare audit-guided and untargeted correction at matched sampling or training budgets on synthetic distributions, particle systems, and proteins. Audit-selected simulation starts improve particle-distance and protein free-energy estimates. Fine-tuning neural samplers with selected data improves regional probabilities in newly generated samples. For proteins, fine-tuning coarse-grained potentials with selected reference structures also improves several structural and free-energy estimates.

Primary area:
probabilistic methods (Bayesian methods, variational inference, sampling, UQ, etc.)
Keywords:
neural samplers, Boltzmann generators, selective inference, distribution-free uncertainty quantification

Reviews

Among:
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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_M2WROpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
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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
  1. 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.
  2. 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?
  3. 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?
  4. Proposition 1 assumes exact conditional target sampling from p(⋅∣A)p(\cdot\mid A), 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 p(⋅∣A)p(\cdot\mid A), and establish conditions under which the KL improvement guarantee remains valid?
5 comments

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 BendB_{\mathrm{end}} 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=qp=q (revised Table S.1):

Selection / assessmentEmpiricalBounds
Same data100%71.8%
Independent data48.3%0.9%

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):

ProcedureSearch force evaluationsPair-distance W1W_1
Uniform-flagged, full search2,850,0000.0803
Uniform-flagged, reduced search51,0000.0798
Model starts, matched force evaluations00.1919

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):

ProteinAudit (s)Training (s)Audit / trainingCPU assignment + bounds (s)
Chignolin118712.6%0.09
Villin232349.8%1.19
Protein G415507.5%3.20

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=4000B=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.

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 splitEqual reductions (κ=0\kappa=0)Unequal reductions (κ=1\kappa=1)
1,5000.00870.0236
6,0000.00920.0283

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 K=32K=32, n=6000n=6000, κ=1\kappa=1: 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)):

KKWeighted − uniform-flagged
4−0.019
8−0.099
16−0.120
32−0.111

Results are means over 5 seeds per KK, using 2,000-step simulations from model-generated structures. Weighting lowers mean free-energy error at each tested KK. In the supplementary-sampling experiments, it also lowers this error by 0.024–0.053 kT at B=500,1000,2000,4000B=500,1000,2000,4000 (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 rr on CC, including samples that leave AA, when the audit bounds hold and the budget rule is followed. The KL guarantee additionally requires samples from the target conditioned on AA. For DW4, we examined deficit-weighted correction with 1,172 chains of 200 MALA steps: 91.8% fall in AA, compared with 33.4% of original-model samples. The table compares samples within AA against held-out references (revised Appendix D.3, Table S.4):

Samples within AAPair-distance W1W_1Energy W1W_1TV across basins
Additional samples0.01110.0900.036
Original model samples0.01470.1090.020
Independent reference samples0.00680.0590.011

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 AA. This gives basin TV of 0.016 versus 0.019 for model samples, and pair-distance W1W_1 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 r(A)=1r(A)=1 and finite KL(pC∥qC)\mathrm{KL}(p_C\|q_C), and let ε\varepsilon bound KL(pC(⋅∣A)∥r)\mathrm{KL}(p_C(\cdot\mid A)\|r). 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.

Reviewer_HXfyOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

The paper addresses the problem that neural samplers often visit all modes of a target distribution yet assign them incorrect relative masses. The authors propose a "regional mass audit": partition the audited domain into cells, select a region "A" as the union of cells whose estimated probability is deficient, and use held-out data to compute one-sided Clopper–Pearson bounds on the target mass and the model mass. These bounds determine correction weights that avoid overfilling the selected region. When corrective samples follow the target conditional distribution, the authors additionally derive a computable lower bound on forward-KL improvement. The audit is applied to supplementary sampling and model fine-tuning across synthetic distributions, particle systems, and proteins.

The strongest contribution is the connection between an interpretable probability deficit and a finite-sample correction budget. However, the molecular experiments mainly establish improvements in particular finite-horizon output distributions. They provide less evidence about equilibrium accuracy, robustness to reference uncertainty, or improvement over standard reference-distribution fine-tuning.

Critical strengths
  1. A well-motivated problem and coherent theoretical construction. Theorem 1 correctly uses independent assessment to avoid selection bias. The budget rules and Proposition 1 follow from transparent probability and KL arguments.
  2. Honest and careful experimental design. The authors report worsening NLL, metric-dependent outcomes, and reversals at larger correction budgets. These results make the study more informative.
Critical weaknesses
  1. The molecular audit’s uncertainty estimates are insufficiently validated for metastable trajectories. Theorem 1 assumes independent assessment samples, whereas the molecular experiments use an approximate effective-count adjustment. Appendix D.4.5 assigns the full sample count when the membership sequence is constant or its block variance is zero. A trajectory trapped in one state can therefore receive unjustifiably narrow intervals precisely when exploration is inadequate. The reported reference-subset checks do not establish reliability in this regime. Although the authors acknowledge that these intervals are approximate, this unresolved failure mode weakens confidence in the regional deficit estimates that drive molecular correction.
Questions for authors
  1. Does audit-selected CG fine-tuning outperform training on an equally sized random sample of reference frames?
  2. Do protein improvements persist across longer simulations and different initializations?
  3. How does the effective-count rule behave when a trajectory observes no transitions between relevant states?
4 comments

We thank the reviewer for highlighting the connection between regional deficits and finite-sample correction budgets, and for recognizing the care taken in our experiments.

Q1: Comparison with training on random reference frames.

Audit-selected training gives lower mean free-energy error than training on random reference frames on all 3 proteins. Table 5 of the original submission compares audit-selected training with uniform-all, which assigns equal nominal frame counts to each cell. For the new baseline, we sample the same number of reference frames uniformly from the training half, without balancing cells. Audit-selected training allocates frames according to the selected cells' deficit scores. Both methods use the same initial model, loss, optimizer, and training budget; only frame selection differs. We evaluate 2,000-step simulations from original-model structures against held-out reference data.

ProteinAudit − random (kT)
Chignolin−0.421 ± 0.073
Villin−0.120 ± 0.038
Protein G−0.059 ± 0.027

Entries are mean ± SD of paired free-energy error differences over 5 seeds per protein. Mean energy distance is also lower with audit-selected training on all 3 proteins. These results show a benefit from selecting reference frames at the same data and training budget (revised Appendix E.3.2, Table S.7).

Q2: Longer simulations and different initializations.

The improvements persist over longer simulations from both model-generated structures and heated model structures. We extended evaluation to 30,000 steps on chignolin and 10,000 on villin, respectively 15 and 5 times the lengths in Section 5.3 of the original submission. For the heated initialization, model structures undergo 2,000 steps at 500 K before returning to the original evaluation temperature. At every tested length and under both initializations, the audit-selected potential gives lower mean free-energy error than the original potential and the potential trained on random reference frames.

Protein / stepsInitializationAudit − original (kT)Audit − random (kT)
Chignolin / 30,000Model−0.441 ± 0.107−0.960 ± 0.115
Chignolin / 30,000Heated model−0.447 ± 0.113−1.020 ± 0.126
Villin / 10,000Model−0.352 ± 0.039−0.067 ± 0.040
Villin / 10,000Heated model−0.380 ± 0.070−0.057 ± 0.059

Entries are mean ± SD of paired differences over 5 seeds per protein; negative values indicate improvement. The table shows the longest simulations. Revised Appendix E.3.2, Table S.8 reports all tested lengths.

Q3: Rare transitions and effective sample size.

When no transitions occur, the fallback rule sets the effective sample size (ESS) to the total frame count. This can produce intervals that are too narrow. We checked the model and reference data in 24 audits and found that the fallback was never used. Our new 4-well test also finds coverage below the nominal level for the block adjustment when transitions are rare. As stated in Appendix D.4.5 of the original submission, these intervals are approximate.

We therefore added a separate assessment without the ESS approximation. We first split trajectories into selection and assessment sets, then constructed the partition and selected a new region A′A' using only selection trajectories. For assessment, we randomly selected 1 frame from each of 16 held-out trajectories per distribution. The binomial bounds are valid when trajectories are independent and each selected frame follows the target or model distribution being assessed. Frames within each trajectory may be correlated, since assessment uses only 1 frame per trajectory.

ProteinPositive deficit bounds / assessments
Chignolin10/10
Villin8/10
Protein G7/10

This separate assessment detects regional deficits in all 3 proteins without using the ESS adjustment (revised Appendix D.4.5).

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.

AuthorsOpenReview ↗

Follow-up on our ealier rebuttal

Dear Reviewer HXfy,

We have added a search-budget experiment and would like to highlight how it complements our earlier response.

For your question about random reference frames, Table S.9(a) also shows the comparison with 4, 8, 16 and 32 audit cells. On chignolin, audit-selected training lowers mean free-energy error by 0.421-0.457 kT compared with training on random reference frames, using 5 seeds per setting and the same planned training budget. The advantage over random selection therefore holds across the tested cell counts (revised Appendix E.3.2).

In the new experiment, we changed the search used to construct the audit cells. We tested 4 settings, with 128-1,024 starting structures and 150–600 search steps, using the same 5 seeds for each of the 3 proteins. We kept the data, cell count and correlation adjustment fixed. Whenever the audit detected a deficit at the original search setting, it also detected a deficit at every other tested setting, even when the selected region changed (revised Appendix D.4.1).

For your concern about correlated trajectories, our earlier response reports a separate check using 1 randomly selected frame from each held-out trajectory. This avoids estimating how many independent observations a correlated trajectory contains. The probability bounds require independent trajectories and the correct target or model distribution for the selected frames, as stated in our response (revised Appendix D.4.5).

We would appreciate your feedback on this check and any remaining concerns about the probability bounds.

Dear Reviewer HXfy,

With the discussion period ending soon, we would appreciate your feedback on our responses and additional results. We have addressed the random-frame comparison, longer simulations, and your concern about correlated trajectories. Could you let us know whether any concerns remain? We would be happy to clarify them before the discussion closes.

Thank you for your time.

Reviewer_5PhmOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
1
Presentation
3
Soundness
1
Read review
Paper summary

The paper proposed to augment or finetune neural samplers with a held-out selection of data samples according to their over/underrepresentation by the sampler. The regional training is constrained by theoretical confidence bounds to avoid over-filling of the targeted region in the finetuning process. The audit-selected regional finetuning improves the generated sample distribution in diverse set of problems including synthetic simulations and real world protein structure problems, leading to more accurate structural and free energy computation in the latter.

Critical strengths

The method proposed in the paper can be developed in a systematic way to identify probability deficit regions in a neural sampler and improving the mode coverage and proportion or the modes in comparison in comparison to alternative baseline approaches.

The paper provides experiments on complex and synthetic scenarios to illustrate the performance of the proposed method

Critical weaknesses

Some of the crucial details of the audit correction method are missing from the main text and also are not specified in the setup of empirical experiments.

1 - How is audit region chosen? Is it some based on an analytical criteria or constraints on coordinates?

2 - How is the audit region partitioned into cells? is it a simple grid or a data dependent approach? This matters both in the computation complexity of the proposed method and I suspect in the performance as if cells are chosen too small the accumulation of probability deficit into an aggregated set AA takes longer, but if they are chosen too large the estimated confidence bounds are going to be trivial. Is there any expert knowledge required to chose the partitions? if so what properties of the target / model distributions should be considered?

3 - As the method doesn't specify the partitioning granularity, there is the issue of soundness of the proposed method, in the case of the claims of matching probabilities. This is not possible in case of large partitions unless for special distributions and discrete cases. Shouldn't there be a need for an iterative correction approach for increasing granularity? Are the corrections applied only once?

4 - After cells with highly confidence deficit are identified, what are the example sampling methods that can provide samples from A or provide more samples from A? Is this step going necessarily dependent on a long MCMC chain? Shouldn't there be converges tests to ensure more samples from A exist in the new batch of samples?

5 - The number of new data samples are chosen based on the bound on λ\lambda to not over-fill the target region. On the other hand finetuning loss is based on a different parameter η\eta which undermines the computations for over-filling in section 4.2 and leads to a different mixture distribution optimal than mλm_\lambda. In fact choosing η≈1\eta\approx 1 leads to over fitting on the new samples. How should η\eta be selected?

6 - Budget doesn't account for reference generation. This is not realistic in most of the sampling applications, as the generation of samples requires running an expensive simulation on evaluating a very complex energy function repeatedly, limiting the application scope of the proposed method.

7 - Not enough experimental results to show the reliability of the method. Some ablation studies on the audit region and cell partitioning, comparison of the two bounds on λ\lambda, choice of η\eta are definitely required for better assessment of the proposed method.

Questions for authors

See previous section.

9 comments

We thank the reviewer for recognizing the value of identifying probability deficits and for highlighting our experiments on synthetic and molecular systems.

Q1: How is the audit region selected?

As described in Section 4.1 of the original submission, we estimate target and model probabilities in each cell using selection data. We combine cells whose estimated target probability exceeds their estimated model probability into AA, then fix AA and compute its deficit bound using independent assessment data. Coordinates or structural features define the cells; probability differences determine which cells enter AA. We have clarified this distinction in the revised manuscript.

Q2: Partition construction and sensitivity.

Appendices D.1–D.4 and E.1 of the original submission describe the cell construction:

SystemCell construction
GMM-40Nearest discovered energy minimum
Many-Well4 sign combinations of 2 double-well coordinates
DW4 / LJ13Energy-minimized basins represented by sorted pairwise distances
CG proteinsClusters of discovered energy minima represented by CA pairwise distances

We choose the structural features, the potential used to find energy minima, and the number of cells for each system. For protein basin search, we use released CG potential checkpoints. The number of cells affects which deficits can be detected. Under the sampling assumptions of Theorem 1, independent assessment gives probability bounds for the selected region AA as a whole, regardless of how many cells were considered during selection.

To test sensitivity to the number of cells, we varied KK from 4 to 32 on chignolin while keeping the nominal training budget fixed. We evaluated each trained potential using 2,000-step simulations from model-generated structures (revised Appendix E.3.2, Table S.9(a)). In the tables below, audit denotes audit-selected training and random denotes training on random reference frames.

KKAudit − originalAudit − random
4−0.263−0.431
8−0.296−0.421
16−0.289−0.457
32−0.272−0.440

Entries are mean paired differences in free-energy error (kT) over 5 seeds per KK; negative values indicate improvement. The gains remain similar across the tested cell counts. Across the 3 proteins, the audit takes 11–41 seconds including data loading. This is 7.5–12.6% of the mean training time across methods in the recorded runs (revised Appendix E.3.1, Table S.6).

Q3: Does correction require finer partitions or multiple rounds?

The audit controls the probability assigned to the selected region AA. Correction can also reduce KL divergence over the entire audited domain even with a coarse partition. Under the assumptions of Proposition 1 of the original submission, this holds when the deficit bound is positive, the correction weight satisfies the audit limit, and the additional samples follow the target distribution conditioned on AA. Finer cells may reveal additional deficits. The original correction experiments use 1 round; Appendix A.5 explains how to repeat the audit by dividing the total error allowance among rounds and using fresh assessment data each time.

We additionally tested 3 rounds of FAB fine-tuning with fresh selection and assessment data in each round. The table reports 4-cell L2L_2 error averaged over all 120 pairs of double-well coordinates and 8 seeds:

RoundAudit-selected dataUntargeted data
10.003690.00412
30.003850.00484

Audit-selected training retains an advantage over untargeted training at round 3. Revised Appendix E.2.5, Table S.5 reports all rounds.

Q4: How are corrective samples obtained and checked?

Appendix D of the original submission specifies the sampling procedures. Targeted and untargeted correction share the procedure and nominal budget within each experiment:

SystemCorrective sampling
Many-WellRejection sampling from the truncated target restricted to AA
GMM-40Importance-weighted resampling within selected cells
DW450- or 200-step MALA trajectories from selected model samples
CG proteins500-step Brownian trajectories from selected basin representatives

These procedures do not always require long MCMC chains. For molecular fine-tuning, we select training frames from existing reference data (Section 4.3 and Appendix E of the original submission). We checked DW4 correction using deficit-weighted allocation with 1,172 chains of 200 MALA steps, retaining 1 final structure per chain (revised Appendix D.3, Table S.4):

MeasurementOriginalAdditional
Fraction in AA33.4%91.8%
Pair-distance W1W_1 within AA0.01470.0111

Results are means over 10 simulation seeds. The within-AA distance comparison uses matched sample counts. Additional samples fall in AA more often, and their pairwise distances agree more closely with the held-out reference. The original GMM and Many-Well experiments also include independent re-audits for remaining deficits and over-filling. Proposition 1's KL guarantee additionally requires the corrective samples to follow the target distribution conditioned on AA.

Q5: How is the training weight related to the correction budget?

For FAB, maximum-likelihood training weights original-model samples by 1−η1-\eta and corrective samples by η\eta (Section 4.3 of the original submission). When all corrective samples lie in AA, the training mixture assigns probability (1−η)q0(A)+η(1-\eta)q_0(A)+\eta to AA. Appendix E.2 of the original submission reports 2 choices:

ChoiceRuleη\eta
Match estimated target mass[p^(A)−q^0(A)]/[1−q^0(A)][\widehat p(A)-\widehat q_0(A)]/[1-\widehat q_0(A)]0.0203
Avoid over-filling using audit bounds[Lp(A)−Uq(A)]/[1−Uq(A)][L_p(A)-U_q(A)]/[1-U_q(A)]0.0126

When the bounds hold, the second choice prevents over-filling in the training mixture. We evaluate the fitted flow separately using newly generated samples. With 414 corrective examples, this choice gives mean regional errors of 0.332 percentage points for audit-selected data and 0.663 for untargeted data. The generated frequency does not exceed the target upper bound in any of the 8 runs. The same appendix varies η\eta and sample count separately to distinguish their effects. For the other models, iDEM uses η=51/512\eta=51/512 for both training methods, while CG fine-tuning uses an estimated likelihood gradient without an η\eta coefficient.

Q6: Reference-generation cost and data requirements.

As stated in Section 5 of the original submission, we study correction when reference data are already available. Both methods share this pool and have matched nominal sampling or training budgets. The comparison tests whether regional selection makes better use of these data. For auditing, known or numerically bounded target probabilities can replace reference trajectories, as in Many-Well (Appendix A.2 of the original submission).

To test the reference-data requirements, we repeated chignolin selection and training using every second or fourth reference block. This retains 1/2 or 1/4 of the available data while leaving held-out evaluation data unchanged (revised Appendix E.3.2, Table S.9(b)):

Reference retainedAudit − originalAudit − random
Full−0.296 ± 0.079−0.421 ± 0.073
1/2−0.306 ± 0.041−0.455 ± 0.058
1/4−0.350 ± 0.088−0.473 ± 0.096

Entries are mean ± SD of paired free-energy error differences in kT over 5 seeds, using 2,000-step simulations from model-generated structures. With 1/4 of the reference data, audit-selected training still gives lower mean free-energy error than both controls.

Q7: Requested ablations.

The original and additional ablations are summarized below:

AblationEvidence
PartitionOriginal Appendix B tests K=8K=8–64. Our response to Q2 adds chignolin results at K=4,8,16,32K=4,8,16,32, with gains over both controls.
2 budgetsOriginal Appendix D.1 reports median Bend/B⋆B_{\mathrm{end}}/B^\star ratios of 1.84–2.01. Across 135 new GMM settings with 200 repetitions each, maximum observed over-filling is 2.5% for each rule at α=0.1\alpha=0.1, using independent Monte Carlo probability estimates. See revised Appendix B.1 and Table S.1 for the subset where p=qp=q.
Training weightOriginal Appendix E.2 varies η\eta with 414 examples, then sample count from 121 to 5,000 at η=0.0203\eta=0.0203. Our response to Q5 gives results with the weight chosen from audit bounds.

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.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of the discussion and manuscript revisions

Dear Area Chair and Reviewers,

Thank you for reviewing our submission and for your efforts during the discussion phase. We summarize the discussion and revisions below. References are to the revised manuscript.

Our paper uses regional probability deficits to guide additional sampling and select training examples. We use probability bounds from independent assessment to set correction budgets that avoid over-filling under the stated assumptions. Under its stated conditions, Proposition 1 gives a lower bound on KL reduction for correction using conditional target samples. We evaluate fine-tuning through new samples from the updated models.

M2WR reported that most concerns had been answered. 5Phm stated that most reproducibility concerns had been addressed and the experimental setup was clear. Both reviewers raised their scores. 5Phm's remaining questions concern guidance for new targets, repeated audits and their cost, and the availability of reference data.

1. Cell construction and parameter choices (5Phm).

Section 4.1 explains when to define cells by coordinate ranges, cluster reference samples, or use energy gradients to find low-energy structures. Detailed benchmark settings remain in Appendices D–E. We explain how cell size affects deficit detection. Under its sampling assumptions, Theorem 1 applies to partitions and regions chosen using selection data and fixed before assessment.

We did not choose cell-construction settings by comparing correction performance. Adjustments for numerical stability are described separately. For the main FAB comparisons, training weights are calculated from regional probabilities or audit bounds. For iDEM, corrective examples make up about 10% of each training batch on all 3 targets.

2. What the statistical audit adds (M2WR, 5Phm).

We test 4 combinations of independent assessment and confidence bounds to measure the effect of each. When target and model distributions are equal, the observed over-filling rate averages 0.9% with both, compared with 100% for empirical correction using the same data for selection and assessment. All methods use the same budget formula across 27 settings, with 200 repetitions each (Table S.1).

3. Selection benefits and sensitivity (HXfy, 5Phm, M2WR).

With the same planned number of training frames and training budget, audit-selected training lowers mean free-energy error relative to random-frame training on all 3 proteins, using 5 seeds each (Table S.7). Improvements over the original potential and random-frame training persist at 30,000 simulation steps on chignolin and 10,000 on villin, from model structures with or without heating (Table S.8).

On chignolin, the advantage over random selection holds at 4, 8, 16 and 32 cells, with 5 seeds per setting (Table S.9). Separate GMM and protein search-budget tests show that deficits detected at the reported settings remain detectable at the other tested budgets, even when the selected regions change (Appendices D.1.1 and D.4.1).

4. Correlated trajectories (HXfy).

We distinguish the approximate effective sample size adjustment from a separate check using 1 randomly selected frame from each of 16 held-out trajectories per distribution. This check gives positive deficit bounds in 10/10 chignolin, 8/10 villin and 7/10 protein G assessments. Its validity requires independent trajectories and the correct target or model distribution for the selected frames (Appendix D.4.5).

5. Repeated audits (5Phm).

The main correction experiments did not rebuild the partition and repeat assessment after a deficit bound of zero or less. Search-budget and cell-count comparisons are separate sensitivity tests. The 3-round FAB experiment instead audits the updated model before each training round, using new independent assessment data (Appendix E.2.5). Section 4.2 and Algorithm 1 distinguish a single round from optional repeated audits, whose cost includes every search, assessment and correction.

6. Cost and application scope (5Phm, M2WR).

In DW4, reducing search force evaluations by 98.2% gives similar mean pair-distance error, 0.0798 versus 0.0803. A control starting from model samples gives 0.1919 at the same total force-evaluation budget as the reduced-search method, counting search and dynamics (10 seeds, Table S.3).

DW4 force counts exclude reference generation and preliminary tuning. Generating a new reference adds to the total cost. Our protein experiments use existing reference simulations to improve a learned potential through selected training frames. Section 4.2 explains when to add samples and how to proceed if suitable corrective samples cannot be obtained within the budget. No reported correction or training run stopped because of insufficient data or budget.

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